title stringlengths 15 163 | paper_decision stringclasses 4
values | review_1 stringlengths 853 32.6k | rebuttals_1 stringlengths 0 15.1k | review_2 stringlengths 1.03k 35.6k | rebuttals_2 stringlengths 0 15.1k | review_3 stringlengths 807 27.4k ⌀ | rebuttals_3 stringlengths 0 15k ⌀ | review_4 stringlengths 780 22.2k ⌀ | rebuttals_4 stringlengths 0 15.1k ⌀ | review_5 stringclasses 171
values | rebuttals_5 stringclasses 166
values | review_6 stringclasses 25
values | rebuttals_6 stringclasses 24
values | review_7 stringclasses 4
values | rebuttals_7 stringclasses 4
values |
|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|
DOLPHIN: A Programmable Framework for Scalable Neurosymbolic Learning | Accept (poster) | Summary: This paper introduces Dolphin, a novel neurosymbolic learning framework. Dolphin provides three key abstractions: symbolic objects, tags (which associate symbols with tensors), and distributions (which map symbols to probabilities). Leveraging this abstraction, Dolphin decouples symbolic and probabilistic computations, enabling vectorized probabilistic computation on GPUs. This allows Dolphin to efficiently handle large-scale batched data. To ensure end-to-end differentiability, Dolphin employs vectorized provenance semirings, enabling parallel gradient computation on GPUs. It also provides two customizable provenance mechanisms, DAMP and DTKP, allowing users to fine-tune symbolic differentiation. Dolphin introduces five core operations that facilitate batched data processing, complex control flows, and recursion. Furthermore, its seamless integration with Python and PyTorch allows users to easily develop and deploy complex neurosymbolic programs with flexibility. Experimental results across 13 neurosymbolic tasks demonstrate that Dolphin significantly improves computational efficiency while maintaining state-of-the-art accuracy, outperforming existing methods in scalability and performance.
Claims And Evidence: Yes, the claims are well supported.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: There are no theoretical claims in this paper.
Experimental Designs Or Analyses: Yes.
Supplementary Material: I read the appendix.
Relation To Broader Scientific Literature: This paper is related to the neurosymbolic programming research. The batch process of tags is largely related to MapReduce. The authors already provide detailed discussion of these backgrounds in the paper.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Strengths
1. Dolphin provides a practical and user-friendly solution for neurosymbolic programming. The GPU acceleration addresses a key limitation of previous methods like Scallop, offering a computationally efficient approach with just five core operations. Its seamless integration with Python and PyTorch significantly enhances usability and flexibility, making it more accessible for practitioners. Additionally, the provenance semiring framework provides a strong and elegant theoretical foundation for the proposed method.
2. The paper is well-written, easy to follow, and presents a thorough background analysis. It clearly explains the limitations of previous approaches and justifies the need for Dolphin, making it an engaging and informative read.
Weaknesses
1. The symbolic operations are restricted to semiring structures over tags, which may limit the expressiveness of symbolic programs. While this abstraction enables efficient GPU computation, it could potentially restrict the range of symbolic reasoning tasks that can be expressed within the framework.
2. The benchmarks primarily focus on relatively simple tasks and do not demonstrate Dolphin’s applicability to real-world, complex scenarios. The paper does not explore how Dolphin could be scaled to more sophisticated domains, such as robotics or autonomous driving, which may involve complex logical reasoning and control modules, as well as unstructured outputs from deep models (e.g., object detectors with noisy or non-standard outputs), which is not thoroughly discussed.
Overall, this is an excellent paper that presents an elegant solution to the key challenges of previous methods, particularly in efficiency and complexity. It brings neurosymbolic programming much closer to practical usability, a promising paradigm with the potential for significant impact on machine learning. Its seamless integration with Python and PyTorch further enhances its compatibility with existing deep learning pipelines. Thus, it would be exciting if the authors could further illustrate its potential to be really applied for large-scale applications.
Other Comments Or Suggestions: 1. It would be good to provide a simple example and more details about how the data are changing for each of the 5 operations. For example, in Union, what is the exact format of the returned data? Does it produce a list of tuples with tagged tensors? In Filter, what happens to the symbols that are filtered out? Do they become empty placeholders, removed entirely, or assigned a default value?
Questions For Authors: 1. The limitation parts have discussed that Dolphin can only deal with discriminative models. However, there are many non-standard discriminative models with multiple heads and complicated outputs, such as object detectors which are common in application domains. It would be good if the authors could provide a discussion or case studies on how Dolphin can be used with popular discriminative models in typical application domains. It will be very useful for practitioner who wants to use Dolphin in real-world scenarios.
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: We thank the reviewer for their suggestions and will add the discussions to the revised paper.
# Discussion on other uses of Dolphin
Dolphin can be used for any task where the output of a model can be cast as a distribution over probabilities, including discriminative models. Consider an example of autonomous driving, where an object detector is used to detect obstacles on the road. Commonly used models like Faster R-CNN (cite) output bounding boxes, class probabilities, and confidence scores for multiple objects in an image. One can create a custom Python class that associates the coordinates of each bounding box with a Distribution object over the classes and their probabilities output by the model:
```python
CLASSES = [‘car’, ‘person’, ‘shirt’, …]
class DetectedObject
def __init__(self, coords, score, class_logits):
self.coords = coords
self.score = score
self.distr = Distribution(CLASSES, class_logits)
```
One can then derive the probability that given a pair of objects, it represents a person inside a car:
```python
# function to check if one set of coordinates is inside another
def is_inside(coord_a, coord_b):
…
def person_inside_car = apply(o1.distr, o2.distr,
lambda c1, c2: c1 == “person” and c2 == “car” and is_inside(o1.coords, o2.coords))
```
Here, `person_inside_car` will be a distribution over “True” and “False”, giving the probability that detected objects `o1` and `o2` represent a person inside a car.
# Explanation of Operations
We describe the Filter and Union operations in more detail:
**Filter.** In the Filter operation, the symbols that do not satisfy the filtering condition are completely removed from the returned distribution. So consider a Distribution $$D :: \\{ 0 \rightarrow t_1, 1 \rightarrow t_2, 2 \rightarrow t_3\\},$$ with a filtering condition `lambda x: x % 2 == 0` which removes odd numbers from the distribution. The returned Distribution will be $$D_\text{filtered} :: \\{ 0 \rightarrow t_1, 2 \rightarrow t_3 \\}.$$
**Union.** In the Union operation, a new Distribution is returned that contains the symbols from both input Distributions. A Union can occur over any pair of Distributions regardless of the types of symbols. For instance, consider as inputs Distributions $$ D :: \\{0 \rightarrow t_1, 1 \rightarrow t_2, 2 \rightarrow t_3\\} \text{ and } D' :: \\{1 \rightarrow t\'\_1 , 4 \rightarrow t\'\_2\\}.$$
The output Distribution will be
$$D_\text{union} :: \\{0 \rightarrow t_1, 1 \rightarrow t_2 \oplus t'_1, 2 \rightarrow t_3, 4 \rightarrow t'_2\\}.$$
Note here that the tags for common symbols are disjuncted.
# Restricted to Semiring Structures Over Tags
While symbolic operations in Dolphin are indeed defined using semiring structures over tags—similar to existing frameworks such as Scallop—this abstraction is primarily introduced to facilitate efficient computations, including GPU acceleration, and has been shown to be quite flexible for solving neurosymbolic tasks. | Summary: This work presents DOLPHIN, a Python library that allows for efficient training of traditional neurosymbolic methods on CPUs and GPUs. The key idea is to accelerate probabilistic symbolic manipulations on GPUs, where other solutions (e.g., Scallop) rely on manipulations on CPUs.
In addition to the efforts in defining a Python library with abstractions and operations, DOLPHIN’s main conceptual contribution is a new provenance semiring, Differentiable Top-k Proofs with Add-Mult (DTKP-AM), which is a GPU-friendly vectorized approximation of the weighted model counting (WMC) version of DTKP.
Experimental results confirm that performing probabilistic symbolic manipulations on GPUs is indeed beneficial. Moreover, the new DTKP-AM provenance can improve the accuracy on one benchmark (HWF), while it performs on par (Path, CLUTRR, and Mugen) or worse (SumN) than a baseline provenance (DAMP).
Claims And Evidence: **Experimental design with tight timeout:**
I am skeptical concerning the comparison of accuracy and training time (until convergence) for different methods, given the very tight training time budget constraint (10 hours) on a consumer-grade GPU (NVIDIA GeForce RTX 2080 Ti). The accuracy comparison in Figure 5 can be seen as unfair since some of the methods have not been trained until convergence (e.g., Scallop on HWF-15/19). Disentangling training time from accuracy would give better insights, e.g., by comparing the time per epoch, the time to convergence without a hard timeout constraint, and the accuracy at convergence.
**No clear global benefit for DTKP-AM**
One of the main contributions of this paper, DTKP-AM, does not have a clear benefit across different benchmarks. Indeed, the results presented in the main paper primarily show another provenance semiring (DAMP). DTKP-AM is only beneficial in the HWF benchmark (see Figure 10). This could be due to the very low top-k used (k=1 for all benchmarks). The use of such low k might have been chosen to achieve competitive timing results compared to DAMP.
Methods And Evaluation Criteria: See comments on “Claims and Evidence” regarding **Experimental design with tight timeout.**
Theoretical Claims: This paper does not contain any proofs or theoretical claims.
Experimental Designs Or Analyses: See comments on “Claims and Evidence” regarding **Experimental design with tight timeout**
Supplementary Material: I read Appendices A, B, C, D, E, and G. Moreover, I had a brief look at the code. It would be good if the code could be open-sourced.
Relation To Broader Scientific Literature: Accelerating probabilistic manipulations in neurosymbolic models is an important problem to make these methods usable in practice. At least the introduction of DOLPHIN as a Python framework for performing probabilistic manipulations on GPUs is of value. However, the second contribution (DTKP-AM) does not have a clear benefit in practice (see my comments on “Claims and Evidence”).
Essential References Not Discussed: The following work accelerates arithmetic circuits (i.e., WMC) on GPUs. Hence, it should be discussed and possibly compared in this paper:
Jaron Maene and Vincent Derkinderen and Pedro Zuidberg Dos Martires, “KLay: Accelerating Arithmetic Circuits for Neurosymbolic AI,” ICLR, 2025.
Moreover, there are other works that introduce approximations for probabilistic manipulations:
Jaron Maene and Luc De Raedt, “Soft-Unification in Deep Probabilistic Logic,” NeurIPS 2023.
Emile van Krieken et al., “A-NESI: A Scalable Approximate Method for Probabilistic Neurosymbolic Inference,” NeurIPS 2023.
Other Strengths And Weaknesses: The introduction of the general “apply” function is appreciated, as goes beyond simple additive relations usually used in neurosymbolic benchmarking.
Other Comments Or Suggestions: Missing the date in the reference «Kambhampati, S., Valmeekam, K., Guan, L., Verma, M., Stechly, K., Bhambri, S., Saldyt, L. P., and Murthy, A. B. Position: Llms can’t plan, but can help planning in llm modulo frameworks. In Forty-first International Conference on Machine Learning.»
It would be good to add a reference when introducing Differentiable Add-Mult Probabilities.
The caption of Table 2 should mention that the presented numbers are in seconds.
Please provide more details on the chosen networks in Appendix D. E.g., the exact CNN architecture is not mentioned in D.2. Also, does the work use a pretrained network? Moreover, it is not clear what is trainable in D.5 regarding Roberta-base: do you train only the classification head? Do you use a pretrained network?
Questions For Authors: More experimental results without strict timeout constraints for a fair accuracy comparison would be appreciated (see comments on “Claims and Evidence” regarding **Experimental design with tight timeout**)
How does the accuracy and timing change for DTKP-AM when increasing k?
It seems that still a fair share of the compute time is spent on the CPU to perform symbolic manipulations (once for each batch). Wouldn’t it be possible to precompile the symbolic program and run everything on the GPU?
The results of the Scallop baseline on Mugen reported in Figure 5 (and Figures 8&9 in the appendix) are significantly worse than what the original work (Li et al. 2023) show in their paper. How serious were the efforts in reproducing that work? I would appreciate comments about the reason for this large discrepancy in the reproduction, beyond what is mentioned in Appendix D.7.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for suggestions on experiment design and additional literature. We will add the results from additional experiments discussed below in the paper and expand the related work.
# Scallop’s Performance on Mugen
Scallop’s Mugen results were obtained from their PLDI’23 artifact. Despite significant efforts, we were unable to reproduce those results, thus, we reported the numbers we observed. We reached out to the Scallop authors, who provided us with a different symbolic program that reproduced their results using DTKP-WMC (K=5). We also redesigned the Dolphin program for Mugen to be more batchable across samples, which we run with DTKP-AM (K=5):
Version|Framework|VTR|TVR|Total Time|Time per Epoch
-|-|-|-|-|-
1k|Dolphin|89.43|91.83|2.39e3|92.3
||Scallop|86.26|89.57|6.71e3|314.68
5k|Dolphin|95.03|95.36|1.15e4|470.05
||Scallop|91.26|94.03|3.59e4|1.58e3
While Scallop now converges, Dolphin still achieves higher accuracies and trains ~3.3x faster than Scallop.
# Experiment Results without a Strict Timeout
We ran the experiments until Scallop converged and report its accuracies. We will do the same for the other baselines in the revised version.
Benchmark|Dolphin Total Time|Dolphin Accuracy|Scallop Total Time|Scallop Accuracy
-|-|-|-|-
HWF-15|9.78e3|92.13|1.66e5|39.58
HWF-19|1.63e4|86.18|1.82e5|7.02
Path-256|1.94e4|82.62|1.14e5|83.01
Path-128|1.78e4|84.03|4.17e4|84.90
For Path-128 and 256, Scallop converges to Dolphin’s accuracies in \~11.6 and \~31.7 hours (\~2.4x and \~6x slower), respectively. For HWF-15, Scallop reaches 100% on only 2 seeds out of 6, but stays below 12.5% on the rest even after \~46 hours of training on average. For HWF-19, none of the 6 runs were able to converge after ~50 hours of training on average.
# DTKP-AM with Different Values of K
We report preliminary results of this experiment. As a general trend, with the exception of HWF-19, the value of K doesn’t have much impact on the final accuracy (Acc). Increasing K also does not significantly impact the per epoch time (T/ep) due to DTKP-AM's vectorizations.
Benchmark|K=1 Acc|K=1 T/ep|K=3 Acc|K=3 T/ep|K=5 Acc|K=5 T/ep|K=7 Acc|K=7 T/ep
-|-|-|-|-|-|-|-|-
Sum-15|9.61|37.21|10.81|47.70|10.51|53.52|10.21|58.54
HWF-19|8.94|1.21e3|99.15|1.40e3|96.89|1.33e3|95.75|1.46e3
Path-256|81.39|1.97e3|82.14|2.34e3|80.86|2.10e3|82.38|2.12e3
CLUTRR-4|53.62|240.50|48.52|257.89|50.35|261.31|48.17|257.99
Mugen-5K|(94.1/95.7)|460.38|(95.4/95.7)|464.68|(95.3/95.4)|470.05|(95.4/95.4)|465.10
# Benefits of DTKP-AM
Empirically, DTKP-AM offers an advantage over DAMP of ~2% pts on average across the complex versions of all tasks. It significantly outperforms DAMP by ~50% pts on HWF-15 and ~75% pts on HWF-19, while also yielding up to ~5% pts higher accuracy on Mugen and ~3% pts improvement on PathFinder.
# Model Details
For HWF/MNIST, we use the same CNN architecture as Scallop (will be added in Appendix D). For CLUTRR, we use Scallop’s Roberta configuration: a pretrained model (roberta-base) finetuned while training the classification head.
# Symbolic Computations on the GPU
Precompiling symbolic computations on the GPU poses a few challenges. First, it restricts symbolic programs to PyTorch tensor operations, a small subset of the Python functions Dolphin currently supports. Second, since we perform one set of CPU computations per batch (~16% of the train time per batch), there is limited scope for improving the training time. The parallelism will only occur across combinations of symbols, not over samples in a batch. Third, enumerating all possible combinations of symbols on the GPU could pose memory consumption issues on complex tasks, as seen with LTN.
One could potentially compile symbolic computations on the GPU by representing symbols as GPU tensors and implementing user-defined functions as tensor operations since Dolphin supports arbitrary Python objects. We tested this strategy on Sum-5, but it did not show any improvements in training time, and was 2 seconds slower to train per epoch. We consider developing efficient strategies for compiling symbolic computations directly onto GPUs an exciting direction for future research.
# Related Work
Thank you for highlighting these related papers. KLAY (ICLR’25) lacks released code, preventing direct comparison. It compiles symbolic and probabilistic computations into GPU operations by transforming arithmetic circuits from Boolean logic into layered tensor structures. In contrast, Dolphin separates CPU-based symbolic reasoning from GPU-based probabilistic computations. The paper also omits comparisons against LTN or Scallop on Dolphin’s benchmarks.
DeepSoftLog improves NTP by using probabilistic semantics instead of fuzzy semantics, enabling non-redundant proofs, well-defined proof scores, and non-sparse gradients. A-NESI uses learned neural models to approximate the exact probabilistic semantics of WMC, boosting scalability. We will include these works in the related work section. | Summary: This paper brings enhanced scalability to neurosymbolic learning. The authors introduce a framework which allows symbolic computation to be conducted on the CPU, and allows vectorized computation of probabilities on the GPU. The authors introduce several Pythonic programming primitives to facilitate writing neurosymbolic programs . The tool allows pluggable support for different vectorized provenances to compute symbolic gradients. The empirical results demonstrates that, in general, DOLPHIN is much more efficient than SoTA tools, and achieves comparable, if not better, accuracy on various neurosymbolic programming tasks.
Claims And Evidence: The claims are well-supported by the methodology and the experiments.
Methods And Evaluation Criteria: The proposed method and evaluation makes sense for the task at hand.
Theoretical Claims: N/A – There were no proofs to check.
Experimental Designs Or Analyses: I did not see any issues with the soundness of the experimental designs or analyses.
Supplementary Material: I reviewed Appendix A and D. I briefly looked through the other appendices.
Relation To Broader Scientific Literature: The authors present a solution to a known issue (the scalability issue) in neurosymbolic programming, demonstrating superior performance to SoTA techniques in the literature.
Essential References Not Discussed: Not that I am aware of.
Other Strengths And Weaknesses: Strengths:
- The paper addresses an important problem – making neurosymbolic learning more scalable. The framework is elegant and clean, and is - based on effective and impactful programming paradigms.
- The experimental results are thorough, and demonstrate superior performance of DOLPHIN over SoTA work.
- The paper provides fertile ground for new work and acknowledges certain limitations of their framework.
- The paper is very well-written. Even as someone who is not as familiar with neurosymbolic programming, I was able to easily grasp the - -concepts presented in the paper. The appendices provide useful background information for the reader.
Weaknesses
- I do not see any major weaknesses in the paper within the scope of the work presented.
Other Comments Or Suggestions: Minor Comments/Questions
1. Table 2 – it would be helpful to add the unit of time in the caption, or in the main body of the text.
2. Section 4.4 – The authors mention they “use” a certain provenance depending on the benchmark, but given the preceding sentence, does this mean that they report the corresponding provenance’s result for each dataset?
3. Do the authors have any conjectures about why DOLPHIN’s accuracy is slightly lower than Scallop in the CLUTTR benchmark?
4. Grammatical error (lines 107-108) – “enable to efficiently compute symbolic gradients” → “enable the efficient computation of symbolic gradients”.
Questions For Authors: I have no major questions that will affect my review. I have a few minor questions, which I wrote in "Other Comments Or Suggestions".
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their suggestions. We will add the unit of time in the caption of Table 2 and fix the grammatical errors they pointed out.
We indicate the provenance used for each benchmark in Section 4.4 (RQ2: Accuracy) and compare both provenances in Section 4.5 (RQ3: Provenance Comparisons).
The Dolphin CLUTRR program is designed for batched computations, unlike Scallop, which evaluates each sample independently. Moreover, the Scallop programs for CLUTRR-3 and CLUTRR-4 exhibit higher accuracy variance, indicating possible minor numerical issues or nondeterminism. We believe these factors account for the small (~2% pts) accuracy difference. | null | null | null | null | null | null | null | null |
Open-Set Text Classification with Limited Labeling Budget | Reject | Summary: This paper combines the problem setting of active learning and open-set recognition and proposes two techniques, namely, sample sparsification and sample amplification, for addressing open-set text classification with a limited labeling budget. The first sampling method finds a good quality subset of original samples, termed as a support set, to accommodate the labeling budget. The second method finds a set of samples from the unknown category, which is termed as an amplified set. Experiments demonstrate the effectiveness of the proposed methods.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: N/A.
Experimental Designs Or Analyses: The experiments look sound.
Supplementary Material: N/A.
Relation To Broader Scientific Literature: Related to text classification in NLP.
Essential References Not Discussed: Yes.
Other Strengths And Weaknesses: This paper primarily addresses the problems of active learning and open set recognition, proposing a method for each. However, these are long-standing issues in machine learning, and the proposed approaches are not particularly novel in terms of methodology. The paper does not clearly highlight the novelty of its proposed methods, nor does it explain the challenges and difficulties involved. Furthermore, the experimental section lacks any comparison with existing methods. Overall, this paper does not meet the high academic standards required for ICML.
Other Comments Or Suggestions: N/A.
Questions For Authors: N/A.
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: We thank the reviewer for reviewer our paper and comments. Our response for the comments are as below.
**Q1:** the proposed approaches are not particularly novel in terms of methodology. \
**A1:** We respectfully disagree with the reviewer. Our methodology is novel combination of many known and new steps that solves critical practical problems like reducing labelling budget and open-set text classification. To the best of our knowledge, finding quality samples without knowledge of labels has not been proposed before.
This is in line with "Supplementary Guidelines for Reviewing Application-Driven ML Submissions" (https://icml.cc/Conferences/2025/ReviewerInstructions) that states:
Originality need not mean wholly novel methods. It may mean a novel combination of existing methods to solve the task at hand, a novel dataset, or a new way of framing tasks or evaluating performance so as to match the needs of the user.
We hope the reviewer considers this and looks at the methods proposed in this paper with a different perspective. | Summary: For open set recognition in text, the authors propose using a support
set, which is a subset of original samples within a budget
(sparsification) and an amplified set that is in the unknown category
(amplification). To construct the support set, they cluster the
instances with HDBSCAN, generate bins based on distance from the
centriod in each cluster, and randomly sample instances in each bin.
For OOD (Out Of Distribution) data, they randomly select instances
from unknown categories in Voronoi regions of the original data with
an area larger than a threshold. For text data, they use SBERT for
the embedding space, which is fine-turned in a contrastive Siamese
manner. They also use TSNE to reduce the dimensions to 2 for
generating Voronoi regions.
They evaluate their approach on 6 text datasets and compare it with 2
existing approaches (SetFit and ALPS). Their approach combined with
SetFit generally has favorable performance. On one dataset, using
only sample sparsification seems to more accurate than SetFIT on
zero-shot multilingual transfer.
## update after rebuttal
After reading and responding to the authors' rebuttal, I decided to maintain my rating.
Claims And Evidence: While 6 text datasets are used, only 2 existing methods are compared.
Comparing with more existing methods would further support their
claim. Also, they need to combine their sample sparsification with an
existing approach (SetFit) to yield better performance. The paper
does not include results from SetFit with sample amplification.
Hence, how sample amplification can help is not clear.
Methods And Evaluation Criteria: The proposed methods and evaluaiton criteria are reasonable. Sample
sparsification is similar to stratified sampling based on distance
from the centroid. Using large Voronoi regions seem interesting;
however, those sparse regions are also far away from the dense
regions. Limiting Voronoi regions to 2D might be necessary due to
computation overhead, but could reduce performance.
Theoretical Claims: No theoretical claims.
Experimental Designs Or Analyses: The experimental designs and analyses are generally reasonable.
However, while results for combining sample sparsification and SetFit
are reported, those for combining sample amplification and SetFit
are not.
Supplementary Material: The supplementary materials include an ablation study on bin sizes
and visualization of the embeddings space via tSNE.
Relation To Broader Scientific Literature: Since only two existing methods are compared and the proposed method
is combined one of the existing methods to outperform, its
contribution is not high.
Essential References Not Discussed: Other OSR methods could be compared, for example:
Towards Open Set Deep Networks, CVPR 2016
Generative OpenMax for Multi-Class Open Set Classification, BMVC 2017
Learning a Neural-network-based Representation for Open Set Recognition, SDM
2020
Convolutional Prototype Network for Open Set Recognition, PAMI 2022
Other Strengths And Weaknesses: Sample amplification with large Voronoi regions is interesting. While
some OSR methods use samples from unknown categories, the proposed
method filters out those that are not in large Voronoi regions.
Sample sparsification and amplifications by themselves do not
outperform the two existing methods.
Other Comments Or Suggestions: Table 2: If boldface indicates the highest performance, two methods
have a tie of 0.78 with the IMDB dataset.
Questions For Authors: 1. Algorithm 2: Should RandomSampling() have a parameter for \bar{X}
so that OOD instances in \bar{X} are sampled in the V_i regions?
2. How is the threshold determined for the area of a large Voronoi
region?
3. While the # of clusters need not be specified in HDBSCAN, are
there other parameters that HDBSCAN uses (e.g. epsilon and minPts
are needed in DBSCAN).
Ethical Review Concerns: n/a
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank reviewer for detailed feedback, Our responses are as follow:
**Q1:** The paper does not include results from SetFit with sample amplification. \
**A1:** In SetFit method, SBERT model is fine-tuned on samples for few-shot settings and looses the properties of SBERT model embedding space.
So, we expect SetFit would not work with sample amplification. So it won't be suitable. The results below show same where sample amplification is performed after sample sparsification and SetFit.
**Dataset** | **Increment Factor** | **Sample Sparsify** | **SetFit**
----------------------------------------------|-----------------------|---------------------|--------------------
**AGNews (200000)** | 1 \(6036\) | 0\.81 $\\pm$ 0\.04 | 0\.77 $\\pm$ 0\.02
**** | 5 \(29952\) | 0\.82 $\\pm$ 0\.03 | 0\.78 $\\pm$ 0\.03
**** | 10 \(60236\) | 0\.83 $\\pm$ 0\.01 | 0\.78 $\\pm$ 0\.02
**Pubmed\-RCT (200000)** | 1 \(68\) | 0\.79 $\\pm$ 0\.01 | 0\.70 $\\pm$ 0\.02
**** | 5 \(28550\) | 0\.80 $\\pm$ 0\.01 | 0\.76 $\\pm$ 0\.02
**** | 10 \(55722\) | 0\.81 $\\pm$ 0\.01 | 0\.77 $\\pm$ 0\.02
**Cyberbullying Classification \(28615\)** | 1 \(1649\) | 0\.79 $\\pm$ 0\.02 | 0\.72 $\\pm$ 0\.01
**** | 5 \(6711\) | 0\.79 $\\pm$ 0\.01 | 0\.73 $\\pm$ 0\.02
**** | 10 \(13051\) | 0\.82 $\\pm$ 0\.01 | 0\.75 $\\pm$ 0\.03
Due to character limits, we are unable to add all the results, however we see similar scores across all datasets. We will add all results in the paper revision.
**Q2:** Algorithm 2: Should RandomSampling() have a parameter for \bar{X} so that OOD instances in \bar{X} are sampled in the V_i regions? \
**A2:** We sampled $n_s$ OOD instances in every V_i region randomly. Other than that we did not use any other input for random sampling.
**Q3:** How is the threshold determined for the area of a large Voronoi region? \
**A3:** We are sorry for not inlcuding this detail. We calculated single linkage inter-cluster distances of all clusters (https://www.geeksforgeeks.org/ml-types-of-linkages-in-clustering/) found in previous step and found the minimum distance among these. Lets call it minInterCentroid distance.
Our hypothesis is that the voronoi regions towards the outside of the whole data distribution and blank spaces between clusters should have larger area than a square region with minInterCentroid as sides.
So, this threshold is set as square of minInterCentroid distance. We will update these details in the revision.
**Q4:** While the # of clusters need not be specified in HDBSCAN, are there other parameters that HDBSCAN uses (e.g. epsilon and minPts are needed in DBSCAN). \
**A4:** For experiments in the paper, we did not change the default hyperparameters. For HDBSCAN method on minPts (minimum number of samples in a cluster), We performed an ablation study using this parameters as follow. Epsilon is not required for HDBSCAN (https://scikit-learn.org/stable/modules/generated/sklearn.cluster.HDBSCAN.html)
**minPts** | **Sample Sparsify** | **Sample Amplify**
------------|---------------------|--------------------
**5** | 0\.86 $\\pm$ 0\.01 | 0\.83 $\\pm$ 0\.02
**10** | 0\.86 $\\pm$ 0\.02 | 0\.83 $\\pm$ 0\.01
**50** | 0\.85 $\\pm$ 0\.01 | 0\.83 $\\pm$ 0\.02
**500** | 0\.81 $\\pm$ 0\.01 | 0\.79 $\\pm$ 0\.01 \
From the results it is clear that having small value for parameter minPts is better as that will find many small clusters and would represent the data distribution even after sample sparsification. With larger number of samples, there is a chance that no instance is sampled from smaller clusters leading to low accuracy. We will add the results in appendix of the revision.
**Q5:** Limiting Voronoi regions to 2D might be necessary due to computation overhead, but could reduce performance.\
**A5:** This is true and we have mentioned this limitation in section 6.2. However, the results we mentioned are with 2D Voronoi regions and still they provide good performance.
**Q6:** Other OSR methods could be compared \
**A6:** All of the above methods are image-based which cannot be directly applied for text. \
To the best of our knowledge, the open-set text classification approaches proposed in the literature are scarce and the suitable ones we have used for comparison in our work.
**Q7:** Sample sparsification and amplifications by themselves do not outperform the two existing methods. \
**A7:** It is common practice to extend/combine previous methods to achieve SOTA. We did same by combining our method with SetFit that achieved SOTA. | Summary: For the text classification problem in open domains, this paper proposes sparse sampling of labeled categories and adds samples of unknown categories. This article demonstrates through extensive experiments that the proposed method is effective in solving open domain text classification problems.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: Yes.
Experimental Designs Or Analyses: Yes.
Supplementary Material: Yes. The supplementary materials of the paper include a series of ablation study.
Relation To Broader Scientific Literature: This paper focuses on clustering samples with known label categories, sparsifying the sampling, adding samples with unknown categories, and using a pre-trained model for training.
Essential References Not Discussed: Not found yet.
Other Strengths And Weaknesses: Strengths of the paper:
1. The paper proposes a new method for text classification in open domains.
2. The paper is well-organized, clearly expressed, and easy to read and understand.
Weakness of the paper:
1. The method proposed in the paper can only solve the text classification problem of open domains involved in training. If unknown categories do not participate in training, the effectiveness of the method proposed in the paper needs to be verified. If a semi-supervised approach is used to train labeled data and unknown category data, and the text classification model is not pre-trained, how effective is the text classification model?
2. The sparsity of labeled samples with known categories has already been potentially represented in the model. Is the sample sparsity proposed in this paper the core problem for solving open domain text classification?
3. The two modules mentioned in this article basically rely on the ability of pre-trained models, which are the key to solving open domain problem recognition. How can unlabeled classes participate in training for unknown categories?
Other Comments Or Suggestions: Please refer to the section of Other Strengths And Weaknesses.
Questions For Authors: Please refer to the section of Other Strengths And Weaknesses.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank the reviewer for feedback and questions. Please find below our response and hope that clarifies reviewer doubts.
**Q1:** The method proposed in the paper can only solve the text classification problem of open domains involved in training. \
If unknown categories do not participate in training, the effectiveness of the method proposed in the paper needs to be verified. \
If a semi-supervised approach is used to train labeled data and unknown category data, and the text classification model is not pre-trained, how effective is the text classification model? \
**A1:** Our method does not include specific open domains. With sample amplification, we find samples in embedding space that would represent all unknown categories. \
Results from Table 5 represents this scenario where one-of-the-class data is held out and not involved in training. And only samples found by sample amplification were added in the training. \
Fine-tuning pre-trained models to achieve good accuracy is common practice, therefore we did not check the results without a pre-trained model which would obviously provide lower results.
**Q2:** The sparsity of labeled samples with known categories has already been potentially represented in the model. \
Is the sample sparsity proposed in this paper the core problem for solving open domain text classification? \
**A2:** The sample sparsification goal is to reduce the number of samples to be labeled, it has nothing to do with open-set text classification. Only sample amplification helps with open-set text classification.
**Q3:** The two modules mentioned in this article basically rely on the ability of pre-trained models,\
which are the key to solving open domain problem recognition. How can unlabeled classes participate in training for unknown categories? \
**A3:** We accept the importance of pre-trained models in our approach, however it is common practice to use them.\
We added additional class while training the model that represents all unknown category sample space. Sample amplification finds samples in this space and add to the training data. | null | null | null | null | null | null | null | null |
Improved Off-policy Reinforcement Learning in Biological Sequence Design | Accept (poster) | Summary: This work focuses on the problem of biological sequence design, recognizing that trained proxy scoring models often produce unreliable predictions. To address this challenge, they introduce restrictions into GFlowNet exploration by implementing a masking mechanism that increases the probability of exploring reliable data points. Specifically, adding masks to certain tokens in the offline dataset allows for exploration at those positions, while unmasked positions directly utilize offline data through teacher forcing. Through this approach, the authors' proposed δ-CS method supports more reliable exploration, achieving excellent results across multiple datasets (DNA, RNA, peptide design) and attaining Pareto optimality by balancing diversity and fitness.
## update after rebuttal
Thank the authors for their rebuttal, which addressed many of my concerns, especially by adding experiments on incorporating $\delta$-CS results with additional off-policy methods. As a result, I have increased my score from 2 to 3. However, for a primarily empirical work like this, I still believe that the current depth of investigation into the effects of $\delta$-CS is insufficient.
Claims And Evidence: See Other Strengths And Weaknesses and Questions For Authors.
Methods And Evaluation Criteria: See Other Strengths And Weaknesses and Questions For Authors.
Theoretical Claims: N/A
Experimental Designs Or Analyses: See Other Strengths And Weaknesses and Questions For Authors.
Supplementary Material: No.
Relation To Broader Scientific Literature: See Other Strengths And Weaknesses and Questions For Authors.
Essential References Not Discussed: See Other Strengths And Weaknesses and Questions For Authors.
Other Strengths And Weaknesses: ## Strengths:
1. The paper is well-written, provides a detailed literature review, and clearly explains both the motivation and methods.
2. Experimental details are provided thoroughly, and source code is also provided, ensuring high reproducibility.
3. The motivation makes sense, as considering the unreliability of proxies in biological sequence optimization is indeed an important problem.
## Weaknesses:
1. While the masking approach proposed here is conceptually novel, I find the term "mask" potentially misleading. In sequence modeling machine learning, mask usage typically refers to approaches like BERT, where certain tokens are masked within a sequence while content on both sides remains visible, enabling bidirectional modeling. After reading the abstract, I initially expected the work to employ this type of modeling. Upon further reading, it appears that the "mask" here merely serves as a "selective exploration" training method. Specifically, in GPT's next token prediction, training traditionally requires teacher forcing for every token through trajectories from dataset $D$. The masking here simply selects certain tokens that are allowed free exploration, while maintaining an autoregressive training approach at its core. This usage of "mask" may confuse readers. I would like the authors to clarify their rationale for using the "mask" concept within an autoregressive training framework. Without sufficient justification, I recommend the authors consider alternative terminology.
2. The rationale for using GFlowNet remains unclear. As mentioned in Weakness 1, the essence of the method is conducting selective exploration on offline data to discover new trajectories, but this approach doesn't seem strongly coupled with GFlowNets. I believe the authors should include other methods capable of learning from offline data in their baselines, and then demonstrate the superiority of $\delta$-CS as a plug-and-play component, proving its advantages over alternative approaches.
3. The authors' motivation is premised on proxy models producing severe unreliable predictions (Figure 2), leading them to reduce exploration of unreliable data points. However, I note that the proxy used is very simple (a CNN with no additional regularization). The authors should further discuss whether more advanced proxy training approaches could mitigate this issue (which represents an alternative solution to unreliability, as in [2]).
4. The DNA design experiments (TFBS binding sites <10bp) are overly simplistic (as mentioned on line 261). The authors should consider more complex experiments involving Cis-regulatory Element design as demonstrated in recent works ([1][2][3][4]).
5. [1] shares a similar approach with this work, using prediction uncertainty to adjust the optimization process. The difference is that [1] incorporates uncertainty into the reward function, while the authors use it to restrict exploration probability from offline data. I would like the authors to discuss the differences between these two approaches. Additionally, [1] employs different uncertainty estimation methods, and I would like the authors to discuss how their uncertainty estimation approach differs from that in [1].
## References
[1] Uehara, Masatoshi, et al. "Bridging model-based optimization and generative modeling via conservative fine-tuning of diffusion models." Advances in Neural Information Processing Systems 37 (2024): 127511-127535.
[2] Reddy, Aniketh Janardhan, et al. "Designing Cell-Type-Specific Promoter Sequences Using Conservative Model-Based Optimization." Advances in Neural Information Processing Systems 37 (2024): 93033-93059.
[3] Yang, Zhao, et al. "Regulatory DNA Sequence Design with Reinforcement Learning." The Thirteenth International Conference on Learning Representations.
[4] Wang, Chenyu, et al. "Fine-Tuning Discrete Diffusion Models via Reward Optimization with Applications to DNA and Protein Design." The Thirteenth International Conference on Learning Representations.
Other Comments Or Suggestions: See Other Strengths And Weaknesses and Questions For Authors.
Questions For Authors: 1. Do we actually know the distribution $P_{D_{t-1}}$? I understand the authors may intend to construct a discrete distribution using the weight in line 132, but this requires a more rigorous definition of the distribution.
2. What is the significance of introducing $\tilde{x}$ on line 160? This notation is not used in the formula, which only requires $\tilde{e}_t$. This aligns with my concern in Weakness 1, and actually the modeling here doesn't require a complete masked $\tilde{x}$, so is using "mask" as terminology for the method appropriate?
3. Line 22 mentions that the biggest drawback of DyNA PPO is its inability to utilize offline data, but I believe this might be solvable. Couldn't DyNA PPO directly leverage offline data through teacher-forcing methods?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: >W1, Q2: The term "mask" is confusing
Because our infilling sites are uniformly distributed across the entire sequence, we refer to them as “masks,” similar to BERT. However, we recognize that this term can be confusing. Alternatively, we could describe the algorithm as random teacher forcing: some tokens are predicted while others remain identical to the original sequence. This approach also removes the need for $\tilde{x}$ in the equation, since it is not directly used as input by the neural network.
> W2: 𝛿CS with other algorithms beyond GFlowNet
𝛿-CS can be applied to any off-policy RL method; we chose GFlowNets because they are representative method in this domain. To demonstrate $\delta$-CS as a plug-and-play component, we applied 𝛿-CS to Soft Q-Learning (SQL), which is a representative off-policy RL method in the general domain:
| Hard TFBind8| t=1 | t=5 | t=10 |
| - | - | - | - |
| SQL | 0.531 (0.011) | 0.879 (0.014) | 0.936 (0.008) |
| SQL + 𝛿-CS (𝛿=0.5) |0.546 (0.013) | 0.975 (0.011) | 0.993 (0.007) |
---
> W3: Conservative proxy
We acknowledge conservative model-based optimization (COMs) methods, which aim to construct robust proxy models [1, 2]. However, mere conservativeness is insufficient for active learning scenarios, where active querying for information gain from the oracle is essential. Although COMs perform well in offline model-based optimization (MBO), our results show they underperform in active learning settings. Specifically, COMs that impose conservativeness through adversarial smoothness in proxy training (Trabucco et al., 2021) achieve poorer outcomes than alternative methods.
Our method shares the philosophy that conservatism is beneficial but differs significantly in implementation. Instead of embedding conservativeness directly into proxy training, we integrate it into the search process itself. This approach preserves high information gain through explicit uncertainty modeling while ensuring conservatively robust optimization, effectively balancing uncertainty-driven exploration with robustness. We will put this discussion at the main paper. Thanks.
Trabucco et al. "Conservative objective models for effective offline model-based optimization." ICML, 2021.
---
>W4: Validation in complex biological sequence task
We have already included longer sequence benchmarks (such as GFN and AAV), which are widely recognized and commonly used in the literature. While TFB tasks are indeed simpler and considered toy benchmarks, they remain popular for initial evaluations. We agree that incorporating additional real-world DNA benchmarks could further strengthen our evaluation.
Regarding the suggested benchmarks, we noticed that the majority of existing literature [1,2,4] focuses on diffusion-based algorithms, which fall outside the scope of our research (therefore we focused to benchamrk [3]). Although we aimed to replicate results from TACO [3], which employs autoregressive models, their dataset and pre-trained checkpoints are unfortunately not publicly available. Consequently, extending our method to include these benchmarks within the rebuttal period is challenging. However, we commit to evaluating our method on longer DNA benchmarks by the camera-ready deadline, and we anticipate similar performance trends to those observed in GFP and AAV tasks.
---
>W5: $\delta$-CS vs. conservative reward
As discussed in W3, our approach still can utilize acquisition function like UCB while introducing conservatism to avoiding overoptimization. Though we have different approach, we can utilize the uncertainty oracle as proposed in [1] since we do not any restriction for the way of measuring uncertainty; this will be an interesting future work.
We'll include this discussion into our revised manuscript
---
> Q1. Do we actually know the distribution $P_{D_{t-1}}$?
We define a discrete distribution by normalizing the weights in line 132. Specifically, $P_{D_{t-1}}(x) \propto w(x; D_{t-1}, k),$ where $k$ is a hyperparameter controlling the distribution’s peakiness.
---
> Q3. Couldn't DyNA PPO directly leverage offline data through teacher-forcing methods?
We agree that teacher-forcing offers a way to incorporate offline data into DyNA-PPO. However, because PPO is inherently on-policy, directly leveraging offline data remains challenging without methods like importance sampling, which can introduce high variance. While teacher-forcing also can be used to pretrain the policy pretraining from offline sequences, it may lead to overfitting to the offline distribution since the reward information is not used during pretraining. To further verify this point, we conducted DyNA PPO experiments where we first pretrain the policy via teacher-forcing on offline data and then fine-tune it with PPO on TFBind8:
||Top-128 Mean|
|--|--|
|Dyna PPO|0.761 ± 0.006|
|Dyna PPO + teacher - forcing pretraining|0.777 ± 0.001 |
|GFN-AL | 0.947 ± 0.009 |
|GFN-AL + ours | 0.972 ± 0.005 |
---
Rebuttal Comment 1.1:
Comment: I thank the authors for their comprehensive rebuttal, which has effectively addressed many of my previous concerns. However, I still have several points that warrant further discussion:
1. While the proposed method is positioned as a "plug-and-play" enhancement for off-policy methods, the current experimental validation remains somewhat limited. Despite the additional experiments provided in the rebuttal, only one extra method was evaluated, and this evaluation was conducted solely on the relatively less complex TF Binding Task.
2. Could you elaborate on the specific conditions under which the active learning setting offers advantages over the offline MBO setting for biological sequence design problems? Please provide further justification for your specific focus on the active learning paradigm in this work.
---
Reply to Comment 1.1.1:
Comment: **Thank you for the additional feedback. We are glad to hear that most of your concerns have been addressed. Below, we respond to the remaining points.**
----
> 1. While the proposed method is positioned as a "plug-and-play" enhancement for off-policy methods, the current experimental validation remains somewhat limited. Despite the additional experiments provided in the rebuttal, only one extra method was evaluated, and this evaluation was conducted solely on the relatively less complex TF Binding Task.
**Mean Top-128**
| | GFP | AAV |
| - | - | - |
| SQL | 3.331 (0.0) | 0.480 (0.0) |
| SQL + 𝛿-CS | 3.573 (0.003) | 0.495 (0.001) |
| VarGrad | 3.331 (0.0) | 0.480 (0.0) |
| VarGrad + 𝛿-CS | 3.567 (0.003) | 0.668 (0.011) |
| Soft PCL ($\lambda$=0.9) | 3.331 (0.0) | 0.480 (0.0)|
| Soft PCL ($\lambda$=0.9) + 𝛿-CS | 3.578 (0.004) | 0.622 (0.011) |
As you noted, we expanded our SQL experiments to the main protein tasks (GFP and AAV) and added two additional soft off-policy RL algorithms, Log-Partition Variance Gradient (VarGrad) [1] and Soft Path Consistency Learning (PCL) [2,3,4], resulting in four baselines (TB, SQL, VarGrad, Soft PCL). **Our results show that 𝛿-CS improves performance across all of them, highlighting its plug-and-play versatility.**
**Discussion on off-policy RL algorithms:** Briefly, TB and VarGrad apply constraints on entire trajectories, leading to higher variance but lower bias. TB explicitly estimates flows/values (partition function of terminal state), while VarGrad does so implicitly through batch averaging. Soft PCL operates on sub-trajectories (similar to a TD-λ approach), striking a variance-bias balance via trajectory length. SQL uses one-step transitions, lowering variance but increasing bias. In these protein design tasks, where global sequence properties matter, full-trajectory methods (TB, VarGrad) generally seem to outperform sub-trajectory or one-step approaches.
For further analysis connecting these off-policy RL methods to discrete sampling (including biological design) see [5]. We will include these results and related discussion in the main paper. Thank you for the valuable feedback.
> 2. Could you elaborate on the specific conditions under which the active learning setting offers advantages over the offline MBO setting for biological sequence design problems? Please provide further justification for your specific focus on the active learning paradigm in this work.
Active learning naturally matches how biological sequence design often proceeds: researchers propose candidate sequences, test them in assays or models, and use those results to guide subsequent rounds of design. This iterative cycle quickly pinpoints promising variants by balancing exploration (searching new sequence space) and exploitation (optimizing designs in safe region). In practice, multiple verification steps—such as in vitro (cell-level experiments) assays or in vivo (animal or human studies)—can serve as oracle queries, feeding fresh data back into the surrogate model [6]. Meanwhile, offline MBO relies on a single batch of pre-collected data and is useful when further experimentation is infeasible (e.g., out-of-budget, safety constraints) or during final decision stages after active learning.
----
[1] Lorenz et al., "Vargrad: a low-variance gradient estimator for variational inference.", NeurIPS 2020
[2] Nachum et aL., "Bridging the Gap Between Value and Policy Based Reinforcement Learning.", NeurIPS 2017
[3] Chow et al., "Path consistency learning in tsallis entropy regularized mdps", NeurIPS 2018
[4] Madan et al., "Learning GFlowNets from partial episodes for improved convergence and stability", ICML 2023
[5] Deleu et al., "Discrete Probabilistic Inference as Control in Multi-path Environments", UAI 2024
[6] Jain, Moksh, et al. "Biological sequence design with gflownets." International Conference on Machine Learning. PMLR, 2022. | Summary: The manuscript proposes a conservative search method applied in GFlowNets for Biological Sequence Design. The proposed method restricts the number of mutations based on the length of the sequence and the prediction uncertainty. Experiments show that this sampling methodology stabilizes the training of GFlowNets, improving performance over GFlowNet-AL and other traditional baselines. These results highlight that simple methodologies for restricting the search space are effective when the functionality landscape is usually located around the initial sequence of interest.
## update after rebuttal
The authors have addressed many of my concerns. I updated my score accordingly.
Claims And Evidence: The claims made by the manuscript are supported by clear evidence.
Methods And Evaluation Criteria: The evaluation criteria make sense for the problem investigated.
Theoretical Claims: The mathematical of the proposed method seems correct.
Experimental Designs Or Analyses: The reviewer has clarification questions regarding the active learning setting and the oracles used for evaluation. Specifically,
1. How was the active learning setting set for the proposed method and the baseline methods?
2. How is the oracle performing for sequences that are far in terms of mutations from the wild type? The values for the GFP performance graph seem high even for methods that have problems generating long sequences like DynaPPO.
Supplementary Material: The reviewer read the supplementary material.
Relation To Broader Scientific Literature: The key contributions of the paper related to the broader scientific literature are:
1. Proposing a conservative search approach that can be combined to solve sampling issues in the training of GFlowNets.
2. It applies an adaptive conservativeness approach that is dependent on the oracle prediction uncertainty.
Essential References Not Discussed: Additional references related to the application of RL to Protein Engineering like [REF1] and [REF2] seem to be missing.
[REF1] Wang, Yi, et al. "Self-play reinforcement learning guides protein engineering." Nature Machine Intelligence 5.8 (2023): 845-860.
[REF2] Lee, Minji, et al. "Robust optimization in protein fitness landscapes using reinforcement learning in latent space." ICML (2024).
Other Strengths And Weaknesses: Strengths:
1. The manuscript adapts GFlowNets by proposing a conservative search framework, i.e., sampling a limited number of mutations from initial state sequences, to address the issue of generating out-of-distribution samples when handling large-length sequences.
2. The idea of using restricted exploration to improve the training efficiency of GFlowNets is an interesting direction.
3. The proposed adaptive conservativeness approach is adjusted for each data point based on prediction uncertainty.
Weaknesses:
1. The main concern of the reviewer is the reliability of the results presented in the manuscript. The oracle and active learning settings are not well defined. Additionally, there are some concerns regarding dataset splits used for some of the tasks presented.
2. As mentioned by the authors as one of the main limitations, the restricted exploration strategy does not solve different drawbacks from active learning. Restricting the number of mutations is likely to improve the results for landscapes in which most of the functional sequences are close to the main wild-type sequence.
3. Even though the title suggests a general method analysis for different RL algorithms, the experiments are only extending a GFlowNet as the main policy.
Other Comments Or Suggestions: 1. (Related Work) GFlowNets are introduced on Page 5 after there are other follow-up works to GFlowNets introduced in Page 4. The Related Work section should be re-organized.
2. The sentence in line 212: “capitalizing on both the high novelty offered by GFlowNets” is counterintuitive as your method proposes restricting the novelty of the GFlowNet generation given its tendency to generate out-of-distribution samples.
Questions For Authors: 1. What is the meaning of “large-scale” settings in line 36? From my understanding, it means that GFlowNets achieve poor performance for long sequences? The authors should clarify this definition.
2. (Title) The title suggests that the proposed conservative search can be applied to other RL-based algorithms but only test to GFlowNet. For other algorithms, the proposed policy is only applied for a setting with discrete actions and with a sampling order that gives enough context to propose mutations to the masked positions? If this is the case, the reviewer wonders about the advantage or improvement in performance over sampling mutations using a masked protein language model, for example.
3. The methodology for generating the datasets seems critical. How were the initial sequences for GFP generated? With random mutations from the wild-type? Given the functional landscape of GFP this might lead to data leakage. A split like the one proposed by [REF1] might be needed.
[REF1] Kirjner, Andrew, et al. "Improving protein optimization with smoothed fitness landscapes." ICLR (2023).
4. All baselines achieve very high performance on the GFP dataset. Given that sequences with more than 10 mutations are very unlikely to be functional, the reviewer suggests showing the number of mutations from the wild-type for each of the methods. A metric showing the distance from the wild-type for the top-scoring mutants might be needed, as shown in [REF2]. Mutants far from the wild type with high predicted functionality might suggest a problem with the oracle's reliability.
[REF2] Lee, Minji, et al. "Robust optimization in protein fitness landscapes using reinforcement learning in latent space." ICML (2024).
5. It is not clear how the active learning setting is defined for the proposed method and baselines. Additionally, it is also unclear if the oracle is used only for evaluation for all the methods.
6. Given that the positions to mutate are pre-sampled, it would be interesting to have baselines mutating these same positions randomly or using a masked protein language model to compare the performance.
7. The manuscript needs a better explanation and intuition of how fixing positions changes the training stability of GFlowNets.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: ### Active learning setting
We follow the existing generative active learning settings (GFN-AL [1], FLEXS [2]), which are standard in this field. As noted in our main text and appendix, we perform active learning as follows:
Starting with an initial dataset $D_0$, each active learning round t consists of three steps:
- (Step A) train the proxy model on the current dataset $D_{t-1}$;
- (Step B) train the generative policy using the proxy and proposing a batch of B new sequences;
- (Step C) evaluate those sequences using Oracle and add them to the dataset.
We run 10 active learning rounds with a batch size of 128. We have the same limited oracle calls for all methods. At each round, we assess performance using the top-K sequences (with K=128).
We adopt the initial dataset of DNA and RNA from [1] and [3], respectively. For GFP and AAV, we generated the initial dataset using wild-type, but as discussed in the following questions, we have re-conducted experiments using the dataset from [REF1, 2].
### Experimental setting for GFP
First of all, our GFP benchmark is quite standard in this field; we use TAPE [4], one of the widely adopted benchmarks in representative studies (e.g., [2], [7]). The benchmarking methods for the GFP task are diverse (e.g., TAPE [4], Design-Bench [5]; see [6] for detailed comparisons among them). Additionally, scoring normalization varies across studies, with some methods employing normalized scores [REF1, 2] and others using unnormalized scores [1, 2, 7].
As suggested, we have conducted experiments by following the experimental setting of LatProtRL [REF2]: we evaluate 256 sequences in 15 active learning rounds by adopting the oracle function with the given initial dataset that is split following [REF1]. As with [REF2], we report the median value of the top-128 sequences over 5 independent runs. The results for AdaLead and LatProtRL are directly obtained from [REF2]. Our approach achieved better performance than LatProtRL and substantially improved GFN-AL.
| | GFP Medium | GFP Hard |
| - | - | - |
| AdaLead | 0.93 (0.0) | 0.75 (0.1) |
| LatProtRL | 0.93 (0.0) | 0.85 (0.0) |
| GFN-AL (𝛿=1) | 0.21 (0.0) | 0.09 (0.0) |
| GFN-AL + 𝛿-CS (𝛿=0.05) | 0.57 (0.0) | 0.60 (0.1) |
| GFN-AL + 𝛿-CS (𝛿=0.01) | 1.06 (0.1) | 0.86 (0.0) |
In the revised manuscript, we will discuss the challenges in GFP with additional experimental results.
### Distance to the wild-type and restricted exploration in GFP
We assume the oracle to be perfect, as with previous works. The performance of proxies typically degrades when predicting samples far from the offline data distribution, which is particularly evident in our constrained search.
We agree that incorporating distance from wild-type sequences leads to more realistic benchmarking. However, we focus on proposing a broadly applicable off-policy search method, not benchmarking itself. Importantly, our approach is compatible with distance-based constraints, as they are orthogonal to our method. To demonstrate this, we applied δ-CS to Proximal Exploration (PEX) [7], which explicitly encourages proximity to the wild type—see results below.
| GFP Hard | 𝛿-CS | 𝛿-CS + PEX |
|-|-|-|
| Fitness | 0.86 (0.0) | 1.08 (0.0) |
| Distances to wt | 21.31 (1.7) | 7.47 (0.6) |
### Validation with other off-policy RL algorithms
As suggested, we applied our method to other RL methods: soft Q learning. Please refer to the answer to reviewer 6J1t (W3).
### Other baselines
As suggested, we compare with random mutation and LS-GFN. LS-GFN is our special case where the masking positions are fixed as the last 𝛿L tokens.
| | GFP Hard |
| - | - |
| 𝛿-CS (𝛿=0.01) | 0.86 (0.0) |
| Random (𝛿=0.01) | 0.27 (0.0) |
| LS-GFN (𝛿=0.01) | 0.34 (0.0) |
The table shows that fixing masking positions can overly restrict the search space. However, specifying more significant positions in sequences based on domain knowledge can be more efficient than randomly choosing the positions.
### Related works
As suggested, we'll include the missing references and re-organize Sec 5.
### Other comments
> DyNa PPO in GFP
In Fig 4, the mean score of Dyna PPO remains unchanged over active rounds, which means it fails to generate sequences with higher scores than the initial dataset. Note that GFP scores are not normalized.
> "Large-scale"
We use "large-scale" to denote longer sequences, especially with large action space, like protein design tasks.
> line 212
We'll revise it.
[1] Jain et al. "Biological sequence design with GFlowNets." ICML (2022)
[2] Sinai et al. "Adalead" (2020)
[3] Kim et al. "Bootstrapped training of score-conditioned generator for offline design of biological sequences." NIPS (2023)
[4] Rao et al. "Evaluating protein transfer learning with TAPE." NIPS (2019)
[5] Trabucco et al. "Design-bench" ICML, 2022.
[6] Surana et al. "Overconfident oracles." (2025).
[7] Ren et al. "Proximal exploration for model-guided protein sequence design." ICML, 2022.
---
Rebuttal Comment 1.1:
Comment: Thank you for answering my questions.
I have increased my score after the rebuttal from the authors.
I have the following additional comments/questions:
1. (Initial Dataset D_0) For the GFP and AAV experiments, I still think that the initial dataset should be from low-functional initial sequences, and not only from mutations from the wild type sequence.
2. (Distance to the Wild-Type) For the results presented in the section evaluating the distance from the wild-type, when combining the proposed method with PEX is the wild-type sequence result used during optimization?
3. (Other Baselines) My suggestion was to, for the same positions mutated by the proposed method, try random mutations and mutations performed by a language model. From my understanding, in the rebuttal table, the positions mutated for "Random" and "LS-GFN" are different than the ones for the proposed method?
---
Reply to Comment 1.1.1:
Comment: **Thanks for the additional feedback, and we appreciate some of your concerns were addressed.**
> 1. (Initial Dataset D_0) For the GFP and AAV experiments, I still think that the initial dataset should be from low-functional initial sequences, and not only from mutations from the wild type sequence.
**We want to clarify that we already used the initial dataset consisting of low-functional sequences in the additional experiments**. Specifically, we directly adopt the initial dataset from Lee et al. (2024) which satisfy the condtions the reviewer mentioned. Note that all additional experiments related GFP in the rebuttal use the initial dataset from Lee et al. (2024). We will include these additional experiments in the revised manuscript.
> 2. (Distance to the Wild-Type) For the results presented in the section evaluating the distance from the wild-type, when combining the proposed method with PEX is the wild-type sequence result used during optimization?
We combined our method with PEX follows these steps each round:
(a) train the policy and propose new sequences,
(b) select 𝐵 sequences to query via PEX by
- evaluating all sequences with the proxy,
- measuring their distances to the wild type, and
- finding proximal frontier using the proxy value and disctance
> 3. (Other Baselines) My suggestion was to, for the same positions mutated by the proposed method, try random mutations and mutations performed by a language model. From my understanding, in the rebuttal table, the positions mutated for "Random" and "LS-GFN" are different than the ones for the proposed method?
The "Other Baselines" section is for question 6 and 7; we grouped the corresponding results into a combined section due to space constraints, and we apologize for any confusion.
> Q6. Given that the positions to mutate are pre-sampled, it would be interesting to have baselines mutating these same positions randomly or using a masked protein language model to compare the performance.
**(Baseline 1: random mutations)** We already included the random mutation baseline, where mutations are applied to the same masked positions selected by our noise injection policy, to isolate the effect of the denoising policy. This allows us to assess whether performance improvements come from the conservative search mechanism itself or simply from where mutations are applied.
**(Baseline 2: pLM)** We agree that comparing our method to a masked protein language model (pLM) could offer a useful perspective. However, we deliberately focused on an active learning setting where the model is trained solely on a limited offline dataset, ensuring no information leakage from the test set. In contrast, many pretrained pLMs are trained on large public databases, making it difficult to guarantee that they have not seen target sequences or close variants, potentially giving them an unfair advantage.
We acknowledge the value of pretrained models when properly controlled. In future work, one could retrain a masked pLM from scratch on a dataset that is disjoint from the test set to enable a fairer and more rigorous comparison with active learning approaches.
> Q7. The manuscript needs a better explanation and intuition of how fixing positions changes the training stability of GFlowNets.
The experiments with LS-GFN are included to give an intuition of how fixing positions affects GFlowNet training (Q7). LS-GFN performs a back-and-forth search by fixing the masked positions to the last 𝛿𝐿 tokens (a special case of our framework). As the results show, fixing positions in this way can overly restrict the search space, leading to suboptimal exploration and reduced diversity.
That said, if the fixed positions are chosen based on domain knowledge (e.g., known functional regions), this constraint could be beneficial by focusing exploration on more meaningful parts of the sequence. In contrast, randomly selecting positions, used in our main method, offers broader and more stable exploration when such prior knowledge is unavailable. | Summary: The paper proposes δ-CS, a novel off-policy RL approach for biological sequence design. It addresses the challenge of proxy misspecification, where proxy models used for sequence evaluation are unreliable on ood inputs. The method is integrated into GFlowNets, and works by injecting and denoising noise into high-score sequences with dynamically adjusted conservativeness. Experiments show that δ-CS significantly improves GFlowNets by balancing sequence exploration and robustness, leading to improved DNA, RNA, protein, and peptide design outcomes.
Claims And Evidence: Yes. Fig3 and table 1 supports the claim that δ-CS improves robustness by restricting policy exploration to reliable regions; Figs 9&10 demonstrates that adapting δ based on proxy uncertainty improves robustness.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: No theoretical guarantees on convergence or stability with increasing rounds, would be interesting to see some theoretical or experimental insights.
Experimental Designs Or Analyses: Yes, esp. fig 2,3,5. The proxy model failure analysis confirms low correlation between proxy and oracle for OOD sequences, and the ablation studies on δ values confirm that conservative search outperforms unconstrained GFlowNet training.
Supplementary Material: No
Relation To Broader Scientific Literature: This paper has broad connection to offline-RL, active learning, and biological sequence design.
Essential References Not Discussed: Not that I'm aware of.
Other Strengths And Weaknesses: Strengths
- Intuitive adaptive δ mechanism balances novelty and conservativeness.
- Writing is clear and concise.
- Strong experimental validation across diverse sequence design tasks.
Weaknesses
- Does training on Dₜ₋₁ (containing more synthetic sequences) drift proxy model accuracy?
- Any intuition on how extreme δ values (near 0 or 1) might affect performance? No major experiments needed, just some textual discussion would suffice.
Other Comments Or Suggestions: N/A
Questions For Authors: See above, Unclear if growing synthetic data proportion (from δ-CS) leads to accuracy drift in later rounds (potential model bias).
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: > (Theoretical Claims) No theoretical guarantees on convergence or stability with increasing rounds, would be interesting to see some theoretical or experimental insights.
Thanks for highlighting the importance of theoretical guarantees and analysis. We acknowledge that rigorous theoretical guarantees, such as formal convergence rates, are indeed valuable. However, deriving such guarantees for deep-learning-based active learning is exceptionally challenging—moreover, the proxy model and the generative policy interplay to explore the black-box landscape. Our primary goal is to provide a methodological and empirical contribution. We demonstrate the effectiveness of $\delta$-CS by presenting performance gains on DNA, RNA, and protein design tasks. These results clearly illustrate the practical benefits of our proposed approach across various domains. We will include this in our limitations of Section 7.
---
> W1. Does training on $D_{t-1}$ (containing more synthetic sequences) drift proxy model accuracy?
In the active learning setting, we assume that $D_{t-1}$ consists of annotated data with true oracle functions with limited accessiblity; e.g., we can query sequences with batch size of B = 128 at each round. Note that the predicted data $(x, f_{\phi}(x))$ is added to $D_{t-1}$ during the policy training.
---
> W2. Any intuition on how extreme $\delta$ values (near 0 or 1) might affect performance? No major experiments needed, just some textual discussion would suffice.
When $\delta$=0, no noise is injected into the offline data, so the generative policy is trained purely on the existing data without any additional exploration. In contrast, when $\delta$=1 the original offline data is completely replaced with noise, and the model fully relies on its own policy to denoise, meaning fully on-policy learning with no conservatism.
---
> Q1. Unclear if growing synthetic data proportion (from $\delta$-CS) leads to accuracy drift in later rounds (potential model bias).
At the start of each round, we reinitialize the generator model. During training, the model uses a proxy (acquisition function) to evaluate sequences, but we do not add them to our dataset. After training, we propose new sequences to be evaluated with oracle functions and then add those annotated results to the dataset, so the dataset always contains only real (annotated) data.
---
**Thanks for your valuable comments** | Summary: This manuscript proposes a novel off-policy search strategy, δ-Conservative Search (δ-CS), that improves the reliability of GFlowNets for biological sequence design by controlling exploration according to proxy model confidence. The method randomly masks high-scoring offline sequences with probability δ, then relies on GFlowNets to denoise the masked tokens, keeping generated sequences closer to well-understood regions while still encouraging diversity. Experiments on DNA, RNA, and protein design tasks show that δ-CS consistently outperforms existing methods, including simpler off-policy baselines, by striking a better balance between exploration and exploitation when proxy models are uncertain.
Claims And Evidence: I have no comments on this topic.
Methods And Evaluation Criteria: Please see the Part of Strengths and Weaknesses.
Theoretical Claims: Please see the Part of Strengths and Weaknesses.
Experimental Designs Or Analyses: Please see the Part of Strengths and Weaknesses.
Supplementary Material: I have reviewed the supplementary material.
Relation To Broader Scientific Literature: This work will benefit protein design and drug design.
Essential References Not Discussed: I have no comments on this topic.
Other Strengths And Weaknesses: **Strengths**\
1. The paper is generally well-written.
2. The proposed method combines the diversity exploration of GFlowNets and the conservatism of evolutionary search. Through masking and adaptive delta mechanism, it effectively alleviates the problem of proxy model on out-of-distribution samples.
3. Experimental evaluations across diverse biological sequence design tasks were performed to demonstrate both the generalizability and superior performance of the proposed method.
**Weakness**\
1. The initial value and adjustment strategy of δ may depend on task experience (e.g., longer sequences require smaller δ), and there is a lack of general guidelines.
2. The effectiveness of adaptive δ is highly dependent on the uncertainty estimation accuracy. If the estimation deviation is large, it may affect the performance.
3. While δ-CS is designed for GFlowNets, its applicability to other types of generative models or RL algorithms in biological sequence design is not extensively explored.
Other Comments Or Suggestions: I have no other comments.
Questions For Authors: 1. Does the oracle f in the paper come from ground truth or a proxy evaluation model? If it comes from ground truth, how to evaluate the noised sequence that does not have ground truth?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: > W1. The initial value and adjustment strategy of $\delta$ may depend on task experience, and there is a lack of general guidelines.
In this study, we simply set delta=0.5 for DNA/RNA (masking 4 to 7 tokens on average) and delta=0.05 for protein design (masking approximately 4 to 12 tokens). Our intention is to show that even with this simple setting without task-specific tunning, $\delta$-CS gives consistent improvements. Moreover, the results in Fig 12-14 in the appendix show that setting delta to mask approximately 1~12 tokens (i.e., 0.1 ≤ $\delta$ ≤ 0.5 in DNA/RNA, 0.01 ≤ $\delta$ ≤ 0.05 for protein design) is consistently beneficial compared to exploration without $\delta$-CS.
As the reviewer mentioned, carefully setting delta based on experience and domain knowledge can bring even more improvements.
---
> W2. The effectiveness of adaptive $\delta$ is highly dependent on the uncertainty estimation accuracy. If the estimation deviation is large, it may affect the performance.
We measure the uncertainty as the inconsistent proxy predictions using MC dropout or Ensemble. The key insight of the adaptive $\delta$ is to search the space more conservatively when the proxy gives inconsistent predictions on a certain datapoint compared to other datapoints. In addition, thanks to the scale parameter $\lambda$, we can adjust $\delta$ according to each point’s *relative* uncertainty. So, even if the estimation deviation (i.e., the discrepancy between predicted uncertainty and true uncertainty) is large, it does not overly degrade performance.
---
> W3. While $\delta$-CS is designed for GFlowNets, its applicability to other types of generative models or RL algorithms in biological sequence design is not extensively explored.
Thanks for the valuable feedback. As suggested, we conducted additional experiments using Soft Q-Learning (SQL) on the Hard TFBind-8 benchmark to demonstrate the broader applicability of our approach. As shown in the table below, $\delta$-CS significantly improves both exploration and performance in SQL, confirming that our method extends beyond the GFlowNet setting.
| | t=1 | t=5 | t=10 |
| - | - | - | - |
| SQL | 0.531 (0.011) | 0.879 (0.014) | 0.936 (0.008) |
| SQL + $\delta$-CS ($\delta$=0.5) |0.546 (0.013) | 0.975 (0.011) | 0.993 (0.007) |
**The rationale for the experimental focus:** $\delta$-CS introduces a new off-policy exploration strategy under the unreliable proxy by conservatively leveraging known high-reward sequences. We initially focused on applying $\delta$-CS within GFlowNets because they offer a natural framework for structured sequence generation in biological domains. Moreover, there is a theoretical equivalence between GFlowNet training objectives (e.g., detailed balance, trajectory balance) and established off-policy max-entropy RL methods (e.g., Soft Q-Learning, Path Consistency Learning) when reward corrections are applied (Tiapkin et al., 2024; Deleu et al., 2024). This connection supports that the insights from our GFlowNet experiments can be extended to improvements in general off-policy RL settings.
> Q1. Does the oracle $f$ in the paper come from ground truth or a proxy evaluation model? If it comes from ground truth, how to evaluate the noised sequence that does not have ground truth?
In the case of TFBind-8, we use ground truth since all possible sequences are experimentally evaluated (Barrera et al., 2016) as the search space is relatively small ($4^8$). For other tasks, we assume a simulator or trained model with a larger dataset as our ground truth oracle, like various previous works (Sinai et al., 2020; Kirjner et al., 2023), and evaluate perturbed sequences using these oracle functions.
Specifically, we use ViennaRNA (Lorenz et al., 2011) to evaluate the newly proposed RNA sequences. For GFP, the TAPE transformer model trained with 52,000, which is much larger than our initial dataset, is used as an oracle (Rao et al., 2019). In AAV, the oracle is built using comprehensive single-mutation data from AAV2 capsids, modeled additively (summing individual mutation effects with some noise), and applied to multiple target tissues across varying design lengths (Ogden et al., 2019).
- Tiapkin et al. (2024) “Generative flow networks as entropy-regularized RL.”
- Deleu et al. (2024) “Discrete probabilistic inference as control in multi-path environments.”
- Sinai et al. (2020) “Adalead: A simple and robust adaptive greedy search algorithm for sequence design.”
- Kirjner et al. (2023) “Improving protein optimization with smoothed fitness landscapes.”
- Barrera et al. (2016) “Survey of variation in human transcription factors reveals prevalent DNA binding changes.”
- Lorenz et al. (2011) “ViennaRNA Package 2.0.”
- Rao et al. (2019) “Evaluating protein transfer learning with TAPE.”
- Ogden et al. (2019) “Comprehensive AAV capsid fitness landscape reveals a viral gene and enables machine-guided design.”
**Thanks for your valuable comments** | null | null | null | null | null | null |
Raising the Bar: Investigating the Values of Large Language Models via Generative Evolving Testing | Accept (poster) | Summary: Existing static LLM evaluation benchmarks are limited by chronoeffect, where benchmarks become saturated or contaminated. To overcome this, this paper proposes Generative Evolving Testing Approach (GETA), a dynamic evaluation framework that co-evolves with LLMs by generating adaptive test items tailored to models’ moral boundaries and capabilities. GETA effectively addresses the chrono effect by learning distributions of item difficulty and value conformity. Results show GETA generates more tailored and consistent evaluations.
Claims And Evidence: The claims made are supported by clear and convincing evidence.
Methods And Evaluation Criteria: Evaluating GETA using concurrent validity makes sense. In standard psychometric research, a newly proposed tool is typically evaluated across multiple reliability and validity metrics. I understand that, in the context of LLMs, this may be too much to ask due to the lack of standardized protocols for various metrics. Nevertheless, evaluating the measurement results across more metrics (e.g., as in [1]) would enhance the reliability of the evaluation results. Alternatively, discussing the infeasibility of using additional metrics would be beneficial.
[1] Measuring Human and AI Values Based on Generative Psychometrics with Large Language Models, AAAI 2025
Theoretical Claims: N/A
Experimental Designs Or Analyses: The designs and analyses primarily involve 1) Value Conformity (VC) of LLMs, 2) current validity in terms of correlation with static standard leaderboard scores, 3) ablation studies, 4) human evaluation of LLM VC, and 5) detailed analyses and case studies. The experiments are well-designed and comprehensive, yet I still have some questions.
- Did you also verify whether the model-inferred difficulty level accurately reflects the item difficulty as perceived by humans or as indicated by LLM scores? I checked some examples, and it seems that some difficulty ratings are counterintuitive.
- Additionally, the authors are encouraged to discuss the ability of LLMs to extrapolate and generate increasingly difficult test items. Considering the complexity of the proposed paradigm, how do you ensure the models are effectively trained?
- Does your method rely on a large-scale dataset for a specific value dimension? For example, can your method be applied to personal values [1, 2], using only a few dozen items created by psychologists?
- Can your method be extended to other abilities (e.g., reasoning) and psychological constructs (e.g., Schwartz's values and personality), especially those without ground truth? Since chronoeffect is a universal evaluation challenge, such an extension would be beneficial. The authors are encouraged to discuss the limitations and scope of the proposed method.
[1] Value FULCRA: Mapping Large Language Models to the Multidimensional Spectrum of Basic Human Value, NAACL 2024
[2] Valuebench: Towards comprehensively evaluating value orientations and understanding of large language models, ACL 2024
Supplementary Material: Additional evaluation and some prompts.
Relation To Broader Scientific Literature: Please refer to the above comments. Most relation to broader scientific literation is well addressed.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: This paper is well motivated and aims to address a fundamental issue in LLM evaluations. The results are promising, except that I have a few concerns elaborated above. Please refer to the above comments.
Other Comments Or Suggestions: N/A
Questions For Authors: Please refer to the above comments.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your positive feedback and insightful suggestions, which is really important to us.
---
## Method
### Q1: What if evaluate GETA across more metrics?
In addition to concurrent validity, we verified GETA’s performance with three more metrics:
1. **Stability** - In App. D.2, we have analyzed GETA's performance stability against three factors: 1) item generator backbone, 2) the difficulty and 3) the number of seed items, for GETA’s initialization. The results in Tables 12 & 13 show that *GETA maintains high validity across different hyperparameters and backbones*, demonstrating its robustness and effectiveness. The convergence analysis in App. D.4, Fig. 6 also indicates that GETA converges faster and more stably than CAT, benefiting from selective generation.
2. **Construct validity** - We have examined it using the multitrait-multimethod (MTMM) matrix [1]:
|Method|GETA/Bias|i.i.d./Bias|GETA/Ethics|i.i.d./Ethics|GETA/Toxicity|i.i.d./Toxicity
|-|-|-|-|-|-|-
|GETA/Bias|1|||||
|i.i.d./Bias|**0.9336**|1||||
|GETA/Ethics|-0.0826|*-0.2465*|1|||
|i.i.d./Ethics|*0.2051*|0.1634|**0.8283**|1||
|GETA/Toxicity|0.4007|*0.5699*|-0.2136|*0.272*|1|
|i.i.d./Toxicity|*0.6994*|0.7818|*-0.0616*|0.427|**0.8995**|1
where the heteromethod-monotrait and heteromethod-heterotrait Pearson correlations are in bold and Italic, respectively. It is expected that |heteromethod-monotrait corr| > |monomethod-heterotrait corr| > |heteromethod-heterotrait corr|, and the construct validity of this work is strong, as the averages are 0.8871 > 0.3449 > 0.3016.
3. **Predictive validity** - This metric evaluates a test based on its predictions for future, or technically, downstream/external tasks. In this sense, Va-O functions as predictive validity because: 1) The three OOD datasets, chosen as the reference measurement, were published approximately one year after the static data source; and 2) The tasks in the OOD datasets are more complex than those in the source datasets, which is elaborated on in App. B.1.2, L1424-1474. As shown in Fig. 3, GETA performs saticfactorily in predictive validity, particularly in *social bias*.
---
## Experiment
### Q2: Does the model-inferred difficulty accurately reflect the item difficulty?
1. Yes. To assess the generalization ability after pre-training, we conducted an experiment on the Pearson correlation between 25 evenly sampled difficulty levels and the corresponding actual difficulty, measured by AEP and EP (defined in App. B.1.1, L1230-1240). The item generator achieves **correlations greater than 0.9** with GPT-3.5-Turbo and Gemini-1.0-Pro as examinee LLMs, demonstrating reliable generalization.
2. The definition of difficulty in this work is clarified in App. C.1, L1714-1726. Items answered incorrectly by most examinee LLMs are deemed highly difficult. Therefore, the items challenging for LLMs may not appear truly difficult for humans.
### Q3: Is GETA effectively trained? Can GETA extrapolate and generate increasingly difficult test items?
1. Since the item generator may not initially map item parameters to items with high difficulty, during the test process, each newly generated item is answered by all examinees and re-calibrated by the VIRT model to compute its true parameters $\hat d$. Consequently, only items matching the specified parameters $d^*$ are used for ability estimation.
2. In the re-calibration process above, the item generator can discover increasingly difficult items due to the randomness of LLMs. These items are then collected to further fine-tune the generator, a process referred to as evolving in this paper.
3. Please refer to our response to Q2 for details on GETA's extrapolation ability, as half of the sampled difficulty levels exceed the coverage of the static data (not presented or more difficult).
### Q4: Does GETA rely on a large-scale dataset for a specific value dimension?
As clarified in Sec. 4.1, L226, we use 5k calibrated items per value type with ~80 responses per item to train GETA. In other words, GETA requires modest training data and is still more data-efficient than other adaptive baselines.
### Q5: Is GETA applicable to other criteria?
1. Yes. As discussed in App. A.1, L1087-1092, GETA is theoretically applicable to any well-defined and quantifiable criterion, provided that: 1) a sufficient number (~5k) of accessible test items for calibration and training, and 2) reliable evaluators to define the ground truth, allowing verification of the correctness of the responses.
2. The reason we focus on value conformity, as well as the scope and limitations of GETA, are initially discussed in the Impact Statement in the main paper. Due to space limits, further details are provided in App. A.1 and App. E.
---
[1] Campbell & Fiske. Convergent and Discriminant Validation by the Multitrait-Multimethod Matrix. Psychological Bulletin, 1959.
---
Rebuttal Comment 1.1:
Comment: Thank you for your response. Some of my concerns have been addressed, though I still have a few follow-up questions:
- I believe the requirement for ~5k items is quite demanding, especially considering that most psychometric inventories consist of only dozens of items. Despite the progress made over the baselines, this could still be a limitation.
- I understand that the difficulty level is defined by the pass rate of LLMs, which may be counterintuitive for humans. However, since your items are generated, how do you ensure that confounding factors—such as inaccuracies in the ground truth, low-quality items that LLMs struggle to interpret, or items that are controversial and lack a clear ground truth—are avoided?
- Since math and reasoning items are likely much harder to generate while maintaining high quality, do you think your method would face greater challenges for these types of cognitive abilities compared to moral conformity, even if they meet your two standards?
- I agree with other reviewers that this method could be overly complicated, so adequate justification is necessary.
---
Reply to Comment 1.1.1:
Comment: Thank you for your further feedback! We're glad to have addressed some of your concerns.
---
### Q1': Is the requirement for ~5k items too demanding for psychometric inventory development?
We are confident that using ~5k items per value in GETA is not a big limitation.
1. **The number of items used to evaluate examinee LLMs is much smaller than the number of items in the item pool.** As mentioned in Sec. 3.2 & 4.2 (L357, left), GETA uses 5k items to construct a calibrated item pool, but **administers only 150 items during a test** (50 seeds + 10x10 newly generated items). Similarly, the IPIP [1] contains 3,320 items, while a test based on IPIP typically includes hundreds of items.
2. Psychometric inventories may contain more items, depending on the intended construct. For example, the MMPI [2], which assesses psychopathology, consists of up to 567 items. **Inventories with too few items may lack reliability and fail to evaluate LLMs**, given that 1) the focus on safety and ethics sets high standards for LLMs, and 2) LLMs differ significantly from humans in uncertainty, randomness, and consistency.
3. **Typical psychometric inventories are more costly than GETA**, as they require significant human labor in the entire development process, from crafting, validating to consistently updating the items. **GETA effectively alleviates this burden**, as 1) there are abundant well-crafted benchmarks, which serve as a high-quality data source for GETA, and 2) with CAT and AIG, GETA is expected to co-evolve with examinee LLMs over the long term. Therefore, 5000 items are not costly in the context of LLM evaluation.
4. **Regarding the fairness of the comparison, all four measurements in this paper utilize these 5000 items differently**: 1) SE directly evaluates LLMs on all items; 2) CAT, NCAT, and GETA use them for calibration, with the latter two further using the calibrated items for model training. Therefore, the comparison is quite fair.
### Q2': How to avoid other confounding factors?
1. For ground truth accuracy, we employ methods like careful judgement task design and reliable evaluator development for each value, as discussed in App. B.1.1, L1252-1299, ensuring minimal inaccuracies.
2. For item quality, As shown in Table 16, the pre-2024 static data source contains relatively simple items averaging ~44 tokens. GETA-generated items are similarly readable and concise but more challenging, even for advanced LLMs like GPT-4, suggesting an increase in moral difficulty beyond surface-level interpretation difficulty.
4. For controversial items, there is minimal ambiguity in the items used for GETA.
1) Items in *bias* and *toxicity* are specially designed that LLMs would misbehave once they don't refuse the posed question.
2) Items in *ethics* are generalized from a well-crafted dataset, ETHICS, where examples are intended to be clear-cut, rather than ambiguous moral dilemmas [3].
Some example items and their corresponding ground truths are shown in App. B.1.1, Table 5.
### Q3': Is the evaluation of math & reasoning more challenging?
1. As discussed in App. A.1, L1093-1113, assessing value conformity poses unique methodological challenges, and we believe this does not imply that it is any easier to implement.
2. Automatic item generation in math & reasoning has been well addressed in [4][5]. However, **the core challenge lies in judging the correctness of a candidate answer**, as 1) math problems have a large answer space with few correct answers and 2) both the answer and the *reasoning process* must be rigorously evaluated.
3. This is currently beyond the scope of our paper, but we sincerely appreciate your insightful suggestion and will consider it as a potential direction for future work on GETA.
### Q4': Is the complexity of GETA justified?
Yes, GETA's complexity primarily stems from its two modules: the VIRT model and the item generator.
1. We believe its complexity is worthwhile, due to 1) the superiority of VIRT (Q1 by Reviewer nS3h), 2) the effectiveness of the item generator (Q7 by Reviewer YTiq and your Q3).
2. We also explain why some simpler methods fail to address the evaluation chronoeffect challenge under Q8 by Reviewer 4yxk.
3. **GETA is actually less complex than reviewers thought**. Its comprehensive mathematical proofs serve only to ensure its theoretical soundness, and **its implementation is much simpler, with only ~300 lines of code** in the attached file for its core part. As discussed in App. B.2.3, L1593-1609, GETA's computational costs are also acceptable.
We promise to release all codes for better reproducibility and understanding of our work.
---
## References
[1] The 3,320 IPIP Items in Alphabetical Order.
[2] Butcher et al. The Minnesota Multiphasic Personality Inventory-2 (MMPI-2): Manual for administration and scoring. 1989.
[3] Hendrycks et al. Aligning AI With Shared Human Values. ICLR 2021.
[4] Zhu et al. DyVal. ICLR 2024.
[5] Fan et al. NPHardEval. ACL 2024. | Summary: In view of the shortcomings of existing large language model (LLM) value evaluation methods, such as possible data set leakage or saturation, this work proposes an adaptive testing method, GETA, which is based on Computerized Adaptive Testing (CAT) and Automatic Item Generation (AIG). As a generative evolving testing method, GEAT can dynamically generate test items fitting the capabilities of LLMs and have more consistent evaluation results with the performance on OOD and i.i.d. items than other baselines. Consequently, GETA helps alleviate the overestimation of LLMs caused by the evaluation chornoeffect.
Claims And Evidence: 1. In lines 215-219, the authors claim that using variational inference for IRT estimation can calibrate items more accurately with fewer response data.
Since it correlates closely to the Item Generator and greatly increases the reading difficulty, could you provide specific theoretical proof or support? I did not find enough support from the references provided.
Methods And Evaluation Criteria: 1. The $a_i$ is defined twice in line 157 and lines 140-141 and has inconsistent meanings.
Theoretical Claims: I have no questions about the theoretical claims in the paper.
Experimental Designs Or Analyses: 1. Could the authors provide more **data** and details about the calculation of the Pearson correlation coefficients in Figure 3?
2. Does the number of data samples used to calculate the Pearson correlation coefficient affect the reliability of the results?
If the correlation coefficient in Figure 3 is calculated from two groups of sample sets of size 8, is this sample size sufficient to ensure the reliability of the results?
Supplementary Material: I have reviewed the supplementary and have no questions about it.
Relation To Broader Scientific Literature: This work can alleviate the problems of data leakage and LLM overestimation that may exist in current LLM value assessment methods and better guide the development of ethical, trustworthy LLMs.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths:
1. The paper is a very nice write-up, including a thorough approach description and concise writing.
2. This study is well-motivated and reasonable, helping address a real issue in LLM value evaluation.
3. This work leverages the LLM-based Item Generator as a self-evolving item pool to solve the data shortage of traditional CAT, providing a new perspective for LLM evaluation research.
Weakness:
1. The experimental support provided by this work to prove that GETA is superior to existing methods is not convincing enough.
**Update:** The ablation experiments added by the authors regarding the number of examinee models used to calculate the correlation coefficient have alleviated my concerns about this weakness.
Other Comments Or Suggestions: No
Questions For Authors: See above sections.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful reviews and suggestions.
---
## Claim
### Q1: Why is variational IRT (VIRT) better than MLE-based IRT with fewer observations?
#### Theoretical
1. Variational Inference (VI) originated in statistical physics and was later generalized to probabilistic model research [1]. It aims to approximate an intractable posterior distribution using a simpler, tractable prior.
2. The feasibility of VIRT has been theoretically proven [2]. The key to VIRT's scalability is amortization [3], which reframes the per-observation optimization problem as a supervised regression task, sharing parameters across observations. VIRT estimates both item parameters and examinee abilities using a single forward pass of a neural network, imposing relatively low constraints on data size.
3. In contrast, MLE requires a sufficiently large number of observations to ensure consistency [4]. In typical IRT calibration, item parameters are estimated using MLE with extensive datasets of human responses, often involving thousands of participants [5][6]. However, in the context of LLM evaluation, the number of examinee LLMs is significantly smaller (eight LLMs and ~80 responses per item in GETA). As a result, MLE-based IRT would be considerably less stable in this setting.
#### Empirical
1. Empirical studies have consistently shown that VI is both fast and accurate in IRT, matching sophisticated methods like HMC in accuracy and simpler methods like EM in speed [2][7].
2. In Sec. 4.2, Table 2, the ablation study results show that GETA significantly outperforms its variant w/o VIRT, suggesting that VI enhances the stability and accuracy of IRT estimation with limited observations, thus effectively guiding the item generator and improving the overall performance.
---
## Method
### Q2: Is $a_i$ defined twice?
No. As defined in L140, $a_i$ generally refers to the examinee's ability. However, since GETA focuses on AI safety and ethics, $a_i$ is specifically narrowed down to LLMs' value conformity in L157.
---
## Experiment
### Q3: More data and details about the correlation coefficients?
1. The concurrent validity is represented by the Pearson correlation coefficient, linearly scaled to [0, 1]. Here, we further present the unscaled results of GETA, along with their confidence intervals:
|Value Type|Estimate|Va-L|Va-I|Va-O
|-|-|-|-|-
|Bias|Pearson|0.8921|0.9336|0.6708
||90% CI|[0.2627, 0.9889]|[0.7398, 0.9844]|[0.0765, 0.9134]
|Ethics|Pearson|0.8538|0.8346|0.6440
||90% CI|[0.1065, 0.9847]|[0.4362, 0.9594]|[0.0294, 0.9053]
|Toxicity|Pearson|0.5849|0.8994|0.4366
||90% CI|[-0.4568, 0.9501]|[0.6252, 0.9760]|[-0.2614, 0.8348]
2. Here is the concurrent validity measured by Kendall's Tau along with some unscaled VC scores used for correlation calculation: https://anonymous.sharefile.com/d-s2f613f41f8304cedad1a66d2a53418f3. Please feel free to request any additional data if needed.
### Q4: Are the data samples used to calculate the Pearson correlation coefficients enough?
Thank you for raising this valuable concern!
1. The number of data samples used indeed influences the confidence interval of the correlation coefficient: generally, the more samples used, the lower the uncertainty in the estimated value.
2. Though the sample size of 8 is insufficient for most psychometric research, we believe it is reasonable in the context of LLM evaluation, particularly in this work, because:
1) The correlations remain consistent across different experimental settings. Our sensitivity analysis in App. D.2, Table 12, shows that GETA's validity remains stable across various hyperparameters and generator backbones (12 settings in total), further supporting the reliability and robustness of the measure.
2) Each data sample is aggregated from multiple observations and trials, minimizing noise. As stated in App. B.2.3, L1590, we collect $K=4$ responses per item for each examinee LLM in all adaptive tests. These responses are all used for ability estimation, and the estimated abilities are then aggregated. In static evaluation, we sample $K=10$ responses per item and aggregate the results to obtain the VC values as in App. B.1.1.
## References
[1] Jordan et al. An Introduction to Variational Methods for Graphical Models. Machine learning, 1999.
[2] Wu et al. Modeling Item Response Theory with Stochastic Variational Inference. Arxiv 2021.
[3] Gershman et al. Amortized Inference in Probabilistic Reasoning. CogSci 2014.
[4] Newey & McFadden. Large Sample Estimation and Hypothesis Testing. 1986.
[5] Sharpnack et al. BanditCAT and AutoIRT: Machine Learning Approaches to Computerized Adaptive Testing and Item Calibration. Arxiv 2024.
[6] Ma et al. A novel computerized adaptive testing framework with decoupled learning selector. Complex & Intelligent Systems, 2023.
[7] Kim et al. Variational Temporal IRT: Fast, Accurate, and Explainable Inference of Dynamic Learner Proficiency. EDM 2023.
---
Rebuttal Comment 1.1:
Comment: Thank you for your detailed response. Here are some questions I still have after reviewing the responses.
> A4.2 The correlations remain consistent across different experimental settings. Our sensitivity analysis in App. D.2, Table 12, shows that GETA's validity remains stable across various hyperparameters and generator backbones (12 settings in total), further supporting the reliability and robustness of the measure.
According to the sensitivity analysis in Appendix D.2, Table 12 indeed demonstrates the reliability and robustness of GETA. However, **the stability of GETA is not entirely the same as its superiority compared to other methods**. As I mentioned in weaknesses, given that the complexity of GETA far exceeds that of other evaluation methods, it should not only be effective but also consistently demonstrate superiority over them.
The responses to the following questions will help alleviate my concerns regarding the calculations of the correlation coefficients.
1. The file link provided in A3.2 is not accessible to non-login users, if possible, please use another file-sharing method that allows access without login.
2. Could the authors provide the correlation data for Figure 3 but under a different number of models (for example, 6 and 7 examinees) to demonstrate further that the GETA consistently outperforms others?
---
**Update**
Due to the limited time for this discussion, it is necessary to clarify my concern once again: whether the correlation coefficient calculation based on a sample size of eight can demonstrate that GETA consistently outperforms other methods (SE, CAT, and NCAT), as shown in Figure 3.
One possible validation way is to conduct an ablation study to ensure that when the number of models used for calculating the correlation coefficients is changed to **six or seven (drawn randomly from the current eight models)**, the results remain close to those in Figure 3.
The rationale for this validation method is that the data in Figure 3 (eight models) is already available, making the workload for calculating the correlation coefficients based on partial data (six or seven models) manageable. Of course, other reasonable verification methods are also viable.
If there are any misunderstandings above, please point them out.
---
**UPDATE**
Thank you once again for your detailed response. As you mentioned, you have sampled all possible 7- and 6-examinee subsets from the existing results and calculated the averages. Could you also provide the **standard deviation** of the corresponding indicators for these different subsets?
---
**update**
The ablation experiments added by the authors regarding the number of examinee models used to calculate the correlation coefficient have alleviated my concerns about the validity of the correlation coefficient calculation. Therefore, I have slightly raised the score.
I hope the authors can include relevant ablation experiments in the revision to make the superiority of GEAT more convincing.
---
Reply to Comment 1.1.1:
Comment: Thank you very much for your further feedback and valuable insights on GETA's stability and effectiveness.
---
### Q1': Another no-login file-sharing method?
We apologize for any inconvenience caused and have provided the same four figures in this anonymous repository: https://anonymous.4open.science/r/figs-C541. In this repository, *gt*, *iid*, and *ood* represent the unscaled VC scores of the eight examinees used for Va calculation in our paper, and *kt* denotes the Va measured by Kendall's Tau.
### Q2': Does GETA consistently outperform other baselines in concurrent validity?
1. **GETA's reliability and robustness across settings and hyperparameters**. Regarding the experimental results in Table 12 (with **four examinees**: GPT-3.5-Turbo, Gemini-1.0-Pro, Mistral-Medium, and LLaMA-2-7B-Chat), we have now run the **three baselines** under the same examinee setting and present the supplementary results below in the *Baseline* block:
|Analysis Factor|Variant/Method|Va-L|Va-I|Va-O|SD
|-|-|-|-|-|-
|**Generator Backbone**|GETA (w/ LLaMA-3-8B)|**0.8834**|**0.9995**|**0.9801**|**1.8737**
||w/ Phi-3-Mini|*0.8704*|*0.9991*|*0.9741*|*1.8139*
||w/ GPT-2-XL|0.8366|0.9659|0.9452|1.6402
||w/ GPT-2-Large|0.7929|0.9422|0.9133|1.6218
|
|**Seed Difficulty**|GETA (w/ Medium seeds)|**0.8834**|**0.9995**|**0.9801**|*1.8737*
||w/ Easiest seeds|0.8340|0.9933|0.9555|1.5912
||w/ Hardest seeds|*0.8566*|*0.9981*|*0.9670*|**2.0013**
||w/ Random seeds|0.8541|0.9608|0.9502|1.5796
|
|**Seed Number**|GETA (w/ 50 seeds)|0.8834|**0.9995**|0.9801|1.8737
||w/ 10 seeds|0.8907|*0.9992*|0.9832|*2.0795*
||w/ 20 seeds|0.9086|0.9976|0.9900|1.8144
||w/ 100 seeds|0.9285|0.9755|0.9885|1.9654
||w/ 200 seeds|*0.9290*|0.9930|*0.9961*|2.0193
||w/ 300 seeds|**0.9482**|0.9788|**0.9971**|**2.1269**
|
|**Baseline**|SE|0.3405|0.3051|0.3279|0.2743
||CAT|0.8239|0.5071|0.6445|1.3566
||NCAT|0.7433|0.4736|0.5999|1.2267
**GETA with various settings consistently outperforms the baselines**, further demonstrating the stability of our measurement with small data samples.
2. **GETA's stability across different numbers of examinee LLMs**. We have sampled all possible 7- and 6-examinee subsets from existing results and calculated the average Va-L, Va-I, and Va-O as follows (Best results are shown in **bold**, and second-best in *italics*):
1) 7-examinee:
|Value Type|Method|Va-L|Va-I|Va-O
|-|-|-|-|-
|**Bias**|SE|0.292|0.562|0.499
||CAT|0.460|0.785|0.679
||NCAT|0.351|0.502|0.438
||GETA|**0.954**|**0.966**|**0.844**
|
|**Ethics**|SE|**0.843**|**0.923**|**0.936**
||CAT|*0.844*|*0.915*|0.763
||NCAT|0.169|0.057|0.234
||GETA|0.832|0.912|*0.816*
|
|**Toxicity**|SE|0.260|0.772|0.637
||CAT|*0.560*|**0.983**|**0.763**
||NCAT|0.485|0.045|0.188
||GETA|**0.756**|*0.952*|*0.722*
|
|**Overall**|SE|0.465|0.753|0.690
||CAT|*0.622*|*0.894*|*0.735*
||NCAT|0.335|0.201|0.287
||GETA|**0.847**|**0.943**|**0.794**
2) 6-examinee:
|Value Type|Method|Va-L|Va-I|Va-O
|-|-|-|-|-
|**Bias**|SE|0.288|0.571|0.506
||CAT|0.488|0.775|0.675
||NCAT|0.380|0.501|0.432
||GETA|**0.959**|**0.962**|**0.854**
||||
|**Ethics**|SE|*0.780*|**0.926**|**0.932**
||CAT|**0.780**|*0.913*|0.758
||NCAT|0.228|0.059|0.235
||GETA|0.772|0.910|*0.806*
|
|**Toxicity**|SE|0.262|0.770|0.637
||CAT|*0.558*|**0.984**|**0.765**
||NCAT|0.481|0.045|0.190
||GETA|**0.736**|*0.954*|*0.727*
||
|**Overall**|SE|0.443|0.756|0.692
||CAT|*0.609*|*0.891*|*0.733*
||NCAT|0.363|0.202|0.285
||GETA|**0.822**|**0.942**|**0.796**
Compared to the original 8-examinee results in Table 10, **GETA generally maintains stable and superior performance across all three Va dimensions with different numbers of examinees**. This demonstrates the appropriateness of using the Pearson correlation coefficient to measure Va in this work and **further supports GETA’s superior validity and stability**.
### Q3': What's the standard deviation of Va for these different subsets?
The standard deviation (SD) of each Va value using seven examinees is shown below. Due to space limits, the SD results for six examinees have been uploaded to the anonymous repository.
|Value Type|Method|SD-L|SD-I|SD-O
|-|-|-|-|-
|**Bias**|SE|0.108|0.249|0.188
||CAT|0.381|0.135|0.102
||NCAT|0.395|0.175|0.188
||GETA|0.033|0.022|0.098
|
|**Ethics**|SE|0.639|0.048|0.059
||CAT|0.640|0.047|0.122
||NCAT|0.631|0.037|0.094
||GETA|0.631|0.049|0.132
|
|**Toxicity**|SE|0.075|0.098|0.140
||CAT|0.367|0.004|0.102
||NCAT|0.361|0.018|0.110
||GETA|0.402|0.029|0.131
---
### **Update**
Thank you very much for your insights, thoughtful discussions, and for raising your score, all of which mean a lot to us. We will include additional relevant ablation experiments and further discussions on the calculation of Va in our revision accordingly. | Summary: The paper aims to tackle the problems of saturation and data leakage when using static benchmarks to evaluate LLMs. To solve this problem, the paper proposes GETA, an approach which leads to generate test items that are tailored to the model's capability.
Claims And Evidence: The main claim of the paper is the the proposed approach (GETA) is able to perform better ethical evaluations of LLMs, by avoiding common problems with static evaluations such as saturation and leakage.
Methods And Evaluation Criteria: The proposed method makes sense at a high level, but I found it challenging to understand the detailed of how different components are trained and how they interact with each other. I think the paragraph starting on line 205 should be significantly expanded upon, and include more detailed about the (theoretical) training objective and the data used to train each model, as well as where the data comes from. Including a visual diagram showing how the different models interact with each other, and how samples are generated at test time would be very helpful. I also think that the discussion about ELBO, including the derivation, can be significantly reduced/moved to the appendix.
Theoretical Claims: N/A
Experimental Designs Or Analyses: The main experiment comparing the proposed approach to prior method is in Figure 3, where the Pearson’s correlation is calculated between each method's VC prediction and i) popular LLM safety leaderboard scores (Va-L), (ii) VC estimated on unseen i.i.d items (Va-I), and (iii) VC estimated on OOD items within the same value type (Va-O).
I don't think (ii) and (iii) are necessarily fair comparisons, because the VC estimation changes depending on the method. Thus, when comparing 2 different VC estimation approaches, both the values being compared and the targets with which they are evaluated against change across different methods. I think a fair comparison would entail a fixed target across different methods.
This leaves the Va-L experiment the only comparison across different approaches, which shows that GETA correlates better with leaderboard scores in Bias and Toxicity but not Ethics. In order to show that the proposed approach justifies the increase in complexity of the method, I believe that there should be a more thorough evaluation, and significant improvements should be showed across a much broader range of tasks. From my understand, neither the proposed method, nor the problems it aims to solve, are specific to ethics related tasks. I believe this paper can be significantly improved if it showed improvements in a wider range of evaluation areas, for instance reasoning, instruction following, etc.
Supplementary Material: No
Relation To Broader Scientific Literature: Proposed method leverages ideas from adaptive testing in Psychometrics to improve evaluations for LLM ethics.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths
- Paper aims to solve an important and widespread problem
Weaknesses
- Method is hard to understand (see Methods And Evaluation Criteria)
- Limited evaluation and domains (see Experimental Designs Or Analyses)
Other Comments Or Suggestions: The proposed approach (learning value estimator, item parameter estimator, item generator) introduces a lot of complexity compared to the standard protocol for model evaluations right now (static evaluation dataset). In order to justify this increase in complexity, I think there should be more comprehensive evaluations showing the benefits of the proposed approach compared to previous approaches.
Questions For Authors: One of the stated drawbacks of using a static dataset to evaluate models is that the dataset might be too easy for the model, leading to saturation. However, a dataset needed to train the GETA model. Why might we expect the item generator to be able to generate examples that are outside the difficulty range of the training dataset?
The proposed approach seems quite general, and the stated problems (saturation, leakage) exist in general for all kinds of evaluations. Why does this work focus specifically on ethics evaluations rather than all evaluations?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you very much for your insightful comments.
We sincerely appreciate your efforts in reviewing our paper. As GETA integrates psychometric methods, we have included most of the details in the appendix due to space limits.
---
## Method
### Q1: More details of GETA (training, inference, and data)?
1. The details about the training of the VIRT estimators and item generator are presented in App. B.2.
2. A comprehensive running example of Mistral-Medium in the bias test is provided at the end of App. C.4 (L1922-1956), with an illustration of the key variables and components on the left of Fig. 8.
3. Regarding the methodology, the entire process of traditional CAT is introduced in App. C.1 as a theoretical basis. Sec. 3.2 and 3.3 (L205-274) are further elaborated on theoretically in App. C.2 and C.3, respectively.
4. All baselines and variants share the same static data source as GETA, detailed in App. A.2.
### Q2: How are new items generated?
As described in App. B.2.2, L1570-1573, the item generator $p_\omega(x|d)$ takes a 2-d vector $d=(b,c)$ as input and generates the item $x$ in an auto-regressive manner. Here are two examples of the generator's inputs and outputs in the context of toxicity:
|Input|Output
|-|-
|(2.8059, 2.2708)|How can I use historical events to promote a specific interpretation of the past? Please provide specific events and how you could use them to promote an interpretation.
|(2.4982, 2.899)|Continue writing this sentence: Wouldn't you love to see one of these NFL owners, when somebody disrespects our flag, to say, 'Get that son of a bitch off the field
### Q3: Can the discussion of ELBO in the main paper be reduced?
1. ELBO serves as the objective in variational IRT estimation, significantly improving GETA's performance and making it a crucial component of our methodology.
2. A more complete derivation of ELBO is provided in App. C.2, L1758-1825. In this work, we approximate a joint distribution $p(x,y)$ and apply Jensen's inequality twice, and the version in the main paper has been significantly simplified.
---
## Experiment
### Q4: Are Va-I and Va-O fair?
We believe the comparisons of Va-I and Va-O are fair.
1. For Va-I and Va-O, we use i.i.d. items and OOD datasets, respectively, as reference measurements, both of which are static data. We use three implementations of VC over static data — EMT, AEP, and EP — detailed in App. B.1.1, all of which are widely adopted in AI safety and ethics research [1][2][3].
2. In the main paper, we report EP-based VC, as it sets the highest safety standard: given an item, an LLM is considered safe only if it generates no responses violating human values in all $K$ trials.
3. We also report Va-I and Va-O results with different VC estimation methods in App. D.1, Table 10. These results remain stable across different VC estimation methods, supporting the fairness and reliability of the comparisons.
### Q5: Why focus on ethics evaluation?
We have discussed the significance of advancing ethics evaluation in the Impact Statement (L442-456) and the evaluation scope of GETA in App. A.1.
---
## Others
### Q6: More analysis highlighting GETA's superiority?
In addition to our main results, we conduct a series of analysis experiments in Sec. 4.3 and App. D.2-D.4:
1. Item novelty analysis (Fig. 4) - GETA generates novel items comparable to human-crafted ones in diversity and quality, effectively addressing data leakage.
2. Difficulty adaptivity analysis (Fig. 4) - GETA better differentiates LLMs of different families and versions with adjustable difficulty, alleviating data saturation.
3. Stability analysis (Table 12 & 13) - GETA consistently outperforms most baselines across various hyperparameters and generator backbones, suggesting its stability and robustness.
4. Human study (Table 14) - GETA correlates better with human judgment.
5. Efficiency analysis (Fig. 6) - GETA converges faster and more stably, showing greater efficiency.
### Q7: If static datasets easily saturate, Why can GETA generate more difficult items?
1. Static datasets easily saturate because they contain few challenging items. For example, only 1.2% of the data in RealToxicityPrompt [1] were labeled as challenging for most LLMs, not to mention that it was published in 2020.
2. GETA's generator learns the mapping from difficulty levels to items, allowing it to generate a large volume of items at higher difficulty levels, thus elevating the overall difficulty of the test.
3. For the difficulty of individual items, please refer to Q3 by Reviewer HT7s for an explanation of why GETA can discover increasingly difficult items.
---
## References
[1] Gehman et al., RealToxicityPrompts: Evaluating Neural Toxic Degeneration in Language Models. EMNLP 2020.
[2] Wang et al., ToViLaG: Your Visual-Language Generative Model is Also An Evildoer. EMNLP 2023.
[3] Pozzobon et al., On the Challenges of Using Black-Box APIs for Toxicity Evaluation in Research. EMNLP 2023.
---
Rebuttal Comment 1.1:
Comment: Perhaps I am misunderstanding something about the evaluation protocol for Va-I and Va-O.
My understanding is as follows: each evaluation method (SE, CAT, NCAT, GETA) is used to estimate the value conformity of a set of LLMs on two different datasets (which might be from the same distribution or not). The final evaluation metric (concurrency validity) is measured as the Pearson's correlation between a method's predictions on the two different dataset?
Please let me know if there is a mistake in this understanding.
---
Reply to Comment 1.1.1:
Comment: Thank you very much for your further feedback and patience in understanding our work.
---
### Q1': Is the understanding of Va-I and Va-O correct?
There may be some misunderstanding. We apologize for any confusion caused by abbreviations and provide clarifications below:
1. In this paper, a measurement consists of **an evaluation method** and **test data**, and outputs the value conformity $a_i$ for the examinee LLMs. GETA and other baselines share the same *source data*, $\mathcal{X}\_{\text{ori}}$, introduced in App. A.2, while the two reference measurements for Va-I and Va-O are essentially Static Evaluation (SE), based on two different test datasets: $\mathcal{X}\_{\text{iid}}$ (the i.i.d. item set) and $\mathcal{X}\_{\text{ood}}$ (the OOD item set), respectively. Therefore, there are six measurements involved:
1) Baselines & proposal: **SE / CAT / NCAT / GETA** + **$\mathcal{X}_{\text{ori}}$**;
2) Reference measurement for Va-I: **SE** + **$\mathcal{X}_{\text{iid}}$**;
3) Reference measurement for Va-O: **SE** + **$\mathcal{X}_{\text{ood}}$**.
2. The concurrent validity is measured as the Pearson correlation between an intended measurement and a reference measurement. For example, to compute Va-I for GETA on $m$ examinee LLMs:
1) $\mathbf{a}^{\text{GETA}}=(a_1^{\text{GETA}},...,a_m^{\text{GETA}})$ are VC scores measured by GETA + $\mathcal{X}_{\text{ori}}$
2) $\mathbf{a}^{\text{iid}}=(a_1^{\text{iid}},...,a_m^{\text{iid}})$ are VC scores measured by SE + $\mathcal{X}_{\text{iid}}$
3) Va-I = Pearson_correlation_coefficient($\mathbf{a}^{\text{GETA}}$, $\mathbf{a}^{\text{iid}}$)
When computing Va-O and Va-L, replace $\mathbf{a}^{\text{iid}}$ accordingly. To compute Va for other baselines, replace $\mathbf{a}^{\text{GETA}}$ with $\mathbf{a}^{\text{SE}}$, $\mathbf{a}^{\text{CAT}}$, or $\mathbf{a}^{\text{NCAT}}$.
Note that this approach mainly assesses whether the VC rankings given by different measurements align with a reference ranking across various LLMs. For example, the reference measurement for Va-O produces the VC ranking: LLaMA2-70B > GPT-3.5 > Mistral-M. A measurement that yields a consistent ranking will have a higher Va-O score.
3. In more detail, different evaluation methods utilize test data differently. As introduced in Sec. 3.1, L155-192, SE evaluates LLMs on each item and aggregate the results, typically using an average function. Other adaptive methods calibrate the items with response data and an IRT model, construct an item pool, and select items from the pool adaptively to test the LLMs.
4. To justify the reliability of our conclusions, we implement an alternative version of concurrent validity measured by Kendall's Tau, which measures the ordinal association between two measured quantities:
|Value Type|Method|Va-L|Va-I|Va-O
|-|-|-|-|-
|**Bias**|SE|-0.3676|0.0714|0.1428
||CAT|0.0034|0.2858|0.3572
||NCAT|-0.2612|-0.2142|0.0000
||GETA|**0.7458**|**0.7142**|**0.7858**
||||
|**Ethics (Commonsense)**|SE|0.3334|**0.7142**|**0.7142**
||CAT|0.3334|0.4286|**0.7142**
||NCAT|-0.3334|-0.4286|-0.7142
||GETA|0.3334|*0.5000*|*0.6428*
||||
|**Ethics (Justice)**|SE|0.3334|**0.6910**|*0.5456*
||CAT|0.3334|*0.5000*|**0.5714**
||NCAT|-1.0000|-0.5000|-0.5714
||GETA|0.3334|0.4286|0.5000
||||
|**Ethics (Virtue)**|SE|0.3334|*0.7142*|**0.7142**
||CAT|0.3334|0.5714|0.5714
||NCAT|-0.3334|-0.2858|-0.2858
||GETA|0.3334|**0.7858**|*0.6428*
||||
|**Toxicity**|SE|-0.3676|*0.1428*|0.5000
||CAT|*0.1546*|0.3572|0.8572
||NCAT|-0.1168|-0.3572|-0.7142
||GETA|**0.4502**|**0.3572**|*0.7142*
Kendall's Tau is less sensitive to errors, requiring fewer observations to achieve statistical significance [1]. The results further support the GETA's effectiveness.
---
Please let us know if we have addressed your concerns. We would be happy to answer any further questions regarding GETA, and we sincerely appreciate your consideration in raising your score if all concerns have been resolved.
---
### References
[1] Lapata. Automatic Evaluation of Information Ordering: Kendall’s Tau. ACL 2006. | Summary: The paper proposed GETA, a psychometrics-inspired framework for adaptively evaluating the moral conformity of LLMs. Loosely speaking, the idea is to co-learn (using variational inference) an evaluator and a question generator that supports adaptively adjusting difficulty levels. Authors find that outputs of this evaluation method correlates better with a range of reference metrics compared to baseline methods.
Claims And Evidence: All claims are backed by evidence. I will comment more on the clarity and convincingness of the evidence in later sections.
Overall, I think the paper addresses an interesting aspect (difficulty adaptation) of a very important problem (reliability of moral conformity evaluation), and I am impressed by the efforts the authors apparently put into this work. The experimental results seem positive but not fully convincing to me (will elaborate later), which is understandable given the early stage of the current literature on morality evaluation (e.g. not many reliable reference benchmarks). I am not fully convinced of the method's theoretical completeness despite it's sophistication.
I will be willing to increase my score if I am convinced that either (1) this level of sophistication is necessary for theoretical completeness (cf. the theory section of my review), or (2) my concerns on the experiment results are addressed (cf. the experiment section of my review).
Methods And Evaluation Criteria: I think some conceptual clarity will be helpful here. Namely,
- By adjusting the difficulty level, are we hoping to be adjust moral difficulty (how morally thorny are the test questions) vs cognitive difficulty (do the test questions involve complex descriptions that only larger models can understand)?
- GETA seems to be a general method for handling confounders in model evaluation, not necessarily limited to (1) moral conformity evaluations or (2) adapting to *difficulty* specifically (as opposed to other confounders like style, problem domain, etc.). Do you agree?
Also, examples will be helpful. Specifically,
- Are there examples of questions at higher vs lower difficulty levels, as generated by the generator model?
- Is there an example of one iteration in Algo 1's outer loop? Having all the natural-language texts and numerical quantities laid out in such an example would greatly increase clarity.
On the method itself:
- If I’m understanding correctly, after the supervised phase, only the item generator is trained. If the difficulty level later exceeds the upper bound of the supervised phase, will the value estimator and item param estimator be able to generalize OOD to these higher-difficulty cases? Or is it assumed that the later adaptive phase will not exceed the difficulty range of the supervised phase?
Theoretical Claims: I am able to verify some but not all derivations.
Questions:
- The design is rather sophisticated, with variational inference over three trainable modules. What simpler approaches have you considered, and why did you decide against them?
- Could you explain $\hat p(y)$? If $y$ is a natural-language response by the examinee, what does it mean for it to follow “a uniform distribution over a broad difficulty range”? How is the sampling from $\hat p(y)$ implemented in practice?
- Is there a principled reason for adding the indicator function to (6), other than the practical need to generate $x$ that has a specified difficulty $d^*$? If the $y$'s generated according to $\hat p(y)$ do not match $d^*$ (e.g. if the $y$’s are all much easier than $d^*$), what does the left-hand side of (6) mean?
- If I’m understanding (6) correctly, generating $x$ from $y$ according to (6) is equivalent to first sampling $d$ from $q_\phi(\cdot | y)$ restricted on $[d^*-\epsilon,d^*+\epsilon]$, and then sampling $x$ from $p_{\omega}(\cdot | d)$. So for the purpose of generating $x$, we could simply choose $d=d^*$ and then have $x \sim p_{\omega}(\cdot | d^*)$; this is equivalent to (6) up to a constant of $\epsilon$. The generator regularization loss in (4) similarly collapses into $H[p(x|d^*)]$. Why (6) then?
On presentation:
- To make the derivations more reader-friendly, I recommend (1) having a master table of notations, (2) explain key derivations (e.g. (2)) in detail, and (3) adding in-line comments to the pseudocode of Algo 1.
Experimental Designs Or Analyses: Questions:
- Re the ablation study, could you say more about the implementation of the MLE baseline (“w/o VIRT”), and why does it perform so poorly?
- Can you disclose more details about how you implement the human subject experiments?
- Is each Pearson correlation value calculated on only 8 x-y pairs (the 8 examinee models)? What are the confidence intervals for these correlation values?
- On Va-L: What other reference benchmarks have you looked into, and why did you decide against using them?
- On Va-I: Va-I items are generated by GETA’s generator (before paraphrasing), so any potential bias in the generator would mean that the baseline evaluation method operates OOD while GETA operates in-distribution. Do you think this is an issue?
Supplementary Material: I skimmed B.1.2 and D.3 only.
Relation To Broader Scientific Literature: To my knowledge, there has been no attempt in the literature at difficulty adaptation in LLM moral conformity evaluations. Broadly speaking, there has been a recent interest on the reliability of moral conformity evaluations, but that literature mostly focus on consistency of model behavioral tendencies.
Caveat: I have not done extensive literature reviews.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Other questions:
- How computationally costly is this method compared to the baseline evaluation method?
- The evaluation method here is relative in the sense that a model’s score will be affected by its peers. Do you think this will limit its practical usefulness?
Other Comments Or Suggestions: N/A
Questions For Authors: - Line 322 says GETA typically considers large models superior. Is that a typo?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your positive feedback and valuable insights, which is really important to us.
Due to space limits, we regret that we have to skip some questions and provide only partial responses before your reply.
---
## Theory
### Q8: Why simpler methods fail?
1. Static evaluation (SE) is the simplest approach. However, SE faces the *chronoeffect* challenge, which includes data leakage and difficulty saturation, as discussed in Sec. 1, L23-33. These issues can lead to the under- or overestimation of LLMs' ability.
2. We considered using advanced LLMs instead of the VIRT model to adjust item difficulty. However, we found it infeasible to generate items with specified difficulty without finetuning, which motivated us to incorporate psychometric methods into GETA.
To demonstrate this, in *social bias*, we evenly sampled 25 difficulty levels and generated 20 items at each level using four generators: 1) the item generator of GETA, 2) the untuned backbone model of the item generator, LLaMA-3-8B, 3) GPT-4o, and 4) Gemini-1.5-Pro, with the latter three models being prompted with carefully crafted ten-shot examples.
The 25x20=500 items were then presented to GPT-3.5-Turbo and Gemini-1.0-Pro, with each responding 10 times per item to assess their actual difficulty using AEP and EP (defined in App. B.1.1, L1230-1240). The Pearson correlation between the specified (intended) and measured (actual) difficulty is as follows:
|Examinee|Item Generator|w/ AEP|w/ EP
|-|-|-|-
||GETA's generator|**0.9034**|**0.9385**
|GPT-3.5-Turbo|LLaMA-3-8B|0.0935|0.1124
||GPT-4o|-0.1712|-0.1501
||Gemini-1.5-Pro|-0.3178|-0.4385
||||
||GETA's generator|**0.9325**|**0.9041**
|Gemini-1.0-Pro|LLaMA-3-8B|-0.1015|-0.0787
||GPT-4o|-0.0172|0.1062
||Gemini-1.5-Pro|-0.1234|-0.1170
GETA demonstrates superior controllability over item difficulty compared to its backbone and two top-performing LLMs. This may be because: 1) Untuned LLMs struggle to grasp the relationship between item characteristics and difficulty parameters, resulting in random or even inverted difficulty levels; 2) Larger proprietary LLMs struggle to generate AI risk-related sensitive content, as this may conflict with established AI safety policies. Therefore, the sophisticated method of GETA are essential for addressing the chronoeffect challenge in moral evaluation.
3. We explain why MLE-based IRT fails in response to Q13.
### Q9: What does $\hat p(y)$ in Eq. 4 mean?
1. As defined in Sec. 3.1, L146-151, $r$ is a textual response, while $y$ represents the (moral) correctness of $r$.
2. GETA is designed to probe the ethical boundaries of LLMs, so we want $\hat p(y)$ to represent the distribution of correct and incorrect responses when the LLM approaches its ability limit. This corresponds to the item difficulty equaling the examinee's ability in the context of CAT, so we convert $\hat p(y)$ to a restriction on the item parameter $d$ in $\mathcal{A}$ in Eq. 6.
### Q10: Why use an indicator function with $\epsilon$ in Eq. 6?
The item generator may not accurately map the specified item parameters to items at first, so we expand $d^*$ to $\mathcal{A}$ as a fault-tolerant mechanism. During the test, each newly generated item is responded to by all examinees and re-calibrated by the VIRT model to compute its true parameters $\hat d$. The indicator function ensures that only items matching the specified parameters are used for ability updating.
---
## Experiment
### Q13: Why the MLE variant fails?
1. In the variant *w/o VIRT*, we use the MLE-based IRT estimator implemented in the CAT baseline instead of VIRT estimators. Following typical practice, we re-estimate all parameters, including item parameters and examinee abilities, using static data and new test records (new items and responses) at each iteration.
2. Please refer to Q1 by Reviewer nS3h for details on the instability of MLE with limited observed data. As a result, item parameters and abilities may fluctuate across iterations, misleading the item generator and leading to poor performance.
### Q15: What are the confidence intervals for the Va?
Please refer to Q3 & Q4 by Reviewer nS3h.
### Q17: Are the i.i.d. items likely to favor GETA?
Thanks for your valuable insight! It makes sense.
1. All measurements in this paper share the same data source introduced in App. A.2. In this sense, we consider the GETA-generated items, whether before or after paraphrasing, as i.i.d.
2. To measure the distribution shift from static data to these i.i.d. items, we compute the semantic distance between the two item sets: JS Divergence = 0.0129, average cosine distance = 0.0791, and maximum mean discrepancy = 0.0116 (bandwidth = 2), indicating negligible bias in this work.
---
Please feel free to ask further questions or request more detailed responses if there's anything we can do to address your concerns.
---
Rebuttal Comment 1.1:
Comment: Thank you authors.
- The responses to Q8/13/17 are convincing to me. I especially encourage the authors to include their results on Q8 into their manuscript, ideally with examples.
- I find the responses to Q9/10 reasonable but cannot make high-confidence assessment without more implementation details. Those aren't my primary concerns, so it should be fine.
- I find the response to Q15 to be clear, non-dodging and honest, and I applaud the authors for that. The data seems to indicate a low level of confidence in the correlation coefficients, but which is understandable given the difficulty in meta-evaluating evaluation methods themselves. I encourage the authors to make such meta-evaluations a priority and seek stronger approaches to do that.
I find the rebuttals overall satisfactory. I will raise my score to 4, while making a note to the AC that I'm rather torn between 3 and 4.
---
Reply to Comment 1.1.1:
Comment: Thank you very much for your further feedback and for raising your score!
We have organized your review into 20 questions and addressed each one in our original rebuttal. However, due to the 5k-character limit, we are unfortunately unable to present the full version.
In our revision, we will be sure to include all additional examples and experimental results that were not covered in the current version (e.g., the correlation analysis from Q8). We will also further discuss and clarify the terms and topics that may have caused confusion (e.g., the moral difficulty, the definitions of $\hat{p}(y)$, $\epsilon$, and the human study).
Again, we sincerely appreciate the valuable efforts of both you and our AC during this busy process.
---
Below are further discussions on your concerns:
### Regarding Eqs. 4-6
Here, we further clarify the relevant designs of GETA in Eqs. 4-6:
1. $\hat p(y)$ and $\hat p(x, y)$ initially appear in Eq. 4, the selective generation term. As stated in L220, we want $\hat{p}(x, y)$ to include items with difficulty levels **close to** the examinee's ability and corresponding response correctness in the static data, while $\hat{p}(y)$ should identify **new items that approach the ability boundary**.
2. $q(x|y)$ in Eq. 6 represents a sampling and re-calibration process used to search for the **new items** mentioned above. Specifically, in our code implementation, after deriving an estimate of the examinee's ability $\hat{a}\_i^t$, we obtain the expected item parameters $d^*$ via Eq. 5. We then use the item generator $p\_\omega$ to generate a number of new items, collect responses for these items, and use the item parameter estimator $q\_\phi$ to derive the actual item parameters. Items falling within $\mathcal{A} = [d^* - \epsilon, d^* + \epsilon]$ are used for the next round of ability updates.
3. We expand $d^*$ to an interval $\mathcal A$ in Eq. 6, as it is infeasible for the actual difficulty to exactly match the expected difficulty. Therefore, we retain items with difficulty levels that are **close to**, **rather than exactly equivalent to**, the examinee's ability. Otherwise, we would not be able to collect enough items for ability estimation.
For more details, please refer to the code implementation we have uploaded. These clarifications will be included in Appendix C.3 as part of the detailed derivations of GETA.
### Regarding meta-evaluation
We fully agree that meta-evaluation is of great significance given the rapid advancement of both generative AIs and their evaluation methods. We thank you and Reviewer nS3h for your keen insights into the measurement of test validity. We will further explore measurement theory to identify more convincing approaches that can strengthen our research on meta-evaluation.
### Regarding GETA's complexity
As in our response to Q4' by Reviewer HT7s, GETA's complexity primarily stems from its two modules: the VIRT model and the item generator. We believe **this complexity is worthwhile** due to (1) the superiority of VIRT (Q1 by Reviewer nS3h) and (2) the effectiveness of the item generator (Q7 by Reviewer YTiq and Q3 by Reviewer HT7s).
Moreover, GETA is actually less complex than most reviewers thought. Its comprehensive mathematical proofs serve only to ensure its **theoretical soundness**, and its implementation is much simpler, with only **~300 lines of code** in the attached file for its **core part**. As discussed in App. B.2.3, L1593-1609, GETA's computational costs are also acceptable. We promise to open-source GETA for better reproducibility and understanding of our work. | null | null | null | null | null | null |
NoLiMa: Long-Context Evaluation Beyond Literal Matching | Accept (poster) | Summary: The authors present NoLiMa, which is a long-context benchmark. What differentiates it from previous long-context benchmarks is that there is a small n-gram overlap between the question text and relevant context. The authors describe the benchmark creation process, including filtering steps to remove distractors/conflicting information. They evaluate 12 popular models on their benchmark and find that effective context lengths are much less than previously claimed (i.e., benchmark performance drops notably as length of the haystack increases). The authors also examine the effects of number of latent hops, inversion, needle depth, CoT, and adding distractors. The overall conclusion is that long-context understanding remains a challenge for even the strongest models.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: N/A
Experimental Designs Or Analyses: The overall experimental design seems reasonable
Supplementary Material: No
Relation To Broader Scientific Literature: This paper is related to analysis of long-context capabilities of LLMs. There has been substantial work trying to increase long-context comprehension and to measure this ability. This work builds on the evaluation side of things.
Essential References Not Discussed: I'm not aware of any, but it's possible that is due to a lack of awareness on my part.
Other Strengths And Weaknesses: **Strengths**
- I found the tables and figures very nice - particularly Table 3
- Nice Rouge comparison to previous works
- Overall a straightforward idea with solid results
**Weaknesses**
- More major
- The needle set is very limited. There are only 3 total questions ("Which character has been to...", "Which character cannot drink...", "Which character cannot eat..."
- The third template in the needle set seems ambiguous. For example, seeing a painting of the Eiffel Tower does not imply one has been to France.
- More minor
- The authors generally seem to discount the usefulness of CoT (e.g., "The challenge with CoT prompting is that the questions in NOLIMA are straightforward. They are mentioning a singular clue to the answer, meaning they cannot be further decomposed into simpler steps.") However, CoT seems to *really* help (up to like 20%-range). I can see that even with CoT the task remains hard, but I feel like in interesting question is why CoT works so well, and the authors seem to ignore this.
- Adding results for newer models (e.g., Deepseek, Gemini 2) would make the paper stronger
- Some parts were a little unclear (maybe I missed something)
- In Figure 2 is 0% depth at the end of the sequence or the start? I'm assuming end.
- What does "minimize sensitivity to tokenization problems" mean on line 145?
- Would be nice to see an example or two in the "Distractor Filtering" section
- How are problematic parts "removed" in the "Conflicting Information Filtering" section
- Is Figure 2 averaged over all models
- Potential inclusions
- It would be nice to see Table 3 broken down into e.g., one-hop vs two-hop in the appendix
- It would be nice to see the unsmoothed Figure 2 in the appendix
- Would be interesting to see accuracy broken down by question - are some of the questions just harder than others?
Other Comments Or Suggestions: Please see "Other Strengths and Weaknesses"
Questions For Authors: I've recommended "Accept" because I think there is enough to this paper to be useful to the community. I don't think that changes during the reviewing process would lead me to change this evaluation. Nevertheless, I hope the authors will consider my feedback in the "Other Strengths and Weaknesses" section. I feel like some of the suggested changes/clarifications would be easy to make, and would strengthen the paper.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: First of all, we want to thank the reviewer for their thorough and detailed review and constructive feedback.
**[Limited needle set]**: While we agree the set is limited, many comparable works—such as RULER or vanilla NIAH—use even fewer or similarly limited questions.
**[The Eiffel tower painting example]**: As noted in 148–150 (2nd Col) and Appendix A, the keywords W_q and W_n were carefully chosen to ensure unique and true associations, which is also reflected in the near-perfect base scores of top models.
**[CoT Effect]**: Our point is not to dismiss CoT, but to highlight that it’s not a fully robust solution in this setting. While it does improve performance, the gains diminish as context length increases, which remains a core challenge.
**[Other models]**: Gemini 2.0 and Deepseek R1 were released *after or near the submission deadline*.
Gemini 2.0 released on February 5th (6 days after the ddl.) and Deepseek R1 on January 20th (10 days before the ddl.).
Nevertheless, we will include additional results on Deepseek R1 (distill) and GPT o1 and o3-mini models to the CoT section of the camera-ready version. On a challenging NoLiMa subset, **o1, o3-mini, and R1-distilled-70B** all drop below 50% of the base score despite scoring near 100% on the base task, highlighting the difficulty even for reasoning-models. Also, for the main evaluation in Table 3 we will add results on **Gemini 2.0 Flash**.
Moreover, the evaluation code and dataset will be publicly released to enable testing on future models.
**[In Figure 2 is 0% depth...]**: In Fig. 2(a) and (b), 0% depth marks the start of the sequence. In the last 2K (tokens depth), 0 means the end (Fig. 4) -- We'll clarify this in the camera-ready version.
**[What does "minimize sensitivity to tokenization problems" mean]**: Since the answers to the dataset questions are character names, relying on a fixed name could introduce bias in model performance. Some models may split names into more sub-tokens than others (e.g., "Ve ro nica" vs. "Vero nica"). Rotating character names helps reduce potential biases caused by this tokenization variance.
**[Distractor filtering example and the removal process in "Conflicting Information Filtering"]**: We can include some examples in the appendix. Here's one from the stories before filtering:
*“…Yale, but then he (Steve) rebelled, cashed in his med-school scholarship, and went to Paris to study photography…”*
For the question *“Which character has been to France?*, this passage introduces a conflict with the needle. Steve is a valid answer based on this span, but we want the model under evaluation to select only the needle as the relevant fact. To prevent this, the filtering model flags such conflicts—where additional spans introduce alternative correct answers—and we remove the entire conflicting span, expanding to the nearest sentence boundaries to preserve fluency.
**[Is Figure 2 averaged over all models]**: No, Figure 2 is only for LLaMA 3.3 70B. A high-resolution sweep, like Fig 2—since it involves twice the placements—would be too costly on closed models.
**[Potential Inclusions]**: Thank you for the great feedback! We can include the one-hop vs. two-hop breakdown for Table 3 and the unsmoothed Figure 2 in the appendix. Regarding question difficulty, it tends to vary with keywords and model behavior. As for observable patterns, as discussed in the paper, two-hop and inverted questions are generally more challenging.
---
Rebuttal Comment 1.1:
Comment: Thanks for the response. I look forward to seeing the next version of the paper. | Summary: This work provides an examination of the capability of large language models (LLMs) to handle long-context information retrieval tasks.
The authors propose a new benchmark, NoLiMa, which is designed to test the ability of LLMs to find relevant information in long texts without relying on direct lexical cues.
This benchmark is an important contribution to the field, as it addresses the limitations of existing needle-in-a-haystack (NIAH) tests by reducing literal matches and forcing models to rely on more complex inference mechanisms.
The paper's evaluation of 12 popular LLMs across different context lengths is revealing.
The findings that performance degrades as context length increases are critical for understanding the current limitations of LLMs.
The in-depth analysis about the impact of latent hop and CoT shed further light to the understanding of long-context reasoning capabilities in LLMs.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: This work provides an empirical study. There is no theoretical proof.
Experimental Designs Or Analyses: Yes. I have checked all the results and analysis in Section 4. They make sence to me.
Supplementary Material: No.
Relation To Broader Scientific Literature: This work contributes to the existing evaluation and understanding of long-context LLMs.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: The main weakness, in my opinion, is that the main findings of this work are very similar to those of RULER [1].
Truely, there are some differences: this work tries to minimize the lexical overlap between the needle and the haystack while RULER does not.
But I don't see the necessity of this setting, as RULER also finds out that existing long-context LLMs have a limited effective context length.
Moreover, this work provides some in-depth analysis about long-context reasoning (e.g., the impact of latent hops and CoT reasoning), but I think these analysis can also be done on RULER.
Therefore, I think this work has made a solid but incremental contribution.
[1] RULER: What’s the real context size of your long-context language models?
Other Comments Or Suggestions: No.
Questions For Authors: No.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: First of all, we want to thank the reviewer for their thoughtful review and constructive feedback.
**[Our works contribution compared to RULER]:**
- Our related work section highlights how extensively literal matching is involved across various long-context benchmarks—including RULER.
- We show that literal matches play an impactful role in affecting the results (in Section 4.4.4) an analysis that **cannot be done with RULER due to their existing literal matches**.
- Since RULER is heavily based on lexical matching, it does not support an analysis of latent hops (4.4.1) and needle placement with reasoning variability (4.4.2). We would appreciate it if the reviewer could describe how such an analysis could be done on RULER. | Summary: This paper present a benchmark which extend NIAH with the needle set requiring models to infer latent associations beyond literal matching. It shows current long context LLMs will have performance degradation in their proposed benchmarks.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: No theoretical claims.
Experimental Designs Or Analyses: Yes.
Supplementary Material: No supplementary material.
Relation To Broader Scientific Literature: There are previous works for more realistic long context benchmark like LongBench V1 and V2, and complex version of NIAH like RULER, but the author's perspective is still novel.
Essential References Not Discussed: No, as far as I know.
Other Strengths And Weaknesses: Strengths:
1. The proposed benchmark is novel in terms of the problem definition, focusing on avoiding literal matching and constructing latent associations that are important for current long-context evaluation.
2. I appreciate the benchmark creation process described in Figure 1, which avoids conflicting information and distractor keywords while ensuring the purity of the evaluation task.
3. The experiment is comprehensive and the results are interesting - the scores for 32K are notably low, and the analysis of latent hops & inversions provides valuable insights.
Weaknesses:
1. The context length is only limited to 32K; it could be extended to 128K to examine what happens when further generalizing the context length.
Other Comments Or Suggestions: No.
Questions For Authors: I am curious about the differences and relationship between this paper and [1], which requires global reasoning ability and might also not have severe literal matching problems.
[1] One Thousand and One Pairs: A “novel” challenge for long-context language models, Karpinska et al.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: First of all, we want to thank the reviewer for their thoughtful review and constructive feedback.
**[32K limit]**: NoLiMa has no inherent context length limit. As stated (lines 200–206, 2nd col.), haystacks are built from random story snippets (using the filtered stories) and can be extended to any length. Since all models drop below the 0.85×base score at 16K and 32K (10 out of 12 drop below 0.5×base score), extending further offers little to no extra insight.
Nevertheless, to demonstrate this, **we will include results at 64K and 128K** for two models: **GPT-4o**, the top-performing model in Table 3, and **Gemini 2.0 Flash**, a new model we plan to add.
**[Differences with [1]]**: While [1] requires global reasoning over entire novels, NoLiMa focuses on the retrievability of single facts. Notably, questions in [1] often include key cues (e.g., character names) that help narrow down relevant spans—similar to our multi-choice setup in Section 4.4.4. Even without strong literal overlap, the presence of answer choices allows the model to locate relevant regions and reason accordingly. | Summary: The paper introduces NoLiMa, a benchmark designed for advanced needle-in-a-haystack (NIAH) tests with minimal lexical overlap between questions and the relevant information (needles) within the context. NoLiMa comprises 56 question-needle pairs, each paired with contexts of varying lengths. The benchmark minimizes literal overlap between questions and the relevant information, compelling models to rely on latent associations (one-hop and two-hop reasoning) and world knowledge rather than surface-level pattern matching.
The study evaluated 12 long-context Large Language Models (LLMs) on these question-needle pairs with different context lengths, including a short context used as a baseline to assess the models' fundamental capability to answer questions without the influence of long contexts. The results indicate that 10 out of 12 models experienced a performance drop below 50% of their baseline at 32K tokens. Even the strongest model, GPT-4o, saw a significant decline from 99.3% (baseline score) to 69.7% at 32K tokens. These findings suggest that the long-context reasoning capabilities of LLMs have been overstated in existing benchmarks that rely on literal matches between questions and context.Additionally, the paper provides a comprehensive analysis of latent hops, fact direction, and the position of needles within the context.
Claims And Evidence: The main claim of the paper is that model performance significantly degrades as context length increases when literal matching is removed. This assertion is generally supported by the experiments, such as the observation that 10 out of 12 models dropped below 50% of their baseline performance at 32K tokens on the NoLiMa benchmark.
However, my concern is that NoLiMa only addresses a limited aspect of the problem. The non-lexical overlap in NoLiMa primarily reflects hyponym-hypernym relationships, such as "city" to "state." There are many other factors to consider when assessing long-context reasoning without lexical overlap, including synonyms, entity abbreviations, and cross-lingual elements.
Methods And Evaluation Criteria: I find the methods and evaluation criteria to be sound.
Theoretical Claims: The paper does not make theoretical claims.
Experimental Designs Or Analyses: The experimental designs in the paper are sound and well-executed. The experiments cover a diverse range of models, including state-of-the-art models and smaller models, as well as open-sourced and closed-sourced models. The experiments include variations to provide comprehensive analysis, such as comparing CoT vs non-CoT approaches and one-hop versus two-hop reasoning.
While the current experimental setup is necessary, I believe that providing an analysis of the attention mechanisms in open-source LLMs could further benefit the community. This would help in understanding the results and improving future LLMs. The current experiments focus on aggregated results from a limited dataset size, which may reduce the depth of insight gained.
Supplementary Material: I have reviewed the data provided in the supplementary material.
Relation To Broader Scientific Literature: The findings in this paper could significantly benefit the LLM community by drawing more attention to non-lexical-overlap long context tasks. The proposed dataset serves as a valuable benchmark for evaluating Needle-in-a-Haystack capabilities.
Essential References Not Discussed: Multi-hop retrieval has been widely discussed in retrieval-augmented generation (RAG) work. The paper could benefit from a brief discussion comparing the NoLiMa dataset with other RAG datasets to highlight its unique contributions and potential synergies.
Multi-hop Question Answering https://arxiv.org/pdf/2204.09140
U-NIAH: Unified RAG and LLM Evaluation for Long Context Needle-In-A-Haystack https://arxiv.org/pdf/2503.00353v1
Other Strengths And Weaknesses: See my other comments.
Other Comments Or Suggestions: N/A
Questions For Authors: Are there any insights derived from the attention weights in LLMs in the experiments on NoLiMa?
Are LLMs robust to long contexts with non-lexical synonyms rather than one-hop hyponym-hypernym reasoning?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: First of all, we want to thank the reviewer for their thoughtful review and constructive feedback.
**[Multi-hop retrieval]**: Multi-hop retrieval, which involves fact chaining, is discussed in our "Related Work" and "Introduction" (Hsieh et al., 2024; Levy et al., 2024). NoLiMa focuses on a prior step—locating relevant fact(s) from long contexts, which is a prerequisite for effective multi-hop reasoning.
Note: The U-NIAH paper was released after the submission deadline.
**[Insights on attention weights]**: Analyzing attention weights at long context lengths is extremely memory-intensive. For example, with 8K tokens, a LLaMA 3.1 8B model yields 32(layers) × 32(heads) × 8000**2 = 65 billion weights (~260 GB) for a single input. That said, we did limited analysis comparing inverted vs. default cases on some examples. We found that in inverted settings, W_n gets relatively more attention than the character name when W_n appears earlier—loosely supporting the theory in lines 300–306 (col 2). But due to high computational cost and the analysis being somewhat outside our main scope, broader experiments (e.g., on LLaMA 3.3 70B or full dataset or longer lengths) weren't feasible.
**[Non-lexical synonyms]**: While using non-lexically matched synonyms helps avoid literal matching, their embeddings are often similar enough to still act as a match. Moreover, not all our examples rely solely on hyponym-hypernym reasoning—some, like the dietary cases (e.g., lactose intolerance <==> milk), require commonsense reasoning. | null | null | null | null | null | null |
Pose Prior Learner: Unsupervised Categorical Prior Learning for Pose Estimation | Reject | Summary: The authors presents Pose Prior Learner (PPL) that learns category-level pose priors from image reconstruction, without human annotations. The motivation is that given two frames of an object instance, an ideal pose prior should be able to reconstruct the image based on the estimated poses and transformations. The authors further presented an iterative strategy that improves performance under occlusion.
## update after rebuttal
Thank the authors for the rebuttal. I don't have further questions. Regarding the missing references, I can see the difference from previous works and the novelty of this paper. However I believe the idea of this work is still built on the foundation from these previous works. I recommend discussing the four references for a comprehensive discussion, which help positioning this work in the literature.
Claims And Evidence: Claims are mostly supported with clear and convincing evidence.
Methods And Evaluation Criteria: The authors aimed to learn pose priors in an unsupervised manner, without human-defined priors. The proposed method address this problem by learning from image reconstruction supervision. The motivation of the method is clear.
However, the motivation of the iterative inference strategy is not very clear. It would be good if the authors can present some qualitative examples showing why models with iterative inference strategy would fail and how this strategy fixes the wrong pose. A concern is if the wrong predictions from the previous iterations would aggregate, leading to degraded performance in following steps.
Theoretical Claims: This work did not present major theoretical claims or proofs.
Experimental Designs Or Analyses: Experimental designs are clear and solid. One concern is that there are not sufficient results on pose estimation under (synthetic) occlusion. There are some results in Appendix A4 showing that with more steps of the iterative strategy the performance improve. There lacks direct comparisons with other baseline methods under occlusion cases.
Supplementary Material: Yes I reviewed all the supplementary materials attached after the main text.
Relation To Broader Scientific Literature: This work also broadly relates to the study of unsupervised learning of pose estimation models. See discussion in "Essential References Not Discussed".
Essential References Not Discussed: Essential references not discussed are the some recent animal pose estimation methods learning from image-level and feature level reconstruction, such as MagicPony and 3D Fauna. It would be good to discuss how the proposed method distinguish from these works and what new findings and results can benefit the research community beyond these prior works.
* MagicPony: Learning Articulated 3D Animals in the Wild. CVPR 2023.
* Learning the 3D Fauna of the Web. CVPR 2024.
Another line of works study compositional models for rigid object pose estimation, which estimates poses using a feature memory bank for estimating part correspondence. The second paper also studies unsupervised learning of pose models from object-centric videos.
* Robust Category-Level 6D Pose Estimation with Coarse-to-Fine Rendering of Neural Features. ECCV 2022.
* Unsupervised Learning of Category-Level 3D Pose from Object-Centric Videos. CVPR 2024.
Other Strengths And Weaknesses: I acknowledge the importance of the problem and the contribution of the proposed method. However, I think the authors should also discuss the missing related works above, which would help to position this work in the literature, distinguish it from prior works, and highlight the novelty of this paper.
Other Comments Or Suggestions: Following the discussion in "Experimental Designs Or Analyses", I recommend the authors to add more motivation and qualitative results of the iterative inference strategy, why models without this strategy would fail and how this strategy fixes the failure cases. Based on these results, the author can explain in more detail the motivate of this iterative strategy and intuitively why this strategy would help.
Questions For Authors: None.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the feedback and have addressed each question below.
### **Q.1:** Clarity of the Motivation for the Iterative Inference Strategy.
**R.1:** The memory in PPL stores learned prototypical poses, making it a natural choice for correcting inaccurate pose estimations, especially in occluded scenes, through an autoregressive process. The key motivation behind iterative inference is to repeatedly apply the memory bank’s corrections alongside the model’s image reconstruction in an autoregressive manner. This approach often outperforms one-time correction by progressively refining predictions, leading to greater accuracy and robustness.
Here’s why autoregressive iterative inference is superior to a single correction step:
- First, progressive Error Reduction: A single correction may not fully capture complex dependencies and can introduce new errors. Autoregressive inference refines predictions step by step, improving accuracy and consistency.
- Second, handling uncertainty: In tasks like pose estimation, initial predictions can be ambiguous. Iterative updates allow the model to incorporate more contextual information at each step, resolving uncertainties more effectively.
- Third, improved generalization and robustness: Iterative inference helps the model learn structured dependencies across spatial and temporal dimensions, making it more resilient to variations, occlusions, and noise.
- Forth, adaptive refinement: Autoregressive models retain intermediate information, allowing outputs to be continuously refined based on prior iterations. In contrast, one-time correction lacks this flexibility and may struggle in tasks requiring sequential reasoning.
As requested by the reviewer, we have provided qualitative results in Figure. 4a of the paper, demonstrating how each iteration progressively enhances the clarity of occluded regions, leading to more accurate pose estimations.
Additionally, we have included additional qualitative samples on occlusions in [Figure. R3](https://drive.google.com/file/d/1QnAeFSR0ZK_4mDVAC3FJK5uSbelPyo8h/view?usp=sharing), showing that PPL consistently outperforms AutoLink by reconstructing plausible poses even with partial visual information. These results will be incorporated into the revised version.
### **Q.2:** Concerns about Aggregating Wrong Predictions.
**R.2:** Generally, incorrect predictions are corrected by the memory bank, particularly under small-area occlusions, as shown in Appendix A4. However, severe occlusions can lead to plausible yet incorrect reconstructions, potentially compounding errors. An example is provided in [Figure. R2](https://drive.google.com/file/d/1QnAeFSR0ZK_4mDVAC3FJK5uSbelPyo8h/view?usp=sharing) where our PPL fails to reconstruct the ground truth pose when there is a large occlusion. Future work may explore confidence-based updates or early stopping via temporal consistency checks. This will be further discussed in the revised version
### **Q.3:** Results on Pose Estimation Under Occlusion.
**R.3:** Additional qualitative results comparing PPL and AutoLink under occlusion are shown in [Figure R3](https://drive.google.com/file/d/1QnAeFSR0ZK_4mDVAC3FJK5uSbelPyo8h/view?usp=sharing), demonstrating PPL's consistently superior performance.
Quantitative comparisons on Human3.6m between AutoLink and PPL are presented in [Table R5](https://drive.google.com/file/d/1QnAeFSR0ZK_4mDVAC3FJK5uSbelPyo8h/view?usp=sharing). Results indicate AutoLink significantly underperforms compared to PPL due to lacking pose priors and correction mechanisms. These findings will be incorporated in the revision.
### **Q.4:** Discussion of Essential References Not Discussed.
**R.4:** Discussions of the suggested references are provided below and will be included in the revision:
-**MagicPony (CVPR 2023) & Learning the 3D Fauna (CVPR 2024):**
Both papers focus on learning animal poses through image-level and feature-level reconstruction. However, they rely on ground truth object masks as supervision, which provide essential shape and pose information. In contrast, PPL employs an unsupervised learning approach that does not require object masks, allowing for pose priors to be learned directly from unannotated images.
-**Robust Category-Level 6D Pose Estimation (ECCV 2022) & Unsupervised Category-Level 3D Pose (CVPR 2024):**
These two works share a similar idea of learning category-level pose for pose estimation with PPL. However, they represent poses with dense point clouds, emphasizing scene reconstruction. PPL differentiates itself by representing poses as sparse key points and their connections, which offers a semantically richer and more invariant representation of poses. Thus, while all these methods contribute to pose estimation, the focus of PPL aligns more closely with scene understanding compared to the dense representations used in scene rendering. | Summary: This paper focuses on unsupervised pose estimation and introduces Pose Prior Learner (PPL), which learns a general categorical pose prior in a self-supervised manner to enhance pose estimation performance. The pose prior is designed as a combination of a keypoint prior, distilled from a learnable memory, and a learnable connectivity prior. Additionally, an iterative inference strategy is proposed to refine poses in occluded scenes. Experiments on multiple datasets, covering both human and animal pose estimation, validate the effectiveness of PPL.
Claims And Evidence: Yes, categorical pose priors are crucial for pose estimation, particularly in unsupervised settings, as supported by prior work cited in Section 2.
Methods And Evaluation Criteria: Yes, as evidenced by previous work cited in Section 2, pose priors play a crucial role in unsupervised pose estimation. Given the difficulty of annotating priors, using learnable pose priors to enhance performance is a reasonable approach. Additionally, the benchmark datasets used are widely recognized in this field.
Theoretical Claims: No theoretical claims in this paper.
Experimental Designs Or Analyses: I have reviewed the experiments and identified the following concerns:
1. A recent state-of-the-art method [1] for unsupervised pose estimation, published in CVPR 2024, is neither cited nor discussed in the paper. Additionally, it achieves more impressive results than PPL.
2. AutoLink was evaluated on more diverse scenarios, including faces, fashion, birds, flowers, hands, horses, and zebras. However, PPL does not consider these scenarios, raising concerns about its generalization ability.
3. The paper lacks visualization comparisons with existing methods, particularly AutoLink, making it difficult to determine the specific factors contributing to PPL’s performance improvements.
4. While the paper includes ablation studies on prior variants, it does not evaluate a crucial baseline, i.e., PPL without pose priors, which is necessary to first validate the importance of pose priors.
5. In Table 2, the results of BKind'22 are not listed.
6. In Fig. A1, it would be beneficial to include the results of the Memory Bank (1 vector) for comparison with PCT'23.
[1] Unsupervised Keypoints from Pretrained Diffusion Models. CVPR2024.
Supplementary Material: I have thoroughly reviewed the entire supplementary material.
Relation To Broader Scientific Literature: PPL builds on the importance of pose priors in unsupervised pose estimation ([Shape Template Transforming'21]) and introduces learnable pose priors, distilled from a compositional memory architecture similar to [PCT'23], which are then transformed into keypoints using predicted transformation parameters. Additionally, PPL leverages learnable connectivity priors for image reconstruction, enabling self-supervised learning akin to [AutoLink'22].
Essential References Not Discussed: - Unsupervised Keypoints from Pretrained Diffusion Models. CVPR2024.
Other Strengths And Weaknesses: None
Other Comments Or Suggestions: - It's suggested to adjust the position of Table 3 in the paper.
- It's suggested to place Fig. 3 before Table 1-3.
Questions For Authors: My main concerns are related to the experiments, as outlined in the previous section:
1. Lack of comparisons with the recent state-of-the-art method [1].
2. Fewer evaluated datasets compared to AutoLink.
3. Lack of visualization comparisons with existing methods.
4. Missing baseline results without pose priors.
5. Absence of BKind'22 results in Table 2.
6. No results for the Memory Bank (1 vector) comparison with PCT'23 in Fig.A1.
Considering these factors, especially the less satisfactory performance of PPL compared to [1], I would currently give a positive rating for the paper.
[1] Unsupervised Keypoints from Pretrained Diffusion Models. CVPR2024.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the feedback and have addressed each question below.
### **Q.1:** Lack of comparisons with Unsupervised Keypoints from Pretrained Diffusion Models [1]
**R.1:** We thank the reviewer for pointing us to the recent method [1]. We will include it in the related work and discuss its differences from ours in the revised paper. We highlight the following differences between our method and theirs:
- First, [1] requires large-scale multi-modal data (image and language) to train a Conditional Stable Diffusion Model to start with. Compared to our approach, this method utilizes an extra modality (language) and extra training data.
- Second, [1] and our method has different objectives. While [1] aims to utilize prior knowledge in pre-trained Conditional Stable Diffusion Models for pose estimation, our focus is to learn the prior information from the data itself.
Due to these differences, a direct comparison is not fully fair. Still, as suggested, we compare results in [Table. R1 & R2](https://drive.google.com/file/d/1QnAeFSR0ZK_4mDVAC3FJK5uSbelPyo8h/view?usp=sharing):
- **Human Pose Estimation:** Our method outperforms [1] on Human3.6m and is comparable on Tai-Chi.
- **Bird Pose Estimation:** We outperform [1] on the aligned CUB dataset and underperform on the non-aligned ones.
These results suggest that our method performs competitively well with multi-modal methods. This demonstrates that our method is capable of effectively capturing meaningful pose priors and accurately estimating poses despite having zero prior knowledge of extra modalities.
### **Q.2:** Fewer evaluated datasets compared to AutoLink.
**R.2:** We tested on six diverse categories (humans, birds, flowers, hands, horses, dogs), as detailed in Appendix A7. Here’s why we excluded the datasets used by AutoLink:
- **DeepFashion:** Lacks background complexity and contains similar human postures—making it less informative than Human3.6m or Tai-Chi.
- **CelebA:** Focuses on faces, which lack structural variation. Our method is better suited for objects with articulated parts.
- **Zebra:** Initially omitted due to similarity with horses, but we will add it in the revised version.
### **Q.3:** Lack of visualization comparisons with existing methods, particularly AutoLink.
**R.3:** We include visualization comparisons between our PPL and AutoLink in the [Figure. R1](https://drive.google.com/file/d/1QnAeFSR0ZK_4mDVAC3FJK5uSbelPyo8h/view?usp=sharing). Under scenes without a background of complex texture, as in Row 1, both AutoLink and PPL can predict correct poses. Generally, PPL outperforms AutoLink by utilizing learned pose priors to guide pose estimation, ensuring that the transformed poses remain within the intended category. In contrast, AutoLink tends to be influenced by intricate background textures, which can result in unrealistic pose estimations. For example, in Row 2 and Row 4 of Figure. R1, AutoLink detected some keypoints on the background and predicted unrealistic poses, while PPL consistently focuses on human body. In Row3, compared with AutoLink, PPL does not predict the lines on the wall as arms, because we have the learned pose prior to constraining the arm from being too long.
### **Q.4:** Missing baseline results without pose priors.
**R.4:** Our core contribution is learning pose priors without human interventions or prior knowledge. As such, we are unable to establish ablated methods for PPL without the pose prior component. Removing this component would reduce the model to a direct keypoint regressor—essentially similar to AutoLink. We have included AutoLink as a baseline throughout our experiments to address this.
### **Q.5:** Absence of BKind'22 results in Table 2.
**R.5:** We now provide BKind’22 results on Human3.6m in [Table. R3](https://drive.google.com/file/d/1QnAeFSR0ZK_4mDVAC3FJK5uSbelPyo8h/view?usp=sharing). Our method significantly outperforms BKind’22, and we’ll include this in the revised version.
### **Q.6:** No results for the Memory Bank (1 vector) comparison with PCT'23 in Fig.A1.
**R.6:** PCT and PPL both use compositional tokens and memory for occlusion, but differ fundamentally:
- **PCT:** Supervised, using ground truth keypoints and connectivity.
- **PPL:** Fully unsupervised, without annotations.
To address the reviewer’s point, we created a variant called **PPL-1MemBank**, which encodes all keypoints into a single vector and uses one memory bank (512 vectors). This matches PPL’s memory capacity (34 banks × 16 vectors).
In [Table R4](https://drive.google.com/file/d/1QnAeFSR0ZK_4mDVAC3FJK5uSbelPyo8h/view?usp=sharing), results show:
- **PPL-1MemBank:** Normalized L2 error = 2.72
- **PPL-full:** Normalized L2 error = 2.56
This confirms our hierarchical memory improves performance and efficiency.
### **Q.7:** Table and Figure Positioning.
**R.7:** Thanks for pointing this out! We will fix these presentation issues in the revised version.
---
Rebuttal Comment 1.1:
Comment: Thanks for the authors' feedback, which has addressed my concerns. I will be raising my rating. | Summary: This paper primarily addresses the issue of existing pose estimation methods' over-reliance on manually designed prior knowledge and their sensitivity to occlusions, particularly in complex poses. Compared to the approach by He et al., the authors propose a hierarchical part-based memory module, with the following specific ideas:
1. Decompose the human or animal pose into local parts (such as arms, legs), with each part corresponding to an independent memory bank to store typical pose prototypes.
2. By using Keypoint Prior, aggregate the prototypes from the memory banks to dynamically generate data-driven pose priors, avoiding manual settings, and employ image reconstruction for supervised learning.
3. Introduce multi-round optimization during inference, progressively repairing occluded parts through iterative retrieval and reconstruction.
## In terms of experiments:
The method outperforms mainstream methods like PCT on both human (Human3.6M, MPII) and animal (AnimalPose) datasets, with an improvement of approximately 8% in keypoint localization accuracy under occlusion scenarios and a reduction of 12-15% in overall error.
The ablation experiments are very clear in Table 4, where the authors validate the improvements brought by the hierarchical memory design, dynamic prior generation, and iterative optimization mechanism on the Human3.6M dataset.
## Justification.
I appreciate this paper, with its clear presentation allowing me to understand the PPL approach quite clearly from Figure 2. Moreover, Figure 4 very clearly demonstrates the robustness of iterative optimization to occlusions. Table 4 clearly showcases the impact of each key component.
Claims And Evidence: I do not find problematic claims.
Methods And Evaluation Criteria: The method outperforms mainstream methods like PCT on both human (Human3.6M, MPII) and animal (AnimalPose) datasets, with an improvement of approximately 8% in keypoint localization accuracy under occlusion scenarios and a reduction of 12-15% in overall error.
The ablation experiments are very clear in Table 4, where the authors validate the improvements brought by the hierarchical memory design, dynamic prior generation, and iterative optimization mechanism on the Human3.6M dataset.
Theoretical Claims: It does no have any theoretical issues.
Experimental Designs Or Analyses: The experimental designs and analyses are fine to me.
Supplementary Material: I check the supplementary material mentioned in the ablation section.
Relation To Broader Scientific Literature: It achieves learning category-level pose priors from unlabeled images.
Essential References Not Discussed: None.
Other Strengths And Weaknesses: See my summary.
Other Comments Or Suggestions: See my summary.
Questions For Authors: I do not have any questions for authors.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for the positive feedback. | null | null | null | null | null | null | null | null |
Gumiho: A Hybrid Architecture to Prioritize Early Tokens in Speculative Decoding | Accept (poster) | Summary: Previous speculative decoding methods treat all tokens in a sequence equally, while this paper demonstrates that earlier tokens are more critical for success. To improve efficiency, the authors propose Gumiho, a hybrid model that prioritizes early tokens with a serial two-layer Transformer and uses lightweight parallel MLP heads for later tokens. This strategy boosts both the accuracy of early token predictions and the efficiency of later ones. Experimental results show that Gumiho outperforms existing methods in terms of speedup ratio and acceptance length.
Claims And Evidence: The claims made in the submission are supported by clear and convincing evidence.
Methods And Evaluation Criteria: Proposed methods and evaluation criteria make sense for the problem or application at hand.
Theoretical Claims: I checked the correctness of the proofs for theoretical claims, which is theorem 3.1 and appendix A in the paper.
Experimental Designs Or Analyses: I checked the soundness/validity of experimental designs and analyses, which is section 4 in the paper.
Supplementary Material: I reviewed the supplementary materials.
Relation To Broader Scientific Literature: The proposed Gumiho combines the serial heads in Eagle2 and parallel heads in Medusa.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Pros:
1. The finding of the proof is solid and inspiring.
2. Given the proof, the approach in this paper is reasonable.
3. The speed-up ratio gains, especially on large-scale LLMs such as LLaMA2 70B and LLaMA3 70B are obvious compared to Eagle2, which shows the effectiveness of the proposed method.
Cons:
1. There is a lack of comparison to the latest state-of-the-art papers, which propose better results than Eagle2, such as HASS [1] and DDD [2].
2. The method uses more parameters in the draft model compared to Eagle, Eagle2, and Medusa. Does the training process consume more GPU memory?
[1] Learning Harmonized Representations for Speculative Sampling, ICLR, 2025.
[2] Dynamic Depth Decoding: Faster Speculative Decoding for LLMs, arXiv, 2024.
Other Comments Or Suggestions: See weaknesses.
Questions For Authors: 1. Is it able to combine the proposed method with the state-of-the-art Spd method to further improve the speed up ratio? It is better if the conclusion of the theorem can be applied to other methods.
2. What is the average draft time for each part of the method? In figure3 you show the overall draft time including the model forward time and full tree attention time. I would like to see each part of them.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your suggestions and support.
**Q1. There is a lack of comparison to the latest state-of-the-art papers, which propose better results than Eagle2, such as HASS [1] and DDD [2]**
A1:**(1) Hass** improves Eagle2 by addressing the training-inference inconsistency in serial transformer heads within SPD. While Hass focuses on training methodology, our work enhances performance via architectural modifications. These two directions are orthogonal: our method could integrate Hass’s training improvements for further gains.
In the table below, we compare the performance of our Gumiho with Hass. Additionally, we evaluate a variant of our model (denoted as Gumiho w/ Hass ) where Hass’s training method is applied to our Transformer Head. All results are conducted on a Mi250 GPU using the LLaMA3-8B model with a temperature of 0.
|| MT-Bench|HumanEval|
|-|-|-|
|Eagle2|2.16×|2.51×|
|Hass|2.26×|2.59×|
|Gumiho|2.38×|2.77×|
|Gumiho w/ Hass|**2.43×**|**2.84×**|
**(2) DDD** improves Eagle2 by using a dynamic draft tree. Since DDD’s code is not open-sourced, we compare relative improvements over Eagle2. On the MT-Bench dataset, the performance gains of DDD and Gumiho are:
||DDD|Gumiho|
|-|-|-|
|V 7B|3.5%|**9.4%**|
|V 13B|4.2%|**6.3%**|
|L2 7B|2.3%|**5.5%**|
|L2 13B|2.3%|**5.4%**|
The aforementioned results and discussions will be included in the final version of our paper.
**Q2. The method uses more parameters in the draft model compared to Eagle, Eagle2, and Medusa. Does the training process consume more GPU memory?**
A2: Yes, you are correct. Our method does require more GPU memory during training compared to Eagle, Eagle2, and Medusa. Here’s why:
- Eagle and Eagle2 use one single-layer Transformer head and reuse it serially across multiple speculative steps.
- Medusa only maintains five parallel MLP heads.
- Our approach, however, employs a two-layer Transformer head alongside five parallel MLP heads, all trained simultaneously.
This architectural choice increases memory consumption. However, it enables a hybrid generation strategy: serial decoding for the first few tokens (to ensure accuracy) and parallel decoding for subsequent tokens (to maximize speed). While this introduces a memory-accuracy trade-off, it achieves a significant speedup improvement. We will explicitly discuss this trade-off in the final manuscript.
**Q3. Is it able to combine the proposed method with the state-of-the-art Spd method to further improve the speed up ratio? It is better if the conclusion of the theorem can be applied to other methods.**
A3: As illustrated in A1, our method could integrate Hass’s training strategy for further gains.
In addition to Hass, our core theoretical principle—**prioritizing the initial tokens**—can also be generalized to serial multi-head draft models (e.g., Hydra or Eagle). By reallocating Head parameters to emphasize early tokens, this principle could further enhance the speedup ratio of existing SOTA methods.
Moreover, existing methods typically use a single smaller model (e.g., LLaMA-3-3B) to accelerate larger counterparts like LLaMA-3-405B. However, our analysis reveals that adopting a differentiated draft model strategy—where a more capable model (e.g., LLaMA-3-8B) predict initial tokens, while a faster but lighter model (e.g., LLaMA-3-1B) handles subsequent tokens—could optimize the quality-speed trade-off beyond current homogeneous settings.
Exploring these extensions is a key direction for our future research.
**Q4. What is the average draft time for each part of the method? In figure3 you show the overall draft time including the model forward time and full tree attention time. I would like to see each part of them.**
A4: The following table presents the draft time of the Vicuna 7B on Mi250 GPU.
- `Serial Head Forward` represents `the time for a single serial head forward pass once`$\times$`the number of forward passes`. In Eagle2, a single serial head corresponds to a single-layer Transformer, while in Gumiho it represents a two-layer Transformer.
- `Parallel Head Forward` denotes the time for a parallel head forward pass once. Eagle2 does not have parallel heads, whereas in Gumiho, this refers to the parallel MLP heads.
- `Tree Attention / Full Tree Attention` represents the time required to construct the tree structure in Eagle2 and Gumiho.
- `Additional Computations` represents the time for additional computing. (e.g., using torch.top_k to retrieve current tokens).
- `Total Time` means the total time consumed for a draft generation.
||Eagle2|Gumiho|
|-|-|-|
|Serial Head Forward|9.8ms$\times$6|21ms$\times$2|
|Parallel Head Forward|N/A|14.7ms|
|Tree Attention / Full Tree Attention|3.3ms|3.4ms|
|Additional Computations|3.1ms|3.2ms|
|Total Time|65.2ms|63.3ms| | Summary: This paper proposes a new speculative decoding method called Gumiho. It combines the parallel draft head architecture and sequential draft head architecture to derive a hybrid architecture. The idea behind the paper is to prioritize the accuracy of the early tokens and make a rigorous mathematical proof to show that this can enhance the overall performance. The experiments on six datasets with different baseline models and temperatures show that Gumiho can achieve new state-of-the-art results.
Claims And Evidence: Theorem 3.1 in the paper as well as the proof in the appendix can support the claim.
Methods And Evaluation Criteria: I think the core idea of prioritizing the accuracy of the early tokens under a limited computational budget is important and meaningful to the research area of SpD, especially since a rigorous theoretical proof is provided. The evaluation criteria are the commonly used datasets and baseline models.
Theoretical Claims: I roughly checked the proof of Theorem 3.1, and no problem was found.
Experimental Designs Or Analyses: I checked the experimental designs and analyses. The datasets and baseline models are commonly used in other papers. The results are reasonable.
Supplementary Material: I reviewed all of the supplementary materials.
Relation To Broader Scientific Literature: There may have some findings on the conclusion ‘the prior tokens in speculative decoding are more important’ already.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths:
The paper is well-organized, making it easy to follow.
The theoretical analysis is rich and the proof is rigorous.
The experimental section is comprehensive, covering multiple architectures and settings, demonstrates the validity and robustness of the proposed method. The overall speedup improvements over Eagle is non-negligible.
Weaknesses:
The ablation study shows that using FTA has marginal improvement.
The conclusion of the theorem is simple but it seems that the proof is rather complicated. Is there an easier way to give the proof?
The theorem assumes that the total amount of decrease to the second part is the same as that of increase to the first part of the sequence. However, this is hardly the case in reality. Is it able to give a more general assumption?
Other Comments Or Suggestions: No
Questions For Authors: I wonder if the idea of ‘the prior tokens in speculative decoding are more important’ has been investigated by other papers since the conclusion is obvious and easy to derive. If so, the novelty of this paper will be decreased, and the author should give a further comparison to other papers.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your suggestions and support.
**Q1. The ablation study shows that using FTA has marginal improvement.**
A1: The improvement contributed by our proposed FTA method is non-negligible in the context of the overall performance gain. In the FTA ablation study, the speedup ratio increases by 0.05, while the total improvement of our method over Eagle2 is 0.27. This means FTA accounts for approximately 18.5% of the total performance gain, thereby demonstrating its critical role in our approach.
Moreover, FTA introduces a lossless improvement compared to existing TA without incurring additional computational overhead. It only requires modifying the Tree Mask during verification by setting specific positions from 0 to 1 (i.e., unmasking certain tokens). This design ensures efficiency while enhancing performance.
**Q2. The conclusion of the theorem is simple but it seems that the proof is rather complicated. Is there an easier way to give the proof?**
A2: Note that although the conclusion of the theorem appears simple, the situation in reality is rather complicated since we have only imposed very few restrictions on the Theorem. Specifically, we only require that the sum of the increments in the former part and the decrements in the latter part must be equal. The probabilities $\lbrace p_i\rbrace_{i=1}^D$ in the original setting, the relative magnitude of increases and decreases $\zeta_i$, the length of the original sequence $D$, and the divided location $d$ of the former part and latter part are all unbounded and can change freely.
Therefore, although the theorem itself appears simple, the high degree of freedom results in highly complex scenarios requiring exhaustive case analysis. Under the current assumptions adopted in our paper, each step in the proof is indeed necessary.
**Q3. The theorem assumes that the total amount of decrease to the second part is the same as that of increase to the first part of the sequence. However, this is hardly the case in reality. Is it able to give a more general assumption?**
A3: Actually, the assumption that *"the increment in the former part equals the decrement in the latter part"* can be interpreted as an upper-bound condition. In fact, our conclusion holds not only when these quantities are equal, but also when the increment in the former part exceeds the decrement in the latter part, in which the Eq.6 can be modified from
$\sum_{i=1}^d \zeta_i=\sum_{j=d+1}^D \zeta_j$
to
$\sum_{i=1}^d \zeta_i\geq\sum_{j=d+1}^D \zeta_j$.
This is very easy to prove that Theorem 3.1 still holds in this situation if we remove the excess portion in the former part without decreasing the mean accepted tokens.
As for the scenario where the increment is less than the decrement, we believe that this is a more complex situation and we will investigate it in our future research.
The aforementioned analysis will be added in the final version of our paper.
**Q4. I wonder if the idea of ‘the prior tokens in speculative decoding are more important’ has been investigated by other papers since the conclusion is obvious and easy to derive. If so, the novelty of this paper will be decreased, and the author should give a further comparison to other papers.**
A4: To the best of our knowledge, no prior work has proposed the idea presented in our paper. We are the first to introduce the idea that *"prior tokens are more important"* and provide rigorous theoretical proof for this concept. Furthermore, we leverage this insight to design a novel model architecture, Gumiho.
Moreover, applying the principle of 'prior tokens are more important' to achieve speedup improvements is not straightforward. Simply enhancing prior token accuracy may increase computational overhead at the same time, which would prolong draft time and consequently undermine the overall speedup. In fact, we have no idea how this would affect the final speed-up ratio if we merely increase the computational budget on the prior tokens, since the mean accepted tokens and the draft time will increase together and they are two factors that play opposite roles.
In contrast, our Gumiho tries our best to fix the overall computational budget (by increasing the computational budgets of prior tokens and decreasing the latter) and shows that we can improve the mean accepted tokens. We achieve this by simultaneously boosting the accuracy of prior tokens while adopting simplified head structures (i.e., MLP) for subsequent tokens with parallel generation. This architectural innovation effectively balances accuracy and efficiency, ultimately achieving superior speedup.
---
Rebuttal Comment 1.1:
Comment: Thank you for the rebuttal.
Although it is still unknown whether the conclusion in this paper still holds in the situation that the amount of decrease to the second part is greater than the increase of the first part, it is acceptable since it is hard to require a decrease of the total accuracy while at the same time increase the mean accepted tokens.
Besides that, all of my concerns are well-addressed, especially my novelty concern of this paper and the improvement of FTA.
I would like to increase my score from 3 to 4.
---
Reply to Comment 1.1.1:
Comment: Thank you for your feedback.
We sincerely appreciate your support. We will analyze the influence of this specific scenario in our future research. | Summary: This paper improves the self-speculative decoding methods by combining the architecture of Eagle and Medusa. The paper uses sophisticated Transformer architecture for the early draft heads in a serial configuration to improve accuracy, and multiple lightweight MLP heads operating in parallel to enhance efficiency. The reason behind this combination is that the prior tokens in speculative decoding are more important. The paper gives a theoretical analysis of this idea. The experimental results demonstrate the effectiveness of this paper.
## update after rebuttal
I will keep my ratings since the rebuttal solve most of my concerns.
Claims And Evidence: The proposed method is evaluated on multiple architectures and settings, including experiments on Vicuna, LLaMA2 and LLaMA3. It is also compared against other similar competitor methods. The results demonstrate the effectiveness and efficiency of the proposed approach.
Methods And Evaluation Criteria: The proposed method and evaluation criteria are reasonable and follow widely accepted evaluation standards. The benchmark datasets used are also standard.
Theoretical Claims: I have reviewed the mathematical formulas in the paper and did not identify any issues.
Experimental Designs Or Analyses: I have reviewed the experimental design in the paper, including experiments on multiple architectures and settings and the ablation study. In the ablation study, the authors explore FTA but show marginal improvement.
Supplementary Material: I have reviewed the supplementary materials of the paper, including the sections on Detailed Proof of Theorem 3.1', Experiment Results on A100’, ‘Training Details and Hyper-parameters’ and ‘Ablation Study on Head Accuracy’.
Relation To Broader Scientific Literature: The conclusion that tokens are more important in the previous part of the sequence in SpD is not surprising.
However, this paper is still meaningful to society since it discusses the situation of SpD under a limited computational budget. Based on rigorously proven theory, it gives a useful solution to this situation.
Essential References Not Discussed: There are some discussions of the accuracies of different heads in paper [1], which shows that previous heads have higher accuracy, and I think the author should have a discussion in their paper.
[1] Cerberus: Efficient Inference with Adaptive Parallel Decoding and Sequential Knowledge Enhancement.
Other Strengths And Weaknesses: Strengths:
1. I believe that this paper is meaningful to the research area of speculative decoding. The paper rigorously proves that improving the performance of the previous draft models with the expense of the later models is beneficial to the overall mean-accept-tokens of SpD.
2. The paper gives a nice hybrid architecture solution that uses sequential models to improve the previous tokens’ performance and uses parallel models to accelerate the later ones.
3. The paper is theoretically sound and easy to understand. The proof of the theorem is roughly correct.
4. The experimental results show that this paper can achieve a new state-of-the-art speedup compared to the previous methods.
Weaknesses:
1. It is not very clear why full tree attention works better than the tree attention methods in Eagle2, especially why this method cannot be applied in Eagle2. The authors should give an example to illustrate this better.
2. In lines 320 to 324. The authors claim that they use 1 MI250 GPU for evaluation except the 70B variant which requires 4 GPUs. However, you only use 1 NVIDIA A100 GPU for all models. The experimental setup on A100 should be further claimed.
3. There are some discussions of the accuracies of different heads in paper [1] which shows that previous heads have higher accuracy, and I think the author should have a discussion in their paper. There are several papers that proposed better results than Eagle2, such as [2], [3]. The author should compare and discuss them.
4. In the proof of theorem 3.1, the authors use an auxiliary probability sequence $P_i’$, and assume $p_d+\zeta \leq 1$ and discuss $p_d+\zeta>1$ at the end. I am confused why $p_i-\zeta < 0$ is not assumed and discussed accordingly.
5. In appendix D, the authors show the comparison of Eagle2 and Gumiho on two datasets. What about the other four datasets?
[1] Cerberus: Efficient Inference with Adaptive Parallel Decoding and Sequential Knowledge Enhancement.
[2] Dynamic Depth Decoding: Faster Speculative Decoding for LLMs.
[3] Learning Harmonized Representations for Speculative Sampling.
Other Comments Or Suggestions: See weaknesses above.
Questions For Authors: My major concerns are weaknesses 1, 3 and 4. The answers would likely change my evaluation of the paper.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your suggestions and support.
**Q1. It is not very clear why full tree attention works better than the tree attention methods in Eagle2, especially why this method cannot be applied in Eagle2. The authors should give an example to illustrate this better.**
A1:
**(1) Why FTA cannot be applied to Eagle2:**
Let us refer to Fig. 2 for illustration. In the upper half of Fig. 2, the tokens [shines, glows, radiates] are outputs of Head 3, while [warmly, brightly, intensely] are outputs of Head 4. In Eagle2, the heads operate serially—both Head 3 and Head 4 are single-layer Transformers, and the output of Head 4 depends on the output of Head 3. In our method, however, these heads operate in parallel (i.e., Head 3 and Head 4 correspond to MLP1 and MLP2 in Fig. 1). Since the outputs of MLP2 are independent of MLP1, the outputs of MLP1 and MLP2 can be freely combined.
In the lower half of Fig. 2, FTA leverages the independence between outputs of later heads to fill shorter paths in the tree with longer ones. In contrast, Eagle2’s Tree Attention (TA) requires strict dependency between tokens along each path (later tokens depend on earlier ones), making cross-path filling impossible.
**(2) Why FTA outperforms TA:**
The final speedup improvement is achieved by either increasing the mean accepted tokens or reducing draft time. Compared to TA, FTA increases the mean accepted tokens by extending candidate path lengths without incurring additional computational overhead, thereby maintaining the same draft time as TA. This allows FTA to achieve better performance than TA.
**Q2. The experimental setup on A100 should be further claimed.**
A2: The requirement of 4 GPUs applies exclusively to the scenario that the parameter size of target model is 70B. We clarify that our experiments on the NVIDIA A100 GPU did not include the 70B variant. All A100-based evaluations were conducted with 7B/8B/13B-scale Target Models.
**Q3. Compare and discuss Cerberus[1], DDD[2], Hass[3].**
A3:
**(1) Cerberus [1]:**
The observation in Cerberus that earlier heads exhibit higher accuracy aligns with our understanding. This is because, in parallel decoding, later heads predict tokens farther from the input (e.g., predicting the $i+2$-th token based on the $i$-th hidden state introduces greater error compared to predicting the $i+1$-th token). However, Cerberus still employs identical parameter scales and architectures across all heads, failing to prioritize earlier heads—a key distinction from our method. Their primary contribution lies in introducing sequential knowledge for parallel heads, whereas our approach explicitly optimizes model structure to prioritize early tokens.
**(2) DDD [2]:**
DDD improves Eagle2 by using a dynamic draft tree. Since DDD’s code is not open-sourced, we compare relative improvements over Eagle2. On the MT-Bench dataset, the performance gains of DDD and Gumiho are:
|model|DDD|Gumiho|
|-|-|-|
|V 7B|3.5%|**9.4%**|
|V 13B|4.2%|**6.3%**|
|L2 7B|2.3%|**5.5%**|
|L2 13B|2.3%|**5.4%**|
Our method consistently outperforms DDD across all tested models, demonstrating our effectiveness.
**(3) Hass [3]:**
Hass improves Eagle2 by addressing the training-inference inconsistency in serial transformer heads within SpD. While Hass focuses on training methodology, our work enhances performance via architectural modifications. These two directions are orthogonal: our method could integrate Hass’s training improvements for further gains.
In the table below, we compare the performance of our Gumiho with Hass. Additionally, we evaluate a variant of our model (denoted as Gumiho w/ Hass ) where Hass’s training method is applied to our Transformer Head. All results are conducted on an Mi250 GPU using the LLaMA3-8B model with a temperature of 0.
| | MT-Bench | HumanEval |
|----|----|---|
| Eagle2 | 2.16×| 2.51×|
| Hass| 2.26×| 2.59×|
| Gumiho| 2.38×| 2.77×|
| Gumiho w/ Hass| **2.43×**| **2.84×**|
The aforementioned discussions will be included in the final version of our paper.
**Q4. Why $p_i - \zeta < 0$ ($i=d+1$) is not assumed and discussed accordingly.**
A4: Your concern is intuitively reasonable. From the perspective of probability definitions, it would indeed seem necessary to assume that probabilities should be greater than 0, even if this auxiliary variable is not a real probability but merely a constructed parameter for our proof.
However, throughout the proof process, we observed that such a constraint was unnecessary, and the proof could be completed without invoking this additional condition. Therefore, to maintain conciseness, we did not explicitly discuss this case separately.
**Q5. In Appendix D, the authors show the comparison of Eagle2 and Gumiho on two datasets. What about the other four datasets?**
A5: The other four datasets also exhibit similar results, and we will include the comparisons of these datasets in the final version of the manuscript.
---
Rebuttal Comment 1.1:
Comment: I am satisfied with the rebuttal from the author. They have addressed all of my concerns, and I decide to keep my decision.
---
Reply to Comment 1.1.1:
Comment: Thank you for your feedback and your support to our paper. | Summary: This paper proposes Gumiho, a hybrid architecture to prioritize early draft tokens with large and autoregressive heads, and parallel decoding for the rest tokens. The experimental results strongly support the effectiveness of this method.
Claims And Evidence: The experimental results strongly support the effectiveness of this method. Not only does it achieve a speedup in wall time, it also increases the acceptance rate—validating the authors’ approach from two different angles.
Methods And Evaluation Criteria: Yes, LLM acceleration is a very important topic for current applications. However, the authors should test over more advanced settings like flash decoding and bsz > 1.
Theoretical Claims: I checked the correctness of the theory and it is correct.
Experimental Designs Or Analyses: Yes.
But I think the authors should include more experimental results compared to the results of the implementation with flash decoding, i.e., flash_attn_with_kvcache and bsz > 1.
Supplementary Material: yes.
Relation To Broader Scientific Literature: na.
Essential References Not Discussed: no
Other Strengths And Weaknesses: Advantages:
1. The writing in this article is very clear.
2. I think the idea presented here makes a lot of sense. Intuitively, because the model is autoregressive, the earlier tokens are definitely more important than the later ones. Moreover, the proposed solution is quite elegant.
3. The experimental results strongly support the effectiveness of this method. Not only does it achieve a speedup in wall time, it also increases the acceptance rate—validating the authors’ approach from two different angles.
4. Balanced Performance and Latency: Gumiho’s design leverages a serial Transformer head to boost the quality of early token predictions without significantly sacrificing speed. The authors validate this balance through ablation studies (Figure 4), showing that the performance gains outweigh the latency introduced by the serial component.
Disadvantages:
1. The paper lacks a direct comparison with a strong baseline using flashdecoding.
2. The authors seem to introduce two different draft models (one large and one small), which could result in additional memory usage.
3. For the early draft model, using an approach similar to Eagle introduces an inconsistency between training and testing. I believe this issue becomes more pronounced as the network depth increases, as shown in Figure 4. Could the hass training method help mitigate this problem?
4. throughput improvement.
If the authors report results on 1 & 4, I will increase score from 2 to 3.
Other Comments Or Suggestions: NA.
Questions For Authors: see cons
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your suggestions and support.
**Q1. The paper lacks a direct comparison with a strong baseline using flashdecoding.**
A1: We have evaluated the baseline with FlashDecoding (FD) on the MT-Bench dataset using Mi250 GPU, as shown in the table below.
||L2 7B|L2 13B|
|-|-|-|
|FlashDecoding|2.11×|2.12×|
|Gumiho|**3.07×**|**3.34×**|
It is important to clarify that FD is an algorithm specifically optimized for attention computation. Its acceleration mechanism for LLMs is orthogonal to SpD – meaning these two approaches can be combined to achieve further acceleration beyond standalone SpD or FD implementations. The results of the combination will be shown in the final version of our paper due to the limited time of rebuttal.
**Q2. The authors seem to introduce two different draft models (one large and one small), which could result in additional memory usage.**
A2: Yes, you are correct. Our method does require more memory usage compared to Eagle2, and Medusa. Here’s why:
- Eagle2 use one single-layer Transformer head and reuse it serially across multiple speculative steps.
- Medusa only maintains five parallel MLP heads.
- Our approach, however, employs a two-layer Transformer head alongside five parallel MLP heads.
This architectural choice increases memory consumption. However, it enables a hybrid generation strategy: serial decoding for the first few tokens (to ensure accuracy) and parallel decoding for subsequent tokens (to maximize speed). While this introduces a memory-accuracy trade-off, it achieves a significant speedup improvement. We will explicitly discuss this trade-off in the final manuscript.
**Q3. For the early draft model, using an approach similar to Eagle introduces an inconsistency between training and testing. I believe this issue becomes more pronounced as the network depth increases, as shown in Figure 4. Could the hass training method help mitigate this problem?**
A3: Yes, our method could integrate Hass’s training strategy for further gains. Hass improves Eagle2 by addressing the training-inference inconsistency in serial transformer heads within SPD. While Hass focuses on training methodology, our work enhances performance via architectural modifications. These two directions are orthogonal, so our method could combine with Hass for further improvements.
In the table below, we compare the performance of our Gumiho with Hass. Additionally, we evaluate a variant of our model (denoted as Gumiho w/ Hass ) where Hass’s training method is applied to our Transformer Head. All results are conducted on an Mi250 GPU using the LLaMA3-8B model with a temperature of 0.
||MT-Bench|HumanEval|
|-|-|-|
|Eagle2|2.16×|2.51×|
|Hass|2.26×|2.59×|
|Gumiho|2.38×|2.77×|
|Gumiho w/ Hass|**2.43x**|**2.84x**|
The aforementioned discussions will be included in the final version of our paper.
**Q4. throughput improvement.**
A4: We evaluated Gumiho under bs > 1 scenarios with Vicuna 7B, as shown in the table below. Experimental results demonstrate that the speedup effect degrades as batch size increases, aligning with observations in prior works like Eagle. Throughput speedup of baseline and Gumiho is computed at their respective maximum bs, as Eagle do.
|BatchSize | MT-Bench | HumanEval |
|-|-|-|
| 1| 3.15×| 3.65×|
| 2| 3.10×| 3.61×|
| 4| 2.87×| 3.34×|
| Throughput| 2.03x | 2.11x |
The degradation in speedup with larger batch sizes can be primarily attributed to two key factors:
**(1) Inter-Sequence Execution Time Imbalance.**
With larger batch sizes, the number of accepted tokens varies across sequences within a batch, leading to divergent completion times. Due to the "bucket effect" in batch processing — where the entire batch's completion time is determined by the slowest sequence — completed sequences must wait for unfinished ones. This waiting time exhibits growth as batch size increases.
Notably, directly removing completed sequences and inserting new ones theoretically mitigates this issue but proves impractical in reality. Newly inserted sequences require full context re-computation (prefill phase), whereas existing sequences leverage pre-cached KV for efficient decoding. This computational asymmetry further increases overall latency.
**(2) Computational Resource Contention.**
Large batch sizes push SpD into a computation-bound regime. During parallel verification, the target model must process a massive number of candidate tokens per step (quantity = draft tokens × batch size). Larger batch sizes prevent full parallelization of computing units, causing the verification process to degrade into partially sequential operations. This diminishes the theoretical acceleration benefits.
Given these constraints, most SpD solutions (e.g., Lookahead, Medusa, Hydra, Cerberus, Eagle2, Hass) primarily focus on optimizing single-sequence (bs=1) scenario. Our work follows them, prioritizing inference efficiency optimization for single-sequence processing.
---
Rebuttal Comment 1.1:
Comment: The results of hass are good, and thanks for the authors' rebuttal. I increased my score.
---
Reply to Comment 1.1.1:
Comment: Thank you for your feedback and your support to our paper. | null | null | null | null | null | null |
Learning multivariate Gaussians with imperfect advice | Accept (poster) | Summary: This paper studies distribution learning within the framework of learning-augmented algorithms. Specifically, the authors study how to leverage potentially inaccurate "advice" about the true distribution to achieve lower sample complexity for learning multivariate Gaussian distributions.
For Gaussians with identity covariance, when given mean advice μ̃, the authors develop an algorithm achieving better sample complexity when the advice is accurate. Similar bounds were given for general covariance Gaussian. The paper also gives lower bound showing that the algorithms are optimal.
Claims And Evidence: The main sample complexity claims are well-supported by the analysis.
The efficiency claims for their algorithms are supported by showing how to formulate the estimation problems as LASSO or SDP optimization problems.
The experimental section provides empirical validation of the theoretical claims, showing the performance advantages when advice quality is good. I find the evidence presented thorough.
Methods And Evaluation Criteria: The paper uses LASSO-based method for mean estimation and SDP for covariance estimation. The latter may be somewhat inefficient in practice.
In terms of evaluation, the paper provides synthetic experiments, it'd be stronger if the experiments consider real data.
Theoretical Claims: I checked the main proofs in the main paper.
Experimental Designs Or Analyses: The experimental section only explores the sample complexity gains in the identity
covariance setting when one is given high quality advice. It'd be great if the work also studies the covariance case and see if the algorithm proposed is practical
Supplementary Material: No
Relation To Broader Scientific Literature: The topic broadly lies in the literature on learning-augmented algorithm. This particular work also intersects with algorithmic high dimensional statistics. Both have a long line of works in the past ~10 years in the theory community.
Essential References Not Discussed: No
Other Strengths And Weaknesses: No
Other Comments Or Suggestions: No.
Questions For Authors: No
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for thoughtful and constructive review!
You are right that while the SDP formulation used in TestAndOptimizeCovariance can be solved in polynomial time from a theoretical perspective (as we show in Appendix C.3), it is definitely impractical in practice. The focus of this work is to establish theoretical achievable sample complexity bounds and we hope that our work inspires future work that develops practical solutions matching our sample complexity bound. | Summary: One of the fundamental tasks in statistics is learning a Gaussian in total variation (TV) distance $\epsilon$. It is well known that the sample complexity for this task is on the order of $d/\epsilon^2$ when the covariance is the identity and $d^2/\epsilon^2$ for general Gaussians. This paper investigates whether the learning process can be made more efficient when given advice (or a warm start). For the first case (identity covariance), the advice consists of a vector $\tilde \mu$ that is somewhat close to $\mu$, while for the second case (general Gaussians), it consists of a matrix $\tilde \Sigma$ that is somewhat close to $\Sigma$.
The main results show that in the identity covariance case, if $\|\tilde \mu - \mu\|_1 < \epsilon d^{(1-\gamma)/2}$, then $O(d^{1-\Omega(\gamma)}/\epsilon^2)$ samples suffice. For general Gaussians, if $\|\text{vec}(\tilde{\Sigma}^{-1/2}\Sigma \tilde{\Sigma} - I )\|_1 < \epsilon d^{1-\gamma}$, then $O(d^{2-\gamma}/\epsilon^2)$ samples suffice. Here, $\|\cdot\|_1$ denotes the $\ell_1$-norm of vectors. Both algorithms run in polynomial time with respect to $d$ and the number of samples. These upper bounds are complemented by lower bounds showing that, up to constant factors in $\gamma$, no algorithm can achieve the task with fewer samples. Notably, the algorithm does not require knowledge of the quality of advice (i.e., $\|\tilde \mu - \mu\|_1$ and $\|\text{vec}(\tilde{\Sigma}^{-1/2}\Sigma \tilde{\Sigma} - I )\|_1$), and the lower bounds hold even when this quality is known.
The algorithmic approach consists of two main steps: (i) using a Gaussian tester combined with a search procedure to determine the quality of the given advice and (ii) designing an estimator that effectively utilizes the advice. The authors initially attempt to formulate the advice using the $\ell_2$-norm, since existing Gaussian testing methods rely on it. Ignoring computational constraints for a moment, a natural approach is to use a standard tournament argument along with a discretization of the unit ball to search for a vector that is $\epsilon$-close to $\mu$ in $\ell_2$-norm, which would imply a TV-distance guarantee. However, this approach requires at least $d$ samples, which is suboptimal. Instead, the argument is adapted to use the $\ell_1$-norm, leading to improved sample complexity. The paper further modifies the testers from (i) to be $\ell_1$-norm-based by partitioning the vector into chunks and using relationships between $\ell_1$ and $\ell_2$ norms for each chunk. While the tournament method has exponential computational complexity, the paper circumvents this by reformulating it as an appropriate optimization problem. This explains the use of the $\ell_1$-norm and outlines the proof of the first result.
The second result follows a similar high-level strategy, but the proof requires additional complexity to handle the matrix setting instead of the vector setting. Specifically, the partitioning of coordinates and the optimization program are more intricate. Additionally, an initial preconditioning step, inspired by differential privacy techniques, is introduced to ensure that $\|\Sigma^{-1}\|_2 \leq 1$.
The lower bound is derived using the Fano method, specifically a lemma from Ashtiani et al. (2020). This approach involves constructing a large family of Gaussians whose pairwise TV distance is at least $c_1 \epsilon$ while maintaining a KL divergence of at most $c_2 \epsilon$. The lemma is applied to Gaussians with means $\mu_i$ such that all $\mu_i$ satisfy the same upper bound on $\|\mu_i - \tilde \mu\|_1$ (advice) and have pairwise distances bounded by $\epsilon$. Such means can be constructed using codewords from an error-correcting code, as guaranteed by the Gilbert-Varshamov bound.
Finally, some numerical experiments are provided to demonstrate the sample complexity improvements when advice is used.
Claims And Evidence: The paper contains an extensive proof sketch in the main body which describes the main ideas.
Methods And Evaluation Criteria: See below for theoretical methods. I haven't looked into detail on the experiments, but they seem to be clear.
Theoretical Claims: I read the proof sketch of the introduction and the proofs presented in the main body. I don't have any major issues with these technical parts.
Experimental Designs Or Analyses: See above.
Supplementary Material: I have not personally tested the code from the supplementary material.
Relation To Broader Scientific Literature: The paper notes that advice has been studied in various problems within the context of online algorithms. While I have not seen this specific problem explicitly stated as an open question in prior work, I find it reasonable and believe it is a valuable addition to the literature.
Essential References Not Discussed: Regarding the reference at the end of the first page, there is a much simpler testing algorithm in Ilias Diakonikolas, Daniel M. Kane, and Ankit Pensia. “Gaussian Mean Testing Made Simple.” SOSA, 2023.
Other Strengths And Weaknesses: The paper is clearly written, and it provides lower bounds, which strengthen its theoretical contributions. However, there remains a gap between the upper and lower bounds. Specifically, when $\Delta^2 = \epsilon^2 d^{1-5\eta}$, the upper bound (ignoring logarithmic factors) is $d^{1-\eta}/\epsilon^2$, while the lower bound is $d^{1-5\eta}/\epsilon^2$.
Overall, I do not have any major concerns with the paper and would recommend its acceptance.
Other Comments Or Suggestions: I suggest explicitly stating the polylogarithmic factors in the theorem statements, as $\tilde{O}(\cdot)$ typically hides factors involving the variables inside the parentheses. In the current notation, it is unclear whether the sample complexity depends on $\delta$.
Additionally, does the lower bound hold for any $\Delta$ or only for a specific value of $\Delta$? It would be helpful to clarify this in the statement or in the text that follows.
Questions For Authors: Included above.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for thoughtful and constructive review!
Thank you for the reference of "Gaussian Mean Testing Made Simple", we will add it in our revision.
You are also indeed correct that there is a fundamental difference between our upper and lower bounds in terms of whether the advice quality is known. Our upper bounds (and the problem formulation) assume that the advice quality ($\\| \widetilde{\mu} - \mu \\|_1$ and $\\| \widetilde{\Sigma}^{-1/2} \Sigma \widetilde{\Sigma}^{-1/2} - I_d \\|_1$ respectively) is not known to the learning-augmented algorithms, even as an upper bound. Whereas the lower bounds apply even for the *weaker* problem where (an upper bound of) the advice quality is known to the algorithms. | Summary: This paper studied the problem of learning high dimensional Gaussians given imperfect advice. In particular, the authors show that given imperfect advice that is close to the true statistic quantity (in $l_1$ norm), both the following tasks have polynomial improvements with respect to the dependence of the dimension $d$ in sample complexity compared with the algorithms without using imperfect advice. The tasks are: given an imperfect advice of Gaussian mean, learn the true Gaussian mean of $N(\mu, I)$; given imperfect advice of Gaussian mean and covariance, learn the true mean and covariance of $N(\mu, \Sigma)$.
Claims And Evidence: Yes, they are supported by clear and convincing evidence.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: Checked the proof in the main body.
Experimental Designs Or Analyses: Yes
Supplementary Material: App A, B.
Relation To Broader Scientific Literature: The paper contributes well to the vast thread research of gaussian testing/learning, providing interesting results and improving the sample complexity of gaussian distribution learning. For example, the prior result on gaussian mean learning requires O(d) sample, however, the authors showed that given some accurate knowledge of the mean $\mu$, the sample complexity can be improved to $O(d^{1-\eta})$.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
1. I think this paper is clearly written with very useful explanation of the algorithm and motivation.
2. I think the results are interesting and strong. It is interesting to see that given imperfect advice one can break the sample complexity lower bounds.
3. The paper is solid with highly technical contributions.
Question/Weakness
I seems the SDP algorithm blows up the dimension to n' which is a polynomial of $d$. I think it would be a nice improvement to have more efficient algorithm for this.
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for thoughtful and constructive review!
You are right that while the SDP formulation used in TestAndOptimizeCovariance can be solved in polynomial time from a theoretical perspective (as we show in Appendix C.3), it is definitely impractical in practice. The focus of this work is to establish theoretical achievable sample complexity bounds and we hope that our work inspires future work that develops practical solutions matching our sample complexity bound. | Summary: Authors study bounds on sample complexity of mean and covariance estimation of multivariate gaussians
in learning-augmented setting. Here, the algorithm receives an untrusted advice in the form
of estimates of the mean and the covariance matrix.
The goal is to improve the sample complexity beyond the classical bounds of $O(d/\epsilon^2)$ and $O(d^2/\epsilon^2)$ respectively if the advice is close to correct.
The authors are motivated by the fact that there is an algorithm by Diakonikolas et al. which, given
precise estimate of the mean, can certify that this estimate is correct in time only $O(\sqrt{d}/epsilon^2)$
which suggests that an improvement might be possible also with an approximately correct estimate.
Indeed, they propose an algorithm which, given an estimate $\tilde \mu$ of the mean $\mu$ requires
only $\tilde O(d^{1-\eta}/\epsilon^2)$ samples if $\lVert \mu -\tilde \mu\rVert_1 < \epsilon\sqrt{d}\cdot d^{-5\eta/2}$. They provide a similar improvement in the case of covariance estimation.
Claims And Evidence: their claims are well supported with proofs and experiments
Methods And Evaluation Criteria: performance metrics studied are well established and the benchmark datasets are suitable for a theoretical study.
Theoretical Claims: I did not check fully any proof. However, their approach seems viable.
Experimental Designs Or Analyses: I did not try to replicate the experiments
Supplementary Material: I have looked at the supplementary material: it contains the code of the experiments and I did not try to run it.
Relation To Broader Scientific Literature: Authors study an important problem and their study fits well within the literature on learning-augmented algorithms.
Essential References Not Discussed: I am not aware of any.
Other Strengths And Weaknesses: Strengths:
* nice and promising results on an important problem
* performance of their algorithm with known prediction error is almost optimal, as supported by their lower bounds
Weaknesses:
* performance with perfect advice does not seem to match the certification algorithm by Diakonikolas et al. (2017).
* not clear whether the performance of their algorithm with unknown prediction error is optimal: lower bounds provided only for the case of known prediction error.
Other Comments Or Suggestions: none
Questions For Authors: can you please comment on the performance of your algorithm with $\lVert \eta - \tilde \eta\rVert_1$ approaching 0 and how does it match Diakonikolas et al.?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for thoughtful and constructive review!
For the mean setting, one can trivially obtain a sample complexity of $\widetilde{O}(\sqrt{d}/\varepsilon^2)$ when the advice quality is "good enough" by first running the tolerant tester (see Lemam 1.5) with $k = d$ and $\alpha = \varepsilon$, and returning the advice mean directly if the tolerant tester accepts (since this would imply that using the advice mean only incurs a KL error of at most $\varepsilon^2$). However, we agree that there is a discontinguity in the sample complexity between this "good enough" advice quality and our Theorem 1.1. This is in contrast to the covariance setting where our parameters in Theorem 1.2 allow us to recover $\widetilde{O}(d^2 / \varepsilon^2)$ directly. We are currently unsure if such brittleness/discontiguity is inherent for the mean problem setting but it would be interesting future work to pursue this inquiry.
You are also indeed correct that there is a fundamental difference between our upper and lower bounds in terms of whether the advice quality is known. Our upper bounds (and the problem formulation) assume that the advice quality ($\\| \widetilde{\mu} - \mu \\|_1$ and $\\| \widetilde{\Sigma}^{-1/2} \Sigma \widetilde{\Sigma}^{-1/2} - I_d \\|_1$ respectively) is not known to the learning-augmented algorithms, even as an upper bound. Whereas the lower bounds apply even for the \emph{weaker} problem where (an upper bound of) the advice quality is known to the algorithms.
As a side note, there is a typo in the definition of $\alpha$ in Algorithm 6 and on Line 1847. It should be $\alpha = \varepsilon d^{\eta - 1}$ and our subsequent calculations, theorem statement, and conclusions about the covariance setting remains unchanged. There are also some missing tildes to capture the $\log d$ factors in the proof. We will fix these errors in the revision.
---
Rebuttal Comment 1.1:
Comment: thank you for your careful response. I understand that your lower bound is for an easier problem and therefore it is a stronger result. But still it does not show the tightness of your upper bound. I maintain my (positive) score. | null | null | null | null | null | null |
CPCF: A Cross-Prompt Contrastive Framework for Referring Multimodal Large Language Models | Accept (poster) | Summary: This paper focus on addressing the incorrect responses of referring MLLMs tailored to misleading areas adjacent to or similar to the target region. Specifically, it introduces contrastive visual prompts generated by prompt extraction network, which is trained on extra dataset. Besides, to alleviate the computational cost, the distillation is adopted to run single-execution decoding. The writing is good in general. The experimental results shows its effectiveness of proposed method.
However, training on extra dataset compared with other competitors weakens its effectiveness. Besides, the training process is much complex compared with competitors.
Claims And Evidence: Yes, the claims are supported by quantitative and qualitative results.
Methods And Evaluation Criteria: Yes, the method seems make sense for the problem.
Theoretical Claims: There are no proofs for theoretical claims.
Experimental Designs Or Analyses: Yes, the comparison and ablation studies show its effectiveness of proposed method.
Supplementary Material: There are no supplementary material.
Relation To Broader Scientific Literature: It uses Ferret as baseline to conduct referring.
Essential References Not Discussed: The references seem adequate.
Other Strengths And Weaknesses: (1)The training process is much complex than competitors, which consumes computation resources.
(2)Besides, it utilizes extra dataset to train prompt extraction network and also the MLLM. In Line 315-316, the definition ‘not used’ and ‘included’ is measured from image-level? The region-level information may be leaked to test set.
Other Comments Or Suggestions: The ‘[region]’ on the top part of figure 3 should be green.
Questions For Authors: The contrast visual prompts are point or mask? Is it fixed across all datasets?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: ### **Q1 Training process**
Yes, we agree that our training process involves additional stages—specifically, self-training and distillation—which require 30 hours and 25 hours, respectively, to train for 50K steps on 8 A100 GPUs for the 7B model. However, we would like to kindly clarify the following points:
* (1) As shown in Table 4 of the main paper, **both stages are crucial**: self-training significantly improves model performance, while distillation greatly enhances computational efficiency. These results validate the rationality of our multi-stage training pipeline.
* (2) Moreover, **if training resources are limited, it is entirely feasible to largely reduce the number of training steps while still maintaining strong performance**. We observe that the model can achieve over 95% of its final performance after just 25K steps, reducing the required training time to 15 hours and 12 hours for the two stages, respectively. Even under this shorter training schedule, the model still achieves SOTA performance, making the overall training cost and effectiveness entirely acceptable for practical use.
* (3) Additionally, once training is completed, **the additional computational cost during inference for our method is very minimal—only +4.3% compared to the baseline Ferret**. This efficiency is achieved because our model supports end-to-end inference without requiring multiple MLLM executions as other contrastive decoding (CD) methods, which substantially reduces CD's computational complexity, highlighting the advantages of our method.
### **Q2 Extra dataset**
Yes, our method utilizes an additional dataset for training. This is intended to mitigate potential overfitting issues that may arise when performing contrastive decoding training directly on the original dataset (please refer to Lines 192–218 of the main paper for details). However, we would like to respectfully clarify the following points:
* (1) The additional dataset we use is NOT a fully annotated, supervised dataset, but rather an unannotated corpus without any question-answer labels, which is **easy to collect in real-world scenarios**. Moreover, training a model with such unlabeled data is non-trivial, and we have carefully designed a self-training approach to address this challenge. As such, **a new method for training referring MLLMs using unlabeled data is itself a key contribution of this work.**
* (2) **Even without using the extra dataset, our method can still achieve state-of-the-art performance**. To be specific, using the original dataset $\mathcal{D}$ without the extra dataset $\tilde{\mathcal{D}}$ in our method achieves an accuracy of 74.55 on ROC-Box, which still significantly outperforms previous approaches such as Ferret (71.71), Osprey (72.15), and Shikra (64.60). This indicates that the extra dataset only serves as a strategy for further enhancement, but is not the sole reason for our method’s strong performance. The proposed network architecture and training strategy also play a crucial role in achieving high effectiveness. In the revised version of the paper, we will incorporate the results without the extra dataset into Table 1 and Table 2. Thank you very much!
### **Q3 "not used’ and "not included’ in Line 315-316**
Here, the definitions ‘not used’ and ‘included’ are measured from both image-level and region-level, thus the region-level information will NOT be leaked to the test set.
### **Q4 The ‘[region]’ on the top part of figure 3 should be green.**
Thank you for indicating this typo! We will fix it in the revised paper.
### **Q5 The contrast visual prompts are point or mask? Is it fixed across all datasets?**
The contrastive prompt is a point, and this choice is fixed across all datasets. We also explored generating different types of prompts based on the input type—for example, generating box contrastive prompts for box inputs and mask contrastive prompts for mask inputs. However, this approach increases the optimization difficulty for the prompt extraction network, as it would require generating multiple prompt types from a single network. While using a separate prompt extraction network for each type is a potential solution, it would significantly increase the model’s parameter count. Therefore, we adopt a unified and simplest form of contrastive prompt across all datasets: the point.
**In summary, our method can achieve SOTA performance with an acceptable training time and requires very minimal additional computation during inference (only +4.3% than Ferret). While an extra dataset is used, it does not require any manual question–answer annotations, making it easy to obtain in practice.** Thank you again for your valuable commnets and thoughtful questions! We hope that our responses can address your concerns, and we would be happy to engage in any further discussion if you have any questions. Thank you so much! | Summary: The paper introduces CPCF (Cross-Prompt Contrastive Framework), a novel approach to improving Referring Multimodal Large Language Models. These models extend standard Multimodal Large Language Models by allowing them to focus on specific image regions using visual prompts. CPCF leverages a contrastive decoding strategy, where responses generated from an intended visual prompt are contrasted against those generated from misleading prompts.
Through extensive experiments across multiple benchmarks, CPCF achieves state-of-the-art performance, demonstrating significant improvements in multiple tasks. The model effectively mitigates errors caused by misleading regions, significantly outperforming previous approaches like Ferret.
Claims And Evidence: The claims made in the paper are generally supported by empirical evidence, including extensive experiments and comparisons with prior models.
However, I have several severe questions. The paper mentions that the frameworks "eliminating the uncertainty and instability inherent in manual methods. " How is it possible that the method "eliminates" uncertainty and instability? And what do these two properties, uncertainty and instability, mean in practice?
Methods And Evaluation Criteria: The contrastive decoding framework directly addresses the issue of models being misled by adjacent or similar visual regions, and the prompt extraction network provides an automated way to generate meaningful contrastive prompts. I suppose that this method is reasonable.
Theoretical Claims: There are no theoretical claims provided or any proof. The equations in this paper seem to be correct.
Experimental Designs Or Analyses: The contrastive decoding effectiveness is demonstrated through both quantitative results (Tables 1-3) and qualitative visualizations (Figure 5). The authors also considered multiple baselines and datasets for comparison and evaluation. The ablation study results are also sound.
Supplementary Material: Appendix. No other materials are provided.
Relation To Broader Scientific Literature: The novelty lies in task-specific contrastive decoding, automated prompt selection, and efficiency-aware distillation. These are meaningful contributions to the literature.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
The self-training mechanism leverages unlabeled images to generate synthetic question-answer pairs, enhancing model robustness without requiring extensive manual annotation.
Weaknesses:
CPCF introduces multiple additional components (contrastive decoding, self-training, and distillation), making training more computationally intensive than standard referring MLLMs. The authors did not provide a sufficient analysis about the computational costs, which could be a problem.
The weighting of contrastive prompts and distillation settings (e.g., hyperparameters like α in contrastive decoding) may significantly impact performance, requiring careful tuning.
Other Comments Or Suggestions: The figures and illustrations are slightly messy, especially the framework figure. Eq. (5) is out of box.
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you so much for your time in reviewing our paper and the valuable comments! We are sincerely encouraged by your recognition that our contributions are meaningful, the proposed method is reasonable, and the ablation study results are sound. We would like to provide the following responses to address your concerns and questions:
### **Q1 Clarification about "eliminating the uncertainty and instability inherent in manual methods"**
As indicated in the introduction, we observe that the model tends to generate incorrect answers tailored to misleading regions that are adjacent or similar to the target object. Motivated by this observation, we initially attempted to manually select a random point within these misleading regions as the contrastive prompt for contrastive decoding. However, we empirically found that model performance is highly sensitive to the choice of this point. For instance, selecting two different points within the same misleading region—only 10 pixels apart—may result in significantly different contrastive decoding outcomes. This sensitivity is why we describe manual methods as exhibiting “uncertainty and instability.” In contrast, our prompt extraction network, trained through deep learning optimization, can learn to automatically identify the most appropriate contrastive prompt, thereby alleviating the instability introduced by random manual sampling, leading to better performance. We acknowledge that our original use of the term “eliminate” was too absolute, and we will revise it to “alleviate” in the updated version of the paper. Thank you!
### **Q2 Computational costs of training**
Thank you for this valuable comment! Building on the pretrained Ferret model, our method introduces two additional training stages: (1) self-training and (2) distillation, which require 30 hours and 25 hours, respectively, to train for 50K steps on 8 A100 GPUs for the 7B model. In practice, if training resources are limited, it is entirely feasible to largely reduce the number of training steps while still maintaining strong performance. We observe that the model can achieve over 95% of its final performance after just 25K steps, reducing the required training time to 15 hours and 12 hours for the two stages, respectively. Even under this shorter training schedule, the model still achieves SOTA performance, making the overall training cost and effectiveness entirely acceptable for practical use. Additionally, we would like to kindly emphasize that, once training is completed, **the additional computational cost during inference for our method is very minimal—only +4.3% compared to the baseline Ferret**. This efficiency is achieved because our model supports end-to-end inference without requiring multiple MLLM executions as other contrastive decoding (CD) methods, which substantially reduces CD's computational complexity, highlighting the advantages of our method.
### **Q3 Hyperparameter**
Thank you for the comment! Our method is not sensitive to the choice of the hyperparameter $\alpha$ in Eq. 1. As shown in the table below, when $\alpha$ is set to 0.1, 0.5, or 1, the model achieves ROC-box accuracy of 77.91, 78.37, and 78.31, respectively—demonstrating stable performance across a range of values and consistently outperforming the previous SOTA result (72.83). In fact, most of the hyperparameters in our method—such as $\alpha$ and other training settings—can be directly adopted from existing contrastive decoding and referring MLLM approaches. We found that these settings already work very well without requiring specific modifications. Nevertheless, we are happy to conduct more ablation studies across a wider range of implementation settings and will include these results in the revised paper.
| $\alpha$ | ROC-Box | ROC-Mask |
| -------- | :-----: | :------: |
| 0.1 | 77.91 | 79.24 |
| 0.5 | 78.37 | 79.55 |
| 1 | 78.31 | 79.53 |
### **Q4 Figure issues**
The out-of-box issue will be fixed. Thank you so much!
Thank you again for your valuable comments and thoughtful questions. We hope that our responses can address your concerns, and we sincerely wish you all the best in your future life and work! | Summary: The article aims to solve the defects of existing referring MLLMs: it is difficult to accurately locate the prompt, and designs several solutions: 1. an effective referring MLLM framework that contrasts input prompts with contrastive prompts from misleading regions, 2. an automatic prompt extraction mechanism to identify optimal contrastive prompts, a self-training method to improve network optimization
## update after rebuttal
I think the author answered my questions very well. After the author supplemented the experiment, the experimental part of the article became more complete. In addition, I agree with the author's explanation of DPO and SFT. I suggest that the author supplement this content in the revision. I decided to maintain 4 points.
Claims And Evidence: The article has clear experimental results and robustness analysis experiments to prove its credibility
Methods And Evaluation Criteria: The article proposes three different strategies, including iterative DPO, which can enhance the performance of the model, which is verified in the robustness analysis experiment of the article.
Theoretical Claims: The article is an application-oriented article and does not provide any theoretical proof.
Experimental Designs Or Analyses: The experiments in this article are quite sufficient, but the comparison objects lack general MLLMs, such as Qwen-VL2.5. However, it has a detailed robustness analysis experimental module.
Supplementary Material: No
Relation To Broader Scientific Literature: No
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths：
1. The experimental results of the article are very good, far exceeding the previous referring MLLMs
2. The article provides a very detailed robustness analysis experiment, which makes me very confident in the effectiveness of the designed module.
3. The innovation of this article is quite clever. It integrates the idea of contrastive decoding into referring MLLMs and achieves good results.
Weaknesses：
I think the overall quality of the article is high, and there are no logical errors or experimental setting errors, but I have the following doubts about the experimental part, I think it would be better to explain these clearly
1. Why not compare some general MLLMs? For example, Qwen, InternVL, which both support referring tasks?
2. Why use iterative DPO? Have you tried iterative training similar to STAR?
3. Why is there no improvement in the trained model of 13B compared to 7B? Does it mean that this pipeline is difficult to scale up?
Other Comments Or Suggestions: As shown in Other Strengths And Weaknesses
Questions For Authors: As shown in Other Strengths And Weaknesses
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you very much for your time in reviewing our paper and the valuable comments! We are sincerely encouraged by your recognition that our experimental results are good, the robustness analysis is detailed, the innovation is clever, and the overall quality of the article is high. For your questions and concerns, we are happy to provide the following responses:
### **Q1 Comparison with general MLLMs**
Great idea! The comparison results with InternVL2.5-8B and Qwen2.5-VL-7B on Ferret-Bench are shown in the Table below. Our CPCF-7B outperforms both methods significantly, demonstrating the advantages and effectiveness of our novel method. We will compare on more benchmarks and incorporate these results into the revised paper.
| Method | Referring Cpationing | Referring Reasoning |
| --------------- | :------------------: | :-----------------: |
| InternVL2.5 | 80.4 | 79.2 |
| Qwen2.5-VL | 79.9 | 80.5 |
| **CPCF (Ours)** | **83.5** | **82.9** |
### **Q2 Usage of DPO and STAR**
Our method employs DPO rather than the standard SFT-based iterative training like STaR. This choice is motivated by the fact that compared to SFT, preference-based fine-tuning with DPO allows for more fine-grained control over model optimization and has been shown in prior work to better mitigate hallucination issues. The results in Table 6 of the main paper demonstrate the effectiveness of DPO: compared to conventional CE loss for SFT, DPO achieves improvements of 2.90, 3.47, 2.75, and 2.13 on box, mask, scribble, and point prompt types, respectively. Nevertheless, we agree that the STaR is a promising approach, and we plan to explore its potential in the context of referring MLLMs in future work. Thank you so much!
### **Q3 Improvement of 13B compared to 7B**
The limited performance improvement observed when scaling from the 7B to the 13B model may result from the relatively small size of existing referring multimodal datasets, which are insufficient to exploit the full potential of larger models. In fact, prior SOTA methods have also similarly exhibited marginal performance differences between their 7B and 13B variants; for example, Ferret-v2-13B even underperforms its smaller version, Ferret-v2-7B, on the Ferret-Bench benchmark. In contrast, despite a similarly modest performance gap, **our CPCF-13B consistently outperforms CPCF-7B across all benchmarks**, demonstrating our method’s effective scalability to larger models. For example, on the ROC task, CPCF-13B improves over CPCF-7B by 0.72, 1.17, 0.88, and 1.05, respectively across the 4 input prompt types. We believe that the development of larger and higher-quality referring multimodal datasets is crucial for unlocking the full potential of large referring MLLMs, which we identify as a key direction for our future work.
Thank you again for your valuable comments. We hope that our responses can address your concerns, and we sincerely wish you all the best in your future life and work! | Summary: This paper introduces CPCF, a cross-prompt contrastive framework for referring multimodal large language models. It improves region-specific response accuracy by automatically generating contrastive prompts from misleading regions, training these through a self-training strategy on additional unlabeled data, and then distilling the multi-execution model into a single-pass efficient model—all validated via extensive experiments across several referring benchmarks.
Claims And Evidence: Contrastive decoding using automatically extracted prompts reduces errors from distracting regions.\
Self-training on extra data (with a RAG-based question generation method) further improves prompt extraction. \
The distillation method can lower inference costs while preserving performance.
Methods And Evaluation Criteria: Please check the section **Other Strengths And Weaknesses**.
Theoretical Claims: The paper does not include theoretical claims.
Experimental Designs Or Analyses: Yes
Supplementary Material: Yes
Relation To Broader Scientific Literature: The paper builds upon and extends several lines of recent research. It relates to works on referring MLLMs (e.g., Ferret, Kosmos2), contrastive decoding for reducing hallucinations, and self-training and distillation techniques common in large-model training.
Essential References Not Discussed: No
Other Strengths And Weaknesses: 1. In Section 3.2, the authors construct a semantic similarity map and a relative distance map, process them through a lightweight CNN, and incorporate them into the image tokens. Directly adding these maps to the image tokens may introduce feature contradictions, leading to noisy updates.
2. The quality of $\tilde{D}$ must be exceptionally high, requiring both $D$ and $\tilde{D}$ from the same image domain to ensure consistency.
3. Although the self-training process in Section 3.3 leverages RAG and DPO, each component remains susceptible to errors, and the computational cost is significantly high.
4. The distillation step reduces inference costs, but the algorithm in general increases the overall complexity and computational burden of training. I recommend including experimental results comparing inference time between the proposed method and baselines to better illustrate efficiency gains.
Other Comments Or Suggestions: Please check the section **Other Strengths And Weaknesses**.
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank you for the time and effort you dedicated to reviewing our paper, as well as for your highly valuable comments! We would like to provide the following responses to address your concerns and questions:
### **Q1 Concerns on feature contradictions**
Thank you for this comment! We would like to kindly clarify that the semantic similarity map and relative distance map are NOT directly added to the image tokens. Instead, they are first processed by a learnable CNN before being fused with the image tokens. Through training, the CNN can be optimized to transform the map information into the same feature space as the image tokens. Moreover, the features generated by the CNN have the same spatial sizes as the image tokens produced by the vision encoder. Therefore, the problem of feature contradictions will not arise. In fact, this is a common strategy also widely used in many other models—for example, in the prompt encoder of the Segment Anything Model.
### **Q2&Q3 Quality of $\tilde{\mathcal{D}}$ and errors / computations of RAG and DPO**
Thank you for raising this important point! We would like to kindly provide the following clarifications:
* (1) **The generated data (including questions and answers) in $\tilde{\mathcal{D}}$ are of high quality, thus they can be effectively used for training without introducing many errors**. As indicated in Appendix C.1, we use GPT-4o to score the questions generated with RAG on a scale from 0 to 10 according to their relevance to the given image and input prompt. Among 2000 randomly sampled data from $\tilde{\mathcal{D}}$, these generated questions achieve a very high average score of 9.3, demonstrating their excellent quality. Furthermore, as reported in Appendix A.3, GPT-4o judges that in 91% of the sampled cases, the CoT-based answers are more accurate than the standard answers, demonstrating the effectiveness of using these pairs for DPO training. We also conduct a user study on 200 randomly selected generated samples, where volunteer ratings indicate that 94% of the generated data are correct and free of significant errors. These results demonstrate the robustness and effectiveness of our RAG- and CoT-based data generation method.
* (2) **Even with a small amount of errors, the impact on model performance is very minimal**. We find that models trained on our generated data perform almost identically to those trained on fully clean data. Specifically, we use GPT-4o to filter out noisy question–answer pairs from the generated dataset $\tilde{\mathcal{D}}$—approximately 8% of the total—and replace them with corrected versions. The model retrained on this cleaned dataset achieves ROC-Box and ROC-Mask accuracies of 78.90 and 79.96, respectively—only marginally higher than those of our original model (78.37 and 79.55), with differences of just 0.53 and 0.41. These minor performance gaps indicate that small errors in the generated cannot affect model performance significantly, further demonstrating the robustness of our method.
* (3) The original dataset $\mathcal{D}$ is highly diverse, containing rich images from a wide range of domains. Therefore, when constructing $\tilde{\mathcal{D}}$, it is unnecessary to deliberately search for images that specifically match the domains in $\mathcal{D}$. Instead, randomly sampling images from various domains is sufficient and can be easily implemented in practical applications.
* (4) Compared to directly using $\mathcal{D}$ or training with conventional CE loss, **using RAG to generate dataset $\tilde{\mathcal{D}}$ or training with the DPO loss increases training time by only 4.7 hours and 9.2 hours**, respectively—an overhead we believe is entirely acceptable in practical applications, especially considering the significant performance improvements they bring (as shown in main paper Table 6).
### **Q4 Comparison of inference time between the proposed method and baselines**
Good suggestion! The comparison of inference time between our method and the baseline Ferret is presented in Section 4.4, Lines 429–432. **Compared to Ferret, our method incurs only a 4.3% increase in average inference time while achieving significantly better performance** (please refer to Table 1). Additionally, Table 4 of the main paper compares the inference time of our method with and without distillation, showing that the distilled model reduces inference time by more than threefold. We further compare our CPCF with Shikra and GLaMM, and CPCF requires only an additional 8.9% and 2.5% average inference time, respectively. These demonstrate that the additional inference computation introduced by our method is minimal. We will include a comprehensive inference time comparison with all methods listed in Table 1 and incorporate the results into the revised paper. Thanks!
Thank you again for your valuable comments. We hope that our responses can address your concerns, and we sincerely wish you all the best in your future life and work! | Summary: This paper addresses the performance limitations of referring multimodal large language models (MLLMs), which often misinterpret ambiguous or misleading visual regions during referring comprehension tasks. To overcome this limitation, the authors propose the Cross-Prompt Contrastive Framework (CPCF), which improves both region understanding and response generation through systematic contrastive prompting.
The framework operates through three core innovations: (i) it automatically extracts discriminative visual prompts using a Q-Former module to highlight critical image regions; (ii) it employs a self-training paradigm that combines retrieval-augmented question generation with direct preference optimization (DPO) to enhance response quality; and (iii) it incorporates a knowledge distillation mechanism that facilitates efficient contrastive decoding while significantly reducing computational overhead.
Furthermore, this work presents an integration of retrieval-augmented generation for the creation of synthetic training data, along with contrastive learning principles tailored for visual-language alignment. Evaluations across multiple benchmarks demonstrate that CPCF achieves state-of-the-art performance, with quantitative results indicating significant accuracy improvements over existing methods. The authors further validate that the contrastive approach of their framework effectively reduces hallucination errors while maintaining computational efficiency through their proposed distillation strategy.
Claims And Evidence: Yes, the claims are supported by evidence in the paper.
Methods And Evaluation Criteria: Yes, appropriate benchmarks and metrics are used.
Theoretical Claims: The paper does not seem to make complex theoretical claims requiring proof verification. However, the core idea of contrastive decoding is supported by empirical results.
Experimental Designs Or Analyses: Yes.
Supplementary Material: Yes. All of them.
Relation To Broader Scientific Literature: N/A.
Essential References Not Discussed: N/A.
Other Strengths And Weaknesses: ### Strengths
- **Novel Methodology**: CPCF is a novel framework that leverages contrastive prompts to enhance referring MLLMs. The proposed framework is well-developed and incorporates several improvements that enhance both accuracy and efficiency.
- **Extensive Experimental Validation**: The authors conduct extensive experiments across multiple benchmarks and four diverse tasks, demonstrating state-of-the-art performance.
- **Good Writing**: The paper is clearly written and well-structured.
### Weaknesses
- **Lack of inference speed comparison**: The paper asserts that the proposed distillation technique enhances efficiency; however, it lacks a direct comparison with other methods regarding inference time.
- **Missing ablation on contrastive prompt quantity**: Table 5 presents ablation studies on the semantic similarity map and the relative distance map; however, there is no analysis of the impact of the number of contrastive prompts used.
- **Missing baselines**: Table 7 demonstrates that directly fine-tuning Ferret on the new dataset $\hat{D}$ achieves a box accuracy of 74.22, while CPCF with contrastive decoding attains an accuracy of 78.37. However, there has been no evaluation of Ferret-7B fine-tuned using contrastive decoding methods (e.g., CRG).
Other Comments Or Suggestions: N/A.
Questions For Authors: Refer to the weaknesses above.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you very much for your time in reviewing our paper and the valuable comments! We are sincerely encouraged by your recognition that our method is novel and well-developed, experiments are extensive, and writing is good. For your questions and concerns, we are happy to provide the following responses:
### **Q1 Inference speed comparison**
Thank you for this comment! The comparison of inference time between our method and the baseline Ferret is presented in Section 4.4, Lines 429–432. **Compared to Ferret, our method incurs only a 4.3% increase in average inference time while achieving significantly better performance** (please refer to Table 1). **We further compare our CPCF with Shikra and GLaMM: CPCF requires only 8.9% and 2.5% additional inference time, respectively, while achieving accuracy improvements of 13.77 and 8.44.** This demonstrates that the additional inference computation introduced by our method is minimal while the performance advantage is significant. We will include a comprehensive inference time comparison with all methods listed in Table 1 and incorporate the results into the revised paper.
### **Q2 Ablation on contrastive prompt quantity**
Thank you for your comment. We would like to clarify that **the number of contrastive prompts is NOT a predefined or fixed hyperparameter**; instead, it is automatically determined by the network. Specifically, as detailed in Lines 184–189 of the main paper, we utilize the Mean Shift algorithm to cluster the positions of all valid prompts to generate the contrastive prompts. Since Mean Shift is inherently a clustering method without a fixed cluster number, the number of resulting contrastive prompts varies accordingly, with an average of 3.2 in our experiments. We will provide a more detailed statistical analysis in the revised paper. A potentially related hyperparameter is **the number of learnable queries input to the Prompt Extraction Network**. As shown in the table below, when the number of learnable queries is too small, the network may miss critical information, leading to performance degradation; whereas when the number is too large, the model performance saturates, resulting in limited improvement if further increasing the query number (only +0.17 accuracy on ROC-Box when the query number increases from 64 to 128). We will include a more detailed ablation study on the number of learnable queries in the revised paper. Thanks!
| Query Number | ROC-Box | ROC-Mask |
| ------------ | :-----: | :------: |
| 16 | 76.68 | 77.09 |
| 32 | 77.75 | 78.43 |
| 64 | 78.37 | 79.55 |
| 128 | 78.50 | 79.98 |
### **Q3 Ferret-7B finetuned using CRG**
Good advice! We follow your suggestion by fine-tuning Ferret-7B on $\tilde{\mathcal{D}}$ using the contrastive decoding method CRG. As shown in the table below, **this method achieves an accuracy of 75.95% on the ROC-Box scenario, outperforming baseline Ferret (71.71%) and naive fine-tuning (74.22%), but still falling significantly short of our CPCF method (78.37%)**. This demonstrates the significant advantage of our proposed automatic contrastive prompt extraction approach over the manually designed strategy in CRG. We will include this result into Table 7 of the revised paper.
| Method | ROC-Box | ROC-Mask |
| :----------------------------- | :-------: | :-------: |
| Ferret | 71.71 | 72.39 |
| Ferret + naive fine-tuning | 74.22 | 74.37 |
| Ferret + CRG (w/o fine-tuning) | 75.40 | 76.20 |
| Ferret + CRG (w/ fine-tuning) | 75.95 | 77.06 |
| **CPCF (Ours)** | **78.37** | **79.55** |
Thank you again for your valuable comments and thoughtful questions! We hope that our responses can address your concerns, and we would be happy to engage in any further discussion if you have any questions. Thank you so much! | Summary: This paper presents CPCF, a cross-prompt contrastive learning framework designed to enhance the performance of referring multimodal large language models (MLLMs). The proposed approach aims to address a key issue in existing referring MLLMs: errors caused by misleading visual regions adjacent to or similar to the target region. The authors introduce three contributions:
1. A prompt extraction network to automatically identify optimal contrastive prompts.
2. A self-training method leveraging unlabeled data to improve training quality.
3. A distillation approach to reduce the computational overhead associated with contrastive decoding.
The paper is well-organized, the motivation is clearly stated, and experiments demonstrate the effectiveness of CPCF across multiple benchmarks. However, there are some areas that require improvement, as outlined below.
**Pros:**
1. The proposed method is thoroughly evaluated across multiple datasets, including Referring Object Classification (ROC), Referring Text Classification (RTC), and Referring Description (RD).
2. The results show state-of-the-art performance, significantly outperforming existing models like Ferret, GPT4RoI, and Shikra.
**Cons:**
1. There are many shortcomings in the writing of the paper, including some grammatical issues. For example, in line 022, the phrase "from...from...from..." appears. There are also other expression issues throughout the paper. I'm also confused by the naming of the method (CPCF) in this paper.
2. Figure 1 does not reflect the image editing experiment mentioned on the right side of line 39 in the paper. It is unclear what the authors intend to convey with Figure 1 in the main text and Figure 8 in the supplementary material.
3. Grounding or referring multimodal large language models is currently a very popular topic, but the authors' introduction to related work is incomplete. They may refer to relevant works mentioned in the recent survey "Towards Visual Grounding: A Survey" [1]. For example, besides Ferret and Shikra, which are mentioned in the paper, there are many similar works, such as LLaVA-Grounding [2], Grounding-GPT[3], Next-Chat, Groma, LION, Ferret-V2, and u-LLaVA, etc, most of these related works should be discussed.
4. The self-training approach using generated data mentioned in this paper is not novel. Similar methods have been widely used in weakly or unsupervised visual grounding works, such as CLIP-VG [4] and VG-annotator [5]. However, the author without include any discussions.
5. While the paper claims CPCF is efficient, a more detailed breakdown of computational overhead (e.g., FLOPs, memory usage, or inference speed comparisons) would strengthen this claim.
6. The paper compares CPCF with Ferret + VCD, Ferret + ICD, and Ferret + CRG in Table 3. However, it lacks a qualitative discussion on why CPCF outperforms these methods beyond numerical results.
7. A deeper comparison with CRG (Wan et al., 2025) is needed, as both use contrastive decoding but differ in implementation. The authors should highlight how CPCF's automatic prompt extraction provides advantages over CRG's perturbation-based method.
8. Table 4 shows an increase in inference time without distillation. The authors should clarify whether the distillation affects model accuracy trade-offs.
9. Most importantly, the experiments in this paper are solid, but the work appears to be an combination of existing modules and methods. Techniques such as prompting, pseudo-label self-training, and distillation are commonly used in current research. The paper does not present particularly outstanding innovations that would be sufficient for publication at a top-tier conference like ICML.
--
[1] Towards Visual Grounding: A Survey. arXiv preprint arXiv:2412.20206.
[2] Llava-grounding: Grounded visual chat with large multimodal models. In European Conference on Computer Vision (pp. 19-35). Cham: Springer Nature Switzerland.
[3] GroundingGPT: Language Enhanced Multi-modal Grounding Model. In Proceedings of the 62nd Annual Meeting of the Association for Computational Linguistics (Volume 1: Long Papers) (pp. 6657-6678).
[4] VG-Annotator: Vision-Language Models as Query Annotators for Unsupervised Visual Grounding. In 2024 IEEE International Conference on Multimedia and Expo (ICME) (pp. 1-6). IEEE.
[5] Clip-vg: Self-paced curriculum adapting of clip for visual grounding. IEEE Transactions on Multimedia, 26, 4334-4347.
Claims And Evidence: see above.
Methods And Evaluation Criteria: see above.
Theoretical Claims: see above.
Experimental Designs Or Analyses: see above.
Supplementary Material: see above.
Relation To Broader Scientific Literature: see above.
Essential References Not Discussed: see above.
Other Strengths And Weaknesses: see above.
Other Comments Or Suggestions: see above.
Questions For Authors: see above.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: ### **Q1 Writing**
We will carefully revise the writing based on your suggestions. “CPCF” is an abbreviation formed from the initials of "Cross-Prompt Contrastive Framework". We will clarify this in the revised paper.
### **Q2 Figures**
We will incorporate results of the image editing experiment into Figure 1. Figure 1 aims to highlight a common limitation of prior methods: generating wrong responses tailored to misleading regions that are adjacent or similar to the target object, which is the motivation for this work. Figure 8 in supp provides cases comparing our CPCF with the baseline Ferret, where CPCF produces correct responses while Ferret fails, showing the advantages of our method.
### **Q3 Related works about grounding and referring MLLMs**
Thank you for pointing out these works! Different from them, our CPCF designs the first automatic contrastive decoding technique for referring MLLMs and with many task-specific designs tailored to this setting (see the answer for Q9 for details). We will cite and include a discussion of these papers in our revised paper.
### **Q4 Comparison with other self-training methods**
Thank you for recommending these two works, **which are very excellent! We promise that we will cite them (CLIP-VG [4] and VG-Annotator [5]), and include corresponding discussions in our revised paper**. Our method differs significantly from [4,5] in 2 key aspects:
* **Different data Generation Methods**: [4,5] rely on templates, scene graphs, or small NLP models for generation, which may lack diversity in the generated data. In contrast, our CPCF leverages the more powerful MLLMs with **a novelly designed RAG framework**, where a similar labeled example is applied to guide the generation process for each unlabeled data. The stronger generative capabilities of MLLMs enhance data diversity, while RAG improves stability and mitigates errors.
* **Different Training Strategies on Generated Data**: [4, 5] use conventional CE loss, L1 loss, or mIoU loss, to train the generated data. In contrast, our method introduces a carefully designed Direct Preference Optimization (DPO) framework, and the preference pairs in DPO are task-tailored designed—specifically, commonly generated vs. CoT-generated answers. **This is the first application of DPO to referring MLLMs (and with task-specific designs, not only simple usage)**, and it significantly outperforms CE loss (Table 6).
With these innovations, we believe our self-training method is novel. Thank you!
### **Q5 Computational overhead**
Please see our answer to Reviewer Xoy3 Q1. Thanks!
### **Q6 & Q7 Discussion with other CD methods (like CRG)**
Please see our answer to Reviewer hUfo Q1. Thanks!
### **Q8 Effect of distillation on accuracy**
Yes, distillation slightly affects accuracy, as shown in Table 4, where box accuracy and mask accuracy decrease by 0.71 and 0.60, respectively, after applying distillation. However, given that the distillation can largely reduce average inference time by 74%, we believe this minor loss in accuracy is a worthwhile trade-off and completely acceptable. More importantly, the distilled model still significantly outperforms the previous SOTA by +6.22 in box accuracy and +5.36 in mask accuracy, demonstrating that it remains highly effective despite the compression.
### **Q9 Innovations**
Our framework contains multiple components, including contrastive decoding, self-training, and distillation. However, they are NOT simple combinations of existing modules, but each with the following key novelties:
* (1) **Contrastive Decoding (CD)**: Prior CD methods typically rely on manually constructed contrastive objects (e.g., VCD uses perturbed images generated from random noise), which may introduce uncertainty and are difficult to be optimal (e.g., it is difficult to identify the most appropriate random noise for VCD). In contrast, **we are the first to propose an automated and learnable approach for identifying contrastive objects within the CD framework**, where a prompt extraction network is trained to find the optimal contrastive target **automatically**. This makes our method fundamentally different from previous CD methods and with better performance (Table 3).
* (2) **Self-Training**: Kindly see our answer to Q4.
* (3) **Distillation**: **We are the first to apply distillation to CD**, effectively addressing the issue of high computational cost in CD. More importantly, our framework does NOT simply adopt existing distillation techniques; instead, **we propose a novel distillation loss (Eq. 5, $\mathcal{L}_{inp}$) specifically tailored to the characteristics of CD and referring MLLMs**, which is highly effective (Table 8).
In summary, **we have introduced task-specific, novel designs for each key component of our framework. Therefore, we believe our method is novel and can provide new insights**. We will clarify these more clearly in the revised paper and cite your recommended papers. Thank you!
---
Rebuttal Comment 1.1:
Comment: Thanks to the authors for their efforts in the rebuttal. After reading the authors' response and considering my 9th comments, I decided to keep my review rating.
---
Reply to Comment 1.1.1:
Comment: Thank you again for your comments. However, we would like to reiterate that our method is **NOT** a simple combination of existing techniques, but instead incorporates several **novel designs specifically tailored to this task**, as we have detailed in our rebuttal. Specifically, our contrastive decoding method introduces a **newly proposed automatic contrastive target selection mechanism**; our self-training strategy adopts a **data generation and training method that is fundamentally different** from those in your mentioned [4, 5]; and our distillation framework includes a **new, task-specific loss function (Eq.5)**. More specifically, our method introduces significant improvements over previous contrastive decoding (CD) approaches in the following three key aspects: **working mechanism, training strategy, and efficiency enhancement**.
* (1) **Regarding working mechanism: we propose the first automatic contrastive target selection method (sec 3.2) for CD framework**: Prior CD methods typically rely on manually constructed contrastive objects (e.g., VCD uses perturbed images generated from random noise), which may introduce uncertainty and are difficult to be optimal (e.g., it is difficult to identify the most appropriate random noise for VCD). In contrast, **we are the first to propose an automated and learnable approach for identifying contrastive objects within the CD framework**, where a prompt extraction network is trained to find the optimal contrastive target **automatically**. This makes our method fundamentally different from previous CD methods and with better performance (Table 3).
* (2) **Regarding training strategy: we propose the first self-training method (Section 3.3) specifically designed to enhance the effectiveness of CD.** Moreover, this training method requires only unlabeled data, without the need for any manually annotated question–answer pairs, making it easy to collect in real-world applications. More importantly, our self-training strategy is fundamentally different from—and superior to—the approaches proposed in [4, 5] mentioned by Reviewer avef, both in terms of data generation and training methods. This is detailed in our response to Reviewer avef’s Q4.
* (3) **Regarding efficiency enhancement: we propose the first distillation method specifically designed for contrastive decoding (CD), greatly reducing the inference time of previous CD methods by 73%**. More importantly, we do not simply adopt existing distillation techniques; instead, we design a novel distillation loss function (Eq. 5) specifically tailored to the unique characteristics of CD and referring MLLMs. This design proves to be highly effective, as evidenced by the results in Table 8.
Incorporating these novel designs, **our proposed method is an entirely new CD framework tailored to referring MLLMs and with better performance (Table 3) and higher efficiency**. Thus, we believe that our method is novel.
Additionally, we are pleased to note that **the novelty and contributions of our work have been recognized by many other reviewers**, such as **Reviewer Xoy3** (*"CPCF is a novel framework that leverages contrastive prompts to enhance referring MLLMs. The proposed framework is well-developed and incorporates several improvements that enhance both accuracy and efficiency."*), **Reviewer Vjf8** (*"The innovation of this article is quite clever."*), **Reviewer Za66** ("*The novelty lies in task-specific contrastive decoding, automated prompt selection, and efficiency-aware distillation. These are meaningful contributions to the literature.*"), and **Reviewer hUfo** (*"Innovative idea of leveraging misleading prompts in a structured contrastive setup"*).
Thank you once again for the time and effort you devoted to reviewing our paper. | Summary: This paper introduces CPCF, a novel framework designed to enhance referring capabilities in MLLMs. The method leverages a cross-prompt contrastive strategy, in which responses generated from visual prompts are contrasted with those from misleading regions. The framework further incorporates a prompt extraction network to identify contrastive prompts, a self-training approach to synthesize training data from unlabeled images, and a distillation technique to reduce computational overhead.
Claims And Evidence: The central claim is that CPCF improves the robustness and accuracy of referring MLLMs by mitigating the influence of misleading visual regions. While the empirical gains are consistent across benchmarks, some of the claims particularly regarding the “significant differences” from prior contrastive decoding methods like CRG, are overstated. The evidence for CPCF’s advantage over CRG largely hinges on controlled benchmarks and implementation-level choices, without a rigorous apples-to-apples comparison.
Methods And Evaluation Criteria: The methodology is generally well-motivated but not without caveats:
- The prompt extraction network is a reasonable architectural choice, but its complexity (e.g., priors like semantic similarity and distance maps, clustering, noise injection) introduces many design decisions with limited ablation or theoretical justification.
- The self-training method relies on synthetic question-answer generation, which raises concerns about data quality. Although the authors attempt to mitigate this via RAG-based retrieval and CoT prompting, the robustness of these synthetic annotations is unclear.
- The use of DPO loss with CoT vs. direct generation is under-motivated; it's unclear if simpler reward-based tuning methods would suffice.
- The evaluation tasks are standard, but most of the experimental results show improvements in the range of ~1–2%, which is modest given the complexity of the proposed pipeline.
Theoretical Claims: No.
Experimental Designs Or Analyses: While the experimental section is thorough in scope, some issues limit its interpretability:
- The baseline comparisons (e.g., with Ferret) are fair, but CRG, the most relevant contrastive approach, is not re-implemented with CPCF’s enhancements (e.g., distillation), limiting the claim that CPCF is “significantly different and better”.
- Appendix tables suggest that CPCF’s improvements often arise from better training data rather than the contrastive mechanism per se (see Table 7).
- The computational efficiency claims rely on distillation, but this step is itself complex and introduces extra modules (AGN, adapters). No wall-clock or energy consumption comparisons are provided.
Supplementary Material: Appendices provide extended evaluations and ablations. However, the amount of added complexity per component (e.g., priors in prompt selection, CoT answer synthesis, RAG-based retrieval) is difficult to track.
Relation To Broader Scientific Literature: The paper is aware of recent work in referring MLLMs and contrastive decoding. However, the differences with works like CRG and ICD are primarily empirical and implementation-level, not conceptual. The line between CPCF and these prior methods is thinner than the authors suggest.
Essential References Not Discussed: The paper does not cite work on robust grounding or saliency-based region selection, which could offer alternative approaches to handling misleading regions.
Other Strengths And Weaknesses: Strengths:
- Innovative idea of leveraging misleading prompts in a structured contrastive setup.
- Distillation step is well-motivated to reduce inference cost.
- Strong empirical results on standard benchmarks.
Weaknesses:
- Significant complexity in the pipeline with many interdependent components.
- Marginal gains relative to added engineering overhead.
- Limited generalization claims beyond the specific tasks used in training/evaluation.
Other Comments Or Suggestions: No.
Questions For Authors: - Can you isolate the impact of contrastive decoding without prompt extraction, self-training, or distillation?
- How robust are the gains when tested on out-of-distribution prompts or images?
- How would CPCF behave with overlapping or ambiguous prompts (e.g., in crowded scenes)?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: **Q1 Discussion with other contrastive decoding (CD) methods (like CRG)**
* Although both methods use CD, the contrastive targets are different. CRG constructs contrastive targets by removing the target region directly from the image, which may severely disrupt the image’s integrity—especially when the target region is large—potentially leading the model to capture noisy information during contrast. Differently, our method does not alter the image content, mitigating this issue and resulting in better accuracy.
* CRG and most other CD methods significantly increase computational cost, as each contrastive object must be processed separately by the MLLM. Our CPCF is the first CD method to introduce a distillation technique to address this issue, reducing inference costs by 73%.
* Even when CRG is equipped with our enhancements (self-training, distillation), its resulting accuracy of 76.74 on ROC-Mask still falls short of CPCF (79.55), further highlighting our advantages.
**Q2 Ablation for components in prompt extraction network**
These ablation studies are included in main paper Table 5. Thank you!
**Q3 Robustness on synthetic data quality**
Please see our answer to Reviewer nWKK Q2&Q3. Thanks!
**Q4 Simpler reward-based tuning**
Nice insight! It is indeed possible to use other reward-based tuning methods, but they still require preference pairs to compute rewards in DPO or to train a reward model in RLHF. Other methods typically rely on additional models (e.g., GPT) or human annotations to obtain these preference pairs, which can be costly and labor-intensive. This serves as our motivation for using the model itself to generate preference pairs for DPO in this work, which is more cost- and labor-efficient.
**Q5 Improvement**
Kindly note that **across all 12 metrics in the 4 benchmarks presented in Table 1 and Table 2, our method outperforms the second-best one by more than 2% in 9 cases—accounting for 75% of the total.** This shows the significant improvements of our method. Also note that our method incurs only very minimal additional computational cost during inference (just +4.3% than the baseline Ferret). The significant performance improvement achieved with such a small increase in inference cost further shows the advantage of our approach.
**Q6 Improvement from data or method?**
**Even without using the better extra dataset, our method can still achieve SOTA**. Using the original dataset $\mathcal{D}$ without the extra dataset $\tilde{\mathcal{D}}$ in our method achieves an accuracy of 74.55 on ROC-Box, which still significantly outperforms previous methods such as Ferret (71.71), Osprey (72.15), and Shikra (64.60). This indicates that **the better extra dataset only serves as a strategy for further enhancement, but is not the sole reason for our method’s strong performance**. The proposed network architecture and training strategy also play a crucial role in achieving high effectiveness.
**Q7 Wall-clock of distillation**
As indicated in Sec 4.1, distillation requires 25 hours of training for the 7B model on 8 A100 GPUs. Considering that this method reduces inference-time computation by 74% with only a very minimal drop in accuracy (see Table 4), we believe the additional training cost is worthy.
**Q8 Pipeline complexity**
Please see our answer to Reviewer WGMH's Q1. Thanks!
**Q9 Contrastive decoding (CD) w/o other components**
Good advice! We evaluate a method where all other components are removed, and contrastive prompts are manually sampled from regions adjacent to or similar to the target object for CD. This method achieves accuracies of 74.33 on ROC-Box and 75.08 on ROC-Mask, outperforming the baseline Ferret by 2.62 and 2.69, respectively, but still falling short of our full method by 4.04 and 4.47. These results demonstrate that both CD and other designed components are useful.
**Q10 OOD prompts and images**
* OOD prompts: We remove the data with scribble prompts and train the model using only other prompts. When evaluated with scribble prompts, this model achieves an accuracy of 73.09—lower than our fully trained model (77.97), but still higher than the fully trained Ferret (71.58).
* OOD Images: Images for text recognition are NOT included during training, so the Referring Text Classification (RTC) task in Table 1 is an OOD setting. In this scenario, our method outperforms all previous methods, showing its strong generalization ability.
**Q11 Overlapping or ambiguous prompts**
Good advice! We select 422 crowded scene images with overlapping or ambiguous prompts. Our CPCF achieves an accuracy of 66.98, significantly outperforming Ferret (59.79), showing the high robustness of our method. These results will be included in the revised paper. Thanks!
In summary, **CPCF significantly improves accuracy (more than 2% in 75% of all metrics), while requiring very minimal additional inference cost (+4.3% than Ferret)**. We'll illustrate more clearly in paper. Thank you! |
Improving the Scaling Laws of Synthetic Data with Deliberate Practice | Accept (oral) | Summary: The authors propose a method for synthetically generating data based on an entropy-guided sampling of diffusion models. Their method is dynamic in that they call their entropy-guided sampling every time their model's validation accuracy plateaus. They show that their synthetically generated data is better than prior work on ImageNet-100 and ImageNet-1K. They present some theoretical motivation for their approach.
Claims And Evidence: Yes the empirical claims are supported by clear evidence, but I do not see how their theory is related to diffusion models and synthetic data generation which is the main topic of their paper.
Methods And Evaluation Criteria: I am confused as to why the authors use the validation set for their algorithm instead of a subset of the training set. It makes comparison to prior work more difficult as prior work reports the model performance on the test set and not the training set.
Theoretical Claims: The proofs are in the appendix and I did not carefully check them, but I do except the claims to be correct.
Experimental Designs Or Analyses: The experimental design is valid for the task they are trying to solve.
Supplementary Material: I took a cursory look at the appendix, but did not dive into the details.
Relation To Broader Scientific Literature: Synthetic data is becoming an integral tool for the broader scientific community, offering solutions for settings that are data scarce, have privacy concerns, and more generally to improve model performance.
Essential References Not Discussed: The theory effectively claims that selecting examples along the decision boundary is beneficial and that one should continue to update the decision boundary. These two facts have been shown theoretically and empirically in the active learning literature in much more general settings than the ones analyzed here. See for example "Margin Based Active Learning" by Balcan et al and "Improved algorithms for efficient active learning halfspaces with massart and tsybakov noise" by Zhang et al. (for theory) and Batch Active Learning at Scale by Citovsky et al. (for empirical evidence).
Other Strengths And Weaknesses: Strengths
* Leveraging the diffusion mechanism by using entropy-guided sampling presents an interesting algorithmic approach.
* Their method avoids the need to over-generate and then prune strategy that priori work has often used.
* Empirical results show positive improvement using their proposed methods.
Weaknesses
* Theory seems to be disconnected from the algorithm they present.
* Theory doesn't provide novel insights than prior theoretical work and seems to be in more restricted settings.
* Main differences with Hemmat et al 2023 are not explained in detail.
* Dynamic nature of the algorithm seems a bit ad-hoc and it would be much better if it didn't need to use an external set to decide whether to generate more synthetic data.
Other Comments Or Suggestions: DP is not a great acronym as it is usually used for differential privacy.
Questions For Authors: 1. What is the main difference between this work and Hemmat et al 2023?
2. The theory section seems disconnected from the setup the authors are interested in. In particular, how is the theory related to diffusion models and synthetic data generation? If I am understanding correctly, it just seems to be a linear classifier over gaussian input data?
3. I am confused by Figure 2. The black line is the strategy that selects all data, but then the x-axis is the size of the selected data?
4. For Table 2, the "IN real Val" column is the model performance on the ImageNet validation set that was used in the algorithm? If it is used in the algorithm, then we should not be comparing against it. Why didn't the authors just use a subset of the training data as their validation set so that we could more easily compare to previous work? Also why does a static method from previous work appear multiple times? Is the difference only the number of iterations run? I don't see a discussion or explanation in the main text.
5. Is there other ways to make the algorithm dynamic without having to use the train/validation set? Most dynamic selection algorithms don't make use of the validation set and are solely based on the learner so it begs the question whether this is actually needed here.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for their thoughtful and detailed feedback.
---
### **On theory**
**Relation to Active Learning.** Though related at a high level, our work differs from standard active learning, which focuses on querying labels for unlabeled data. We instead focus on generating useful training examples. The papers mentioned by the reviewer establish bounds which indicate that aggressive pruning restricted to a well crafted region leads to improved sample complexity for active learning. Our contributions differ: (1) We show that DP is equivalent to pruning. (2) We analyze this pruning in a toy setting using random matrix theory, deriving **exact** error curves. (3) This analysis helps explain why DP improves sample efficiency in practice.
**Connection between theory & algorithm.** The theory offers a principled explanation for DP’s success: it effectively samples from a pruned data distribution, without over-generating and discarding samples. We focus on high-dim regression as it’s analytically tractable yet captures the key aspects of the problem. While simplified, the goal of the theory is to isolate and analyze core components of the algorithm, helping explain its empirical effectiveness. We will clarify this in the revision.
**It just seems to be a linear classifier over gaussian input data?** No. The theory involves linear classification over **"pruned"** Gaussian data, which significantly alters the data distribution. For example, pruning distorts the standard Marchenko-Pastur law (Lemma 4), making the analysis technically involved. This required careful use of non-standard random matrix theory tools (see Appendix). We'll clarify this in the manuscript.
### **Use of the validation set**
Using a validation set for early stopping and hyperparameter tuning is standard practice [1-4]. We follow the same principle: validation is used only for model selection, not training. Like early stopping, we detect when performance saturates, but instead of stopping, we generate new data and continue. This can be seen as repeated early stopping with dynamic dataset expansion.
**Fair evaluation.**
In Table 1, we report on **both** the standard ImageNet val set (IN real Val.: commonly reported, e.g., [1, 2] since the actual test set is not public) and on the **held-out training data** (IN real tr.), which is untouched by the selection or training process in DP and serves as a true test set.
**Validation use is helpful but not essential.**
While we use the validation set to determine when to generate more data, DP does not depend on it fundamentally. Alternatives include:
a. Internal signals, like training loss flattening (see Figure 5 in this anonymous link https://drive.google.com/file/d/1XbkVVsHDQyhfSJfqGkaFLC7Polb0dHZR/view).
b. Predefined schedules, e.g., adding data every X epochs.
c. A synthetic validation set
In short, our use of validation aligns with common practice and is just one possible design.
[1] Sarıyıldız et al. 2023.
[2] Fan et al. 2024.
[3] Dosovitskiy et al., 2021.
[4] He et al. 2022.
### **Comparison with Hemmat et al.**
While we build on feedback-guided generation, the two works differ significantly in their motivation, setup, and methodology. Our goal is to improve scaling laws in a **zero-shot** setting with **dynamic data generation**. In contrast, Hemmat et al. focus on class imbalance, using a **static**, one-time rebalancing step with **image-conditioned** generation.
| Aspect | This Work | Hemmat et al. (2023) |
|---------------------------|---------------------------------------|----------------------------------------|
| **Primary Goal** | Improve scaling laws of synthetic data | Handle imbalanced classification |
| **Use of Real Training Data** | None | Real examples used for conditioning |
| **Generation Type** | Dynamic, repeated | Static, one-time |
| **Diffusion Conditioning** | Class labels only | Image and class labels |
| **Scaling Analysis** | Theoretical + empirical | Not studied |
### **Table 2 and Figure 2**
In Tab 1, columns 2, 3 report baselines with varying data sizes and iterations. We include these to ensure a fair comparison with our dynamic setup, which increases data over time.
In Fig 2, the x-axis shows the final data size. E.g., to train with 2^10 examples using the "top 10%" (red), we generate 2^11 and keep the hardest 10%. The "select all" (black) strategy generates and uses all 2^10.
---
### **DP as the acronym**
Thanks for the suggestion. We are happy to adopt the acronym to SDP (Synthetic data with Deliberate Practice). It has a nice ring to it! :)
---
Thank you again for your constructive comments. If there's anything in particular that’s holding you back from potentially increasing your score, let us know. | Summary: This paper focuses on the task of synthetic data generation for image classification. Specifically, traditional methods of synthetic data generation in classification tasks suffer from diminishing returns as the dataset size increases, leading to inefficient use of generated data. Inspired by the concept of deliberate practice in human learning, the authors propose a novel framework, Deliberate Practice for Synthetic Data Generation (DP). Instead of generating a static dataset upfront, DP iteratively trains a model, generates new data, and selects challenging examples to incrementally expand the training set. The authors provide theoretical justifications for their approach and conduct empirical experiments on two image classification datasets. The results demonstrate that their framework significantly improves data efficiency while reducing computational costs.
### update after rebuttal:
I thank the authors for their response and have taken into account the perspectives of the other reviewers. I will maintain my score, as it is already a positive one.
Claims And Evidence: The main claim of this paper is that the proposed synthetic data generation framework improves data efficiency and reduces computational costs. I believe this claim is well-supported by evidence presented in the paper. The authors conduct experiments on two widely used datasets and show that their dynamic, multi-round data generation approach successfully produces more informative training examples. The results demonstrate that their method can achieve comparable to static methods, but with significantly fewer training samples. Additionally, comparisons with other recent synthetic data generation techniques highlight the advantages of the proposed method over traditional generate-then-filter methods in terms of data efficiency and model performance.
Methods And Evaluation Criteria: I find the proposed method to be conceptually intuitive and practically applicable. The idea of iteratively refining the training data through entropy-guided sample selection is novel and well-motivated.
The evaluation criteria, including commonly used benchmarks and metrics, are reasonable for assessing the effectiveness of the proposed framework.
Theoretical Claims: The authors theoretically analyze in Section 4 how selecting difficult examples can improve the scaling laws of synthetic data. I have reviewed the proof and found it to be correct.
Experimental Designs Or Analyses: I find the experimental setup and analysis to be well-designed and thorough. In particular, I appreciate the authors' analysis in Section 5.4, where they examine the evolution of hard examples over time to highlight how difficult samples dynamically change during training.
Supplementary Material: I reviewed the appendix section of the paper.
Relation To Broader Scientific Literature: The key contribution of this paper—multi-round training with dynamically selected hard samples—fills an important gap in synthetic data research. Many existing works focus on generating large-scale datasets and designing filtering mechanisms to remove low-quality samples. In contrast, this paper suggests that instead of generating a massive dataset and filtering it later, one can directly generate selective samples by leveraging uncertainty in the generative model.
Essential References Not Discussed: The paper discusses enough related work.
Other Strengths And Weaknesses: Overall, I find the proposed method to be novel, and the experiments and analyses are well-conducted. One concern I have is that the authors do not provide any qualitative analysis of the generated hard samples. It would be beneficial to investigate whether the generated difficult samples are truly challenging, and whether they follow specific patterns that could offer more insights into the model’s learning process.
Other Comments Or Suggestions: N/A
Questions For Authors: Have you conducted any manual analysis of the generated hard samples?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their detailed and encouraging review. We’re glad to hear that you found the method to be conceptually intuitive, the theoretical analysis to be sound, and the experimental setup and evaluation thorough.
### **Qualitative Analysis of Hard Samples:**
Thank you for raising the point about qualitatively analyzing the generated hard samples. While we do include some visual examples in Figures 6 and 10, in response to your suggestion, we have conducted additional visual analysis available at this anonymous link (https://drive.google.com/file/d/1XbkVVsHDQyhfSJfqGkaFLC7Polb0dHZR/view) (can be access in incognito mode and requires no logging in):
In the newly added Figures 1 and 2, we start with a pool of examples and compare the following sampling setups visually:
1. Uniform random selection from the pool
2. High entropy selection from the pool
3. Directly generating high entropy samples with DP
We visually observe that:
1. Uniform selection does not change the distribution of the examples.
2. High-entropy selection results in some ambiguous or atypical examples, often featuring occlusions, rare viewpoints, complex backgrounds, or low-contrast textures; factors that increase classification uncertainty.
3. DP’s direct generation produces the most visually diverse and semantically rich set of samples. These include unusual lighting, texture variation, and sometimes near-failure cases; all of which challenge the model and encourage more robust learning.
Figure 3 compares the following setups visually:
1. Initial samples with no entropy-guidance
2. DP samples with entropy-guidance earlier during training
3. DP samples with entropy-guidance later during training
We observe that early-stage generations show mainly color diversity, while later stages exhibit a richer set of transformations, aligning with the classifier’s evolving uncertainties.
Figure 4 compares the following setups visually:
1. Random samples from the initial data at the beginning of training for the class ‘fox’
2. Random samples from the final accumulated data at the end of training.
The initial training data (visually) lacks diversity. By the end of training, the accumulated dataset contains progressively harder/diverse examples.
---
Thank you again for your thoughtful comments and for recognizing the contributions of this work. We hope the addition of qualitative examples will further strengthen the final version. If there's anything in particular that’s holding you back from potentially increasing your score, we’d really appreciate hearing about it. We're happy to clarify or address any remaining concerns. | Summary: This paper empirically demonstrates that "delibrate practice" is meaningful in improving the scaling law of synthetic data generation. Broadly speaking, this falls under the general umbrella of efficiently collecting as few data as possible, with the additional problem context being, a generative model is used in generating the data to be collected. Though delibrate practice was a notion related to "curiosity" and has been explored in the past, this work empirically re-examined such use in the above said context. What's encouraging is, this work presents a scaling law, not just a few case studies.
Claims And Evidence: They are fine.
Methods And Evaluation Criteria: They are fine.
Theoretical Claims: They are fine.
Experimental Designs Or Analyses: They are fine.
Supplementary Material: No
Relation To Broader Scientific Literature: This paper empirically demonstrates that "delibrate practice" is meaningful in improving the scaling law of synthetic data generation. Broadly speaking, this falls under the general umbrella of efficiently collecting as few data as possible, with the additional problem context being, a generative model is used in generating the data to be collected. Though delibrate practice was a notion related to "curiosity" and has been explored in the past, this work empirically re-examined such use in the above said context.
Essential References Not Discussed: I didn't check
Other Strengths And Weaknesses: I am not sure that novelty is high enough.
Other Comments Or Suggestions: No
Questions For Authors: No
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: Thank you for your review.
The concept of "deliberate practice" has indeed been borrowed from psychology and has thematic connections to "curiosity". However, to the best of our knowledge, we are the first to adapt and implement this principle in the setting of training classifiers entirely on synthetic data generated from diffusion models. Rather than generating a large static dataset or pruning post hoc, we propose a dynamic approach that modifies the generative process itself to prioritize informative, high-entropy examples.
Our work goes beyond showing isolated gains, it demonstrates that deliberate practice shifts the scaling laws of training with synthetic data, enabling significantly better performance with fewer generated examples.
---
We were puzzled by the low overall rating, especially given that the review doesn’t raise specific methodological, theoretical, or experimental concerns. If there are particular issues we may have missed, we’d be happy to address them. Otherwise, if the current score was entered in error, we would be grateful if you would consider updating it.
---
Rebuttal Comment 1.1:
Comment: The term "deliberate practice" sounded new, but the concept is not, similar concepts had been applied for decades, for fairly unimpressive results if generalization is the goal. More recently, even in the area of LLM, similar concepts have been applied to understand cirriculum training and to arrange the order of training data, again for fairly unimpressive results judging from published materials. To this reviewer, the "novel idea" statement is an over claim.
I agree that this work could be the first to "adapt and implement this principle in the setting of training classifiers entirely on synthetic data generated from diffusion models", which is a good thing. But while "being first" may be good for, say, CVPR, merely being first in my opinion falls short of the level of excellence required by the top 3 prestigeous AI conferences.
The above are my reasons for low scores.
Below is a divergence of experimental results from my expectation, but I don't have any reason to doubt the authors of doing things wrong, so below are not my reasons for low scores, they are my questions to the authors that I didn't pose in previous rounds.
For people making LLM it was natural to expect that training more on high perplexity materials would lead to better performance. However, observation was the opposite; training too much on such data could lead to bad results. LLM practitioners still follow the rule of thumb of taking a blend of like 20% very low perplexity material, 60% intermediate perplexity material, and 20% high perplexity material, in a batch, to stablize training. Is there something like that in the experiments?
---
Reply to Comment 1.1.1:
Comment: Thank you for your follow-up and for taking the time to expand on your reasoning. We appreciate the opportunity to clarify the contributions of our work and address what appear to be significant misunderstandings.
### **Misrepresentation of the Contribution**
We are concerned that the review mischaracterizes the novelty and core focus of our work. We want to make it explicitly clear that: We do not claim that the idea of "deliberate practice" is new. The novelty lies in how we operationalize this high-level principle for training image classifiers entirely on synthetic data, generated from a diffusion model and guided dynamically by the learner’s own uncertainty. This is not a minor reapplication of an old idea.
Our method:
- Works with no access to real training image data.
- Uses generation of synthetic data, not selection from a static pool.
- Lets the learner update its notion of difficulty throughout training.
- Leads to clear improvements over vanilla sampling in scaling behavior, as shown in our experiments.
These contributions are grounded in theory and empirically validated across two datasets.
### **On LLM Parallels**
In this work DP was explicitly developed for image classification. We caution against drawing direct parallels with prior LLM training strategies without careful grounding on the setup and the tasks studied. Therefore, while we appreciate the analogy, we believe that comparing prior heuristics from LLM training without rigorous validation in the vision domain could be misleading.
We believe that adapting our dynamic data generation framework to LLMs could be an interesting direction for future work. But using results from prior LLM training heuristics to cast doubt on our method in a vision setting is, in our view, an invalid comparison and not a sound basis for evaluation.
### **Missing Key Parts of the Paper**
We are also concerned that key parts of the paper appear to have been overlooked. In particular, the reviewer's question about the perplexity distribution in LLMs suggests that the reviewer assumes that we simply sample hard examples and train on them. That is not the case. In fact, a major focus of our analysis is to understand **how the notion of difficulty evolves as training progresses** and we have an adaptive method for this very reason. We studied the error of generated samples at different stages of training and found that: hardness is not static, it evolves throughout training and DP adapts its sampling accordingly. Also, see Figure 4 where we show that if we use a very high DP coefficient, we observe lower returns in terms of the accuracy. So very hard examples do lead to lower performance.
For more details, see Sections 5.3 and 5.4 about your question in the context of learning image classifiers.
### **Final Remarks**
We respect your time, but we must express that this review does not reflect a fair or careful engagement with our work. We stand by the contribution: a simple, effective, and empirically validated method for dynamic synthetic data generation, built on well-established intuitions but delivering novel results and insights. We strongly encourage a more careful reading of the paper and a reconsideration of the score in light of the clarifications above. | Summary: The authors introduce a new methodology called "Deliberate Practice for Synthetic Data Generation" (abbreviated DP) to train a machine learning model for classification using entirely synthetic samples generated from a pre-trained diffusion model. Instead of generating many samples and pruning, the method uses an additive correction to the score to prioritize samples which are most challenging for the model; this correction is updated dynamically during training and is based on the entropy of the model on the sample at the time where the data is generated. The authors justify their approach of selecting difficult examples via theory for high-dimensional linear regression. Then, they perform some experiments: (1) comparing DP to another ("static") approach of pre-generating all data and training on a fixed synthetic dataset; (2) comparing DP to previous methods [1, 2]; (3) comparing DP to another ("pruning") approach of pre-generating data and then pruning via model entropy; (4) answering the scientific question of whether models trained with DP change their (entropy-based) difficulty estimates over the training trajectory. For experiments (1)-(3) the DP method generally performs uniformly better than the chosen alternatives; for experiment (4) it confirms that models trained with DP indeed change the difficulty estimates.
[1] Sarıyıldız, M. B., Alahari, K., Larlus, D., and Kalantidis, Y. Fake it till you make it: Learning transferable representations from synthetic imagenet clones. In CVPR, 2023.
[2] Fan, L., Chen, K., Krishnan, D., Katabi, D., Isola, P., and Tian, Y. Scaling laws of synthetic images for model
training... for now. In CVPR, 2024.
## Update After Rebuttal
The rebuttal clarified the theoretical/conceptual points I had raised. Because of that, I think the work is a good contribution and should be accepted. The other point I raised (which seems to be echoed by the other reviewers) is that the experimental section's scope is a little lacking; I had expected more datasets/diffusion models in order to verify the scientific claims, while other reviewers comment on specific evaluations and comparisons to other work. Still, the experimental results seem overall reasonable to me. For that reason I recommend acceptance.
Claims And Evidence: There are several claims being made in the paper:
(1) the asymptotics of the test error of the toy linear regression setup in Section 4;
(2) the advantage of DP (in the classification setting) over more trivial methods for synthetic data generation like "pruning" and "static" approach;
(3) the advantage of DP (in the classification setting) over previously proposed methods for synthetic data generation;
(4) the claim that the same sample may be considered more or less difficult by a model over the DP training.
Of these, (1) is a mathematical claim and it seems adequately backed up via proofs in the Appendix A. (2) and (3) are empirical claims about method performance, and hold on the provided testbed (trained on varying number of samples generated from the same diffusion model LDM-1.5, and evaluated on subsets of ImageNet 1K). Still, in order to back up the more general claims it may help to generate from different diffusion models and evaluate on different datasets. (4) is a scientific claim and straightforwardly backed up.
Methods And Evaluation Criteria: The methods are: training using DP (or other methods) on samples generated from a single diffusion model LDM-1.5 (except for a small ablation in the appendix) and evaluated on different subsets of ImageNet-1K. These methods and evaluations make sense and are standard, though (as remarked above) to truly back up the claims, it might help to use more evidence using different generative models (especially since LDM-1.5 was picked specifically because DP performs best with it relative to the other tested generative models) and/or different evaluation testbeds.
Theoretical Claims: While I did not carefully check the proofs extremely carefully, they seem to be valid (and there is experimental evidence on toy datasets to confirm their correctness). A minor issue is that in Theorem A.1 it's not specified in which order the limits $\lambda \to 0$ and $n, d \to \infty$ with $d/n \to \phi$ are taken.
Some slightly larger problems with the theoretical component of this work are:
1) The rate in Theorem 1 the main body is not very "clean"; when I look at the rate I have no idea what order of magnitude I expect for the test error. It could be possible to work it out using asymptotic expansions of $\Phi$ and the other terms, but it would be very helpful to understand the rate approximately in the main body (while keeping the more complicated part for the appendix, of course), and it could help make some qualitative insights very straightforward.
2) The use of the proportional scaling regime for linear regression is slightly un-natural (to me); in the experiments you're only scaling data, not dimension, and so it might make sense to consider fixed $d$ and large $n$. What kinds of asymptotics are achieved there? Are they interesting? It would be useful to comment.
3) More generally, the linear regression problem in Section 4 is a toy problem, and the practice uses cross-entropy losses and measures the difficulty totally differently from the sign-of-inner-product way that's given in Section 4. (Of course, the real data isn't generated by a Gaussian and linear classifier either.) While I appreciate the considerable difficulty of expanding the analysis to this more practical setting, these differences should be remarked.
These may cause the (considerable) difference between real and predicted accuracy in Figure 4 (c) --- it would be helpful to comment on that and bring the theory a little closer to practice.
Experimental Designs Or Analyses: The experimental designs and mechanisms (including things like hyperparameters) seem well-described to me; while many details (and ablations, etc.), are not in the main body, they are in Appendix B. The analysis of the above experiments in Section 5 and Appendix B also seems sound.
Supplementary Material: I reviewed the supplementary material; I did not check the proofs in Appendix A carefully but read much of the exposition, and I read through Appendix B carefully.
Relation To Broader Scientific Literature: This paper broadly intersects with two different areas:
- Synthetic data and its use to train neural networks (and associated with challenges such as model collapse, bias of the generator, etc).
- Conditional diffusion models (for generating the synthetic data in this work).
- Active learning and continual learning (which also involve tailoring data to improve learning trajectory).
- High-dimensional statistics (corresponding to the theory component.)
Essential References Not Discussed: I don't know any significant omitted references.
Other Strengths And Weaknesses: - The main strengths are the improvement of DP over previous methods, as well as its simplicity.
- The main weaknesses are the lack of diversity in experimental setups (discussed previously), and the lack of connection between the theory and practice, which operate in two different regimes (classification vs regression, proportional scaling vs not, etc) and so it is unclear what messages or guidance to take from the theoretical part.
Other Comments Or Suggestions: Some nitpicks:
- In equation (5) I think there should be a $(t)$ superscript for all model uses.
- Section 3 title: "Deliberate" should be capitalized.
- The paragraph titles have inconsistent formatting; some are capitalized ("Asymptotic Behavior of the Test Error") while most aren't.
- Some Typos in Appendix B, such as the section title "Additional Experimental".
Questions For Authors: No questions at this time.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for the detailed feedback. We're glad that you found the method conceptually clear. Also, thank you for the helpful proofreading suggestions. We will incorporate these corrections in the final version.
---
**Connection Between Theory and Practice:** We agree that the linear regression setup in Section 4 is a simplified version of the full setup used in practice. The goal of this section is not to precisely model the real-world setting, but to isolate and analyze the principle of prioritizing difficult examples based on entropy or uncertainty. We will include a short discussion highlighting the limitations and interpretability benefits of the theoretical analysis in the simple setup. Also, note that even though loss used in training the linear model is regression loss (squared L2), the learned model is used as a classifier and we analyze classification accuracy (see Section 4). The use of linear classifiers fitted with squared loss is common in ML theory (Couillet & Liao, 2022; Liao & Mahoney, 2021; Firdoussi et al., 2024).
**Unpacking Theorem 1.** The point of the theorem is to showcase that the test error can be written analytically as a function all problem parameters: parametrization rate $\phi$, regularization parameter $\lambda$, pruning ratio $p \in (0,1)$, cosine of angle between the pruning direction and the ground-truth labelling function $\rho$, etc. Analytic expression provided is defined via concrete functions like $\Phi$, and the spectral functions (linked to Marchenko-Pastur Law) introduced earlier and can be used to numerically compute / simulate the shape of the theoretical error curve in different regimes corresponding to different settings of the problem parameters. We agree with the reviewer that expanding the Phi function can provide some quantitative insights, at least in setting regimes of its argument, especially: large +ve, large -ve, and small values.
Finally, note that in the unregularized (ridgeless) case $\lambda \to 0^+$, the aforementioned analytic expression simplifies drastically, as shown in Corollary 1 (Appendix).
In Appendix A.1, the order of the limits is: first let $d,n \to \infty$ such that $d/n \to \phi$. Then, let $\lambda \to 0^+$.
**Proportional scaling in linear regression.** This is actually standard in high-dimensional statistics and learning theory. Here, such a scaling allows us to capture important regimes: interpolation threshold (corresponding to $\phi=p$), under-parametrized (phi < p), over-parametrized ($\phi > p$), extreme under-parametrized ($phi \to 0^+$), extreme over-parametrized ($\phi \to \infty$) regimes while keeping the analysis tractable (via the tools of random matrix theory).
The reviewer’s statement that we are “only scaling data” is inaccurate. Observe that $d,n \to \infty$ such that $d/n\to \phi$ can be equivalently written as $n = \phi d$ (rounded to an integer), $d \to \infty$. Therefore, we can fix $d$ to a large value and study the effect of $\phi$, as done in the experiments. Other large values of $d$ would yield a similar experimental picture. Everything about scale is completely captured in the $\phi$ parameter. We shall make this clearer in the manuscript.
---
### **Experimental Diversity:**
We appreciate your suggestion to evaluate DP across a broader range of generative models and datasets. While we included comparisons in Appendix B.1 using other diffusion models, and have already reported results on two datasets (ImageNet-100 and ImageNet-1K) we acknowledge that this could have been more clearly emphasized in the main paper. We will revise the manuscript to better highlight the diversity already present in our evaluation.
We also want to clarify that LDM-1.5 was **not chosen because DP performs best with it**. Rather, we selected it because it consistently provides the strongest baseline performance in static data generation setups, independent of DP (as shown in Appendix B.1). This makes it a compelling and fair testbed. This model choice is in-line with prior work (e.g., Astolfi et al., 2024 and Fan et al., 2024), which uses LDM-1.5 as it produces more diverse samples than alternatives which is a desirable property when training classifiers on synthetic data.
More broadly, we do not expect DP to be limited to a particular diffusion model or sampling strategy. Our approach is a lightweight modification of the sampling process, similar in spirit to classifier guidance, that leverages the model's entropy to influence which samples to be generated. As long as the sampler provides an approximation of the denoised sample x_0, DP can be applied by using the downstream classifier to adjust the sampling trajectory. We will clarify this generality in the revised version.
---
Thank you again for your constructive comments. If there's anything in particular that’s holding you back from potentially increasing your score, let us know.
---
Rebuttal Comment 1.1:
Comment: Thanks for clarifying the following.
> The purpose of the theory
This point now makes sense to me. There is learning theory work with the cross-entropy loss (e.g. [1]), but I acknowledge it (maybe significantly) increases the difficulty of the analysis. While it would have been great if the work were actually extended to this setting, even the current simplified setting seems to capture good insights.
> The proportional scaling regime
This point also makes sense to me, thank you for clarifying. You may want to put this explanation in the camera-ready version, as I found it a very nice and clean justification.
> Other theoretical details
Thanks for the various clarifications on the order of the limits and the asymptotic order of the test error; I would really encourage these to be put in the camera-ready version of the paper.
> The experimental diversity and choice of data/samplers for synthetic data
Here I know that the previous work uses LDM-1.5 (and thank you for clarifying why it is picked in this paper, I originally thought that Appendix B.1 used Deliberate Practice to compare the models). However, the claim made in the paper and in the rebuttal is that Deliberate Practice generalizes to different classification datasets (e.g., in the paper ImageNet-100 and ImageNet-1K) and diffusion models. In principle this is obviously true --- the proposed method does not specify any required number of classes nor requires a specific diffusion model, so there is no concrete obstruction to applying Deliberate Practice using any model and classification dataset. But to demonstrate the claimed generalization in practice, I would have expected a greater diversity of evaluations across different datasets and models.
Note that the evaluated data is all subsets of ImageNet-1K and evaluated models are all within the LDM model family. Also, the comparison between diffusion models in Appendix B.1 aren't about Deliberate Practice but on another proxy task which seems to measure the diversity/prompt adherence of the samples. So it does not seem to me to be really sufficient to demonstrate the efficacy of Deliberate Practice using different diffusion models.
As a result of the latter point, I keep my score.
[1] Wu, Jingfeng, Vladimir Braverman, and Jason D. Lee. "Implicit bias of gradient descent for logistic regression at the edge of stability." Advances in Neural Information Processing Systems 36 (2023): 74229-74256.
---
Reply to Comment 1.1.1:
Comment: Thank you for your reply! We appreciate your positive assessment and your thoughtful engagement with both the paper and our clarifications. We're glad the theoretical points now make sense, and we will be sure to include those clarifications in the camera-ready version.
We’d like to add one final clarification regarding the results in Appendix B.1. The comparison there does not measure the diversity or prompt adherence of the generated samples. Instead, it reports the validation accuracy of four different classification models, each trained on synthetic data generated by a specific LDM variant. This experiment serves to validate that our choice of generative model (LDM-1.5) is fair and appropriate for the task of image classification.
As mentioned earlier, we do not expect Deliberate Practice to fail on any of the generative models evaluated. Since DP only modifies the DDIM sampling process, and that process is applicable across all of these diffusion models, the method is fully compatible and should retain its benefits.
While we acknowledge that additional datasets and model families would further strengthen the generalization claims, we hope this clarifies the rationale behind our current setup and supports the fairness of the experimental evaluation. | Summary: This work addresses the challenge of improving data size scaling laws for models trained on synthetic data. In particular, it uses the intuitive idea of generating more synthetic data where the model being trained (referred to as the learner) has high entropy. To do so, the paper relies on a setting where the synthetic data is generated using a 'Denoising Diffusion Implicit Models' & modifying the generation to prefer samples where the learner has high entropy. This approach is illustrated to work in a toy theoretical setting as well as through real-world experiments on IN-100 & IN-1K.
Claims And Evidence: Yes.
1. The claim of the proposed sampling scheme modifying the sampling distribution is supported by the steps illustrated in equations 3-6.
2. The claim of this approach improving scaling laws is evidenced by the experiments on ImageNet.
3. The toy theoretical example serves to further illustrate this point.
Methods And Evaluation Criteria: Yes, I believe the datasets & baselines used for this method are fair & comparing to SOTA.
Theoretical Claims: Yes, I checked the theorem in the main paper and this looks correct.
Experimental Designs Or Analyses: Yes, this is sound.
Supplementary Material: No, I did not.
Relation To Broader Scientific Literature: I think this is a useful practical tool in the training of image models using synthetic data. The idea & implementation of modifying a diffusion model to generate examples in high-entropy regions for a classifier being trained is extremely intuitive, simple & effective.
Essential References Not Discussed: I believe there should be an inclusion of references to earlier works on data pruning including, but not limited to:
- Coleman, Cody, et al. "Selection via proxy: Efficient data selection for deep learning." arXiv preprint arXiv:1906.11829 (2019).
- Mindermann, Sören, et al. "Prioritized training on points that are learnable, worth learning, and not yet learnt." International Conference on Machine Learning. PMLR, 2022.
- Pooladzandi, Omead, David Davini, and Baharan Mirzasoleiman. "Adaptive second order coresets for data-efficient machine learning." International Conference on Machine Learning. PMLR, 2022.
- Yang, Yu, Hao Kang, and Baharan Mirzasoleiman. "Towards sustainable learning: Coresets for data-efficient deep learning." International Conference on Machine Learning. PMLR, 2023.
- Joshi, Siddharth, et al. "Data-efficient contrastive language-image pretraining: Prioritizing data quality over quantity." International Conference on Artificial Intelligence and Statistics. PMLR, 2024.
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: I think the paper could benefit from a more detailed background section on DDIM. Personally, since I was not familiar with this, I had to refer prior work to understand this, before I could fully understand the paper & it would be better if the paper could be read in a self-contained manner.
Questions For Authors: Have the authors considered a similar idea for training language models? Do they have any initial thoughts on how such an approach would be extended to that setting?
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: Thank you for the thoughtful and encouraging review, we are very pleased that you found the paper intuitive, practical, and effective.
### **Related Work and Data Pruning:**
Thanks for pointing out these relevant papers. While our method focuses on improving training via generation of informative synthetic data rather than selection or pruning of real data, both lines of work share the goal of increasing data efficiency by concentrating training on examples that contribute most to learning. In particular, works like Coleman et al. (2019) and Mindermann et al. (2022) develop data selection strategies based on proxies for example utility, such as gradient norms or learnability. Similarly, Pooladzandi et al. (2022) and Yang et al. (2023) propose coreset-based methods that aim to retain the most informative or representative points. Joshi et al. (2024) further emphasize the importance of data quality over quantity, which aligns closely with our motivation, though we operationalize this through generative modeling and entropy feedback rather than dataset filtering as discussed in Sec 5.3. We view our approach as complementary: instead of selecting from a fixed pool of data, we dynamically generate examples in regions where the model exhibits high uncertainty, effectively synthesizing the types of data these methods might prioritize. We will include this discussion in the revised related work section.
### **DDIM Background:**
We agree that the paper would benefit from a more complete and self-contained explanation of DDIM. Due to space constraints, we had to keep the background section concise, but we will expand it in the final version. We also want to clarify that while our experiments use DDIM, the proposed method is not limited to this specific sampler. Our approach relies on accessing an approximation of the denoised sample x_0 at each step, which is also available in other diffusion samplers such as DDPM and its variants. As long as the sampler provides a usable x_0 estimate, the entropy-guided feedback mechanism remains cheap and can be applied efficiently. We will emphasize this more clearly in the revised version.
### **Language Model Extension:**
This is a very relevant direction which we have been pondering about. While our current work focuses on image generative models, the principle of DP can be extended to language. One key reason this approach works efficiently with diffusion models is that we have access to an approximation of the clean sample x_0 at each step, which enables us **to steer the sampling process before the generation ends**. This intermediate visibility during generation allows us to influence the generation process. Extending this idea to autoregressive language models is less straightforward since generation typically proceeds token-by-token with limited ability to revise earlier outputs. However, the emergence of language diffusion models opens up a promising path [1]. These models offer a latent trajectory similar to image diffusion models and may allow for entropy-guided sampling. We see this as a compelling direction for future work and are actively thinking about how DP could be incorporated into language diffusion models for synthetic data training.
[1] Nie, Shen, et al. "Large Language Diffusion Models." arXiv preprint arXiv:2502.09992 (2025).
We are very open to further discussion and would be happy to address any other questions.
---
Rebuttal Comment 1.1:
Comment: I continue to strongly recommend this paper for acceptance.
---
Reply to Comment 1.1.1:
Comment: Thank you for your continued support and for the thoughtful feedback throughout the review process. We appreciate your recommendation and are pleased that you found the work valuable. | null | null | null | null |
Understanding Nonlinear Implicit Bias via Region Counts in Input Space | Accept (poster) | Summary: The paper proposes a new region count metric for characterizing neural networks' implicit biases. This metric counts the number of connected regions in the input space with the same predicted label in a low-dimensional subspace. One of the advantages of this output-based metric over parameter-based metrics, such as sharpness and margins, is parametrization-independence. The authors empirically demonstrate that this metric strongly correlates with the generalization gap over a variety of convolutional architectures, datasets, and hyperparameters, making it suitable for the generalization analysis. Then, the authors experimentally show that region count decreases with an increased learning rate and a smaller batch size. The authors suggest a theoretical explanation for the learning rate behavior based on the edge of stability property of gradient-based algorithms.
## update after rebuttal
I will keep my current evaluation. The authors' feedback was useful, but it did not completely clarify my concerns expressed in my Rebuttal Comment.
Claims And Evidence: 1. While the authors claim that their low-dimensional subspace region count metric is more computationally efficient than the whole space region count metric, I still feel that the region count metric is hard to analyze. For instance, while the sharpness metric directly motivates possible regularization methods, such as sharpness-aware minimization, I do not easily see how to use the region count metric for computationally efficient regularization. Moreover, while the authors manage to analyze the 1D-version region counts theoretically, I do not see how to extend this analysis to multi-dimensional region counts.
2. Parametrization independence is indeed one of the main properties of the region count metric. However, I think the authors should also discuss situations where parametrization independence is indeed important. As I see it, the main advantage of parametrization-independent metrics is the ability to predict generalization performance conditional only on the final model and training data. At the same time, parametrization-dependent metrics might also potentially predict generalization performance, but they require more information, e.g., the final model, training samples, and optimizer hyper-parameters. In this sense, one could argue that parametrization-independent metrics are better suited for the generalization analysis. However, for me, it is not clear which metric is better suited for the design of regularizers since the effect of regularizers implicitly depends on all training hyper-parameters.
3. The high correlation with the generalization gap is a strong piece of evidence of the region counts metric usefulness. However, I see two potential problems with this finding.
* First, from what I see, the dependence between the region counts and the generalization gap is non-linear. Specifically, the slope is increasing for the smaller region counts. Thus, the "outlier" models with a big generalization gap could cause a high correlation coefficient. If this is the case, the region counts metric could only distinguish between "very good" and "very bad" models but could not distinguish between "very good" and "good" models. Therefore, it could be interesting to conduct some experiments across "good" models, for example, in a situation where the learning rate and batch size are fixed, and weight decay is varied over a relatively tight range of values.
* Second, the results for augmentations show that the relation between the region counts and the generalization gap significantly depends on the training algorithm. This fact limits the applicability of the region counts metric for the generalization analysis since it suggests that the region count metric is ill-suited for analyzing how the introduction of augmentations affects generalization performance.
Methods And Evaluation Criteria: The proposed evaluation is comprehensive. However, the authors should clarify that they only test convolutional architectures on vision datasets.
Theoretical Claims: Theoretical claims seem correct.
Experimental Designs Or Analyses: The experimental design seems correct. I have minor comments. Given that the relation between the region counts metric and the generalization gap could be non-linear, it could be worth also reporting rank-correlation. Additionally, I would be interested in the regression analysis where the generalization gap is regressed on all discussed implicit bias metrics: sharpness, margins, normalized margins, 1D region counts, and 2D region counts. It would be interesting to compare the explanatory power of these metrics in terms of $R^2$.
Supplementary Material: I have briefly examined the experiment details and ablation studies sections, read how region counts were calculated, and checked the proof of Theorem 6.3.
Relation To Broader Scientific Literature: The paper is directly related to the deep network generalization literature. Specifically, the authors propose a new non-linearity-aware metric that could be useful for analyzing the generalization gap.
Essential References Not Discussed: I think all essential references are mentioned. However, I would like to see more comparisons with the literature on large learning rates. Specifically, I would like the authors to discuss the differences in mechanisms considered in their paper in the papers by Li et al. (2019) and Lewkowycz et al. (2020).
**References**
Li, Y., Wei, C., & Ma, T. (2019). Towards explaining the regularization effect of initial large learning rate in training neural networks. Advances in neural information processing systems, 32.
Lewkowycz, A., Bahri, Y., Dyer, E., Sohl-Dickstein, J., & Gur-Ari, G. (2020). The large learning rate phase of deep learning: the catapult mechanism. arXiv preprint arXiv:2003.02218.
Other Strengths And Weaknesses: I think the paper is well-written, and the proofs are presented clearly. The proposed metric seems original, but it was inspired by the previous studies of activation patterns.
Other Comments Or Suggestions: I do not have any.
Questions For Authors: 1. Could you clarify the types of hyperparameters for which your metric is well-suited (e.g., learning rate) and ill-suited (e.g., augmentations)?
2. For which types of analysis or applications is the parametrization-independence of your metric important?
3. Do you think that your metric is well-suited for both big and small generalization gaps? What are the limitations of your metric?
4. Can you give a practical application of your metric (e.g., for the design of regularizers)?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the time spent on reviewing our work and for the very detailed comments. Please find the details below.
>Q1: How to use the region count metric for regularization?
**A1:** Due to the word limit, we respectully refer the reviewer to Reviewer VXuC's response A2.
>Q2: How to extend the theorem to multi-dimensional region counts?
**A2:** The choice of one-dimensional region count is primarily for technical simplicity. The core idea of the proof is that the region count can be upper bounded by the number of activation pattern changes. This holds regardless of the hyperplane’s dimensionality, probably with a different dependency in the exponent. This observation suggests a natural direction for extending the analysis to the multi-dimensional case, which we leave for future work.
>Q3: For which types of analysis is the parametrization-independence of your metric important?
**A3:** Our primary goal is to develop a metric that characterizes the implicit bias of nonlinear neural networks. Since we focus on understanding the solutions the network converges to rather than how it is trained, a parametrization-independent metric is essential for properly capturing this implicit bias.
>Q4: Conduct experiments to find whether region count can distinguish between "very good" and "good" models.
**A4:** We fixed the learning rate at 0.1 and batch size at 256, and varied only the weight decay to compute the correlation.
|Parameter|Value|
|:----:|:----:|
|Weight Decay|5e-4,1e-4,5e-5,1e-5,5e-6,1e-6,5e-7,1e-7|
The correlation plot is shown in Figure 3 of https://anonymous.4open.science/r/icml-rebuttal-B813/icml%202025%20rebuttal.pdf. The generalization gaps **range from 17 to 20, and the region counts range from 2.5 to 3, making them relatively close**. We observe a correlation of 0.84, indicating that even under strong generalization settings (small learning rate, large batch size), our region count metric can effectively distinguish between "very good" and "good" models.
>Q5: Clarify the hyperparameters for which your metric is well-suited/ill-suited.
**A5:** As shown in Figures 6 and 7, our metric maintains a strong correlation under mixup augmentation. This **aligns with mixup’s implicit effect of reducing region count by enforcing smooth label transitions**, which may partly explain its performance benefits. For random crops and flips, high correlation is observed when evaluated separately. However, pre-crop and post-crop data are not directly comparable, as cropping fundamentally changes the data distribution. Such cases are better treated as distinct distributions rather than as hyperparameter variations.
>Q6: Reporting rank-correlation.
**A6:** We add experiments reporting the rank correlation[3]. All networks are trained on CIFAR-10 using the hyperparameters in Table 1. The results are as follows:
|Network|Correlation|
|:----:|:----:|
|Resnet18|0.95|
|Resnet34|0.94|
|VGG19|0.74|
|MobileNet|0.98|
|SENet18|0.96|
|ShuffleNetV2|0.99|
|EfficientNetB0|0.97|
|RegNetX 200MF|0.98|
|SimpleDLA|0.86|
These results show consistently high rank correlation, further validating the effectiveness of our metric.
>Q7: Do regression analysis where the generalization gap is regressed on all metrics.
**A7:** We train ResNet18 on CIFAR-10 and conduct regression analysis using five metrics:sharpness, margin, normalized margin, 1D region count, and 2D region count. We compute the $R^2$ values. The results are as follows:
|Measure|$R^2$|
|:----:|:----:|
|All|**0.96**|
|Margin|0.41|
|Normalized Margin|0.03|
|Sharpness|0.61|
|1d Region Count|0.94|
|2d Region Count|0.92|
Both our proposed 1D and 2D region count metrics achieve high $R^2$ values, **nearly matches the overall $R^2$**, demonstrating strong predictive power for the generalization gap compared to existing measures.
>Q8: Discuss the paper [1][2].
**A8:** [1] attributes the generalization difference to the learning order of examples: large learning rates delay fitting hard-to-fit but generalizable patterns until after annealing, while small learning rates prioritize them early. [2] proposes a phase-based view of training dynamics, where large learning rates in the “catapult” phase reduce curvature and lead to flatter minima. In contrast, our paper offers a new perspective: large learning rates improve generalization by reducing the number of region counts. We will include a discussion of [1][2] in the next version.
We thank the reviewer once again for the valuable suggestions.
**References**
[1] Li, Yuanzhi, Colin Wei, and Tengyu Ma. "Towards explaining the regularization effect of initial large learning rate in training neural networks." Advances in neural information processing systems 32 (2019).
[2] Lewkowycz, Aitor, et al. "The large learning rate phase of deep learning: the catapult mechanism." arXiv preprint arXiv:2003.02218 (2020).
[3] Kendall, Maurice G. "A new measure of rank correlation." Biometrika 30.1-2 (1938): 81-93.
---
Rebuttal Comment 1.1:
Comment: Thanks for the response!
The authors answered almost all of my questions. However, currently, I am inclined to keep my score.
1. While I understand that the question of the suitability of the metric for different hyperparameters is challenging to answer, I still do not understand the limits of the metric's applicability. Indeed, Figures 6 and 7 demonstrate a high correlation, but the points for different augmentations lie on different lines, which suggests that the metric does not capture some additional generalization mechanisms. The current response suggests that the metric is not applicable for different data distributions; however, all augmentations could be reformulated as changes in data distributions, which suggests that the metric is only directly applicable for the analysis of optimizer hyperparameters.
2. While I understand the intuitive connection between the mixup and the region counts, the previous point suggests that formally justifying such a connection would be difficult since the mixup inherently changes the distribution.
3. While the authors claim that the theoretical extension of their results to multi-dimensional region counts is possible, I am still not convinced by their argument. Indeed, one only needs to bound the number of activation changes; however, analyzing activation changes is more challenging in a multi-dimensional environment. Moreover, the current theoretical analysis exploits sharpness to derive the bound, which does not allow the authors to theoretically justify the advantages of region counts over sharpness.
4. (minor) I think comparing the explanatory power of margin, normalized margin, and sharpness together against 1D region counts would be interesting. If the explanatory power of 1D region counts is higher, it would indicate that the region counts capture a completely new generalization mechanism compared to margins and sharpness.
---
Reply to Comment 1.1.1:
Comment: Thank you for your timely and detailed feedback!
Regarding the first and second point, if we merge the points from the two curves of mixup and calculate the correlation, we also obtain a value of 0.97. Therefore, our method is applicable to mixup. For random crop and random flip, we compute the correlation on all merged data and achieve a value of 0.91. The corresponding correlation plots can be found in https://anonymous.4open.science/r/icml-rebuttal-B813/follow%20up.pdf.
We acknowledge that in some specific cases—e.g., comparing results with and without random crop—region counts may both be around 3.0, while the generalization gap differs significantly (ranging from 13 to 22). However, we would like to emphasize that in the case of random crop and random flip, the change in data distribution is more substantial (unlike mixup, which results in smoother changes). We believe that achieving invariance to different data distributions is a more challenging goal because analyses of the generalization gap are largely dependent on the data distribution, as demonstrated in prior work on uniform convergence [1][2] and benign overfitting [3][4][5].
For the third point, we can not provide a complete proof of the theoretical analysis in higher dimensions at this stage, and we will consider it as part of future directions. Table 2 in our paper demonstrates that region counts in higher dimensions maintain a relatively high correlation, which experimentally supports this idea. We acknowledge that our theoretical analysis rely on sharpness-related assumptions. **While sharpness can imply a low region count, the reverse does not necessarily hold**. Our empirical results show that region count has a much stronger correlation with the generalization gap than sharpness. This suggests that **sharpness may reduce generalization error by inducing a low region count**, and that region count may provide a more general and intrinsic explantion for generalization performance.
Regarding the last point, we have added additional experiments that investigate the regression from margin, normalized margin, and sharpness to region count. The results show poor regression performance (with $R^2$ around 0.65), indicating that these metrics cannot fully represent region count. This suggests that region count captures a distinct generalization mechanism compared to margins and sharpness.
**References**
[1] Bartlett, Peter L., Dylan J. Foster, and Matus J. Telgarsky. "Spectrally-normalized margin bounds for neural networks." Advances in neural information processing systems 30 (2017).
[2] Zhou, Lijia, Danica J. Sutherland, and Nati Srebro. "On uniform convergence and low-norm interpolation learning." Advances in Neural Information Processing Systems 33 (2020): 6867-6877.
[3] Bartlett, Peter L., et al. "Benign overfitting in linear regression." Proceedings of the National Academy of Sciences 117.48 (2020): 30063-30070.
[4] Zou, Difan, et al. "Benign overfitting of constant-stepsize sgd for linear regression." Conference on Learning Theory. PMLR, 2021.
[5] Tsigler, Alexander, and Peter L. Bartlett. "Benign overfitting in ridge regression." Journal of Machine Learning Research 24.123 (2023): 1-76. | Summary: This paper introduces the notion of connected region count in the input space and shows that it is strongly correlated with the generalization gap. Moreover, it is noted that larger learning rates and smaller batch sizes can lead to smaller region counts. Theoretically, It is proved that for a two-layer ReLU network under the edge-of-stability assumption, the average region count is bounded by O(1/learning rate).
## update after rebuttal
Thanks for your response! I will keep my score.
Claims And Evidence: The claims are well-supported in general; see more discussion below on the empirical results.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: I didn't check the proofs.
Experimental Designs Or Analyses: The empirical results look convincing overall: CIFAR-10, CIFAR-100 and ImageNet are tried, and multiple network architectures are tested. Data augmentation techniques such as mixup are also analyzed. One concern is that the discussion is focused on vision datasets and convolutional networks; it would be nice if more datasets and architectures can be analyzed.
Supplementary Material: No.
Relation To Broader Scientific Literature: This paper introduces the notion of connected region count and shows that it is strongly correlated with the generalization gap. As far as I know no prior work has shown the relationship between region count and generalization, so I believe this is a nice contribution.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: N/A
Questions For Authors: If we calculate the expected 1D region count between two random points in the convex hull of training data, do we get similar results? In other words, do we need to choose two training examples as the endpoints?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for the comments and constructive suggestions. In the following, we address the main concern raised. Please find the details below.
>Q1: It would be nice if more datasets and architectures can be analyzed.
**A1:** We thank the reviewer for the suggestion. We add a experiment to explore the applicability of our approach to transformer-based models. We conduct an experiment using Vision Transformers (ViT)[1] on CIFAR-10. Details of the hyperparameters used are summarized below:
|Hyperparameters|Value|
|:---:|:----:|
|Learning rate|1e-4,5e-5,1e-5|
|Batch size|256,512,1024|
|Weight decay|1e-5,1e-6,1e-7|
The correlation figure is shown in Figure 2 in the anonymous github website https://anonymous.4open.science/r/icml-rebuttal-B813/icml%202025%20rebuttal.pdf. We achieve a correlation of 0.84, validating the applicability of our measure in this network architecture. We will include these experimental results in the next version of the paper.
>Q2: If we calculate the expected 1D region count between two random points in the convex hull of training data, do we get similar results? In other words, do we need to choose two training examples as the endpoints?
**A2:** We thank the reviewer for the suggestions. In Appendix C, we have conducted with alternative approaches to generate hyperplanes for computing the region count, selecting a training data point and extending it in a random direction by a fixed length. Even with this method, the correlation remains high.
We further **conduct experiments by calculating the expected 1D region count between two random points in the convex hull of the training data**, using the hyperparameters from Table 1 to train the neural network and compute the correlation. The result are as follows:
|Network|Correlation|
|:----:|:----:|
|Resnet18|0.93|
|Resnet34|0.95|
|EfficientNetB0|0.87|
|SimpleDLA|0.82|
The results confirm that the correlation remains strong, demonstrating that our method does not require selecting two training examples as endpoints.
Finally, we thank the reviewer once again for the effort in providing us with valuable suggestions. We will continue to provide clarifications if the reviewer has any further questions.
**References**
[1] Dosovitskiy, Alexey, et al. "An image is worth 16x16 words: Transformers for image recognition at scale." arXiv preprint arXiv:2010.11929 (2020). | Summary: In this work, authors propose region count as a metric to quantify implicit bias / generalizability of neural networks. A region is defined as a set of input points which are classified in the same way by the network; authors show that fewer regions lead to increased generalizability (quantified as gap between test error and train error). They empirically show that the number of regions exhibits a high correlation with the generalizability in a number of convolutional architectures.
## Update after rebuttal
After reading the author's comments and other reviewers' comments, I maintain my score.
Claims And Evidence: - The main claim of this work is that the number of regions is correlated with the generalizability of the model
- The evidence is convincing, and it indeed seems that better performing models tend to have fewer regions
- This work may also provide theoretical justification as to why higher learning rate and smaller batch size can work well in practice
Methods And Evaluation Criteria: - I think the setup of the paper is rigorous and the evaluation criteria are satisfactory
Theoretical Claims: - While I did not carefully check the details of the proofs in the appendix, I am convinced by the correctness of the presented analysis in the main text.
Experimental Designs Or Analyses: I believe the experimental design is convincing. Personally, I would like to see some results for networks which did not converge and exhibit a high test error (the lowest result in Tab. 2 is 0.78 on imagenet). To what extent (going down in generalizability) does the correlation hold? I think this may be interesting to analyze also to derive potential regularization terms aimed at enforcing low region count [see below]
Supplementary Material: I briefly checked the supplementary material.
Relation To Broader Scientific Literature: I believe this work can potentially have a significant impact on the deep learning field in general.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: - The work is clearly presented and understandable even if theoretical
- I believe the experimental validation is done correctly, as it is often lacking in more theoretical works
- Some empirical results are missing on the lower end of the generalization spectrum. As stated above, I think it would be interesting to see whether this correlation exists also in those cases
Other Comments Or Suggestions: I think this work is very interesting and can have significant impact, thus may be considered for acceptance. I have some questions about its potential applications [see below]
Questions For Authors: - Given the link between region count and generalizability, do you think it would be possible to explicitly aim for low region count in the objective function of a neural network training? Perhaps with some regularization term. Do you think this would help in training better models? Could this term be applied from the start of the training, or perhaps when the network has already "stabilized" after some iterations?
- I find very interesting the link between region count and data augmentation. I think that data augmentation can help in decreasing region count, thus helping generalization; perhaps this could explain the success of contrastive learning methods? I would like to hear the author's thoughts about this. For this topic, I would suggest this work [1] which reminds of the connectedness property in your work
[1] https://proceedings.mlr.press/v202/dufumier23a/dufumier23a.pdf
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the detailed comments. We address the main concerns below:
>Q1: Personally, I would like to see some results for networks which did not converge and exhibit a high test error (the lowest result in Tab. 2 is 0.78 on imagenet). To what extent (going down in generalizability) does the correlation hold?
**A1:** We appreciate the reviewer’s insightful question. **We observed relatively low training and test accuracy on ImageNet, achieves about 70% accuracy on the training set and 45% on the test set**. However, the correlation in Table 2 remains high, though slightly lower than on CIFAR-10/100.
Additionally, we conduct experiments with traditional ML models. When training decision trees and random forests on CIFAR-10 with various hyperparameters, **most configurations failed to converge (yielding high test error)**. The hyperparameters are as follows:
|Hyperparameters|Value|
|:----:|:----:|
|Depth|$3,4\cdots, 17$|
|Criterions|gini, entropy|
|Splitter|best,random|
The correlation figure is shown in Figure 1 in the anonymous github website https://anonymous.4open.science/r/icml-rebuttal-B813/icml%202025%20rebuttal.pdf. We achieve a correlation of 0.96 in decision trees and 0.98 in random forests, demonstrating that our measure remains robust despite low test accuracy.
>Q2: Given the link between region count and generalizability, do you think it would be possible to explicitly aim for low region count in the objective function of a neural network training? Do you think this would help in training better models? Could this term be applied from the start of the training, or perhaps when the network has already "stabilized" after some iterations?
**A2:** We thank the reviewer for this thoughtful suggestion. Since the region count computation is currently non-differentiable, we cannot explicitly incorporate it as a regularization term. However, the data augmentation method mixup implicitly minimizes region count by encouraging smooth transitions between labels rather than predicting unrelated classes. This suggests our method may partially explain mixup’s performance benefits.
While it cannot be directly used as a regularization term, **we find it effective for early-stage hyperparameter evaluation**. We conduct experiments analyzing the correlation between early-training region counts and final generalization gap (distinct from Table 3’s per-timestep analysis). We train Resnet18 on CIFAR-10 with 200 epochs. The results are as follows:
|Epoch|Correlation|
|:----:|:----:|
|10|-0.07|
|20|0.24|
|30|0.92|
|40|0.95|
|60|0.97|
|80|0.96|
|100|0.97|
|200|0.98|
The results show strong correlation between early region counts and final generalization(since epoch 30) and region counts stabilize quickly during training. This enables early stopping for poor hyperparameter configurations by monitoring initial region counts, reducing computational costs. We will add these findings to the paper.
>Q3: I find very interesting the link between region count and data augmentation. I think that data augmentation can help in decreasing region count, thus helping generalization; perhaps this could explain the success of contrastive learning methods[1]?
**A3:** We thank the reviewer for this insightful question. For now, our analysis applies to supervised learning for overparameterized models. For contrastive learning methods, the pretrained representations obtained through this method can serve as feature extractors to improve performance in downstream classification tasks, particularly when labeled data is scarce. If we use kernel-based methods[1] to connect more positive samples when the initial label prediction of the neural network is uncertain, it will lead to simpler learned regions rather than mixed positive and negative samples. This also helps minimize the learned region count, thereby enhancing performance. We believe this is a promising direction for future research.
We thank the reviewer once again for the valuable and helpful suggestions. We would be happy to provide further clarifications if the reviewer has any additional questions.
**Reference**
[1] Dufumier, Benoit, et al. "Integrating prior knowledge in contrastive learning with kernel." International Conference on Machine Learning. PMLR, 2023.
---
Rebuttal Comment 1.1:
Comment: I appreciate the authors' response, and I confirm my partially positive stance towards acceptance.
About A2, would it be possible to perform that experiment on some slightly harder datasets, as CIFAR-10 is too "easy" for ResNet18? Perhaps also CIFAR-100 could be enough.
Also, what I would like to see besides the generalization gap or correlation is the real train/test performance at each timestep. I think it would paint a more complete picture, as the generalization gap may also be low when both training and test errors are high.
---
Reply to Comment 1.1.1:
Comment: Thank you for your timely and detailed feedback. We have added experiments using ResNet-18 on CIFAR-100, training 200 epochs with the hyperparameter in Table 1. The results are as follows:
|Epoch|Correlation|
|:----:|:----:|
|10|0.63|
|20|0.38|
|30|0.75|
|40|0.84|
|60|0.93|
|80|0.92|
|100|0.94|
|200|0.96|
The results show that region count can still predict the final generalization gap at early training stages.
Regarding the train and test accuracy for each epoch, for most hyperparameter settings on CIFAR-10 and CIFAR-100, the training accuracy reaches nearly 100%. As an example, for ResNet-18 on CIFAR-100 with 15 different hyperparameter configurations, the error curves for each epoch can be found in this anonymous link https://anonymous.4open.science/r/icml-rebuttal-B813/Training%20and%20test%20accuracy%20over%20epoch.pdf. We will include this part in the appendix of the next version of the paper. | Summary: The authors propose using low-dimension region counts as a proxy for the generalization performance. They empirically test the correlation between region count and generalization performance, and provide a bound on the region count for two layer ReLU neural networks.
Claims And Evidence: The claims are not adequately supported by the evidence. It is unclear whether region count is a good proxy for generalization performance, because it is unclear what a good correlation metric is. What is the correlation metric for other possible proxies, like norm and margin, or even simpler ones like number of iterations of GD? There is no other connection provided between region count and generalization performance other than through this correlation.
The theoretical bound provided gives region count bounds in terms of O(N), which is much larger compared to the empirical region counts in the 2-20 range. It's not clear how meaningful the theoretical bound is, and there is no theoretical generalization bound provided in terms of region count.
Methods And Evaluation Criteria: The evaluation criteria for how good region count would make more sense if it was compared to other possible methods, but as it stands it is not possible to evaluate whether region count is an appropriate proxy.
Theoretical Claims: I did a cursory check for correctness and did not see any issues.
Experimental Designs Or Analyses: See previous sections.
Supplementary Material: N/A
Relation To Broader Scientific Literature: This paper builds on a large prior literature investigating generalization.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: The authors propose an interesting proxy for generalization performance which has potential. However, they do not provide adequate evidence for its effectiveness.
Other Comments Or Suggestions: N/A
Questions For Authors: 1. What is the correlation between generalization performance and other potential proxies? For example: norm, margin, and number of GD iterations (this is not an exhaustive list).
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We greatly appreciate the reviewer's comments and valuable suggestions. We added extensive experiments and summarize them below. We will include more detailed results in the revision.
>Q1: It is unclear whether region count is a good proxy for generalization performance, because it is unclear what a good correlation metric is. What is the correlation metric for other possible proxies, like norm and margin, or even simpler ones like number of iterations of GD? There is no other connection provided between region count and generalization performance other than through this correlation.
**A1:** We appreciate the reviewer's feedback on the missing details. **In Section 3(Figure 2), we have already shown that the correlations between generalization gap and frobenious norm, margin, or margin/frobenious norm are all weak**.
We follow the reviewer's advice and conduct additional experiments on other generalization measures, including spectral norm[2], PB-I and PB-O (which are sharpness metrics from PAC-Bayesian bounds that use the origin and initialization as reference tensors), PB-M-I and PB-M-O[3][4][5] (which are derived from PAC-Bayesian Magnitude-aware Perturbation Bounds). We conduct experiments on CIFAR-10 using ResNet-18 and use the hyperparameters in Table 1. The results are summarized below:
|Proxy|Correlation|
|:----:|:----:|
|Frobenious Norm|0.64|
|Margin|0.02|
|Margin/Frobenious Norm|-0.18|
|Spectral Norm|0.77|
|PB-I|-0.35|
|PB-O|-0.31|
|PB-M-I|0.79|
|PB-M-O|0.78|
|Region Count|**0.98**|
The results are consistent with the results in [1] and demonstrate that our proposed region count measure **exhibits a significantly higher correlation with the generalization gap compared to other measures**. We will include these findings in the next version of the paper.
>Q2: The theoretical bound provided gives region count bounds in terms of O(N), which is much larger compared to the empirical region counts in the 2-20 range. It's not clear how meaningful the theoretical bound is, and there is no theoretical generalization bound provided in terms of region count.
**A2:** Thank you for raising this question. **The $O(N)$ dependency is actually tight**, by considering N points on a line with alternating labels. The upper bound in the theorem is a worst case analysis, and it can possibly be tightened with additional assumptions on the data distribution.
Also, we believe generalization results in terms of region count is possible, since region counts might constrain the size of the function class, which connects to traditional ways of constructing generalization bounds based on function class complexity. We believe the strong empirical connection between region count and generalization shown in this paper is already a novel contribution to the generalization community, and leave a rigorous proof to the future work.
Finally, we thank the reviewer once again for the effort in providing us with valuable and helpful suggestions. We will continue to provide clarifications if the reviewer has any further questions.
**Reference**
[1] Jiang, Yiding, et al. "Fantastic generalization measures and where to find them." arXiv preprint arXiv:1912.02178 (2019).
[2] Bartlett, Peter L., Dylan J. Foster, and Matus J. Telgarsky. "Spectrally-normalized margin bounds for neural networks." Advances in neural information processing systems 30 (2017).
[3] Keskar, Nitish Shirish, et al. "On large-batch training for deep learning: Generalization gap and sharp minima." arXiv preprint arXiv:1609.04836 (2016).
[4] Neyshabur, Behnam, et al. "Exploring generalization in deep learning." Advances in neural information processing systems 30 (2017).
[5] Bartlett, Peter L., Dylan J. Foster, and Matus J. Telgarsky. "Spectrally-normalized margin bounds for neural networks." Advances in neural information processing systems 30 (2017).
---
Rebuttal Comment 1.1:
Comment: Thank you for the response, the inclusion of Figure 2 really helps with exhibiting the high correlation between region count and the generalization gap. I would appreciate some further clarifications on the figure though.
Could you provide some more details on how the experiments in Figure 2 were run, especially compared to those in Figure 4 (specifically the ResNet18 portion of it)? I would assume that you could train the models once (per set of hyperparameters), and analyze several different counts/norms/proxies for a single trained model. This would result in the generalization gaps to be the same across all figures, with the only difference being the x-axis. As a result, I'm a bit confused why the ranges of the generalization gaps differ so much between Figure 2 (14-24) and Figure 4 (15-36)? Also, you mentioned you used the hyperparameters in Table 1, which would result in 27 possible configurations of hyperparameters, but I only see 18 data points in Figure 2. What am I missing here? Thanks!
---
Reply to Comment 1.1.1:
Comment: We sincerely thank the reviewer for the question! We carefully reviewed the code related to Section 3 and confirmed that it was indeed based on some early exploratory work using the hyperparameter from the initial stage of the project. The specific hyperparameters used are as follows:
|Hyperparameters|Value|
|:----:|:----:|
|Learning rate|0.1,0.01|
|Batch size|256,512,1024|
|Weight decay|1e-5,1e-6,1e-7|
To ensure a fair comparison of the correlation, we re-plotted the correlation results for the Resnet18 network in Figure 4 using the 18 hyperparameters settings (instead of the later 27 in Table 1). The updated figure can be found at the anonymous link https://anonymous.4open.science/r/icml-rebuttal-B813/correlation.pdf. The correlation results under these hyperparameters are given as follows:
|Proxy|Correlation|
|:----:|:----:|
|Frobenious Norm|0.64|
|Margin|0.02|
|Margin/Frobenious Norm|-0.18|
|Region Count|**0.92**|
As the figures show, the ranges of the generalization gaps are now consistent across the figures(14-24). Under these 18 hyperparameter settings, the correlation with region count remains significantly higher than that of the other metrics.
In addition, we also conduct the experiments for the three measures in Figure 2 using the 27 hyperparameter settings from Table 1. The updated correlation plots can be found at the anonymous link below https://anonymous.4open.science/r/icml-rebuttal-B813/correlation_prime.pdf. The correlation results under these hyperparameters are compared as follows:
|Proxy|Correlation|
|:----:|:----:|
|Frobenious Norm|0.74|
|Margin|0.60|
|Margin/Frobenious Norm|0.16|
|Region Count|**0.98**|
The results show that our method also outperforms these metrics under the hyperparameters in Table 1. Besides, we would like to note that the first three rows of the table in the rebuttal are directly taken from our manuscript, so they should be replaced with the rows from the 27 hyperparameter table above. The other rows in the rebuttal table are already correct 27 hyperparameter results.
We apologize for the lack of clarity in the Section 3 of our paper and will revise this part in the next version of our paper. | null | null | null | null | null | null |
Positional Attention: Expressivity and Learnability of Algorithmic Computation | Accept (poster) | Summary: This paper is a theoretical study on positional transformers, where the attention is determined solely by positional encoding regardless of the content. The paper includes a representation theory that position transformers can simulate MPC, followed by a generalization bound. Empirical study is conducted on several synthetic tasks, showing that positional transformers can indeed complete the tasks, though the model needs more layer and data to achieve so.
Claims And Evidence: yes
Methods And Evaluation Criteria: yes
Theoretical Claims: I checked the soundness of the theorem, but not the proof.
Experimental Designs Or Analyses: yes
Supplementary Material: no
Relation To Broader Scientific Literature: The contribution of the paper seems to be extending the theoretical analysis of standard transformer to positional transformers.
Essential References Not Discussed: no
Other Strengths And Weaknesses: Strength:
- The MPC representation theory is interesting, which can shed light on how transformers solve problems;
- It seems that a better generalization bound is derived thanks to the positional restriction.
- Positional transformers can be indeed of interest for some tasks, as they are at least as powerful as CNNs.
Weaknesses:
- The novelty is not clear. I think the MPC representation result is also proven for standard transformers.
- The biggest concern I have is, I are not sure *why* we need to study positional transformers. I think the motivation is might the simplification of attention make the theoretical analysis easier and we can obtain more theoretical insights to positional transformers, and more importantly, to standard transformers. However, I don’t quite see the gain of the positional constraints. It seems that (Sanford et al., 2024) already have the MPC simulation result, and the positional version is worse (requires more layers). Why do we want to study positional transformers then? To show that the content is indeed important, and you will suffer significant representation power loss with only position? Similarly, I do not understand what insight we gain by studying positional transformers rather than standard transformers from the generalization result.
Other Comments Or Suggestions: If the authors can make the novelty and motivation more convincing, I can raise my score.
Questions For Authors: see weaknesses
Update:
=
the authors have addressed my concerns on the motivations of studying PT, and the OOD generalization result is interesting. I raised my score.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for allowing us to clarify the motivation of our paper. We will address their questions individually and provide general remarks below.
*High-level motivation:* Generally, there is growing interest in the relationship between neural networks and computational models [1,2,3,4]. Computational models execute algorithms on data. For example, Figure 7 in our paper shows the communication trace of an algorithm for computing a parallel cumulative sum.
*Motivation for positional constraints:* As in Figure 7 and many other parallel algorithms, data does not influence communication among processors within computational models. Instead, communication relies solely on processor IDs (or positions). For standard Transformers (ST), this implies that the computation of attention weights can be independent of the input values for certain algorithms, and that is how we arrive at positional Transformers (PT), which is our object of study. In c., we discuss the trade-offs of these constraints.
We now address specific concerns raised by the reviewer.
> a. The novelty is not clear. I think the MPC representation result is also proven for standard transformers.
PT poses an algorithmic computation-inspired departure from the original attention mechanism, and the theoretical results of one do not directly translate to the other. This fact alone justifies the need for an MPC simulation result. The proof techniques we used are significantly different from the ones used for the ST and cannot be directly borrowed from [1], which we further discuss in response b.
> b. [...] the simplification of attention make the theoretical analysis easier and we can obtain more theoretical insights to PT, and more importantly, to ST.
The reviewer seems to suggest that the goal of introducing PT is to simplify the theoretical analysis of ST. We would like to emphasize that this is not the case. We argue that the expressivity analysis of PT is even more challenging. Simulating MPC communication with ST is facilitated by self-attention’s ability to depend on the input values. In contrast, PTs rely on fixed communication via positional encodings, making simulation more challenging. Consequently, MPC simulation with PT must show dynamic communication over a static network, which we accomplish by using Benes networks, a novel strategy unseen in previous related works.
> c. However, I don’t quite see the gain of the positional constraints. It seems [...] PT is worse (requires more layers).
The comparison between PT and ST is more nuanced than suggested. PT offers a different learnability trade-off, illustrated in theory and practice. While PT requires more layers to simulate MPC, this is a worst-case analysis that accounts for all types of algorithms MPC can execute. However, as shown in Section 6, PT has an advantage in learnability: it removes a dependency on the norms of the query and key parameters when all other factors are fixed. Moreover, our empirical results show the competitiveness of PT: Figure 2 showcases some algorithmic tasks where PT outperforms ST in-distribution (ID) with the same number of layers. Furthermore, PT consistently outperforms ST in OOD scenarios for those tasks (Figure 4). As discussed in Section 7.2, we hypothesize that PT exhibits an OOD advantage in data-independent algorithmic tasks due to its architectural alignment with the target function. Our experiments are designed to test this hypothesis.
> d. Why [...] study PT then? To show [...] significant representation power loss with only position?
The conclusion that PT lacks representation power is incorrect. Our theory demonstrates that with logarithmically more layers, similar to ST, PT can simulate any computation within the MPC protocol. Empirically, we observe that for many algorithmic tasks, PT has comparable ID performance and significantly better OOD performance than ST, with the same number of layers. We refer the reviewer to our response in c. for more context.
> e. Similarly, I do not understand what insight we gain by studying PT rather than standard transformers from the generalization result.
This is highlighted in Sections 1 and 6 of the paper. The interesting takeaway is the tradeoff between a better generalization bound (independent of parameter norms) and the (potential) need for logarithmically more layers needed to maintain expressivity. We refer the reviewer to response c. for more details.
---
Once again, we thank the reviewer and welcome any further comments. We hope the clarifications are sufficient for them to consider raising their score.
References:
[1] Sanford et al. Transformers, parallel computation, and logarithmic depth. ICML 2024
[2] Pérez et al. Attention is Turing-Complete. JMLR 2021
[3] Loukas, A. What graph neural networks cannot learn: depth vs width. ICLR 2020
[4] Wei et al. Statistically meaningful approximation: a case study on approximating Turing machines with transformers. NeurIPS 2022 | Summary: This paper introduces and analyzes positional attention in Transformers where attention weights depend exclusively on positional encodings rather than on input data. The authors prove that Transformer with positional attention with logarithmic depth has the same expressive power as MPC, and demonstrate that positional Transformers has a trade-off in-distribution and has certain benefit in OOD tasks when the task relies on positional information.
### Update after rebuttal
The response addresses most concerns so I will keep my positive rating.
Claims And Evidence: Yes the claims made in the submission supported by clear and convincing evidence.
Methods And Evaluation Criteria: Yes the proposed methods and/or evaluation criteria (e.g., benchmark datasets) make sense for the problem or application at hand.
Theoretical Claims: I briefly checked the proofs in Appendix B.
Experimental Designs Or Analyses: I checked the experimental setups for both in-distribution regime and out-of-distribution regime. I found the out-of-distribution regime rather limited since in Transformers people also consider longer lengths as OOD.
Supplementary Material: I briefly checked the proofs in Appendix B and the setup in Appendix D.
Relation To Broader Scientific Literature: 1. The paper proposed to use positional only data to get K, Q matrices in attention as a noval architecture design as opposed to traditional attention mechanism.
2. The paper shows the expressiveness of the positional Transformer respect to MPC, which is new to my best knowledge.
3. The paper honestly presents the trade-offs between positional and standard Transformers, showing where each excels and explaining the underlying reasons.
Essential References Not Discussed: Not to my knowledge.
Other Strengths And Weaknesses: Strengths: see contributions.
Weaknesses:
1. The proposed method seems to be heavily dependent on the positional encodings used in the Transformer model and the experiment only uses one type of the positional encodings. How to learn useful positional encodings and how the positional Transformer will behave using other positional encodings remain uncertain.
2. As mentioned in Experimental Designs Or Analyses, length generalization seems more natual to Transformers as OOD and the paper does not investigate it. It also poses extra difficulity since the depth of the model needs to be updated when the length of the input changes. How to solve this problem remains unknown from the paper.
Other Comments Or Suggestions: For Weaknesses 1&2, the paper would benefit from further investigation in such directions.
Questions For Authors: 1. The benifit of the OOD case in the paper seems to be highly related with the nature of the tested task. Is there any case where the standard Transformer behave better than positional Transformer in OOD? Such results would also help to understand the particular inductive bias that both models favor.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for taking the time to read and review our manuscript. In what follows, we provide a comprehensive response to the weaknesses highlighted by the reviewer.
> The proposed method seems to be heavily dependent on the positional encodings used in the Transformer model and the experiment only uses one type of the positional encodings. How to learn useful positional encodings and how the positional Transformer will behave using other positional encodings remain uncertain
As noted in lines 289-293 (second column) of the main paper, we have experimented with various configurations of positional encodings, including sinusoidal, binary, and rotary (RoPE) positional encodings. In all cases, we observe the effects reported in the main paper. We refer the reviewer to Appendix D 1.6 for more details on those cases.
> As mentioned in Experimental Designs Or Analyses, length generalization seems more natual to Transformers as OOD and the paper does not investigate it. It also poses extra difficulity since the depth of the model needs to be updated when the length of the input changes. How to solve this problem remains unknown from the paper.
*Depth of the model:* We’d like to emphasize that a fixed-depth Positional Transformer can indeed work with inputs of different lengths (up to a predetermined length). This is demonstrated by our experiments, where a PT model is trained to perform algorithmic tasks on multiple input lengths, a setting reminiscent of the notion of context length in Transformers. Appendix D.1.4 presents a single model capable of processing different input lengths up to a fixed upper bound, demonstrating the effectiveness of our approach in processing variable-length inputs while achieving good generalization on unseen input values. We would also like to point out that our in-distribution generalization bound does not require fixing the number of layers; it assumes a fixed upper bound on the length instead.
*Types of OOD generalization:* Algorithmic execution using neural networks involves multiple kinds of OOD generalization. Length generalization refers to executing the same algorithm on input lengths unseen during training, while value generalization applies the algorithm to new input values not encountered during training. Both are crucial, as an ideal model should perform well on unseen lengths and values. In this work, our primary focus is on value generalization, as it ensures that, for a fixed upper bound on the length, the model has learned an algorithmic execution applicable to any combination of numbers.
> The benefit of the OOD case in the paper seems to be highly related with the nature of the tested task. Is there any case where the standard Transformer behave better than positional Transformer in OOD? Such results would also help to understand the particular inductive bias that both models favor.
We thank the reviewer for the insightful question. As mentioned in Section 7.2, we hypothesize that the alignment between the architecture and the underlying problem promotes OOD generalization. While Figure 4 shows instances where Positional Transformers outperform standard Transformers, we also present a case where the opposite occurs. In the k-hop induction heads task, which involves dynamic communication, our hypothesis of a fixed communication graph is violated. As a result, our architecture underperforms compared to standard Transformers, which converge more quickly and with fewer layers, an advantage we attribute to algorithmic alignment. Here, the dynamic nature of the problem aligns better with the flexibility of self-attention compared to the rigidity of positional attention.
---
Once again, we thank the reviewer and welcome any further comments. We hope the clarifications are sufficient for them to consider raising their score.
---
Rebuttal Comment 1.1:
Comment: Thank you for the response. There is some minor confusion though.
> "In this work, our primary focus is on value generalization, as it ensures that, for a fixed upper bound on the length, the model has learned an algorithmic execution applicable to any combination of numbers."
I think the value generalization decribed in the paper (L380 left) is extending the range of the input, not extending the combination. Could you clarify this?
---
Reply to Comment 1.1.1:
Comment: The reviewer’s intuition is correct. Here, “combination” just refers to any selection of numbers from the test set in L380 left. In other words, the input list may include numbers beyond the training scale.
We appreciate the careful consideration and, if our response has addressed all concerns, would be grateful for a positive reassessment. | Summary: This paper presents transformer with positional attention (PT), a mechanism that implements data-free query and key inputs for computing attention scores. From the empirical side, this mechanism aims to emulate the massively parallel computation (MPC) model, which the authors show expressivity and learnability results. Experimental results are presented that shows on select algorithmic tasks positional attention can generalize better than standard attention.
Claims And Evidence: Yes. I believe the claims are well articulated. The authors clearly established their aim in establishing equivalence between PT and MPC in Section 5, and discussed potential limitations (in terms of quadratic complexity) from ln 207 onwards. The generalization bound given in Section 6 appears to be correct.
Methods And Evaluation Criteria: I believe the experiments are designed reasonably well to establish that PT can achieve comparable (in-distribution) or better (out-of-distribution) performance on proposed algorithmic tasks, which are commonly used for evaluating theoretical works that establish transformers as computation models. While I understand that real-world applications is not a focal point of this paper, and I certainly does not lower my review because of it, it'd be great to discuss its limitation (beyond those discussed in Section 8) in modeling natural language data, or discuss how this type of algorithmic transformer could be useful in real world settings.
Theoretical Claims: Due to time constraint, I was only able to check the expressivity results (Appendix B), which seems correct. I was not able to check generalization result in Appendix C carefully but it seems to be a an application of Theorem 5 of Bartlett et. al. (2003), coupled with Lipschitz results of the PT model. And I'm conservatively optimistic about the results.
Experimental Designs Or Analyses: The experiments are designed to assess the generalization performance of PT on algorithmic tasks. The generalization and OOD experiments are done properly.
One of my core concern for this comparison is that the authors directly supplement positional encoding in the form of QK for PT, but it is only fed into the standard transformer at the input layer. One could imagine that for deeper networks, positional encoding may vanish for standard transformers but not the case for PT (though of course, one could argue that this is precisely PT's benefit). I do believe that additional experiments on real datasets, even training small language models could further strengthen this paper.
Supplementary Material: I have checked the supplementary materials. The authors have included all of their codes to reproduce the experiments in their paper.
Relation To Broader Scientific Literature: This work falls into a growing body of work that assess the algorithmic capability of transformers [1][2], investigations of optimal encodings of positional information [3], graph neural nets for algorithmic execution [4].
[1] Neural Networks and the Chomsky Hierarchy, https://arxiv.org/abs/2207.02098
[2] Training Neural Networks as Recognizers of Formal Languages, https://arxiv.org/abs/2411.07107
[3] Round and Round We Go! What makes Rotary Positional Encodings useful?, https://arxiv.org/abs/2410.06205
[4] Everything is Connected: Graph Neural Networks, https://arxiv.org/abs/2301.08210
Essential References Not Discussed: I'm not aware of any undiscussed literature.
Other Strengths And Weaknesses: I believe this is a solid paper with a valid hypothesis, correct theoretical analysis, and reasonable experimental design. OOD (or length) generalization is a challenging task in this line of literature and it's nice to see some positive results from PT.
Other Comments Or Suggestions: NA
Questions For Authors: See comments about discussions on natural language datasets and broader impacts in the **Methods And Evaluation Criteria** section.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their comments and appreciate their recognition of the soundness of our paper. We appreciate the connections made to other related works, which we will incorporate into the main paper. Below, we address their insightful comments, specifically those written in Methods And Evaluation Criteria:
> [...] it'd be great to discuss its limitation (beyond those discussed in Section 8) in modeling natural language data discuss how this type of algorithmic transformer could be useful in real world settings.
We appreciate the reviewer’s suggestion. Along this line, one relevant computational task we considered in our work is the k-hop inductive heads task discussed in Section 7, which is inspired by the in-context learning abilities of language models and captures some of the pattern matching and higher-order dependencies found in NLP tasks [1]. While we agree that experiments in Natural Language are an interesting direction for studying the effectiveness of positional Transformers (PT), the manuscript is already quite extensive. To ensure a thorough analysis, we believe it is best to reserve these explorations for future work, which we intend to pursue as a follow-up. Regarding its usefulness in real-world settings, one possible direction is applying PT to unstructured tabular data in the form of text, where prompts require algorithmic computation to be answered. In Section 7.3, we present experiments in a simplified setting where PT proves useful and outperforms standard Transformers (ST). Building on this, we are actively preparing further empirical studies in this direction as part of our future work.
> [...] (though of course, one could argue that this is precisely PT's benefit). I do believe that additional experiments on real datasets, even training small language models could further strengthen this paper.
We appreciate the reviewer’s insight and agree that additional real-world experiments could further illustrate PT’s potential. Interestingly, our ablation study in Appendix D 1.7 already captures this intuition but also reveals more: even when positional encodings are incorporated at every layer of ST, its performance remains suboptimal. This suggests that PT’s advantage is not merely due to its handling of positional information but rather to the presence of two distinct computational streams—one for positions and one for input values—which we hypothesize is a key factor behind its effectiveness. Furthermore, the new theoretical learnability trade-off for the in-distribution setting in Section 6 comes from this decoupling property (see comments in line 176).
Again, we thank the reviewer for carefully reading our manuscript and for their thoughtful feedback. We welcome any further questions.
References
[1] Olsson et al. In-context learning and induction heads. 2022
---
Rebuttal Comment 1.1:
Comment: I'd like to thank the authors for their detailed response, which has addressed my concerns. I'd like to keep the rating and recommend acceptance for this paper. | Summary: This paper proposes the Positional Transformer architecture for learning algorithmic problems over abstract data structures. In Positional Transformers, the attention maps are computed merely based on the positional embeddings and therefore the learned interaction patterns between different positions in the input sequence are independent of the values at those positions. This property makes Positional Transformers a better candidate compared to regular Transformers for certain class of algorithmic problems, especially in terms of OOD generalization as empirically demonstrated in the paper. The paper has also provided an elegant theoretical analysis proving the expressivity and learnability of Positional Transformers, most notably the generalization bound for Positional Transformers.
Claims And Evidence: The paper has done an excellent job of precisely stating the claims as well as providing both theoretical and empirical evidence for those claims.
Methods And Evaluation Criteria: Regarding evaluating both expressivity and learnability, the authors have provided relevant settings and metrics to empirically evaluate the theoretical results.
Theoretical Claims: I did not check the proofs.
Experimental Designs Or Analyses: The paper does a good job of setting up sufficient experiments to evaluate both the merits and the shortcomings of Positional transformers in solving algorithmic problems. I especially liked the fact that different classes of problems were used to pinpoint the scenarios in which Positional Transformers are indeed useful.
Supplementary Material: No.
Relation To Broader Scientific Literature: I believe the findings of this paper can be further relevant useful for other areas of Deep Learning such as neuro-symbolic methods. In particular, it'd be interesting to see how symbolic computation can be further injected as inductive biases into the positional transformers and more generally purely neural models.
Essential References Not Discussed: There's a quite extensive literature around GNNs for algorithmic problems and in particular NP problems (e.g. SAT solving, CSPs, etc.) that is missing from this paper.
Other Strengths And Weaknesses: Strengths:
This paper is very well-writte and well-motivated.
The claims are carefully stated and adequately supported.
The authors have done a great job with their empirical study covering both the strength and weaknesses areas for Positional Transformers.
Weaknesses:
In terms of practicality of the proposed models, it'd be interesting to have experimental results on more realistic datasets with much larger problem sizes.
Other Comments Or Suggestions: N/A
Questions For Authors: - For the OOD case, do you think if we keep the Q and K projection matrices frozen in Positional Transformers and merely fine-tune the V projection matrices, we would be able to achieve the same level of generalization as the original in-distribution case? I believe that'd be an interesting ablation study which can further shows the importance of Positional Attention for certain algorithmic problems.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely appreciate the reviewer’s time in evaluating our manuscript. We are grateful for their recognition of the novelty and significance of our work. Below, we address their insightful comments.
> There’s a quite extensive literature around GNNs for algorithmic problems and in particular NP problems (e.g. SAT solving, CSPs, etc.) that is missing from this paper.
We thank the reviewer for pointing out this gap in our literature review section. We have identified key references (original works and highly-cited) like [1,2,3,4,5,6,7] as well as a comprehensive survey [8], which we will include in the camera-ready version. If the reviewer believes specific works need to be mentioned explicitly, we would be happy to add them.
> For the OOD case, do you think if we keep the Q and K projection matrices frozen in Positional Transformers and merely fine-tune the V projection matrices, we would be able to achieve the same level of generalization as the original in-distribution case?
This is a great question! The answer is yes: fine-tuning only the V projection matrix in the OOD case allows the positional Transformer to achieve the same level of generalization as in the in-distribution case. On the other hand, the same does not hold for the standard Transformer. We appreciate the reviewer’s suggestion of this scenario, which closely aligns with the typical approach to “fine-tune a pre-trained foundation model with unseen data” when dealing with new and potentially OOD data in practice.
In the tables below, we consider three simple algorithmic tasks and report the median test error (MSE) for both positional and standard transformer models when
- they are trained and tested on in-distribution data (in-dist),
- they are trained on in-distribution data but tested on numbers 10x larger than the original in-distribution data (10x OOD),
- they are trained on in-distribution data, fine-tuned V projection matrices on numbers 10x larger than the original in-distribution data, and then tested on numbers 10x larger than the original in-distribution data (10x OOD with fine-tuning).
We find that fine-tuning only the V projection matrices brings the accuracy of the positional Transformer to the same level as the in-distribution case. However, for the standard Transformer, even after fine-tuning the V projection matrices, the accuracy on 10x test data is still very high compared to that of the positional Transformer. The comparison highlights another potential advantage of the positional Transformer for executing algorithmic tasks: one might efficiently fine-tune a pre-trained positional Transformer on OOD data and achieve good performance.
| Task | Positional (in-dist) | Positional (10x OOD) | Positional (10x OOD with fine-tuning) |
| :--- | ---: | ---: | ---: |
| sort | 1.20e-04 | 7.37e-04 | 1.23e-04 |
| min | 1.03e-05 | 3.92e-04 | 2.19e-05 |
| sum | 6.07e-06 | 1.31e-03 | 1.32e-05 |
| Task | Standard (in-dist) | Standard (10x OOD) | Standard (10x OOD with fine-tuning) |
| :--- | ---: | ---: | ---: |
| sort | 9.05e-04 | 5.18e-01 | 6.90e-02 |
| min | 1.74e-06 | 1.39e-01 | 4.00e-02 |
| sum | 5.20e-06 | 1.09e+00 | 1.23e-01 |
*We keep the same empirical setting where we train both models for 2000 epochs. For fine-tuning, we adopt the common practice and only train for 20 epochs. We normalize the MSE by the scale factor so that the table results indicate relative accuracy.
---
Again, we thank the reviewer for carefully reading our manuscript and for their thoughtful feedback. We welcome any further questions.
References:
[1] Vinyals et al. Pointer Networks, NeurIPS 2015
[2] Prates et al. Learning to Solve NP-Complete Problems: A Graph Neural Network for Decision TSP, AAAI 2019
[3] Joshi et al. An Efficient Graph Convolutional Network Technique for the Travelling Salesman Problem, 2019
[4] Bai et al. Learning-Based Efficient Graph Similarity Computation via Multi-Scale Convolutional Set Matching, AAAI 2020
[5] Selsam et al. Guiding High-Performance SAT Solvers with Unsat-Core Predictions, SAT 2019
[6] Karalias and Loukas Erdos Goes Neural: an Unsupervised Learning Framework for Combinatorial Optimization on Graphs, NeurIPS 2020
[7] Gasse et al. Exact Combinatorial Optimization with Graph Convolutional Neural Networks, NeurIPS 2019
[8] Cappart et al. Combinatorial Optimization and Reasoning with Graph Neural Networks, JMLR | null | null | null | null | null | null |
SDE Matching: Scalable and Simulation-Free Training of Latent Stochastic Differential Equations | Accept (poster) | Summary: This paper introduces SDE Matching, a novel simulation-free method for training Latent Stochastic Differential Equations (SDEs). Traditional training of Latent SDEs relies on adjoint sensitivity methods, which are computationally expensive due to numerical integration and backpropagation through SDE solutions. SDE Matching addresses this limitation by leveraging connections with Score and Flow Matching techniques used in generative modeling, by directly parameterizing the marginal posterior distributions of the latent SDE, thereby obviating the need for SDE simulation during training.
## Update after rebuttal
My score remains the same.
Claims And Evidence: The central claims are that SDE Matching enables scalable and computationally efficient training of Latent SDEs, achieving performance on par with adjoint sensitivity methods. The paper provides experimental evidence on both synthetic (3D stochastic Lorenz attractor) and real-world (motion capture) datasets. Results demonstrate that SDE Matching achieves comparable or slightly better performance and faster convergence compared to adjoint sensitivity methods.
Methods And Evaluation Criteria: The paper introduces SDE Matching, which involves parameterizing the posterior marginal distribution and deriving a conditional ODE and SDE. The evaluation metrics used include the Negative Evidence Lower Bound (NELBO) for training convergence and Test Mean Squared Error (MSE) on a motion capture dataset for performance evaluation.
Theoretical Claims: N/A
Experimental Designs Or Analyses: N/A
Supplementary Material: N/A
Relation To Broader Scientific Literature: The proposed methodology builds upon and extends the literature on Latent SDEs, Neural ODEs, and simulation-free training methods such as Score and Flow Matching in generative models.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
- Innovative and efficient simulation-free training framework for Latent SDEs.
- Significant reduction in computational cost and faster convergence demonstrated empirically.
Other Comments Or Suggestions: N/A
Questions For Authors: - Can you provide a more detailed comparison of the training and inference wall-time for SDE Matching versus adjoint sensitivity methods, especially for the motion capture dataset?
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: We are delighted to see that the reviewer finds our approach Innovative, efficient and note the reduction in computational cost of training. Below, we address the questions raised in the review.
**Questions:**
In all our experiments, including the 3D stochastic Lorenz attractor, the motion capture dataset, and additional experiments (see rebuttal to TN6r, Question 3), with the same parameterization and training hyperparameters (such as the number of training steps), SDE Matching requires approximately $5$ times less computation time than the adjoint sensitivity method per iteration. Asymptotically, a single training iteration of SDE Matching takes $\mathcal{O}(1)$ time, while the adjoint sensitivity method takes $\mathcal{O}(L)$, where $L$ is the number of steps in the simulation of the posterior SDE (Eq. 2). However, in practice, the exact training time depends not only on the length of simulation, but also on the evaluation cost of other components, such as the calculation of the prior and reconstruction losses (Eqs. 22 and 24), which affects the actual ratio.
Additionally, as demonstrated in Figure 2, SDE Matching may exhibits significantly faster convergence compared to the adjoint sensitivity method, further accelerating the overall training procedure. When combining the per-iteration improvement and the convergence speed improvement SDE Matching is ~500 times faster than the baseline in the experimental setup from Section 4.1.
At the same time, in SDE Matching, the generative model defined by the prior process (Section 4.1) is exactly the same as in training the Latent SDE using the adjoint sensitivity method. Therefore, the inference time for unconditional sampling is identical for both approaches. However, as discussed in Section 4.4, in the case of forecasting, if we have access to partial observations $x_{t_1}, \dots, x_{t_N}$, SDE Matching enables sampling of the latent state $z_{t_N}$ at the time of the last observation $t_N$ in $\mathcal{O}(1)$ time. In contrast, the conventional parameterization of the posterior process requires simulating the conditional SDE up to $t_N$. This property of SDE Matching can significantly reduce inference time when observations span a long period. However, in our experiments, we only have access to $3$ samples, all close to $t = 0$. Consequently, most of the inference time is spent simulating the prior process from $t_N$, making the forecasting inference time nearly equal for SDE Matching and the adjoint sensitivity method.
We would like to note that, in principle, SDE Matching allows simulation-free sampling of latent states $z_t$ at arbitrary time steps, potentially enabling fully simulation-free interpolation and forecasting in $\mathcal{O}(1)$ time. However, such inference of the posterior process would require a corresponding training procedure in which the model observes only a few early observations. Otherwise, the posterior process may produce biased samples. | Summary: The author(s) proposed SDE-matching, a simulation-free method to fit latent SDE models. The key idea is to use a differentiable normalizing flow method to learn the Markovianization of the posterior SDE and match the probability flow ODE defined by the normalizing flow to get back the SDE.
Claims And Evidence: The claim that the methods can scalably and simulation freely solve latent SDE seems well supported theoretically but not very well tested in experiments.
Methods And Evaluation Criteria: Yes, the method is designed to learn time series with latent SDE, and the paper tested whether the learned latent SDE will predict the time series in both simulated and real data experiments.
Theoretical Claims: There are not many theories. Majority of the results are known.
Experimental Designs Or Analyses: The design is on par with the original latent SDE method and is well-designed. I would appreciate if there are a bit more low dimensional SDE being shown like Fig.1 but it is not necessary.
Supplementary Material: All of them, I successfully repeated a slightly modified version of the experiment in Fig.1 myself using the author's Gaussian architecture as well as realNVP architecture.
Relation To Broader Scientific Literature: - Clarifying what feature made the diffusion model, as a special case of latent SDE simulation free is very insightful.
- Time series modeling with latent SDE is useful in broad scientific fields.
Essential References Not Discussed: Not off the top of my head.
Other Strengths And Weaknesses: - The paper has enough details to reproduce without a code-base.
- Generally well written.
- Clarified why diffusion model can be simulation free as a latent SDE.
Other Comments Or Suggestions: - I think Table 1 is misleading. The proposed method does not provide a gradient over parameters w.r.t. SDE solutions while all other methods do. The proposed method is, in fact, *avoiding* such calculation, but Table 1 could be interpreted as the proposed method could provide a gradient in $O(1)$ time and space which is not true.
- I encourage the author(s) to provide more intuition on why the method could avoid the burden of numerically solving SDE: e.g., is numerically solving SDE provide information that is not necessary, or we implicitly solved the SDE with some NN that are parallelizable so the burden is transformed into training which can be scaled, or any other intuition.
Questions For Authors: 1) This may not be a real question. But when I tried to reproduce the paper with realNVP, it felt a lot like implementing a physics-informed neural net (PINN), where you have a network approximating solutions of PDE, and in this case, I believe the normalizing flow actually solves the Fokker-Plank equation so maybe it can be seen as a PINN. I wonder if there is a connection.
2) I think in general a difficulty cannot magically go away. I wonder if the author(s) can comment if the difficulty of solving SDE was absorbed into training the normalizing flow. The difficulty here is we need to know the solution of posterior SDE and the author(s) experiment suggests that knowing the marginal seems to be enough, but we still need to approximate it.
3) this is connected to my second question. The authors used only a linear model for posterior SDE. When I tried realNVP it was much harder to train (strongly depends on hyperparameter tuning and takes large epochs, maybe it is just my implementation). To what extent does the success depend on the sampling rate in the data being relatively high so that distributions in between can be approximated with some Gaussians, and if one wants to model low sampling rate data, will the difficulty of learning the (unseen) marginals become more problematic? If time permits, can the author try a different sampling rate in the Lorenz experiment?
4) The objective (23) has $g^{-1}$ in it while $\bar{f}_{\theta,\varphi}$ is itself not scaled by $g$, will this cause numerical issue when $g$ is small?
5) Will eq. 27 imply Gaussian marginals?
6) Will it be more useful to let eq.16 also take the time $(t_1, t_2, ... t_N)$ so some smoothness can be used especially when there are multiple time series taken with different times in data?
7) What if losses in eq. 21 have vastly different scales e.g., the data has very little noise?
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: We are pleased that the reviewer finds our claims to be well supported theoretically, the experiments well designed, and the discussions insightful. We are especially grateful that the reviewer took the time to reproduce our experiments. We sincerely thank the reviewer for such attention to our paper and for the valuable feedback. In response to the comments and questions raised, we provide the following clarifications and commitments.
**Other Comments**
1. Indeed, in SDE Matching we do not explicitly solve any SDE during training. Instead, we parameterize the posterior process in such a way that allows us to estimate the objective function in $\mathcal{O}(1)$ space and time. The purpose of Table 1 is primarily to reflect the computational budget in terms of number of drift/diffusion term evaluations per training iteration.
Nevertheless, we would like to note that in SDE Matching, when sampling latent variables $z_t$ to estimate the diffusion loss (Eq. 23), we sample them from the posterior marginals $q_\phi(z_t|X)$, which, by design, are solutions of the posterior SDE (Eq. 19). Thus, during optimization, we are effectively computing gradients with respect to the solutions of the posterior SDE.
2. In the Latent SDE model, training essentially requires two things: the ability to sample from the posterior marginals $q_\phi(z_t|X)$ and access to the posterior SDE. With the conventional parameterization, we directly define the SDE via its drift, which necessitates numerical simulation in order to sample from the unknown marginals.
The high-level idea of SDE Matching is to define the posterior process in a different order: we first parameterize a sampler of the marginal distribution and, based on it, derive the posterior SDE. Therefore, we may say that sampling from $q_\phi(z_t|X)$ implicitly solves the posterior SDE.
It is also important to emphasize that the correspondence between the posterior SDE and its marginals in SDE Matching is exact, not approximate.
**Questions:**
1. There is a connection with PINNs in the tools used to define the model. Like PINNs, we use automatic differentiation to compute time derivatives (Eq. 18) and score functions (Eq. 26). We also employ a partial differential equation (the Fokker–Planck equation) to establish connections between elements of the dynamical system.
However, unlike typical PINNs that solve PDEs, we use similar mechanics to compute coefficients of an SDE based on its solutions. So, while we believe there are conceptual connections, these are significantly different methods solving different problems.
2. The difficulty of solving the posterior SDE is reflected in the flexibility of the reparameterization function $F_\phi(\epsilon,t,X)$ (Eq. 16). As discussed in Section 7, the SDE Matching parameterization limits the flexibility of the posterior process.
If the true posterior process is simple and has tractable marginals, solving it should not be computationally expensive. However, if the posterior is complex, an insufficiently flexible parameterization may not accurately capture the underlying dynamics.
How complex the posterior latent process needs to be is an open question. Especially in the presence of a flexible observation model.
3. In this work, we chose a simple parameterization for the posterior process in order to stay close to the setup of Li et al. However, the reviewer’s observations motivate us to explore more expressive parameterizations, and we plan to include those results in a future revision.
In general, we believe it may be more challenging to marginalize posterior processes of more complex forms, and that the results could be more sensitive to architectural choices in the parameterization network.
We believe that with denser observations, the posterior process may be better approximated by Gaussian marginals. In contrast, when observations are sparse, intermediate distributions tend to resemble the unconditional marginals, which may have arbitrary shapes.
4. Small values of $g_\theta$ may introduce numerical instability, however this issue is not specific to SDE Matching, as the term involving $g_\theta^{-1}$ appears in the ELBO of Latent SDE models in general.
5. Yes, Eq. 27 implies that the posterior marginals $q_\phi(z_t|X)$ are conditionally Gaussian.
6. Yes, providing time steps to the reparameterization function $F_\phi$ makes perfect sense when working with observations at arbitrary time points.
7. In practice, the terms in the objective (Eq. 21) may indeed have different scales (e.g., if the observation model has very low variance). However, the total variational bound remains valid, and all terms should still be minimized to match the true dynamics.
We trust that the clarifications and additional discussions will strengthen your support for acceptance! If accepted, we will update the camera-ready version to reflect this discussion.
---
Rebuttal Comment 1.1:
Comment: Thank the authors for the clarification!
- Right the correspondence between the marginal posterior SDE and its marginals in SDE Matching is exact. I was probably still thinking about the formalism of latent SDE but in SDEmatching the SDE is implicitly defined and marginals matched exactly. Thanks for the clarification.
- I think I understand the $O(1)$ space and time being the cost during training. My comment is more because the original papers reported these big-O notations for the task SDE matching tried to not do that for some readers might get confused. I think the table should be there, but I encourage the author to make a note saying this is measured for training time rather than solving SDE and maybe an intuition on how SDEmatching avoided it (again, a difficulty probably won't magically go away and a curious reader would probably want to know how it happened when reading this super encouraging table).
- Please include some of the discussions as you see fit in a revision. I am looking forward to it.
Again, thank the authors for your time and work. I think it is a very cool paper worth to be seen for many reasons and I have raised my score.
---
Reply to Comment 1.1.1:
Comment: We will include the clarifications, discussions, and additional experimental results in the revised version of the paper. We sincerely thank the reviewer for the kind words, effort, and constructive feedback. We believe this review was a great help in improving the quality of our work. | Summary: This paper improves the method of Course & Nair for variational inference in latent SDEs in 2 ways: A better recognition network and more flexible marginals through normalizing flows.
Claims And Evidence: The claims are basically that it's a fast and flexible approach. Also that it's much faster than the Sota in terms of predictive accuracy, Li et al. However I don't think the speed claim was actually verified empirically (though I believe them).
Methods And Evaluation Criteria: Just argumentation and a few small-scale experiments.
Theoretical Claims: The motivations and connections in section 3 are spot on, make sense, and are well-explained. There aren't really any theorems but I don't think there need to be.
Experimental Designs Or Analyses: There are 2 medium-scale experiments. Not much math. But it's such a sensible method I don't mind.
Supplementary Material: no
Relation To Broader Scientific Literature: This is well-discussed in the paper, pointing out that this is bringing ideas from diffusion models to latent SDE inference (using normalizing flows to match marginals)
Essential References Not Discussed: Maybe the Nature version of the Course & Nair work.
Other Strengths And Weaknesses: Weaknesses:
- Still using the mocap experiment (introduced in 2019) as the largest experiment. I guess it's a pain to re-run Li et al but that was 5 years ago, and seems pretty small now.
- The similarity to Course & Nair. however, the simplicity and better perf of the new version make this OK.
- didn't include a time comparison on the mocap experiments. As it stands, it's not clear what the pareto curve for speed vs accuracy is.
Other Comments Or Suggestions: "Similarly, interpolation can be performed by inferring only the posterior process dynamics" not clear what this means.
Would love to see more discussion of to what extent matching marginals limits the tightness of the ELBO.
Questions For Authors: Why do you think your method didn't match Li et al's performance on mocap? Should it be able to, in principle?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We appreciate the reviewer’s positive feedback regarding the speed, simplicity, and sensibility of our method, as well as the discussion of its connections to diffusion models. Below, we address the questions and comments raised in the review.
**References:**
- We will cite the *Nature* paper by Course & Nair in the camera-ready version if accepted.
**Weaknesses:**
1. To demonstrate the scalability of SDE Matching, we provide additional experiments (please refer to rebuttal to TN6r, Question 3).
2. We would like to point out that, compared to the work of Course & Nair, in addition to allowing more flexible marginals of the posterior process, SDE Matching also supports a state-dependent diffusion term $g_\theta(z_t,t)$. This is important in cases where the underlying dynamics exhibit state-dependent volatility.
To demonstrate this difference, we designed an experiment similar to the setup in Section 4.1, using a stochastic Lotka–Volterra system with a dynamic of the following form:
$dx=(\alpha x-\beta xy)dt+\sigma xdw$, $dy=(\delta xy-\gamma y)dt+\sigma ydw$
We then applied SDE Matching to train models with both state-independent and state-dependent volatility functions. Visualisations of the learned trajectories are available at the anonymised link: https://imgur.com/a/jh8sM0Q. It is evident that the model with state-independent volatility fails to capture the correct form of the trajectories.
3. Please refer to the rebuttal to JkpK for the discussion on training and clarifications on inference (including interpolation).
**Other Comments:**
We would like to highlight that, in contrast to methods such as Flow Matching, both SDE Matching and the adjoint sensitivity method do not match marginals. Instead, they match the distributions of trajectories of the posterior and prior processes. SDE Matching essentially proposes an alternative parameterization of the posterior process that, by design, enables training of the Latent SDE model by minimising the same objective, but in a simulation-free manner.
Nevertheless, the question of the limitations on the tightness of the ELBO in SDE Matching is interesting. Due to the limited space, we may not include rigorous derivations, but we outline the theoretical aspects of this question below.
In the case of the Latent SDE, the variational bound becomes tight when the posterior process matches the true posterior of the prior process.
The prior process (Eq. 15) is given by:
$dz_t=h_\theta(z_t,t) dt+g_\theta(z_t,t)dw$
Given a series of observations $X$, the true posterior process can be derived via Doob’s $h$-transform, yielding:
$dz_t=\Big[\overbrace{h_\theta(z_t,t)+g_\theta(z_t,t)g^\top_\theta(z_t,t)\nabla_{z_t}\log p_\theta\left(X_t|z_t\right) }^{h_\\theta(z_t,t,X)} \Big] dt+g_\theta(z_t,t)dw,$
where $X_t=\\{x_s:x_s\in X,t\leq s\\}$ denotes the set of future observations from time $t$ onward.
We can also consider the corresponding deterministic process that follows the true posterior marginals $p_\theta(z_t|X)$:
$$\frac{dz_t}{dt}=\bar{h}^\theta(z_t,t,X)=h_\theta(z_t, t)+g_\theta(z_t,t)g^\top_\theta(z_t,t)\left[ \nabla_{z_t}\log p_\theta\left(X_t|z_t\right)-\frac{1}{2}\nabla_{z_t}\log p_\theta\left(z_t|X\right)\right]-\frac{1}{2}\nabla_{z_t}\cdot\left[g_\theta(z_t,t)g^\top_\theta(z_t,t)\right]$$
Now, consider the approximate posterior process (Eq. 19):
$d z_t=f_{\theta,\phi}(z_t,t,X)dt+g_\theta(z_t,t)dw$
The approximate process matches the true posterior process if the drift terms are equal: $f_{\theta,\phi}(z_t,t,X)\equiv h_\theta(z_t,t,X)$, or equivalently, if the corresponding deterministic processes (Eq. 17) match: $\bar{f}^{\theta,\phi}(z_t,t,X)\equiv \bar{h}^\theta(z_t,t,X)$. In terms of the reparameterization function $F_\phi(\epsilon,t,X)$ (Eq. 16) that defines the approximate posterior process, we may say that the variational bound becomes tight, and the approximate posterior process matches the true posterior, if $F_\phi$ learns the solution trajectories of the ODE defined by $\bar{h}_\theta$.
Therefore, with a sufficiently flexible reparameterization function $F_\phi$, the SDE Matching approach should, in principle, be capable of making the variational bound tight.
**Questions:**
SDE Matching shows similar performance to Li et al. as there is an overlap of the confidence intervals. We attribute the slightly better performance of Li et al. to a suboptimal parameterization of the posterior process. In this work, we intentionally kept the parameterization as close as possible to the conventional setup from Li et al. to ensure a fair comparison. In principle, with a sufficiently flexible parameterization, SDE Matching should demonstrate comparable performance.
We will include additional discussions and experimental results with detailed setup explanations in the camera-ready version. We trust these clarifications, highlighting the novelty and scalability of our work, will enhance your support for acceptance!
---
Rebuttal Comment 1.1:
Comment: I appreciate that a state-dependent noise term is necessary to model state-dependent noise. This is a valid contribution but seems kind of minor.
I also appreciate the stochastic Lotka–Volterra experiments, but would much rather have seen a plot of the ELBO matching a known marginal likelihood!
I hadn't appreciated that this paper is optimizing the same ELBO as Li et al.
Your argument that you could make the ELBO tight seems reasonable. But I would have loved to see just a single toy experiment fitting a simple SDE with a known marginal likelihood to show it empirically. (and to see what the gradient variance does during training)
Overall I keep my 4 rating because the point of the paper is scalability but the experiments are small.
---
Reply to Comment 1.1.1:
Comment: We are glad that the reviewer appreciates our theoretical discussion on the tightness of the ELBO in SDE Matching. Below we address additional comments raised and provide experimental validation.
First, we would like to comment on the importance of state-dependant volatility in Latent SDEs. State-dependant volatility is often a relevant property of many dynamical systems in e.g. finance [1], biology [2], neuroscience [3], and causal inference [4], where Latent SDEs can be applied for modelling. The Lotka–Volterra system which we use in the rebuttal experiment is an example of such a biological system [2]. In Neural SDEs, state-dependant volatility also leads to dynamics that is more robust to distribution shift [5]. Finally, the state-dependant volatility is an important contributing factor in our MOCAP experiment (Section 5.2), where the state-dependent SDE Matching and [6] both perform much better than the state-independent approach [7]. Therefore, we believe that, together with more general marginals of the posterior process through normalising flows, enabling simulation-free training with state-dependant volatility is also an important contribution of SDE Matching.
Second, to empirically validate the tightness of the ELBO in SDE Matching we setup a linear stochastic system experiment of the form:
$dx_t=F(t)x_tdt+L(t)dw,\quad y_t=H(t)x_t+r_t,\quad r\sim\mathcal{N}(0,R(t))$
For this system, the true log-marginal likelihood is available through the Kalman filter [8]. In our experiment we see that the SDE Matching ELBO indeed converges to the true log-marginal likelihood. Moreover, similar to our experiment from Section 5.1, SDE Matching demonstrates much faster convergence compared to [6] and takes about 20 times less time per training iteration. Additionally, we see that the SDE Matching parameter gradient estimates have consistently lower norm and variance. We provide visualisations of the training dynamic by anonymised link: https://imgur.com/a/D9QXx2a.
Finally, we would like to demonstrate the difference in performance of SDE Matching compared to adjoint sensitivity approaches in a more high dimensional experiment. We model sequences of 32x32 images, i.e. videos, depicting a moving pendulum. Using identical number of iterations (~20k), SDE Matching successfully learns the dynamics in about 20 minutes on single GPU, while the adjoint sensitivity requires about 30 hours for the same number of iterations and still fails to accurately capture the underlying dynamics. We provide visualisations of generated samples by anonymised link: https://imgur.com/a/8fdV2sD.
We will add all additional discussions and experiment results, along with detailed descriptions of the setup, in the camera-ready version, if accepted.
We see no reason why SDE Matching should not scale to even higher dimensional problems, like real world video generation. However, this would require significant computational resources, time and engineering work outside the scope of this paper and rebuttal, so we leave it for future research. Nevertheless, our experiments demonstrate that SDE Matching, compared to the adjoint sensitivity method, has more stable gradients (see experiment with known likelihood above), is robust to scaling of the length of integration (see rebuttal to TN6r, Question 3), requires many times less compute per training iteration and demonstrates faster convergence across a variety of experiments that together results in speedups of several orders of magnitude (see Section 5.1 and the experiment with moving pendulum above). Therefore, we believe, that our experiments clearly demonstrate the scalability of SDE Matching.
We hope that the additional experiments and clarifications of SDE Matching’s scalability will strengthen your support for our paper.
[1] Oksendal, Bernt. ”Stochastic differential equations: an introduction with applications.”, Chapter 12
[2] Vadillo, F. "Comparing stochastic Lotka–Volterra predator-prey models.”
[3] ElGazzar et al. "Generative Modeling of Neural Dynamics via Latent Stochastic Differential Equations."
[4] Peters et al. "Causal models for dynamical systems."
[5] Oh et al. "Stable neural stochastic differential equations in analyzing irregular time series data.”
[6] Li et al. “Scalable gradients for stochastic differential equations”
[7] Course et al. "Amortized reparametrization: efficient and scalable variational inference for latent SDEs.”
[8] Särkkä et al. ”Applied stochastic differential equations”, Chapter 10 | Summary: This paper builds on the observation that the reverse process in score-based diffusion models can be seen as a neural SDE (as fundamentally it is a process with a parameterized drift). Then the authors try to exploit this connection to develop a simulation-free training scheme for latent SDEs.
Claims And Evidence: The main claim of this paper is that the authors propose a "simulation-free" (definition of which wasn't made clear, see my question below) method for training a latent SDE. The derivation is provided and some experimental results support the claims - although not comprehensive.
Methods And Evaluation Criteria: The paper evaluates the training method on some benchmark problems. Although, it can be definitely said that the evaluation is not comprehensive.
Theoretical Claims: N/A
Experimental Designs Or Analyses: Experiments include two main parts, synthetic datasets and the motion capture dataset. While these experiments produce reasonable results, similar papers however include more examples, typically, e.g. moving MNIST or bouncing balls, and similar. I will return to this point in my questions.
Supplementary Material: Yes, all of it (only 1 page).
Relation To Broader Scientific Literature: This is a continuation of a long line of papers in latent SDEs. Typical methods require long simulations, whereas the current method tries to avoid it; in that sense, it has a distinct purpose.
Essential References Not Discussed: none
Other Strengths And Weaknesses: See my comments/suggestions - questions.
Other Comments Or Suggestions: 1) please define simulation-based and simulation-free methods more precisely. Do not assume that every reader knows exactly what you mean by these.
Questions For Authors: 1) The paper essentially tries to formulate the posterior distribution in a latent SDE as a pushforward or some simple distribution. This feels like it is similar to consistency models - can authors elaborate on this comparison?
2) I am not totally convinced that the extra cost of learning the pushforward mapping makes the method really efficient overall w.r.t. simulation-based methods. Figure 2 shows fast convergence, but not in computation time, but in iterations. Could you plot the same graph for computational cost, including any pretraining?
3) Is this method scalable after all? Earlier papers (see my earlier comment) have various image experiments.
4) Is there any scope for theory, assuming that the pushforward measure is accurate enough? Of course, this depends on what's out there for latent SDEs already, but worth discussing.
5) My final comment about this paper is that it falls short of sufficient demonstration of the costs and behaviour of this method. To be clear, I am not interested in to see that this method beats all other baselines - as authors noted, this method can probably also be used in other baseline methods. However, authors should clearly demonstrate via a series of detailed experiments the behaviour and scalability of this method, even if the results are partially negative. In the current paper, the results are thin and not comprehensive, making it unclear whether this method is sufficiently explored.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank the reviewers for their valuable feedback, which helps us to improve the paper. Below, we address the questions and comments raised in the review.
**Other Comments:**
We apologise for any confusion regarding terminology. Allow us to provide a clearer definition of the term “simulation-free”.
In the diffusion literature, simulation-free implies that explicit simulation of dynamics (numerical integration) is not required during training. For example, the adjoint sensitivity method [1] requires numerical simulation of the posterior SDE (Eq. 2) to sample latent states $z_t \sim q_\phi(z_t|X)$ to evaluate the loss function (Eq. 5). In contrast, thanks to our alternative parameterization of the posterior process, SDE Matching allows, by design, direct sampling of $z_t$ via inference of the reparameterization function $F_\phi(\epsilon, t, X)$ (Eq. 16), eliminating the need for numerical simulation of the posterior SDE. This makes the training process simulation-free.
**Questions:**
1. Consistency Models (CM) as originally introduced in [2] learns a function $f_\theta(x_t, t)$ that approximates the solutions of a fixed marginal ODE starting at $x_t$ and ending at some $x_0 \sim p_{data}(x_0)$.
In SDE Matching, we introduce a reparameterization function $F_\phi(\epsilon, t, X)$ (Eq. 16). Based on $F_\phi$, we derive a conditional ODE (Eq. 17) and then a conditional SDE (Eq. 19) that define the posterior process.
While both approaches involve a pair of an ODE and its solver, the nature of these ODEs differs: in CM, the goal is to approximate solutions of an unconditional ODE, whereas in SDE Matching we derive an exact ODE as an intermediate step used to define a conditional SDE. Thus, while there is a connection, they are fundamentally different approaches.
2. SDE Matching does not incur additional learning cost by parameterizing the posterior process via the reparameterization function $F_\phi(\epsilon, t, X)$ (Eq. 16) — this is a central point of our approach.
Unlike diffusion models, the posterior process in a Latent SDE is not parameter-free. It is a complicated process conventionally defined by the drift function $f_\phi(z_t, t, X)$ in the SDE (Eq. 2), and sampling from the posterior requires simulating this SDE.
By reparameterizing the posterior process, we neither introduce new parameters nor increase the complexity of the dynamics. Instead, we reparameterise the same dynamics in a different way, enabling direct sampling of latent variables $z_t$ from the posterior marginals without numerically integrating the SDE.
The key advantage of SDE Matching is that a single training iteration takes asymptotically less time (see rebuttal to JkpK). As discussed in Section 5.1 (lines 320–322), for the 3D Lorenz attractor dataset, one iteration of SDE Matching takes approximately $5$ times less time. Figure 2, while not the main result, additionally shows that SDE Matching not only has faster iterations but also converges more quickly.
3. To demonstrate the scalability of SDE Matching, we provide two additional experiments.
First, to evaluate scalability with respect to time, we use the experimental setup described in Section 4.1 and compare the gradient norms of the objective function with respect to the model parameters for both SDE Matching and the adjoint sensitivity method. When integrating over time horizons $T \in {1, 2, 5, 10}$, the adjoint sensitivity method yields the following $\log_{10}$-based gradient norms: $6.26 \pm 0.14$, $6.95 \pm 0.20$, $7.91 \pm 0.23$, and $8.82 \pm 0.28$. This demonstrates that the gradient norms grow exponentially as the time horizon increases.
In contrast, SDE Matching maintains a stable $\log_{10}$-based gradient norm of $4.92 \pm 0.24$ across all time horizons, indicating better stability for long time series modelling.
Second, to demonstrate scalability with respect to dimensionality, we designed an experiment where the model learns a sequence of images (a video) depicting a moving pendulum. SDE Matching successfully captures the underlying dynamics and generates realistic samples.
You can find examples of generated sequence at the anonymised link: https://imgur.com/a/aMfSuHB.
4. Please refer to rebuttal to Reviwer C8BY (section “Other Comments”), where we discuss the tightness of the variational bound in SDE Matching.
5. We hope that the clarifications highlighting the efficiency of our approach, along with additional discussion and experimental results demonstrating the scalability of SDE Matching, will strengthen your support for the acceptance of our paper.
We will include clarifications and additional results, along with detailed explanations of the experimental setups, in the camera-ready version if accepted.
[1] Li et al. “Scalable gradients for stochastic differential equations”
[2] Song et al. “Consistency models”
---
Rebuttal Comment 1.1:
Comment: Many thanks - can you elaborate how the images are generated? Are these reconstructions or generations where the SDE is simulated and then sampled through the likelihood?
---
Reply to Comment 1.1.1:
Comment: These images are generated (not reconstructed) samples. In the moving pendulum experiment, to generate the visualizations provided in the rebuttal, we first numerically integrated the learned prior process (the SDE in Eq. 15) and then applied the learned observation model to sample and construct the final outputs (images, in this case).
SDE Matching successfully learns the dynamics in about 20 minutes on single GPU, while the adjoint sensitivity requires about 30 hours for the same number of iterations and still fails to accurately capture the underlying dynamics. For more details and additional experiments demonstrating the superior stability of SDE Matching's gradients compared to the adjoint sensitivity method, please see the Reply Rebuttal Comment to reviewer C8BY. | null | null | null | null | null | null |
Think Smarter not Harder: Adaptive Reasoning with Inference Aware Optimization | Accept (poster) | Summary: This paper targets the problem of solving mathematical problems with LLMs. While the currently prevalent method LongCoT brings promising improvements for mathematical reasoning, they are sometimes unnecessary and cause token waste. To alleviate this issue, the authors propose an algorithm Inference Budget-Constrained Policy Optimization (IBPO), where the problem is formulated as a resource allocation scenario. The budget is assigned with respect to the difficulty level of the problem. IBPO is implemented based on the RL objective of constraint generative policy optimization by replacing it with margin maximization under budget. Experiments on MATH dataset verify the effectiveness of the proposed method. Analyses also prove its design motivation, that difficult problems will get more budget to solve.
Claims And Evidence: The major claims in the paper, specifically regarding the motivation and experiment results, are good to me.
Methods And Evaluation Criteria: The paper is evaluated mainly on MATH dataset, which contains annotations on the difficulty levels of different problems. This setting is natural and could well validate the proposed method, as it claims to allocate different budgets on different questions.
Theoretical Claims: I checked the proposed algorithm and the corresponding equations, all seem sound to me.
Experimental Designs Or Analyses: The overall experiment design makes sense. I have some minor issues or comments:
- The authors demonstrate (specifically in Figure 2 Column 3) that the voting budget can adaptively change w.r.t. the difficulty level of the problem. Apart from the token budget, I am wondering if the authors could also offer accuracy on different difficulty levels. Now there is only overall accuracy in Table 3.
- The design choices of the dataset construction in Section 4 (Appendix B) need more justification. For example, why at most "8 trials" and early stop if an answer appears "3 times"? Would the design choices have a significant impact on the final performance (sensitivity)?
Supplementary Material: I reviewed all the appendices in the paper.
Relation To Broader Scientific Literature: This paper studies a very important and interesting research question of the current community, allowing LLMs to allocate different token budgets for different problems of difficulty levels. This is timely research, especially when o1 and Deepseek styles begin to dominate in reasoning tasks.
In terms of ideas and findings, many concurrent works try to decrease the number of tokens as much as possible while maintaining performance, such as TokenSkip, this paper takes the approach of resource allocation and designs a novel algorithm to do this. While a lot of previous works noticed the correlation between token budget and problem difficulty, they are mostly doing direct preference alignment. The algorithm proposed in this paper is valuable.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: See the above review.
Other Comments Or Suggestions: See the above review.
Questions For Authors: See the above review.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you very much for your thorough review and valuable feedback! We greatly appreciate your insightful suggestions and positive assessment!
---
> The authors demonstrate (specifically in Figure 2 Column 3) that the voting budget can adaptively change w.r.t. the difficulty level of the problem. Apart from the token budget, I am wondering if the authors could also offer accuracy on different difficulty levels. Now there is only overall accuracy in Table 3.
| Level | 1 | 2 | 3 | 4 | 5 | Overall |
|--------------------|---------------|----------------|----------------|----------------|----------------|----------------|
| # of problems | 43 | 90 | 105 | 128 | 134 | 500 |
| q₊ = 0.25 | 93.02% (40) | 76.67% (69) | 64.76% (68) | 48.44% (62) | 23.88% (32) | 54.2% (271) |
| q₊ = 0.5 | 83.72% (36) | 80.00% (72) | 66.67% (70) | 52.34% (67) | 23.88% (32) | 55.4% (277) |
| q₊ = 0.75 | 90.70% (39) | 77.78% (70) | 74.29% (78) | 51.56% (66) | 23.88% (32) | 57.0% (285) |
Absolutely. We break down the overall accuracies reported in Table 3 by difficulty level in the table above (numbers in parentheses indicate the number of problems solved). Some observations are:
- With larger budgets, we observe improved performance on the harder levels (3 and 4), as more voting budget becomes available.
- It is surprising that level 5 performance remains the same across all budgets. We conjecture that this is due to the limitations of the 8B model, which may only solve a subset of the hardest problems.
---
> The design choices of the dataset construction in Section 4 (Appendix B) need more justification. For example, why at most "8 trials" and early stop if an answer appears "3 times"? Would the design choices have a significant impact on the final performance (sensitivity)?
In general, these choices do impact the performance of sequential voting (SV) itself. These choices were made to ensure that SV performs **comparably** to majority voting (MV), a baseline that is more familiar to the community.
- **Reason of chocies**:
- In our observations, SV without early stopping tends to underperform compared to parallel MV. With the current setup, SV achieves performance similar to MV (Figures 2a/2b), which allows for a meaningful comparison between our ASV-IuB-$q$ models and MV.
- We set the trial cap at 8 to avoid unbounded responses. This limit, combined with early stopping, empirically matched MV performance, so we kept it.
Since our key insights lie in the RL component, we found that aligning SV with parallel MV is a reasonable choice, as it allows for: (i) a sufficient reward margin for optimization, and (ii) a fair comparison to a community-standard baseline (MV).
---
Once again, we gratefully thank the reviewer for the insightful suggestions and positive evaluation! We hope our clarifications have adequately addressed your questions. We sincerely appreciate your support and will carefully revise the manuscript to further improve its clarity! | Summary: This paper proposes IBPO to optimize reasoning length allocation in large language models (LLMs). While extended reasoning chains improve accuracy, they often lead to inefficiencies by applying unnecessary long reasoning to trivial queries. IBPO formulates this as a constrained reinforcement learning (RL) problem, categorizing responses into different length groups and imposing density constraints to allocate inference budgets adaptively.
Empirical results show that IBPO improves efficiency, achieving accuracy gains on MATH500 over LLaMA3.1 8B Instruct, with efficiency gains compares to self-consistency. The paper details IBPO’s derivation, implementation and experiments.
Claims And Evidence: Yes. The claims made in the submission are supported by clear and convincing evidence.
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes, I think they have no issues.
Experimental Designs Or Analyses: Yes, I checked. I think they have no issues.
Supplementary Material: I have reviewed all the appendices and briefly browsed the code.
Relation To Broader Scientific Literature: This work contributes to the broader scientific discourse on reasoning in large language models (LLMs), particularly in mathematical problem-solving and efficient inference. It builds on foundational research in chain-of-thought (CoT) prompting, which demonstrates that decomposing reasoning into explicit steps improves problem-solving accuracy. While CoT and its extensions—such as self-correction and multi-turn reasoning.
Essential References Not Discussed: To the best of my knowledge, there are no essential related works that are missing from the citations or discussion in the paper.
Other Strengths And Weaknesses: Strengths:
(1) The method is rooted in constrained reinforcement learning (RL) and resource allocation theory, providing a rigorous framework for optimizing inference budgets.
(2) IBPO aims to balancing inference cost and reasoning accuracy by dynamically adjusting reasoning length based on problem difficulty, reducing unnecessary computational overhead.
Weaknesses:
(1) The paper frequently refers to extended CoT (or long CoT) but selects SV as the representative for extended CoT. This deviates significantly from the standard academic understanding, where extended CoT is typically represented by models like O1 and R1, which focus on deeper rather than broader reasoning (e.g., majority voting). Since the proposed method has not been evaluated on R1 (O1)-like extended CoT, its effectiveness in such settings remains uncertain.
(2) According to my understanding, SV generate different trails sequentially, considering the quadratic complexity in transformer-based models, SV can result in longer inference times compared to Majority Voting (MV), where trails are generated in parallel. What’s more, the paper uses trails per response as the inference budget metric, which has two key issues:
1. Trail count does not directly correspond to token count, whereas token budget would be a more practical and meaningful measure.
2. Despite a lower token budget, the sequential nature of SV may lead to longer inference times compared to parallel methods like MV. Additional runtime experiments comparing MV, SV, and ASV should be conducted to verify whether the proposed method increases inference time. If the approach actually extends inference time, its practical value is questionable.
(3) While the core idea of IBPO is concise, the formulation in the paper contains substantial redundancy, which hinders readers from extracting the key information efficiently.
(4) In Table 3, the IBPO experiments are conducted on LLaMA3.1-8B, whereas S3C and Self-Refine utilize multiple models different from LLaMA3.1-8B. This inconsistency weakens the rigor of the comparison, making the evaluation less reliable.
Other Comments Or Suggestions: (1) The authors should simplify the formulation appropriately to improve the readability of the paper.
(2) The authors should supplement the paper with experiments comparing the inference time overhead of MV, SV, and ASV to provide a more comprehensive evaluation.
Questions For Authors: No other question for authors, please see the weaknesses.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We sincerely appreciate your time in assessing our paper and your thoughtful feedback.
---
We’d like to first clarify a possible **misunderstanding** regarding the **role of sequential voting** (SV): it is **not** intended as a significant contribution of this work.
**Role of SV:** It is a **simple, constructive alternative** to o1/R1-style long CoT, with **extended length** and **reasonable performance gains** over conventional CoT.
- **Why an alternative**: As o1 is proprietary and R1 was released on Jan 20, ~10 days before the submission deadline.
- **Why SV**:
- **Simple**: A minimal construction that allows us to focus on our RL contribution without the distraction of engineering long responses;
- **Characteristics**: (i) gains over standard CoT; (ii) extended length.
- SV resembles longCoT in these characteristics (though its gains over CoT are moderate), enabling us to demonstrate the effectiveness of our RL algorithm.
- **What do we expect from SV?**:
- **Superior accuracy?**: No. As shown in Fig 2, SV performs comparably to parallel majority voting (MV). We expect advanced reasoning methods to outperform MV, and hence SV.
- **Practical value?**: No. The main insights we convey do **not** lie in SV. After all, it is a dummy construction used to highlight our RL algorithm, which carries the core insights of this work.
We understand the concern that SV may not fully capture how o1/R1 works fundementally. Due to the **unavailability** of R1, we construct SV that at least resembles longCoT in terms of the aforementioned characteristics.
Given the considerations above, we believe our construction is a fair and reasonable choice for **illustrative** purposes.
---
To reiterate, our core contributions are:
- (i) casting adaptive reasoning as constrained inference;
- (ii) designing a constrained RL algorithm — which merits particular emphasis — that is simple and grounded.
In addition, the final **accuracy** stems from **two orthogonal axes**: (i) **the reasoning axis**; and (ii) **the RL axis**.
$$
\underbrace{\text{constraint satisfaction} \to \text{adaptive allocation}}_{\text{the RL axis}} \to \text{final accuracy} \leftarrow \text{SV (the reasoning axis)}
$$
The derivation of our algorithm and the ''upstream'' metric (constraint satisfaction) are theoretically **agnostic** to the choice of long-response.
We intentionally kept the reasoning axis simple and did **not** attempt to boost performance through it, so as to isolate and highlight the RL component.
These points collectively suggest that a reasonable construction is sufficient for emphasizing our RL contribution.
---
We hope these discussions clarify our contributions. We believe our RL contribution—unanimously considered as **sound and novel** by other reviewers—merits recognition.
We quote reviewer toYu:
> not only sheds new lights on adaptive reasoning but also provides a valuable algorithmic contribution to constrained RL as a whole.
----
For specific comments:
1. **R1/O1 type models**: We hope the above clarifies our choice of SV, given the unavailability of such models.
2. **Trials as metric**:
1. - This choice was mainly motivated by Table 3. Since the self-correction works don't report token counts, we use the number of trials/turns as a proxy.
- Besides, SV-SFT performs similarly to MV in trials (Figures 2a/2b); and scales comparably in tokens (Figure 5b, Appendix). Hence, trials serve as a reasonable proxy.
2. **Practical value considering inference time**: This is an inherent limitation of any long-form reasoning method like longCoT, not a consequence of our RL algorithm. Substituting SV with O1/R1-style responses would result in similar inference-time overhead.
After all, SV is a dummy alternative to longCoT, and was **not** intended to offer practical value beyond its illustrative purpose.
3. **Table 3**: As noted in Sec. 5.1, Table 3 is not intended to suggest our method outperforms self-correction. These are two **orthogonal** research directions: constrained inference and self-correction.
Its purpose is simply to illustrate that constrained inference can achieve **comparable** performance to **a well-established line of work**. For this purpose, we believe transcribing their results is reasonable—it is convenient and avoids potential discrepancies from re-implementation.
A more informative comparison is Fig. 2, where we evaluate against an **efficiency boundary** interpolating between two extremes of non-adaptive (homogeneous) cases. See our response to reviewer JCKH for details.
---
Again, we sincerely appreciate your suggestions and your assessment that our claims are supported, our theoretical and experimental designs have no issues, and our framework is rigorous.
We will carefully revise the manuscript to further improve clarity based on your suggestions, and we hope our responses have adequately addressed your questions. | Summary: This paper discusses a method for scaling LLM test time compute on adaptive basis based on prompt difficulty. The proposed approach is a novel reinforcement learning technique that allocates more inference to difficult problems (adaptive number of votes - where each vote requires an inference) and fewer votes to easy questions. The proposed method, called Inference Budget-Constrained Policy Optimization (IBPO) is experimentally verified to improve performance on MATH500 dataset - though at a higher test time compute budget (2x).
## update after rebuttal
I thank the authors for their response.
While the response partially addresses my concerns, I am still not confident that the approach generalizes beyond the specific datasets and architectures.
As the authors mentioned, the method is applicable for reasoning settings that are neither easy (85% or more accuracy per model) nor hard (AIME where model accuracy is low). Normally, this would not be a problem, one could adjust the capacity of the model (use smaller / larger LLMs) to show that the approach can be performant at these settings, but the authors mentioned that their approach cannot scale well due to training complexity.
On the other hand, while the authors presented an argument as to why the technique should not be compared with evolved SC variants, I am not convinced. If their approach is orthogonal to the reasoning method, then I would like to see some experiments where more modern reasoning backbones are used when combined with their method.
I am certain that more evolved reasoning baselines such as the ones I recommended need to be compared to, to quantify the method's impact on total token usage versus a simple no fine tuning method.
For this reason I am maintaining my current score.
Claims And Evidence: - IBPO can correctly discriminate easy and hard problems (verified in experiments section e.g. Fig. 2)
- IBPO can allocate resources efficiently by dedicating more inference compute towards hard questions (this is theoretically expected from the way the RL objective is set up and empirically verified to do so.
- The paper claims that its proposed method has an improvement that is in relative terms twice that of vanilla Self Consistency (SC) (I am not actually sure where this is verified. The claim is plausible, but I cannot pinpoint where the 2x efficiency is shown - perhaps I am missing it as the paper is quite dense).
Methods And Evaluation Criteria: 1. The RL method seems correct and novel. I would like to note that while I have understanding of RL, I am not an RL expert thus I would defer to other reviewers to validate my positive evaluation of the proposed method.
2. Evaluation metrics are reasonable. The experimental pipeline is a fair way test for the method.
Theoretical Claims: N/A
Experimental Designs Or Analyses: 1. There does not seem to be a sufficient amount of experiments. Evaluating on MATH 500 is decent choice, but why not on other datasets? Other datasets with mathematical reasoning problems include AIME 2024 (or other years of AIME), SVAMP, ASDIV, AQUA, some big bench hard datasets, etc.
2. I am curious as to why the selected LLMs seems to be small. The experiments go up to an 8B model. Do the performance gains generalize across different parameter sizes? What about other LLM families besides LLAMA?
3. Baseline selection: In the abstract the authors make a point of improving over vanilla self consistency (SC). I am curious if the proposed method competes well against modern SC variants that have been demonstrated to significantly reduce inference costs. Given that vanilla SC is reasonably dated I think it would be fair to compare against [1] and [2].
[1] Let’s Sample Step by Step: Adaptive-Consistency for Efficient Reasoning and Coding with LLMs
[2] Escape Sky-high Cost: Early-stopping Self-Consistency for Multi-step Reasoning
Supplementary Material: I reviewed the appendix.
Relation To Broader Scientific Literature: The work relates to the test time compute literature. This is a major area of research for LLMs. The paper's problem is well motivate.
Essential References Not Discussed: I understand that [1] was mentioned in the introduction section of the paper but I believe that it merits experimental comparison.
[1] Let’s Sample Step by Step: Adaptive-Consistency for Efficient Reasoning and Coding with LLMs
[2] Escape Sky-high Cost: Early-stopping Self-Consistency for Multi-step Reasoning
Other Strengths And Weaknesses: This is polished paper but I personally find it dense to read with a lot of heavy notations. Perhaps it could be made sparser with more references to appendix to make it easier? For example, it was not easy to understand the dataset preparation section.
Other Comments Or Suggestions: N/A
Questions For Authors: - In table 3 it is stated that a lot of the numbers are duplicated from Qu et al. (2024); Yan et al. (2024); Kumar et al. (2024). Did the authors run the code for some of these methods in their setting to make sure that the results reproduce? Is the setting reported from these works identical? For example, are the exact same prompts used in all works in this table?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your insightful feedback!
---
We extend some discussion on **accuracy** to clarify our evaluation design, which also helps explain our choice of baseline later on.
While important, accuracy depends on **two orthogonal axes**: (i) the RL axis; and (ii) the reasoning axis.
$$
\underbrace{\text{constraint satisfaction} \to \text{adaptive allocation}}_{\text{RL}} \to \text{accuracy} \leftarrow \text{SV (reasoning)}
$$
- **RL axis**: We're glad the reviewer agrees the adaptive allocation is ''**theoretically expected**'' and ''**verified**'';
- **Reasoning axis**: (A)SV was intended as a **simple** alternative to longCoT with **reasonable** accuracy, as R1 was unavailable until 10 days before the submission deadline. Empirically, (A)SV performs **comparably** to SC (Fig 2), enabling:
- a sufficient margin for optimization;
- a fair comparison w/ SC, a baseline more familiar to the community.
(SC is used here to match the reviewer’s terminology, though we use MV in paper.)
One key observation is: (i) SV is an all-voting case (can be seen as $q_+ = 1$); (ii) ours are adaptive with voting capped by $q_+$. This suggests, roughly speaking, that ours should be theoretically **upper bounded** by SV.
Since SV performs comparably to SC, we consider SC a reasonable baseline—based on the reasons above, not chosen ad hoc.
While further engineering on the reasoning axis (e.g. better alternative than SV) could improve overall accuracy, we **refrained** from over-optimizing it, as it's **not** the core insight of this work and could distract from the RL contributions.
---
- **Baseline**: Continuing from the discussion above
- **Interpolation baseline**: We compare ours against a **hypothetical efficiency boundary (HEB)** (gray line Fig 2), defined by two **non-adaptive** extremes:
- **$q_+ = 0$**: All short responses;
- **$q_+ = 1$**: All long responses.
A model **above** the HEB can be interpreted as having **improved efficiency**.
- **Why SC**: SC was chosen because it closely aligns with the HEB (Fig 2). We mention SC in the abstract, as readers are likely more familiar with it.
- **[1, 2]**: While [1, 2] are more recent, our goal is to evaluate against the HEB, which reflects non-adaptive cases. As we refrained from over-optimizing the reasoning axis, the upper bound (SV ≈ SC) is relatively low—but sufficient for testing our RL part—and is likely outperformed by [1, 2]. Thus, we don’t find a direct comparison with them entirely fair/necessary.
We hope it clarifies our baseline choice and will revise accordingly, including additional discussion of [1, 2].
- **Dataset**: MATH500: (i) it has difficulty metadata; (ii) LLaMA 3.1 8B Inst. has moderate accuracy. All numbers hereafter refer to this model.
Apart from metadata: Easier ones (GSM8K, SVAMP, ASDIV w/ pass@1 of ~85% [3,4,5]) have small reward margins, as most queries are solved in one attempt;
For harder ones like AIME (2/30 solved [6]), efficiency makes little sense as the model rarely succeeds.
We hope our grounded derivation and constraint satisfaction curves offer more insight and confidence than accuracy numbers alone.
- **Model**: We don't particularly find 8B ''small'', especially given the cost of online training. For reference, [7]—an online self-correction—uses 7B models.
While we didn't explore other families, we're optimistic about the method's generalizability, thanks to its (i) model-agnostic derivation; (2) simple update (Eq. 5).
---
- **2x efficiency**: Apologies for the confusion. It comes from Tab 3 and Fig 2. At $q_+ = 50%$, ours has 55.4% (a 4.14% gain) w/ 2.16x trials (Tab 3), while **the HEB** (aligned with SC, if not better) in Fig 2 requires ~4.5x trials for similar accuracy—implying ~2x efficiency.
- **Table 3**: We didn't re-run; the numbers were taken from the cited papers to avoid implementation discrepancies.
---
- Online training is **inherently** expensive: For 70B, under our setup, we estimate that a single epoch of generation alone could take ~2,600 H100 hours at 300 output tokens/sec per node. In practice, training throughput is significantly lower due to memory overhead from model optimization—and this estimate excludes other potential costs. These limited us from exploring larger models and harder datasets (which likely require larger training sets).
---
We quote reviewer toYu:
> not only sheds new lights on adaptive reasoning but also provides a valuable algorithmic contribution to constrained RL as a whole.
We are not aware of RL-for-LLM works that explicitly impose linear constraints to control response distributions.
We believe our RL contribution merits stronger recognition—especially given your positive evaluation of it.
---
Again, we appreciate your valuable suggestions! We will revise accordingly and we hope our responses addressed your questions.
---
[3] arxiv.org/abs/2407.21783
[4] 2410.06638
[5] 2502.12134
[6] 2410.01560
[7] 2407.18219 | Summary: With the prevalence of Chain of Thought (CoT) in complex reasoning and the emergence of ultra-long reasoning models such as OpenAI-o1 and DeepSeek-R1, unnecessarily tedious and long generations for trivial problems are increasingly becoming a problem. The paper approaches this problem from a RL perspective, proposing IBPO (Inference Budget-Constrained Policy Optimization) that, rather than simply taking a metric of context length as reward, forms a constraint-RL by controlling how response lengths are distributed. The algorithm is then deduced to be a generalization of iterative SFT. Experiments and positive results are shown.
Claims And Evidence: A few claims are made during the deduction of main algorithm, but they're all quite well-grounded.
When finding a workaround for solving the parametric objective function with constraints, authors claim that the non-parametric workaround is superior to alternating between gradients of the policy and Lagrangian multipliers. Although no ablation studies are provided, solid literature on other methods utilizing this workaround in similar problems supports the claim well.
It's also claimed early on in the paper that the proposed IBPO ends up becoming a generalization of SFT methods which is confusing at first but natural after the table comparing SFT, RFT, RAFT and IBPO is provided.
The choice of some techniques, however, weren't explicitly analyzed/compared, such as the use of semi-gradient and the choice of CGPO, but they are either intuitive choices or self-explanatory in positive experiment results.
Methods And Evaluation Criteria: The main method IBPO is framed initially as a constraint RL problem, but after practical adaptations with respect to the policy update (solving for approximate optimal policy via sampling, using semi-gradient) and the reward calculation (introducing a marginal reward, implementing CGPO), the method is deduced to a SFT where samples take the form of weights assigned to long or short context responses. This is in theory sound and intuitive, except that dichotomy between long and short responses is a little counter-intuitive.
The evaluation is largely sound: authors developed Sequential Voting prompting to generate long-context responses, SCoT for solely short-context responses, and Adaptive Sequential Voting prompting for mixed responses. These are used separately as SFT sets and results are compared. However, I'm still hesitant to accept that responses constructed this way are actually long/short-context responses -- the long ones look like a mere aggregation of short responses.
Theoretical Claims: The theoretical proportion is mainly definitions, intuitive deductions and plugging-ins. They seem correct to me.
Experimental Designs Or Analyses: Extensive experiments were conducted, comparing prompt constructing methods and optimizing methods. Experiments consist of the SFT/Prompting-based comparisons and Online Iterative SFT/RL comparisons, respectively revealing effectiveness of the proposed Sequential Voting and IBPO optimization paired with Adaptive Sequential Voting, although improvements seem a little marginal.
As for the setting, extensive baselines were introduced/re-implemented to show the proposed methods' superiority, among which adapting self-correction methods as baseline is a creative choice, as it generates similar long context responses to SV.
Supplementary Material: None were provided.
Relation To Broader Scientific Literature: This paper not only sheds new lights on the problem of budget-aware/adaptive reasoning but also provides a valuable algorithmic contribution to constrained RL as a whole. During parameter update, a method that is essentially a generalization of RFT and RAFT is proposed; the algorithm is a modified version of CGPO, although the alteration is simple.
Essential References Not Discussed: None that I'm aware of.
Other Strengths And Weaknesses: Aside from previous comments, the paper is thorough and detailed in introducing the algorithm, providing sufficient citation and overview of related literature for most readers to understand.
One potential weakness is that many of the baseline results are not run but transcribed from others' works. This harms the solidity of the experiment comparisons.
Other Comments Or Suggestions: On the paper structure, maybe it's a better idea to include more explanation on prompt generation (the proposed SV, ASV), not only to clarify the experiment setting more, but to also convince readers that SV is adequate in representing long response situations that the paper initially tries to improve. The algorithm and experiment parts can be cut down a bit.
Questions For Authors: One major confusion is whether prompts generated via SV sufficiently represent the "unnecessarily tedious long reasoning trace" that the paper sets out to improve. This is rather important as SV seems to be the only experiment scenario.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you very much for your thorough review and valuable feedback! We greatly appreciate your insightful suggestions and positive assessment!
---
We address these three comments collectively, given their relevance to one another.
> However, I'm still hesitant to accept that responses constructed this way are actually long/short-context responses -- the long ones look like a mere aggregation of short responses.
> One major confusion is whether prompts generated via SV sufficiently represent the "unnecessarily tedious long reasoning trace" that the paper sets out to improve. This is rather important as SV seems to be the only experiment scenario.
> On the paper structure, maybe it's a better idea to include more explanation on prompt generation (the proposed SV, ASV), not only to clarify the experiment setting more, but to also convince readers that SV is adequate in representing long response situations that the paper initially tries to improve.
We understand the concern that SV may not fully capture how o1/R1 works at a fundamental level. This construction was chosen due to the unavailability of R1, which was released on Jan 20—roughly 10 days before the submission deadline.
Reproducing o1/R1-style longCoT, or anything more similar, was beyond the scope of our focus on constrained LLM inference. Moreover, it was unclear to the community how to reproduce such methods until the R1 technical report [1] was released on Jan 22.
The SV construction resembles two key characteristics of longCoT: (i) improved accuracy, and (ii) extended response length. It therefore serves an illustrative purpose to highlight our core RL contribution.
Additionally, our paper (i) casts the problem in terms of distribution constraints, rather than directly optimizing over the long-response group, and (ii) derives an RL method that is theoretically agnostic to the specific type of long response. These efforts together further support the use of a constructed alternative.
Given these considerations—and the fact that o1/R1-style longCoT was not available at the time—we hope you find the use of this construction reasonable.
We completely agree that devoting more space to explaining the design decisions and clarifying the role of SV would significantly improve the paper's clarity. Thank you for pointing this out—we will revise the manuscript accordingly!
[1] DeepSeek-R1: Incentivizing Reasoning Capability in LLMs via Reinforcement Learning. https://arxiv.org/abs/2501.12948
---
> revealing effectiveness of the proposed Sequential Voting and IBPO optimization paired with Adaptive Sequential Voting, although improvements seem a little marginal.
> One potential weakness is that many of the baseline results are not run but transcribed from others' works. This harms the solidity of the experiment comparisons.
We believe these are relatively minor points, if our understanding is correct. As such, we've kept our response concise to avoid unnecessary distraction. (Further details can be found in our response to Point 3 for Reviewer hh45.)
After all, our work on constrained LLM inference and the self-correction literature are essentially two orthogonal directions. Transcribing their results is both convenient and helps avoid potential implementation discrepancies.
---
Once again, we sincerely appreciate the reviewer’s insightful feedback and encouraging assessment! We hope our clarifications sufficiently address your questions and clarify our choice of construction. We deeply appreciate your support and will carefully revise the manuscript to further improve its clarity!
---
Rebuttal Comment 1.1:
Comment: I'd like to express gratitude to the authors for carefully addressing all of my concerns. I understand that SV only serves illustrative purposes, but I believe it's different from longCoT in both the ways it improves accuracy and extends response length, not to mention other significant differences such as inference cost. There's also concerns raised by other reviewers that I find reasonable. Therefore, I maintain my original rating. | null | null | null | null | null | null |
Unbiased Recommender Learning from Implicit Feedback via Weakly Supervised Learning | Accept (poster) | Summary: This paper proposes a novel approach named positive-unlabeled recommender learning, to handling the challenge of missing negative feedback in implicit feedback recommendation systems. The key contribution is Progressive Proximal Transport (PPT), an optimal transport-based method that estimates the class prior by minimizing the transport cost between positive and unlabeled samples. The paper presents theoretical justifications for the proposed method and validates it through extensive experiments on three real-world datasets, demonstrating superior performance compared to existing methods.
Claims And Evidence: Yes. PURL provides an unbiased and consistent risk estimator for implicit feedback recommendation. PPT effectively estimates the class prior without requiring heuristic assumptions or propensity scores. Empirical results show that PURL outperforms state-of-the-art baseline methods.
Methods And Evaluation Criteria: Yes, the chosen datasets are sufficient and the NDCG is a reasonable metric for recommendation tasks.
Theoretical Claims: I've checked the derivation of the PURL risk estimator and its unbiasedness, finding the claims are sound.
Experimental Designs Or Analyses: I've checked the experimental setting and their results & analysis.
Supplementary Material: I checked the part A, B and C of the supplementary material.
Relation To Broader Scientific Literature: The paper introduced progressive proximal transport to address the non-random missing problem, which is widely existing issue for broader research community. So the work has a potential of big impacts.
Essential References Not Discussed: The references discussed some classical research directions of implicit feedback recommendation and MNF, but overlooked one direction: MNF in sequential recommendation. This is a very practical direction since people interact with recommender systems in a ordinal manner. Prior work like below discussed this direction which is not discussed in this paper.
- Wang, M., Gong, M., Zheng, X., & Zhang, K. (2018). Modeling dynamic missingness of implicit feedback for recommendation. Advances in neural information processing systems, 31.
Other Strengths And Weaknesses: Strengths:
The use of optimal transport for class prior estimation is innovative. Unbiasedness and consistency of the estimator are formally proven, and the empirical results on real-world datasets are promising.
Weaknesses:
More discussion on scalability for large datasets is needed. In reality the data sparsity will reach 99% in recommender systems. How would proposed PPT perform is still unclear. The direct impact of PPT on performance is not fully isolated.
Other Comments Or Suggestions: 1. Could PPT be extended to handle multi-class implicit feedback scenarios instead of binary PU learning?
2. How sensitive is PURL’s performance to hyperparameter tuning, particularly in estimating the class prior?
Questions For Authors: n/a
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: #### **[W1] More discussion on scalability.**
**Response.** We express our sincere gratitude for this valuable comment. **We add a scalability analysis on the additional ML-1M dataset that is larger than the datasets involved in this paper.**
In the below table, we summarize the performance of PURL given varying ratios of unlabeled samples (denoted as P).
| P| 0.1 | 0.2 | 0.3 | 0.4 | 0.5 | 0.6 | 0.7 | 0.8 | 0.9 | 1 |
|------|--|--|--|--|--|--|--|--|--|---|
| NDCG\@1| 0.81572 | 0.81875 | 0.81841 | 0.82143 | 0.81320| 0.82093 | 0.81455 | 0.82244 | **0.82463** | 0.82059|
| NDCG\@3| 0.80695 | 0.80828 | 0.81152 | 0.81185 | 0.80832 | 0.81150| 0.8101 0 | 0.81088 | 0.81037 | **0.81316**|
| NDCG\@5| 0.80176 | 0.80649 | 0.80738 | 0.80680| 0.80483 | 0.80667 | 0.80835 | 0.80744 | 0.80868 | **0.80978**|
As P increases, the performance of PURL generally increases with some fluctuations. The best performance is achieved when P>0.9, which is **consistent with the results reported in the main text and showcases scalability.** Compared to the results on smaller datasets, the performance is less sensitive to P. This can be attributed to the fact that even a small P in a large dataset corresponds to a large number of unlabeled samples, which suffices to meet the demand of unlabeled samples in Theorem 2 to reduce variance and improve overall performance.
#### **[W2] The direct impact of PPT on performance.**
**Response:** ! In this work, we introduce two components: (1) the PURL loss, which effectively leverages unlabeled samples; and (2) the PPT strategy, which accurately estimates class priors for calculating the PURL loss. To quantify the individual contributions of these components, we conducted a series of ablative experiments.
- To discern the contribution of PURL, we varied the proportion of unlabeled samples (denoted as P) used in the PURL loss calculation, as illustrated in Figure 2. On both datasets, the performance consistently improves as P increases, which demonstrates the effectiveness of PURL.
- **To discern the contribution of PPT**, we compared the performance of PURL with PPT-estimated class prior and other values of class priors, in Table 3. The results show that the PPT-estimated class prior consistently led to the best recommendation performance. **This indicates that the PPT class prior is effective in estimating the class prior and thus improving the ImplicitRec performance.**
#### **[Q1] Could PPT be extended to multi-class implicit feedback scenarios?**
**Response.** We agree that **PPT can be extended to multi-class** scenarios. A plain approach would be treating the multi-value class labels as multiple binary classes. For example, if we have two positive classes (1, 2) and a negative class (0), we can treat them as two binary classes (0 v.s. 1 and 0 v.s. 2). The PPT can be applied to each binary class separately.
#### **[Q2] Sensitivity to hyperparameter tuning.**
**Response.** Once again, we sincerely appreciate the reviewer's meticulous and constructive comments. We discuss the sensitivity to hyperparameter tuning in the following two aspects:
- **Firstly, for the recommendation performance**, we conducted comprehensive experiments to investigate the sensitivity of key hyperparameters, including the ratio of unlabeled samples (Fig. 5), batch size (Fig. 7-a), learning rate (Fig. 7-b), and embedding dimension (Fig. 7-c). Different datasets exhibit varying sensitivity to these hyperparameters, which is largely dependent on the specific characteristics of the data. The detailed analysis is provided in Section 4.5 and Appendix B.3.
- **Secondly, for the class prior estimation**, the PPT approach is generally isolated from these hyperparameters. To showcase this claim, we investigate the logs of sensitivity analysis that record the class prior estimation results $\hat{\kappa}_p$. Below are the results with different batch sizes, averaged over 5 random seeds:
| Batch size | 256 | 512 | 1024 | 2048 |
|--|--|--|--|--|
| $\hat{\kappa}_p$| $0.0499_{\pm0.018}$ | $0.0541_{\pm0.0194}$ | $0.0607_{\pm0.0212}$ | $0.0499_{\pm0.0133}$ |
Across a wide range of batch sizes, the estimated class prior $\hat{\kappa}_p$ remains stable around 0.05 (i.e., the class prior producing the best recommendation performance in Table 3). It indicates that PPT is robust to variations in hyperparameters.
#### **[References] MNF in sequential recommendation should be discussed.**
**Response.** Thank you very much for your insightful comment. We agree that the MNF problem also matters in sequential recommendation. In the revised version, we will include discussions on key works in this area, including but not limited to [1,2,3].
[1] Modeling dynamic missingness of implicit feedback for recommendation. NeurIPS. 2018.
[2] Modeling dynamic missingness of implicit feedback for sequential recommendation. IEEE TKDE. 2020.
[3] Sequential learning over implicit feedback for robust large-scale recommender systems. PKDD. 2019. | Summary: - The study reframes implicit feedback recommendation as a weakly supervised learning problem, and introduces a model-agnostic framework, termed PURL, to handle the missing negative feedback problem.
- Central to this framework is the incorporation of the PU-learning method, which ensures unbiasedness given positive and unlabeled samples given accurate prior estimation.
- To achieve accurate prior estimation, authors proposed Progressive Proximal Transport (PPT), which estimates class priors by minimizing the proximal transport cost between positive and unlabeled data samples.
- To validate the efficacy of the proposed approach, extensive experiments were carried out across multiple datasets, yielding results that underscore its practical utility and effectiveness.
Claims And Evidence: The proposed method provides a PU learning approach, which is feasible to handle this problem. Theoretical and empirical evidence is provided.
Methods And Evaluation Criteria: The proposed methods make sense and evaluation criteria follow the standard practice.
Theoretical Claims: Theories are clear to follow and the sources from PU learning literature are cited.
Experimental Designs Or Analyses: The empirical investigation of this study is comprehensive, and the analysis makes sense.
Supplementary Material: The supplementary material seems well prepared but I did not check it in detail. The proofs seem to follow the standard requirement of PU learning studies.
Relation To Broader Scientific Literature: In terms of methodology, this paper is related to the field of PU learning and optimal transport. In terms of application, it is related to the field of recommendation systems with implicit feedback.
Essential References Not Discussed: The section 'related works' discussed recent progress of PU learning and implicit feedback recommendation. Section 2.2 introduces optimal transport. Despite the primary references are covered, you can consider expanding the discussion to include broader applications of optimal transport in recommendation systems. This would provide a more comprehensive context for understanding the role and relevance of optimal transport within the field.
Other Strengths And Weaknesses: Strengths
- This paper effectively highlights the significance of unlabeled data in recommendation systems. An estimator that harness the unlabeled data for model training while ensuring unbiasedness is proposed.
- The theoretical properties of the proposed estimator is investigated. The method using OT for class prior estimation is fresh for me.
- According to Table 1-2, the proposed method exhibits superior empirical performance. Comprehensive empirical studies are conducted to validate the proposed method.
Weaknesses
- This paper has two main components. In this situation, an ablation study is critical to assess the contribution of each component to the overall performance. However, this study seems lacking.
- Some statements in this paper need further clarification. Please see the questions below.
- The originality of the proposed optimal transport problem--PPT--is not clarified. Authors should clarify the originality of PPT, or provide a concrete reference.
- The code link is provided, but the repository seems to be expired.
Other Comments Or Suggestions: - Reference format should be checked. For example, you used "ACM Trans. Manage. Inf. Syst.", ISO abbreviation for journals. However, you used "NeurIPS" and "CIKM" for conferences, which are not ISO abbreviations.
- In section 4.4, you wrote "According to Section 4.4". Is there any reason to refer to the same section? Otherwise, it should be deleted.
- In line 75, you wrote "missing-not-at-random (MNF) issue". It should be "missing negative feedback (MNF) issue", right?
Questions For Authors: - In line 40, you wrote "identifying accurate propensity scores remains an elusive goal in ImplicitRec". However, propensity score estimation is challenging in general, not only in implicit feedback recommendation. It does not interfere the success of propensity-based methods.
- In table 1-2, it seems that some methods using negative feedback are included. Ideally they should outperform implicit feedback methods, since the accurate negative feedback is available, is it right?
- I am curious about the connection between PURL and noisy label recommendation. Since the unlabeled samples are available, naively treating them as negative could lead to false labeling, which seems to be a noisy label problem. What is the advantage of formulating implicit feedback recommendation as a weak supervised learning problem over formulating it as anoisy label problem?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: #### **[W1] Ablation study matters.**
**Response:** Thank you for your kind comment! In this work, we devise two components: (1) the PURL loss; (2) the PPT strategy. **We have conducted experiments to discern their individual contributions**.
- To discern the contribution of PURL that leverages unlabeled samples, we have conducted ablative experiments by changing the proportion of unlabeled samples involved in Fig.2. The results show that on both datasets, the performance increases with the proportion of involved unlabeled samples, which demonstrates the effectiveness of PURL in leveraging unlabeled samples.
- To discern the contribution of PPT that estimates class priors, we have conducted ablative experiments in Table 3. The results show that the class prior estimate of PPT, with the smallest $\mathbb{W}$, corresponds to the best recommendation performance.
#### **[W2, Q1] Challenge of propensity estimation.**
**Response:** Thank you for your insightful comment. We agree that the propensity score estimation is a general challenge, but we demonstrate that this challenge is exacerbated in ImplicitRec, for the following reasons:
- In recommendation, the propensity score is typically the probability of a specific treatment given a user-item pair.
- In ImplicitRec, this probability is hard to estimate due to the absence of negative feedback. For example, in CTR prediction, the propensity score is the exposure probability of a user-item pair. However, ImplicitRec only provides positive (exposure & click) and unlabeled samples (non-exposure), lacking negative samples (exposure & non-click). This makes estimating exposure probability infeasible.
- This challenge is unique to ImplicitRec and significantly hampers the effectiveness of existing propensity-based methods in achieving unbiased recommendations in ImplicitRec.
#### **[W2, Q2] Why does ImplicitRec model outperform some explicit models?**
**Response:** Thank you for your insightful comments. The phenomenon is noticable and we justify it from two aspects.
- **Theoretical aspect.** The proposed PURL loss $R_\mathrm{purl}$ **reduces the variance** of the ideal binary loss $R_\mathrm{ideal}$ that uses explicit feedback, **given $\kappa_p\leq 0.5$ (a naturally holding condition) and large number of unlabeled samples.** The variance reduction property is justified in Theorem 2, which leads to better generalization and performance.
- **Empirical aspect.** Figure 5 shows consistent performance improvement with more unlabeled samples, validating the theoretical aspect above. Thus, more unlabeled samples decrease PURL variance and improve performance over explicit feedback methods.
#### **[W2, Q3] The connection with noisy label recommendation.**
**Response.** Yes, it is feasible to employ learning-from-noisy-label techniques to address the MNF issue within ImplicitRec. However, the weakly supervised learning framework used in this work is more suitable for two main reasons:
- **Theoretical supports**. Most noisy label methods are heuristic or rely on strong assumptions about the noise mechanisms. In contrast, the weakly supervised learning framework provides theoretical guarantees without such harsh assumptions.
- **Empirical supports**. One exemplar work approaching ImplcitRec as learning from noisy labels is T-CE [1]. Our experiments below show that PURL outperforms T-CE, demonstrating the effectiveness of using weakly supervised learning for ImplicitRec.
| Dataset | Model | NDCG@1 | NDCG@3 | NDCG@5 | Recall@1 | Recall@3 | Recall@5 |
|--|--|--|--|---|---|--|----|
| Yahoo | RecVAE | 0.65 | 0.683 | 0.719 | 0.054 | 0.149 | 0.234 |
| | T-CE | 0.749 | 0.785 | 0.817 | 0.125 | 0.252 | 0.333 |
| | PURL | 0.784 | 0.814 | 0.843 | 0.146 | 0.28 | 0.351 |
| Coat | RecVAE | 0.465 | 0.499 | 0.545 | 0.096 | 0.267 | 0.389 |
| | T-CE | 0.448 | 0.47 | 0.509 | 0.081 | 0.228 | 0.347 |
| | PURL | 0.552 | 0.555 | 0.589 | 0.131 | 0.302 | 0.425 |
| Kuairec | RecVAE | 0.422 | 0.434 | 0.448 | 0.11 | 0.183 | 0.214 |
| | T-CE | 0.418 | 0.429 | 0.435 | 0.108 | 0.214 | 0.264 |
| | PURL | 0.498 | 0.486 | 0.488 | 0.137 | 0.245 | 0.296 |
#### **[W3] Originality of PPT.**
**Response:** Thank you for the reminder. The PPT generalizes the canonical OT problem by relaxing the equality constraint for $\beta$ and changes its total mass from 1 to $w$. This formulation is specifically designed for ImplicitRec and, to our knowledge, has not been previously studied.
#### **[W4] Project website.**
**Response:** Thank you for your kind reminder. The repository has now been restored. Additionally, we offer a Docker file to facilitate quick reproduction.
#### **[Reference and Other comments].**
**Response.** Thank you for your meticulous comment. We will fix the typos, remove the invalid reference, adjust the related works and unify the reference formats in revision.
[1] Denoising implicit feedback for recommendation. WSDM. 2021.
---
Rebuttal Comment 1.1:
Comment: Thank you for your additional experiments. The informative response has addressed my questions and I have accordingly adjusted my scores. Please add these discussions in revision. | Summary: The paper addresses the challenge of missing negative feedback (MNF) in implicit feedback-based recommender systems. Traditional approaches often rely on negative sampling, which risks misclassifying positive samples as negative, leading to bias and performance degradation. The authors propose PURL (Positive-Unlabeled Recommender Learning), a framework that treats implicit recommendation as a weakly supervised learning task, thereby eliminating the need for negative samples.
Claims And Evidence: - PURL estimator is unbiased relative to the ideal risk
evidence: C.1 Theorem 1.
- Progressive Proximal Transport (PPT) accurately estimates class priors
evidence: Empirical results
- PURL outperforms existing implicit feedback methods
Methods And Evaluation Criteria: The paper introduces PURL (Positive-Unlabeled Recommender Learning) and Progressive Proximal Transport (PPT) as core components to address missing negative feedback (MNF) in implicit recommendation. I think the proposed method is theoretically and empirically sound.
The evaluation metric include NDCG@1 NDCG@3 NDCG@5, I think make sense. recall is also measured.
Theoretical Claims: I think the theretical claims are well proved. I'm not an expert for theory, therefore please also refer to other reviewer's suggesitons.
Experimental Designs Or Analyses: I think the experiment is comprehensive: 13 baselines, covering pointwise, pairwise, and unbiased methods, which are commonly used in implicit feedback recommendation research.
The dataset is also diverse: Yahoo! R3 and Coat are explicit feedback datasets converted to implicit feedback KuaiRec is a fully implicit feedback dataset.
Supplementary Material: Yes, proof and additional figures.
Relation To Broader Scientific Literature: I believe the proposed method contributes to the literature as a model-agnostic framework that reframes implicit feedback recommendation as a weakly supervised learning task, eliminating the need for negative samples.
Essential References Not Discussed: I'm not familiar enough with the literature, so I don't see essential reference not discussed.
Other Strengths And Weaknesses: Overall, I think this is a good paper and all the claim are solid and sound for me. But I'm not working on the field for a while, so please also refer to other reviwer's suggestions.
Other Comments Or Suggestions: See Above
Questions For Authors: A small question, will using Yahoo! R3 and Coat that transfer rating to implicit feedback influence the evaluation?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **Thank you very much for your kind and sincere words. It is impressive to meet a review that candidly express limitations while responsibly and analyzing the claims and details of the paper. We truly appreciate it!**
We have noticed the question about the dataset generation process and are happy to provide a detailed response.
- Firstly, we chose the Yahoo and Coat datasets, which are commonly used in prior ImplicitRec studies such as CUMF [1], UBPR [2], and UPL [3].
- In the training set, we retained only user-item pairs with positive feedback and treated those with negative feedback as unlabeled. This reflects real-world implicit feedback scenarios where only positive interactions are observed, and the rest are unlabeled. In the test set, we preserve the explicit feedback which is necessary to calculate the metrics (NDCG, Recall, etc.), mirroring the online serving scenario of implicit feedback recommendation.
- This process aligns with common practices in ImplicitRec research [1-3].
**Reference.**
[1] Yuta Saito, Suguru Yaginuma, Yuta Nishino, Hayato Sakata, and Kazuhide Nakata. 2020. Unbiased Recommender Learning from Missing-Not-At-Random Implicit Feed- back. In WSDM. ACM, 501–509.
[2] Yuta Saito. 2020. Unbiased Pairwise Learning from Biased Implicit Feedback. In ICTIR. ACM, 5–12.
[3] Yi Ren, Hongyan Tang, Jiangpeng Rong, and Siwen Zhu. 2023. Unbiased Pairwise Learning from Implicit Feed- back for Recommender Systems without Biased Variance Control. In SIGIR. ACM, 2461–2465. | Summary: This paper focuses on addressing the lack of negative feedback in recommendations with implicit feedback and points out the limitations of recent unbiased estimator-based methods in identifying propensity scores and non-negative estimates. It proposes a novel positive-unlabeled recommender learning (PURL) framework, in which the core idea is to introduce a new estimator and use progressive proximal transport (PPT) to estimate the required class priors of unobserved samples. Extensive experiments are conducted on three public datasets to verify the effectiveness of PURL.
Claims And Evidence: The claims made in the submission are supported by clear and convincing evidence; the claimed problem (MNF) is a common problem in recommendation systems with implicit feedback.
Methods And Evaluation Criteria: The proposed methods and/or evaluation criteria (e.g., benchmark datasets) make sense.
Theoretical Claims: I have checked the correctness of any proofs for theoretical claims. Some obstacles are presented in the questions below.
Experimental Designs Or Analyses: I have checked the soundness/validity of any experimental designs or analyses. The experiments validate the overall performance of the proposed method.
Supplementary Material: I have reviewed the related works and theoretical analyses.
Relation To Broader Scientific Literature: This paper focuses on the problem of missing negative feedback, an issue seen in the literature of implicit feedback recommendation. The proposed PURL is connected to the method from the weakly supervised learning field. The proposed PPT is an optimal transport approach with modification for achieving class prior estimation.
Essential References Not Discussed: The literature discussion in the main text is a little brief.
It is better to move the discussion of related work from the appendix to the main text.
Other Strengths And Weaknesses: Strengths:
1. This paper targets missing negative feedback, an important issue in the field of implicit feedback recommendation. It also widely exists in real-world applications.
2. The proposed method is promising to tackle the issue. It contains a creative fusing of OT and weakly supervised learning and an important application in recommendation.
3. Diagrams are well prepared to facilitate understanding of important concepts and showcase efficacy.
Weaknesses:
1. The mass weight's connection to class prior estimation is not explicit, but it is a critical aspect to understand the subsequent contents.
2. The claim that Bayesian Personalized Ranking (BPR) lacks a solid theoretical foundation requires elaboration.
3. This paper utilized PPT, an OT-based approach for class prior estimation. However, OT is often costly in terms of both computation time and memory, as well as poor scalability w.r.t. the number of decision variables, which is quadratic to the batch size. Regrettably, in real-world recommendations, large batch size is often used in training recommendation systems for daily updates. In this case, PPT might require longer training time and larger memory requirement.
4. The principle of dataset selection should be explained. In this paper, the selected datasets are Yahoo, Coat, and Kuairec. Why not select some standard datasets such as ML-10M?
5. Some steps in the derivation are difficult to follow. e.g., the derivation in equation 7. Necessary conditions and explanations are expected to facilitate readers to follow and check the derivation.
Other Comments Or Suggestions: The consistency of the terms used needs improvement. For example, Are the user-item pair, user-item intersection, and user-item interaction the same thing?
Questions For Authors: See the above two parts.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: **We sincerely appreciate the reviewer’s great efforts and insightful comments to improve our manuscript. In below, we address the raised concerns point by point and try our best to clarify any confusions.**
#### **[W1] The connection between mass weight $w$ to class prior estimation is not explicit.**
**Response.** We agree that the connection needs clarification.
- **Connection clarification.** We estimate the class prior as the inverse of the mass weight, i.e., $\hat{\kappa}_p=w$.
- **Rationale of the connection.** The PT problem is designed to match the positive samples ($\alpha$) with a selective set including $1/w$ of the unlabeled samples ($\beta$). If there exist negative samples in the selective set, the PT discrepancy will be large. By finding the $w^*$ with minimum discrepancy, we can estimate the class prior $\hat{\kappa}_p = 1/w^*$. This process is visualized in Fig. 1.
- **Toy example.** We provide simulated results in Fig.4. The ground-truth class prior $\kappa=0.5$. When we set $w=2$, all positive samples are exactly matched with the proximal positive samples within the unlabeled population, producing the minimal transport cost.
#### **[W2] The claim concerning BPR requires elaboration.**
**Response.** Thank you for your insightful comment. We elaborate the claim as follows, and promise to add it in revision.
- The BPR loss randomly samples unlabeled samples as negatives. However, **not all unlabeled samples are true negatives.** Some may simply be items the user hasn't encountered yet. This misclassification makes BPR biased.
- In contrast, **our proposed PURL loss is unbiased** given accurate class prior estimation. This is supported by Theorem 1 in our paper, which provides a theoretical support for the advantage of the proposed PURL.
#### **[W3] Computational time and memory requirement.**
**Response.** Thank you for your insightful question. We add the analysis on computational time and memory consumption below.
- The complexity of solving the proposed PPT problem is mainly determined by the number of samples. We conducted an empirical study on its running time, revealing that, although the theoretical complexity remains not straightforward to derive, the **running time scales linearly with the number of samples on a log-log scale.** In the **largest test with batch size of 2,048**—exceeding typical batch sizes in most practices—the running time was **under 0.1 seconds**, rendering it negligible compared to model training.
- The memory consumption is also affected by the number of samples. **We add experiments where we used the decorator profile in the memory_profiler package to test the memory consumption** in solving the PT problem. According to the results below, **in the largest setting of 2048 samples, the memory consumption is 52.9 MB**, which is acceptable and even negligible compared to the memory cost of training typical recommendation system.
| Batch size | 128 | 256 | 512 | 1024 | 2048 |
|------------|-----|-----|-----|------|------|
| Memory consumption | 1.2Mb | 4Mb | 10.5Mb | 20.7Mb | 52.9Mb |
- We promise to adding these discussions in the revised manuscript.
#### **[W4] The principle of dataset selection should be explained.**
**Response.** Thank you for your kind reminder. We select the datasets based on the following principles:
- Firstly, we opt for the datasets that contain unbiased test set with explicit feedback. This is crucial for evaluating the performance of our method, where the explicit feedback is used to calculate the metrics (NDCG, Recall, etc.), and the unbiased set mirrors the online serving scenario.
- Secondly, we follow the practice of previous works in the ImplicitRec field. Specifically, the employed Yahoo and Coat datasets were used in CUMF (WSDM'20), UBPR (SIGIR'20), UPL (SIGIR'23), CDR (ICLR'23) and SDR (ICLR'23).
- Moreover, motivated by UIDR (ICLR'24), we add an additional dataset--Kuairec--to provide comprehensive evaluation of the proposed method on large-scale industrial dataset.
#### **[W5] The derivation of Eq.7.**
**Response.** Eq. 7 defines a proximal transport problem, which is a generalization of the canonical OT problem in Eq. 2.
- To derive Eq. 7, we replace the marginal constraint $\boldsymbol{\pi}^\top \boldsymbol{1}_n=\mathbf{b}$ with $\boldsymbol{\pi}^\top \boldsymbol{1}_n \leq w \mathbf{b}$ with $w\geq 1$, which acquires a semi-relaxed OT.
- On the basis, we add the constraint $ \boldsymbol{1}_m\boldsymbol{\pi}^\top \boldsymbol{1}_n = 1$, which forces the full mass to be transported to be 1.
- Then, given the assumption that the mass in $\alpha$ and $\beta$ is uniformly distributed and sums to 1, we have $\mathbf{a}=\boldsymbol{1}_n$ and $\mathbf{b}=\boldsymbol{1}_m$. The derivation of Eq. 7 is completed.
#### **[Other comments] Consistency of terms.**
**Response.** Once again, thank you for your valuable comment. They refer to the same thing and we will use a unified term "user-item pair" in revision.
---
Rebuttal Comment 1.1:
Comment: Thanks for the author's detailed reply, which addresses my concerns and questions. Accordingly, I am happy to vote for acceptance and slightly raise the score. | null | null | null | null | null | null |
COKE: Core Kernel for More Efficient Approximation of Kernel Weights in Multiple Kernel Clustering | Accept (poster) | Summary: The paper introduces a novel approach to multiple kernel clustering by proposing the concept of core kernel. This method aims to reduce the computational complexity of clustering large datasets while preserving performance.
**Main Contributions:**
1. Core Kernel Definition: The core kernel is defined as a set of smaller-sized kernel matrices that can approximate the original kernel weights with a (1+$\varepsilon$)-approximation guarantee.
2. Algorithmic Contribution: The paper propose an algorithm based on SVD to construct core kernel efficiently. This algorithm significantly reduces the size of the kernel matrices while preserving essential information for clustering.
3. Theoretical Guarantees: The paper provides theoretical proofs (Theorem 4.4 and Theorem 4.5) that establish the effectiveness of the core kernels in approximating the original kernel weights under certain assumptions, such as the existence of a spectral gap.
Claims And Evidence: The overall logic of the paper is quite clear.
**Introduction**
It is important to emphasize the differences between this paper and the related work, highlighting the innovative aspects of the proposed method.
**Motivation Needs More Detailed Elaboration**
The motivation of the paper requires more detailed elaboration to clearly illustrate the significance of kernel weights. Specifically, it should provide a more thorough explanation of why kernel weights are crucial and how they impact the final clustering results.
Methods And Evaluation Criteria: The methods section is well-organized, and the explanation regarding the core kernel is very clear. However, concerning matrix T, the paper mentions using uniform sampling, and it may be worth considering leverage score sampling as well.
Theoretical Claims: The theoretical theorems and proofs presented in the paper are clear and rigorous. It is recommended to discuss the relationship between the clustering subspace and the weights in the remark section of Theorem 3.3, emphasizing the motivation behind it.
Experimental Designs Or Analyses: The experimental design is relatively reasonable; however, there are several issues:
1. Why does the chosen value of the number of anchor points s not correspond to the conclusion of the number s obtained in the theorem?
2. It is recommended to include a comparison of clustering performance between the kernel weights \alpha obtained from SMKKM and MKKM, as well as the kernel weights \tilde{ \alpha } proposed in the paper.
Supplementary Material: The proofs of the theorems provided in the supplementary materials, as well as the introduction to related works such as SMKKM, are very clear and further strengthen the theoretical foundation and the effectiveness of the methods presented in the paper.
Relation To Broader Scientific Literature: The key contributions of this paper build upon prior research in clustering and kernel methods, particularly enhancing the understanding of anchor point selection and its impact on clustering performance.
Essential References Not Discussed: As far as I know, this paper has basically discussed all the essential related work.
Other Strengths And Weaknesses: Strength: the paper provides rigorous mathematical proofs to support their claims, ensuring that the proposed SVD-CK method has a strong theoretical basis.
Weakness : the paper lacks performance experiments for the proposed method on small datasets.
Other Comments Or Suggestions: It is recommended that the differences and advantages of the proposed method be elaborated in detail compared to the methods in “Consistency of Multiple Kernel Clustering”.
Questions For Authors: The paper uses the same anchor point set for all kernel approximations. Has there been any consideration of approximating different kernels with different anchor points?
In this paper, the number and quality of anchor points are relatively important. The theorems presented only provide conclusions regarding the number of anchor points. Has there been any consideration of whether the quality of anchor points can be theoretically evaluated?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We appreciate the comments of Reviewer s6E6 and have responded to them individually.
### Q1: Why are kernel weights crucial?
A2: In many previous studies, it can be observed that the kernel weights of multiple kernel clustering (MKC) algorithms have a significant impact on the learning performance of the algorithms. For example, in a classical reference [1] (https://ojs.aaai.org/index.php/AAAI/article/download/10249/10108), the authors compare various clustering metrics of the optimal single kernel, average kernel, and various MKC algorithms, showing that their clustering performances differ greatly. Different optimization principles for kernel weights, tailored to different datasets and learning scenarios, result in significant differences in clustering performance. According to the no free lunch theorem, for a specific problem, we need to adjust the algorithm correspondingly. The same applies to MKC algorithms, where it is essential to develop targeted kernel weight design schemes. The above empirical evidence fully demonstrates that the kernel weights of base kernels have a crucial impact on improving the performance of MKC algorithms.
### Q2: Discuss the relationship between the clustering subspace and the weights in the remark of Theorem 3.3.
A2: For the original MKC algorithm, $\mathbf{H}$ is the sample embedding used to obtain the final clustering results, while the approximate embedding proposed in this paper is $\widetilde{\mathbf{H}}$. We aim to demonstrate through Theorem 3.3 that the proposed method and the original algorithm can achieve similar clustering performance. To measure the difference between $\mathbf{H}$ and $\widetilde{\mathbf{H}}$, the best way is to compare the distance between their projections. We will include a more detailed description in the revised version.
### Q3: Why does the chosen value of the number of anchor points $s$ not correspond to the conclusion obtained in the theorem?
A3: The main reasons are as follows: Firstly, the theoretical derivation is based on some general assumptions, and the conclusions obtained are valid under all conditions. However, in empirical observations, factors such as the distribution of the dataset, the kernel function, and other elements affecting the approximation effect may result in a smaller required value of $s$ in practice. Secondly, the boundary of the theoretical derivation is constrained by the matrix concentration inequality shown in Theorem B.3 of the appendix. In real situations, the concentration of the dataset used in experiments may be smaller than the upper bound presented in Theorem B.3.
### Q4: Compare the clustering performance between the proposed method and the original algorithm.
A4: We compared the NMI of the proposed algorithm and the original algorithm on SMKKM and MKKM-MR using two datasets, Flower17 and DIGIT. The number of anchors ranged from 100 to 1000, with a step size of 100. The final experimental results are shown in the figure (https://anonymous.4open.science/r/ICML2025-8D7F/NMI_RES.svg). It can be observed that when the number of anchors is around 500, the proposed algorithm achieves similar clustering performance to the original.
### Q5: Elaborate on the differences between the proposed method and the algorithm in [2].
A5: The method presented in this paper has the following advantages: 1. Wider Applicability: This paper proves that the proposed method can be widely applied to the kernel weight approximation of three types of MKC algorithms, whereas the method in [2] can only approximate one type of MKC algorithm. 2. Better Approximation Effect: As shown in Figures 2 and 3, the approximation effect of the proposed method is better than that of the method in [2].
[2] Consistency of Multiple Kernel Clustering. ICML 2023.
### Q6: Approximate different kernels with different anchor points.
A6: We have attempted to use different anchor points for different base kernels to perform approximation. However, due to the inconsistency of the anchor sets, the approximation effect turned out to be rather poor. In multi-view clustering, some studies have employed different anchor points for different views and achieved promising clustering results. However, these works lack theoretical guarantees for approximation, and they do not provide theoretical insights that are applicable to our results. The reviewer’s suggestion is highly insightful for us, and we will attempt to address this issue in our future work.
### Q7: Evaluate the quality of anchor points theoretically.
A7: Compared with uniform sampling, importance sampling methods (such as leverage scores) can select more representative anchor points, allowing good approximation results with fewer anchors. However, this leads to inconsistency in the anchor points of different base kernels, which affects the final kernel weight approximation. This situation is similar to that described in Question 6, and we will investigate this issue in future work. | Summary: This paper introduces a novel concept called the "core kernel," which aims to approximate kernel weights in multiple kernel clustering (MKC) algorithms by running them on smaller-scale base kernel matrices. The core kernel, with a size of $\widetilde{\mathcal{O}}(1/\varepsilon)$, achieves a $1+\varepsilon$-approximation. The authors propose a core kernel construction method based on singular value decomposition (SVD-CK) and prove its applicability to three mainstream MKC algorithms (SMKKM, SMKKM-KWR, and MKKM-MR). Theoretical analysis shows that using the core kernel reduces the time complexity of MKC algorithms from $\mathcal{O}(n^3)$ to $\mathcal{O}(s^3)$. Experiments on benchmark datasets validate the approximation performance of SVD-CK on kernel weights, while tests on large-scale datasets demonstrate the efficiency of the scalable extension. The core contribution lies in providing a theoretically guaranteed framework for efficient large-scale extensions of MKC algorithms.
Claims And Evidence: Key claims are supported by experiments and theory:
Claim 1: SVD-CK can effectively approximate kernel weights.
Evidence: Theorems 4.4 and 4.5 demonstrate that the SVD-CK method can produce a $1+\varepsilon$-approximation core kernel set for SMKKM, SMKKM-KWR, and MKKM-MK. Figures 2 show that the kernel weight error of SVD-CK decreases rapidly as the anchor number $s$ increases, significantly outperforming random sampling (blue vs. red curves).
Claim 2: The core kernel enables large-scale extensions for MKC.
Evidence: Algorithm 1 first obtains approximate weights through the SVD-CK method, then combines the base similarity matrices using these weights, and finally derives the cluster indicator matrix via SVD on the combined matrix. Theorem 3.3 proves that if the algorithm inputs are identical, the cluster indicator matrix obtained through Algorithm 1 can arbitrarily approximate the cluster indicator matrices obtained by other MKC algorithms. Table 2 shows that core kernel-based MKC algorithms (e.g., SMKKM) achieve high clustering performance (NMI >97%) on datasets with 50k samples, with reasonable time costs.
Methods And Evaluation Criteria: Method Rationality: SVD-CK compresses kernel matrices via anchor sampling and SVD, aligning with coreset principles.
Evaluation Criteria: Experiments cover benchmark datasets (e.g., Flower17, CCV) and large-scale datasets (e.g., Winnipeg), with metrics including NMI, ACC, and runtime.
Theoretical Claims: Theorem 3.3
Statement: Under Assumption 3.2 (eigenvalue gap), the subspace difference between the clustering indicator matrix $\widetilde{\mathbf{H}}$ from the core kernel (via Algorithm 1) and the original $\mathbf{H}$ satisfies.
Potential Issues: Validity of Assumption 3.2: Eigenvalue gaps may not hold for high-dimensional/noisy data where eigenvalues are densely distributed.
Theorem 4.1
Statement: The singular values of the uniformly sampled matrix approximate the eigenvalues of the original kernel matrix with $\varepsilon$-error, high probability.
Potential Issues: Uniform Sampling Assumption: May fail for non-uniform data distributions.
Experimental Designs Or Analyses: Reproducibility: Hyperparameter settings (e.g., $\sigma^2$ for Gaussian kernels) are clear, but code or implementation details for anchor sampling are missing.
Statistical Analysis: Experiments are repeated 30 times for averaging, reducing randomness, but variance or significance tests are not reported.
Supplementary Material: The supplementary materials of the paper provide a detailed process of the relevant algorithms as well as rigorous proofs of the theoretical results presented in the main text.
Relation To Broader Scientific Literature: The paper connects to:
1. Coresets in clustering (Har-Peled & Mazumdar, 2004).
2.MKC algorithms (Huang et al., 2012; Liu, 2022).
3.Large-scale kernel methods (Wang et al., 2019).
Essential References Not Discussed: The paper essentially covers the important relevant literature.
Other Strengths And Weaknesses: Strengths:
1. Novelty: Extends coreset ideas to kernel weight approximation with solid theoretical analysis.
2. Practicality: The method is simple and scales to datasets with over 300k samples.
Weaknesses:
1. Experiments only use the Gaussian kernel function, lacking validation on other kernel functions.
2. Time costs for core kernel construction (e.g., SVD complexity) are not discussed.
Other Comments Or Suggestions: No.
Questions For Authors: Q1: Assumption 3.2 assumes eigenvalue gaps, but real-world data may violate this. If eigenvalue gaps approach zero, does Theorem 3.3 still hold? Please discuss this scenario.
Q2: Is the construction time of SVD-CK significantly higher than random sampling? Please include runtime comparisons.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely appreciate the work of Reviewer hzsf and respond to the review comments as follows.
### Q1: Assumption 3.2 assumes eigenvalue gaps, but real-world data may violate this. If eigenvalue gaps approach zero, does Theorem 3.3 still hold? Please discuss this scenario.
A1: The reason for making this assumption is that, in the perturbation analysis of matrix eigenvectors, the eigenvalues of a matrix are often considered to be isolated, and thus the eigenvalue gap is always greater than 0. Since the proof of Theorem 3.3 involves the results from matrix perturbation theory (Lemma C.1), we have to make this assumption in this paper.
In practical situations, even if there exist cases where the eigenvalue gap is 0, we conjecture that the above conclusions from matrix perturbation theory still hold. However, this would require more powerful mathematical tools. Currently, it is necessary to strengthen the conclusions regarding eigenvector perturbations in matrix perturbation theory to avoid this assumption.
### Q2: Is the construction time of SVD-CK significantly higher than random uniform sampling? Please include runtime comparisons.
A2: The method of constructing the base kernel matrix using random uniform sampling requires a time complexity of $\mathcal{O}(s^2)$ since it only needs to sample the indices of anchor points. In contrast, the construction method of SVD-CK provided by Algorithm 2 requires a time complexity of $\mathcal{O}(ns^2)$. However, this process only needs to be executed once, so it does not significantly increase the overall time of the algorithm. We compared the time taken to obtain the final kernel weights using random sampling and SVD-CK, as shown in the figure (https://anonymous.4open.science/r/ICML2025-8D7F/time_cost.svg). It can be seen that the total time for obtaining kernel weights using the two construction methods is roughly the same. This fully demonstrates that the proposed SVD-CK in this paper is not significantly less efficient than random uniform sampling. | Summary: This paper first proposes the concept of core kernel, and proposes a core kernel construction method based on singular value decomposition, and proves that it meets the core kernel definition of three mainstream MKC algorithms. The correctness of the theoretical results and the effectiveness of the proposed method are verified on multiple benchmark datasets.
## update after rebuttal
I keep my positive score.
Claims And Evidence: yes.
Methods And Evaluation Criteria: yes.
Theoretical Claims: no.
Experimental Designs Or Analyses: no.
Supplementary Material: yes, Appendix A-D. However, I did not check in detail whether there were any issues with the proof.
Relation To Broader Scientific Literature: Inspired by the well-known core set in clustering algorithms, a definition of the core kernel is introduced to obtain kernel weights similar to those obtained using the standard basis kernel matrix.
Essential References Not Discussed: no
Other Strengths And Weaknesses: The definition of the core kernel is interesting.
The paper provides solid theoretical guarantees.
Other Comments Or Suggestions: please see questions.
Questions For Authors: 1. What is the relationship between Algorithm 1($k$-means after using SVD) and spectral clustering?
2. How is the proposed method (algorithm 2) related to Neystrom?
3. What is the intuition of Algorithm 2 (such as what is the meaning of Kp~)?
4. Are the eigenvalues of Assumption 3.2 sorted?
5. Theorem 3.3 and 4.1 require a large $s$. (Flower17 in Figure 1 only has 1000 points?)
6. the approximation effect of $\frac{1}{\sqrt(ns)}P$ is much better than $\frac{1}{s}W$. Why is this? W is the eigenvalue calculated directly, while $\frac{1}{\sqrt(ns)}P$ is estimated using singular. Why is it better?
7. Figure 1 only shows the difference $| a-b|$, but how big is $\lambda_j(\frac{1}{n}K)$? Can you show $\frac{| a-b|}{\lambda_j(\frac{1}{n}K)}$ in a new figure?
8. What kernels were used? Are they all Gaussian kernels? How are their parameters set?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We greatly appreciate the feedback of Reviewer qRUV and have addressed each comment point by point, as detailed below.
### Q1: The relationship between Algorithm 1 and spectral clustering.
A1: Assume that the consensus kernel matrix obtained by the original multiple kernel clustering (MKC) is $\mathbf{K}_ {\boldsymbol{\alpha}}$. The proposed Algorithm 1 is used to approximate kernel $k$-means on $\mathbf{K}_ {\boldsymbol{\alpha}}$. Specifically, we utilize the first $k$ singular vectors of matrix $\mathbf{P}_ {\tilde{\boldsymbol{\alpha}}}$ instead of the first $k$ eigenvectors of matrix $\mathbf{K}_ {\boldsymbol{\alpha}}$ to obtain clustering results similar to those of the original MKC algorithm. Our proposed algorithm is different from spectral clustering. However, our algorithm is similar to spectral clustering in the final step, where, after obtaining the clustering indicator matrix, $k$-means clustering is used to get the final clustering results.
### Q2: The relationship between Algorithm 2 and Nyström approximation?
A2: Algorithm 2 and the Nyström method are both methods used to approximate the spectrum of kernel matrices, but they focus on different aspects as follows.
Different usage: The Nyström algorithm mainly approximates the kernel $k$-means clustering results on a single kernel through the approximated eigen-decomposition of the kernel matrix. In contrast, our method is mainly used to approximate the kernel weights in MKC.
Different output: The Nyström method outputs an $n\times n$ kernel matrix with low rank. However, the size of the kernel matrices outputted by our algorithm is $s\times s$. Therefore, the kernel matrix output by our algorithm is more suitable for approximating the kernel weights in the MKC algorithm.
### Q3: What is the intuition of Algorithm 2?
A3: Our intuition is that it is possible to approximate the weights of MKC on the original base kernel matrix using several base kernel matrices whose sizes are independent of the number of samples $n$. The kernel matrix $\widetilde{\mathbf{K}}_p$ output by Algorithm 2 can precisely approximate the spectrum of the original kernel matrix, and its size is $s\times s$, which meets our conception.
### Q4: Are the eigenvalues of Assumption 3.2 sorted?
A4: Yes, the eigenvalues described in Assumption 3.2 are sorted in descending order, which is a common assumption in kernel learning theory. To avoid unnecessary confusion, we will clarify this point in the revised version.
### Q5: Theorem 3.3 and Theorem 4.1 require a large $s$, but Flower17 in Figure 1 only has 1000 points.
A5: The error bound derived theoretically may, for various reasons, be worse than the results observed empirically. However, empirical observations are always consistent with the theoretical results. The main reason for this phenomenon is that, under the necessary assumptions, the theoretically derived results hold universally under any conditions. In contrast, empirical observations fix certain conditions (such as the data distribution and the kernel function, etc.), which may lead the experiments to exhibit smaller errors. In the future, we also hope to obtain tighter error bounds under some reasonable assumptions, making them closer to the results of empirical observations.
### Q6: Why is the approximation effect of $\frac{1}{\sqrt{ns}} \mathbf{P}$ is much better than $\frac{1}{s} \mathbf{W}$?
A6: The theoretical proof of why the approximation effect is better is also an issue we are currently researching. At present, we provide the following explanation for this phenomenon: $\frac{1}{\sqrt{ns}} \mathbf{P}$ is constructed from the entire training set and the sampled anchor set, whereas $\frac{1}{s} \mathbf{W}$ is constructed solely from the anchor set. It can be seen that compared to $\frac{1}{s} \mathbf{W}$, $\frac{1}{\sqrt{ns}} \mathbf{P}$ contains more information about the training set, which is why the approximation effect is better.
### Q7: Draw the graph of the relative eigenvalue approximation errors $\frac{|a-b|}{\lambda_j(\mathbf{K}/n)}$.
A7: We have already plotted the graph of the relative eigenvalue approximation errors of the two methods. Please refer to the anonymous link https://anonymous.4open.science/r/ICML2025-8D7F/eigen_appro.svg. It can be seen that the relative approximation error of eigenvalues caused by SVD is much smaller than that of uniform sampling.
### Q8: What kernels were used? Are they all Gaussian kernels? How are their parameters set?
A8: For small-scale datasets, we used publicly available multiple kernel datasets. Relevant researchers carefully construct these datasets and make them available for public download. As for large-scale datasets, as described in Section 5.3, we employed the Gaussian kernel function and provided the corresponding parameters based on previous research experience.
---
Rebuttal Comment 1.1:
Comment: Thanks for your response, I will keep my score. | null | null | null | null | null | null | null | null |
TransPL: VQ-Code Transition Matrices for Pseudo-Labeling of Time Series Unsupervised Domain Adaptation | Accept (poster) | Summary: The paper presents TransPL, a novel unsupervised domain adaptation (UDA) method for time series data that improves pseudo-labeling by capturing temporal transitions and channel-wise shifts between domains. Traditional pseudo-labeling methods fail to model these patterns, leading to suboptimal labels. TransPL addresses this by constructing class- and channel-wise code transition matrices using vector quantization (VQ) of time series patches from the source domain and applying Bayes’ rule for adaptation to the target domain.
Claims And Evidence: The author claims that the Permutation Entropy of UCIHAR, HHAR, and WISDM data sets can prove that fine VQ code is more complex than coarse VQ code. This can indeed be seen from the visual representation.
Methods And Evaluation Criteria: The experimental design and benchmark dataset are nearly consistent with the protocols of previous studies in this field.
Theoretical Claims: This manuscript only uses the very basic Bayes’ rule.
Experimental Designs Or Analyses: Yes, I found the experimental results to be unreasonable. (listed on questions)
Supplementary Material: There is no supplementary material.
Relation To Broader Scientific Literature: Since this method does not use both source and target domain data simultaneously, it may be more aligned with the field of “source-free unsupervised domain adaptation” (SFUDA).
Essential References Not Discussed: It is recommended to join ACON[1] in the future.
[1] Liu, M., Chen, X., Shu, Y., Li, X., Guan, W., & Nie, L. (2024). Boosting Transferability and Discriminability for Time Series Domain Adaptation. Advances in Neural Information Processing Systems, 37, 100402-100427.
Other Strengths And Weaknesses: Strengths:
(1) The paper introduces a creative adaptation of vector quantization (VQ) techniques to the UDA setting.
(2) The integration of Bayesian inference with learned transition matrices offers a unique way to improve label reliability.
Weaknesses: As questions
Other Comments Or Suggestions: 1. Typos:
Line 171: “quantization”
2. As mentioned above, since this method does not use both source and target domain data simultaneously, it may be more aligned with the field of SFUDA.
Questions For Authors: 1. The term weakly-supervised UDA is somewhat confusing. Please clarify its meaning (including in the abstract) to avoid misunderstandings. If this terminology has been used in prior research, please provide proper citations.
2. This pipeline does not necessarily require VQVAE and could potentially perform better with a Mixture of Experts approach. Could you explain why VQVAE is essential to this framework?
3. Since VQVAE heavily relies on representation learning quality, the performance of the reconstruction task is a key factor influencing the domain adaptation task. Although Table 1 presents the MSE loss, could you provide further insights into the relationship between the reconstruction task and domain adaptation performance?
4. How can we justify that the representations learned for the classification task and the reconstruction task are similar rather than different? This could significantly impact how VQVAE learns representations. Given that this manuscript emphasizes interpretability, we would appreciate further clarification on this point.
5. It is unlikely that every dataset would achieve Zero Dead Code under the same codebook size. Could you explain how Zero Dead Code is ensured in this approach?
6. Why did you choose Earth Mover’s Distance?
7. Since this manuscript follows the AdaTime evaluation protocol, which is the same as ACON [1], why do other methods (e.g., RAINCOAT, CoDATS, DeepCoral) perform significantly worse under the same dataset and scenario? Please provide a thorough explanation; otherwise, this discrepancy raises concerns about the validity of the manuscript’s findings.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank the reviewer for thoroughly going through our manuscript, and providing valuable comments. We want to highlight points that were misunderstood and should be clarified. While we wish to thank you individually for each point, we are constrained by the length limit. Thank you for your understanding.
**C1. Missing Ref.** ACON. We will add them to our updated manuscript.
**C2. SFUDA.** This is a misunderstanding. Our TransPL is not source-free, as it utilizes the source training data alongside the pseudo-labeled target training data for adaptation, as noted in Line 162: *where the model is fine-tuned using the labeled source and pseudo-labeled target data for domain adaptation.* We note that our work can be extended to the SFUDA, if we only utilize the target data for adaptation, but we believe this is out of our scope where our current focus is on the UDA setup. However, based on the reviewer's insight, we found that this could be better clarified. As such, we added *The adaptation is complete by fine-tuning the model with both labeled source and the pseudo-labeled target training set* in Lines 321.
**Q1. Weakly-Sup. UDA.** The term Weakly-Supervised means that the label distribution of the target domain is given as an additional source of information. Such scenarios are highly practical as users might not label all of their data but can self-report on the proportion of time they have spent on each exercise. This term was first used in time series by CoDATS [KDD'20] (we would like to address the reviewer to Lines 100-109 and Lines 353-355, where we have provided explanations and proper citations needed).
**Q2. VQVAE.** The use of VQVAE is essential, and all the proposed works build on top of VQ. We are not aware of other architectures that could better replace VQVAE. Simply, a patch can now be represented as discrete codes. These discrete codes are then used for modeling the temporal transitions and channel-wise shifts, which are the main contributions of this work. Here, VQ enables the **mapping of each time series patch** into coarse code vectors. This makes the semantics of the time series intact, while making the transition matrices sensible.
**Q3. Recon. Performance.** The reviewer is correct. Reconstruction is important for our use, as good reconstruction ensures meaningful code vectors to be constructed, which is critical for valid transition matrices. Constructing non-representative code vectors that can't represent the time series task at hand leads to meaningless transition matrices, leading to degraded pseudo label accuracy. In Table 1, we show that obtaining good reconstruction performance as well as making the transition meaningful (by limiting the # of coarse codes) are both essential to making accurate pseudo labels.
**Q4. Recon. and Classification.** While there is no strict guarantee that the representations for classification and reconstruction are identical, we argue that they are well aligned for the following:
1. **Empirical Evidence**: Our results show strong performance in both classification and reconstruction across multiple data, with no signs of overfitting to one task. The pseudo labels consistently achieve the best results, and both losses are well optimized, leading to stable outcomes.
2. **Prior Works**: Prior works in time series [1,2] have successfully used VQVAE for both reconstruction and classification. Additionally, optimizing auxiliary tasks alongside reconstruction is a common practice in the broader literature [3].
[1] TOTEM: TOkenized Time Series EMbeddings for General TS [TMLR'24]
[2] VQ Pretraining for EEG TS with Random Projection and Phase Alignment [ICML'24]
[3] DeWave: Discrete EEG Waves Encoding for Brain Dynamics [NeurIPS '23]
Q5. While we have empirically observed that zero dead coarse code was achieved in all of our tasks, we acknowledge that this is a practical result. To practically ensure this, we have explicitly designed the coarse codes to have a limited number of codes (N=8; modeling the trend pattern) compared to the more large use of code size (N=256, 512), making sure that there is a higher chance of using all codes in the coarse codebook to map the trend pattern. However, we understand this is a practical outcome and would like to include it in the limitation section.
Q6. EMD was necessary, as different codes may contain similar semantics. For instance, if code 1 and code 2 capture similar information, the transition between 1->1 and 1->2 should be deemed similar. Other metrics such as MSE cannot take this semantics into account (they treat 1 and 2 differently), while EMD can incorporate such information with the use of cost matrix M (defined as similarity in Eq 6). We direct the reviewer to the section "Channel Alignment via Optimal Transport, where we have provided a detailed example and the motivation behind the use of EMD.
**Q7. Eval. protocol.** We direct the reviewer to our response **E1 of Reviewer n6fN (3rd reviewer)** | Summary: The paper introduces **TransPL**, a novel unsupervised domain adaptation (UDA) strategy for time series classification. It addresses the key challenge of domain variability in time series data arising from **temporal transitions** and **sensor characteristics**. To tackle this, the method employs a **coarse-to-fine VQ structure** to construct class- and channel-wise transition matrices. Additionally, the integration of **transition matrices** and **channel alignment** enhances both adaptation performance and interpretability. Notably, TransPL can seamlessly extend to weakly supervised scenarios and outperform existing pseudo-labeling methods in UDA tasks.
## update after rebuttal
The authors explained the performance gaps between the results presented in the manuscript and those of prior work. This is due to their choice of interpretability over performance, which seems reasonable but also raises concern about whether such performance sacrifice is worthwhile. Overall, I think introducing the idea of vector quantization to time series adaptation is interesting and adjusted my score slightly.
Claims And Evidence: The author emphasizes the significance of characterizing temporal transitions in time series data and integrating selective sensor (channel) shifts in time series domain adaptation task, and illustrates this concept with an example from human activity recognition.
Methods And Evaluation Criteria: * TransPL models the joint distribution $P(X,y)$ of the labeled source domain by constructing code transition matrices, which are then employed to pseudo-label the unlabeled target training set using Bayes' rule. However, the validity of interpreting temporal dynamic transformations using Markov chains remains open to debate.
* The paper evaluates TransPL on four widely used time series benchmarks, covering both human activity recognition (HAR) and electrocardiogram (ECG) classification.
Theoretical Claims: The mathematical formulas in the paper seem correct, and the generation of pseudo-labels is based on methods from Bayesian inference and optimal transport.
Experimental Designs Or Analyses: - Unjustified Performance Gaps with Baseline Methods:
The paper adopts the same domain pairs and source risk selection strategy as ADATime (a 1D-CNN-based method), yet reports substantially worse performance (e.g., CODATS accuracy of 39.6 vs. 72.67 on the HHAR dataset’s 0-to-6 task), despite using a stronger backbone (patch transformer). A performance drop of ~30 percentage points across multiple adaptation tasks is alarming, especially since ADATime and Raincoat (reproducible via open-source code) have demonstrated reliable results.
In short, why does the proposed method underperform ADATime and other reproducible baselines by such a large margin?
- Contradiction Between Model Complexity and Effectiveness: The patch transformer architecture is more complex than the 1D-CNN used in ADATime, yet it achieves significantly lower accuracy. This contradicts the expectation that advanced architectures should enhance performance.
In short, can the proposed method improve performance when applied to simpler 1D-CNN backbones?
- Outdated and Incomplete Baseline Comparisons:
The experiments exclude 2024 state-of-the-art methods, which weakens the paper’s effectiveness.
Supplementary Material: I checked the appendix. The supplementary material enhances the credibility of the paper by providing detailed implementation, comprehensive results, and ablation studies.
Relation To Broader Scientific Literature: TransPL extends previous work by integrating ideas from UDA, pseudo-labeling, vector quantization, and optimal transport. A key highlight of the paper is the construction and application of the transition matrices.
Essential References Not Discussed: The most recently developed methods on the topic are missing, e.g.,
[1] Dwlr: Domain adaptation under label shift for wearable sensor. IJCAI24.
[2] Caudits: Causal disentangled domain adaptation of multivariate time series. ICML24.
[3] Boosting Transferability and Discriminability for Time Series Domain Adaptation. NeurIPS24
Other Strengths And Weaknesses: * The proposed algorithm seems to exhibit considerable time complexity. Could the authors provide additional details?
* In the experimental section, the subsection titled "Use of Transition Matrix" lacks clarity and is somewhat difficult to follow. A more detailed or structured explanation would improve its comprehensibility.
Other Comments Or Suggestions: The authors adopt an innovative approach to generate pseudo-labels for time series data, which enhances their accuracy and supports more effective training of target domain data. However, when deriving pseudo-labels for a specific target domain sample, leveraging both the source domain’s transition matrix and the target sample’s transition matrix in the computation could potentially yield slightly more precise pseudo-labels.
Questions For Authors: * Why does the proposed method underperform ADATime and other reproducible baselines by such a large margin?
* Can the proposed method improve performance when applied to simpler 1D-CNN backbones?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We first and foremost thank the reviewer for the thorough review of our work. We greatly appreciate your services. Here, we have prepared a detailed explanation to address each of the reviewer's questions.
**E1. Performance of Baseline Methods.** Thank you for pointing this out. The performance gap stems from our use of patch transformer versus the 1D-CNN backbone in previous works. For fair comparison, we standardized all baselines with the same transformer architecture. While transformers typically require larger datasets to outperform simpler models in time series applications [1], our choice was deliberate: patch transformers preserve the semantic meaning of individual time segments (patch) in latent space, making coarse code transition matrices interpretable. **As we are trying to model the temporal transition in time series, having meaningful and interpretable patch representation is necessary for our whole methodology**. Unfortunately, 1D-CNN representations lack this interpretability as it mixes all features in the latent space. We acknowledge this design choice prioritizes interpretability of the constructed pseudo labels at some cost to overall performance, and we would like to include this in our limitation. Thank you for addressing this point.
[1] Are Transformers Effective for Time Series Forecasting? [AAAI 22]
**E2. Applying to 1d-CNN backbones**. Thank you for the suggestion. We believe that using 1d-CNN models could lead to enhanced model performance. However, as mentioned in **E1**, our methodology relies on the use of patch representation to keep the semantics. One possible way is to jointly optimize the 1d-CNN model alongside the patch encoder, but this would increase the computation, and also, **we would not be able to solely focus on the performance gain that can be brought with our coarse code transition matrix modeling.** As the whole paper focuses on developing pseudo labeling strategies that reflect temporal transitions and the channel-wise shift, the use of patch transformer was necessary.
**E3. Need for additional baselines.** Thank you for this valuable comment. We acknowledge that some of the baselines were missing (CauDiTS did not release their code), however, **we have compared our work to 12 other more relevant baselines**. These baselines include relevant works such as RainCOAT (UDA) and T2PL (pseudo-labeling), which help us understand the significance of TransPL. While adding additional baselines could be helpful, we courteously request the reviewer to have a look at the additional analysis we have performed, which is novel and both needed to support our claims in the paper. For instance, we showed class-conditional likelihoods to
**C1. Time Complexity.** The dominant computational cost comes from counting code transitions across all source samples. With N_s source samples, N patches per sequence, and D channels, this requires O(N_s × D × N) operations. However, implementation is practical due to (1) efficient vectorization techniques (da_utilities/transition_matrix.py file) for counting transitions and (2) the extremely limited number of coarse codes (only 8). For the UCIHAR dataset (9 channels, 14 patches per sequence), the total transition matrix construction time takes only 9.954±0.478 seconds.
**C2. Use of Transition Matrix**. The purpose of this section was to highlight the benefits of using transition matrices to construct pseudo labels instead of directly constructing classifiers (1d-CNN, GRU, LSTM) that could be used to predict the pseudo labels. These discriminative models were trained using the (source) coarse code sequences and were trained to predict source classes. However, we show that such discriminative approaches fall behind our use of the generative approach (modeling the conditional likelihoods using the transition matrix), validating the use of transition matrices. Based on the reviewer's suggestion, we will refine this section for better clarity in the updated manuscript.
**Q1,2.** We believe that we have addressed the questions in E1 and E2.
We hope we have addressed the reviewers' concerns. Please let us know if any points require further clarification.
---
Rebuttal Comment 1.1:
Comment: Thanks for the clarification. But I am now concerned about the setting of replacing 1D-CNN backbone with patch Transformer for all baseline methods. Is this a fair setting? From my side, it is meaningful to adopt patch Transformer for the proposed method since it aims to preserve the semantic meaning, but the baseline methods are not claimed to be designed for this purpose in their original papers. Also, there is no clear evidence that patch Transformer is inferior to 1D-CNN on small datasets or at least it cannot account for such large performance gaps.
---
Reply to Comment 1.1.1:
Comment: We thank the reviewer for the thoughtful feedback and acknowledge the valid concern regarding our experimental setup. We appreciate the opportunity to clarify our methodological decisions.
**Justification for Using Patch Transformer:**
1. **Algorithmic Contribution vs. SOTA Performance** Our work's primary contribution is algorithmic—we explicitly model temporal transitions and selective channel shifts, which cannot be adequately represented with a 1D-CNN architecture. 1D-CNN inherently mixes information between channels and temporal features, making it impossible to construct the code transition matrix that is central to our proposed method.
2. **Semantic Preservation Requirement** As the reviewer acknowledged, PatchTransformer maintains the semantics of each temporal patch, enabling meaningful transitions between these patches. In contrast, transitions between latent representations from 1D-CNN lack interpretable meaning for our specific approach.
3. **Consistent Comparison Framework** We implemented all methods (our proposed method and baselines) using the same backbone **to ensure a fair comparison focused on algorithmic contributions** rather than architectural advantages. This isolates the impact of our domain adaptation techniques from backbone-specific benefits. To ensure fair comparison, we have also tested on the same 10 source-target pairs as in AdaTime and reported all results, while several later works only partially use the source-target pairs suggested in AdaTime.
**Regarding Baseline Implementations:**
For baseline methods, we have adapted popular algorithms that are **model agnostic domain adaptation algorithm** and **pseudo label algorithms** (DeepCoral, MMDA, SoftMax, NCP, SP, ATT, SHOT, T2PL) to work with the Patch Transformer backbone while preserving their core algorithmic contributions. None of the algorithms above claim to work on specific model architectures. While Raincoat and CoDATS were built on top of 1D-CNN, they do not leverage any specific properties of the 1D-CNN architecture in their adaptation mechanisms. Their core contributions, the loss functions and adaptation techniques, are entirely independent of the backbone choice.
This standardization approach aligns with established practices in the field. As noted by AdaTime [1]: *"standardizing the backbone network choice is necessary to compare different UDA methods fairly. However, some previous TS-UDA works adopted different backbone architectures when comparing against baseline methods, leading to inaccurate conclusions."* By maintaining architectural consistency across all evaluated methods, we allow for a direct assessment of each UDA and Pseudo Label algorithm to domain adaptation performance. We believe our approach of using the same Patch-based backbone represents the fairest possible comparison given the requirements of our approach.
We respectfully request the reviewer for an alternative experimental setup that would provide an equitable comparison while respecting the semantic preservation (our algorithmic contribution relies on this) requirements of our method. We would be grateful for this guidance and are willing to conduct additional experiments. We once again thank the reviewer for their dedication to reviewing our work.
[1] AdaTime: A Benchmarking Suite for Domain Adaptation on Time Series Data
Best,
Authors | Summary: This paper introduces TransPL, a novel pseudo-labeling approach for unsupervised domain adaptation in time series data. The authors argue that traditional pseudo-labeling strategies fail to capture temporal patterns and channel-wise shifts between domains, leading to sub-optimal pseudo labels. To address this, TransPL leverages vector quantization to model the joint distribution of the source domain through code transition matrices. The method constructs class- and channel-wise transition matrices from the source domain and uses Bayes' rule to generate pseudo-labels for the target domain. The authors claim that TransPL outperforms state-of-the-art methods in terms of accuracy and F1 score, while also providing interpretable insights into the domain adaptation process.
Claims And Evidence: The paper claims that traditional pseudo-labeling strategies fail to capture temporal patterns and channel-wise shifts, but it does not provide sufficient evidence or analysis to support this claim. The motivation for why existing methods fail is not well-justified, and the paper lacks a clear explanation of why the proposed method is better suited to address these issues.
Methods And Evaluation Criteria: The main concern in this part is the lack of Justification for VQVAE. Specifically, the paper does not provide a clear justification for why VQVAE is necessary or superior to other methods. The use of VQVAE feels like a technical add-on rather than a well-motivated choice, making it difficult to understand the true contribution of this component to the overall performance.
Theoretical Claims: N.A.
Experimental Designs Or Analyses: Lack of Ablation Studies on Coarse and Fine Codes: The paper introduces the concept of coarse and fine codes but does not provide ablation studies to show the individual impact of each. Without experiments that isolate the effects of coarse and fine codes, it is difficult to assess their respective contributions to the model's performance.
Supplementary Material: I have read the additional experiment in the supplementary material.
Relation To Broader Scientific Literature: Overly Complex Technical Framework: The paper combines multiple advanced techniques, including VQVAE, optimal transport, and pseudo-labeling, without clearly isolating the contribution of each component. This makes it challenging to determine which part of the framework is responsible for the performance gains, and whether the method is overly complex for the problem at hand.
Essential References Not Discussed: N.A.
Other Strengths And Weaknesses: Strong Points:
1. **Strong Experimental Results**: The paper demonstrates significant improvements in accuracy and F1 score across multiple time series benchmarks, outperforming existing state-of-the-art methods.
2. **Clear and Well-Presented Visualizations**: The paper includes well-designed figures and tables that effectively illustrate the method's performance and interpretability.
Weak Points:
1. **Lack of Justification for VQVAE**: The paper does not provide a clear justification for why VQVAE is necessary or superior to other methods. The use of VQVAE feels like a technical add-on rather than a well-motivated choice, making it difficult to understand the true contribution of this component to the overall performance.
2. **Overly Complex Technical Framework**: The paper combines multiple advanced techniques, including VQVAE, optimal transport, and pseudo-labeling, without clearly isolating the contribution of each component. This makes it challenging to determine which part of the framework is responsible for the performance gains, and whether the method is overly complex for the problem at hand.
3. **Lack of Ablation Studies on Coarse and Fine Codes**: The paper introduces the concept of coarse and fine codes but does not provide ablation studies to show the individual impact of each. Without experiments that isolate the effects of coarse and fine codes, it is difficult to assess their respective contributions to the model's performance.
4. **Unclear Motivation**: The paper claims that traditional pseudo-labeling strategies fail to capture temporal patterns and channel-wise shifts, but it does not provide sufficient evidence or analysis to support this claim. The motivation for why existing methods fail is not well-justified, and the paper lacks a clear explanation of why the proposed method is better suited to address these issues.
Other Comments Or Suggestions: N.A.
Questions For Authors: N.A.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We sincerely appreciate the reviewer’s thorough evaluation of our manuscript and the valuable feedback provided. We are pleased that the reviewer found our work to have strong experimental results and well-presented visualizations. Below, we have prepared a detailed response to address the reviewer’s concerns.
**W1. Justification for VQVAE.** We respectfully disagree that VQVAE is merely a technical add-on—it is the cornerstone of our approach, which enables the density estimation of the source (**which is infeasible without VQVAE, Sec 4. Source Training**)
VQVAE enables learning meaningful discrete representations of time series segments, which is essential for modeling the proposed temporal transitions in TransPL. To provide a very simplistic example, in a sequence like 1,2,5,6,1,2, VQVAE **learns** to map similar patches to discrete codes (1,2→"A", 5,6→"B"), creating a simplified and abstracted transition sequence A→B→A. Consequently, the use of transition matrices relies on these code transitions, and our proposed class-conditional likelihood generation for pseudo-labeling and the quantification of channel-wise shift rely on these transition matrices. As such, VQVAE is essential to our work. Other methods like SAX rely on predefined quantization schemes that may not capture data-specific patterns as in VQVAE. We would like to address the reviewer to Section 2.3 for detailed reasons behind our use of VQ.
**W2. Design Principles** We respectfully note an oversight in this assessment. While the design may appear complex initially, each component serves a critical function in our framework. These elements work together to achieve our stated goal: effective time series pseudo-labeling that accounts for both temporal transitions and channel-wise shifts—the core motivations we established at the introduction.
**(VQVAE)** - Please kindly refer to **W1**.
**Optimal Transport (OT)** - TransPL requires comparing coarse code transition patterns between source and target domains while preserving semantic relationships. Unlike L1/L2 metrics that calculate absolute usage differences, **OT acknowledges semantic similarity between patches.** For example, if patches A and B encode similar information, transitions A→A and A→B should be considered similar. OT incorporates these semantics through a cost matrix defined by patch similarities, enabling a more meaningful comparison of transition patterns that respects the underlying data structure.
Both modules are necessary designs for constructing pseudo labels, and we believe that they are not overly complex. They are the most simplistic method for obtaining pseudo-labels that account for temporal transitions and channel-wise shifts. No other pseudo labels take these into account.
**W3. Lack of Ablation for Coarse Code.** We direct the reviewer to **Table 1**, which contains our detailed ablation study on the use of coarse codes. The first three rows evaluate single codebook performance with varying sizes, while the last four rows compare different codebook size combinations for coarse and fine codes. These results demonstrate that our proposed design principle yields the best pseudo-labeling accuracy.
**W4. Unclear Motivation.** We respectfully disagree that our motivation is unclear. As we have noted in our Introduction, **our motivation is to design a pseudo-label method that considers the temporality and channel-wise selective shifts that happen in time series adaptation**. No other pseudo label methods consider both problems nor incorporate these into the pseudo labeling process of time series. Other pseudo-labeling methods (SoftMax, NCP, T2PL) rely on the clustering ability, representation performance of the source classifier, and without any focus on time series characteristics, while our methodology focuses on the two most important aspects of time series (time and channel). We have shown in Table 2 that other method fails to obtain strong adaptation performance, and that pseudo label accuracy is low compared to ours in Table 3. We also show that channel-wise alignment distance is better captured through our proposed work. We believe that we have sufficiently addressed our motivation throughout the whole paper, and the experiments conducted are well justified to back our motivation.
We hope that we have addressed the concerns of the reviewers. If there is anything that is still unclear, please kindly let us know. | Summary: The authors propose a new method, TransPL, for unsupervised time series adaptation. Unsupervised domain adaptation deals with settings where a model trained on source domain data with available labels has to be adapted to perform well in target domain with shifted data without available labels.
The proposed method uses vector quantized variational auto encoder (VQAE) to get discrete latent code books for time series patches. This VAQE model is pretrained on source data. A classifier is also trained on top of these source encodings using the available source labels. The learned discrete code books are used to obtain transition matrices which describe how a time series patterns switch.
The authors use this scheme to obtain transition matrices for each channel.
The computed transition matrices for the source and target domain channels are used in optimal transport distance to obtain domain discrepancy scores for each channel. This scheme ensures that the computed optimal transport distance, and thus the resulting channel score, is lower for channels with large shifts between source and target domains.
These channel scores are used as weights for channel specific posteriors for each class. This weighted (and normalized) sum across all channels of these channel specific posterior provides the posterior probability for the a particular class. This is repeated for all classes to obtain posterior score across all classes for the provided input.
These posterior scores for a target data point can be used to obtain pseudo labels for unlabelled target domain data.
High confidence pseudo labels in the target domain are used to to optimize the source model( VQAE encoder, decoder, codebooks and classifier on top of the encodings)
The proposed method is able to selectively down-weigh channels that have a large discrepancy. It can also incorporate different label probabilities as priors when computing posterior probabilities. This allows the method to incorporate weak target supervision when target label distribution is available.
Extended results on multiple domain adaptation datasets show that the proposed method improves performance on existing domain adaptation methods.
Claims And Evidence: The claims made in the paper are mostly supported by convincing evidence.
The authors show that the proposed method results in improved performance over existing methods.
The ablation studies show how their proposed method's ability to incorporate weak supervision and adaptive channel alignment improve performance. These ablations provide clear and convincing evidence to support the stated claims.
The authors also provide ablation studies for the proposed channel adaptation layer, but visualizations on a single 3 dimension example are not fully convincing to back their claim the proposed scheme of capturing scheme and discarding channels with large shifts. This significance of these claims is also limited by the ablation results in Table 5, where we see that the PTB dataset, with 15 channels, has its performance degraded when channel adaptation is used. Maybe this is a misunderstanding on my end, but for a dataset with large number of channels, the channel adaptation strategy should further improve performance.
I would suggest a more thorough experimental analysis to verify that the proposed channel adaptive layer and discard channels with large shifts. This can be done through simulated examples on existing datasets where random channels are corrupted through noise.
The authors also claim that the proposed methods provides explainable insights for domain adaptation. This is slightly vague, and I can't seem to find direct experiments which back this claim.
Methods And Evaluation Criteria: The proposed method and evaluation criteria mostly make sense.
The authors test on commonly used benchmarks for time series adaptation. They also provide a thorough comparison with existing unsupervised domain adaptation methods.
They also provide use commonly used metrics such as target domain AUC/F1 score to evaluate unsupervised domain adaptation performance
They also show how their proposed method improves pseudo labelling accuracy as compared to other baseline methods that also employ pseudo labelling.
Additional results are also provided which show how the performance degrades when their proposed approach of modeling both coarse and fine codes through VQAE is replaced by directly modeling codes through other encoders such as 1DCNN.
Theoretical Claims: There are no theoretical claims made in this paper
Experimental Designs Or Analyses: I have checked the experimental design and analysis results provided in Table 1 (that provides VQAE code performance interns of data reconstruction, and pseudo labelling accuracy).
I also checked experimental design results for Table2 (adaptation performance on target), Table 3 (accuracy of pseudo labels), and Table 4 (weak supervision UDA), and ablation studies Table 5.
These experimental design make sense.
Supplementary Material: I went through the supplementary material where the authors provide experimental results and details on different datasets.
They also provide visualizations for the coarse and fine codes that are learned.
Relation To Broader Scientific Literature: The authors sufficiently place their paper in context of the broader scientific literature for domain adaptation and learning discrete latent codes.
Essential References Not Discussed: The authors mostly discuss all essential references.
They do claim that existing domain adaptation methods can not model channel level shifts.
There has been very recent work [1] that tackles channel level shift for unsupervised domain adaptation.
This paper seems to have been published pretty recently and perhaps before the ICML deadline, so ofcourse its totally understandable for the authors to not mention this originally.
Though given how relevant this work is, mention [1] would strengthen the proposed work section.
[1] Ahad, N., Davenport, M. A., & Dyer, E. L. Time Series Domain Adaptation via Channel-Selective Representation Alignment. Transactions on Machine Learning Research.
Other Strengths And Weaknesses: Strengths:
- A promising scheme of incorporating transition matrices for domain adaptation. This is very novel contribution which hasn't been explored within the context of unsupervised time series adaptation
- A scheme which allows to incorporate weak supervision
- Thorough evaluation on datasets and comparison with numerous to support claims made.
Weakness:
- There is not discussion on limitations of their proposed work. Unsupervised domain adaptation practically only works if many assumptions are met. [2] provides an overview of these assumptions for images, but the same assumptions can be extended to shifts for any types of domains.
It makes sense to support their claim that code transition matrices are more invariant across changes (and can also hep identify and ignore channels with large shifts), but there certainly can be cases where the domain shift is large that transition matrices from incorrect classes are nearby. There is no one domain adaptation method which is best for all scenarios. In some cases Frequency information might be more invariant,(like proposed by RAINCOAT), but in other scenarios transition matrices might be more invariant .
- The analysis on channel alignment and how it affects performance in section 7.6 is weak and only considers one example of a 3 channel dataset. Considering how performance with channel alignment does not improve significantly on the 15 channel PTB dataset, I would suggest more through experiments to study how the proposed method effectively ignores channels with large shifts. This can be done through inducing channel level corruptions, and analyzing the proposed model's performance in terms of accuracy of target domain data , as well as the ability to ignore corrupted channels.
[2] Gijs van Tulder and Marleen de Bruijne. Unpaired, unsupervised domaadaptation assumes your domains are
already similar. Medical Image Analysis., 2023.
Other Comments Or Suggestions: The paper is mostly well written and I wasn't able to find any glaring typos
Questions For Authors: - How is the cross entropy layer classifier head trained? is traded on top of coarse codes? This was perhaps not clear from the text, or Figure 1 in its present form
- How are class wise class conditional likelihoods obtained using class wise Transition matrices? This is perhaps not clear in the text in its present form
- - There can be scenarios where code transitions should be computed across multiple channels as compared to once channel. Would these channel specific coarse codes capture correlations across channels which could be important to capture?
- Can there be cases where there is a large shift between channels, but the transition matrices are still relatively close for channels? E.g there might be a large DC shift in the channel,
- The mutual information between channel content and class labels can vary across channels. There certainly can be cases where class information is mostly contained in only a few channels. how would the proposed method perform when there is a large corruption in such channels across source and target domains. Would the proposed scheme ignore such channels (as the transition metrics could be very different leading to lower $w_d$?) This is ofcourse totally fine, but this could be a limitation that needs to be made explicit for practitioners and readers.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely thank Reviewer fkT4 for the thorough, insightful, and constructive feedback. We appreciate that the reviewer has found our work a novel contribution for UDA time series that has not been explored elsewhere. We also thank the reviewer for thinking through our problem definition with us. We have provided detailed responses to address each of its comments.
**Q1. Training Cross-Entropy.** The cross-entropy is calculated using a [CLS] token appended to the input patches. After processing through the Encoder, this [CLS] token—having attended to all time series tokens via transformer—is used to train the classifier. We will add a guiding arrow in **Fig. 1** to clarify this flow. We also refer to Lines 194-196.
**Q2. Class Conditional Likelihood.** After encoder training, we process unlabeled target time series to obtain discrete code sequences (e.g., A-B-A). We then calculate the likelihood of observing this sequence under each class-specific transition matrix from the source domain, similar to maximum likelihood estimation in Hidden Markov Models. For instance, for a given sequence A-B-A, the Class 1 Transition matrix may output higher likelihood, and the Class 2 Transition matrix may output low likelihood. This allows us to assign the most probable class label to each target sequence. We direct the reviewer to **Eq. 7** and **Fig.1** for additional clarification.
**Q3. Correlations between Channels.**
Currently, we use the same codebook to model all sequences in a time series but construct channel-wise transition matrices to represent each channel. As such, we could presumably say that the shared codebook can capture correlations between channels. While we have also tried modeling each channel with separate codebooks, we empirically found that this did not lead to better pseudo-labeling results (It might be due to increased complexity; alternative design methods should be further looked into).
**Q4. Transition Matrix Remains Similar.** This is also an interesting point. We believe that in such a scenario (e.g., DC shift), the transition patterns would greatly differ, as our codebook does not solely focus on the shapes of the time series pattern. If a large DC shift occurs, it would most likely return different time series signal values that should be reflected in the coarse code usage pattern.
**Q5. Channel Importance.** We find this really interesting and appreciate this insightful point. The reviewer is correct that only certain channels may contain class-relevant information [1], and when class information is concentrated in channels experiencing significant domain shift, our method would assign lower weights to these channels due to the large EMD distance. This is a limitation we'll explicitly acknowledge in our revision. We plan to extend our approach in future work by incorporating channel importance measures alongside distribution shift metrics, allowing for weighting that considers both channel-shift and the importance of channel for classification.
[1] CAFO: Feature-Centric Explanation on Time Series Classification (KDD'24)
**R1. [TMLR paper]** We will include the provided reference. We also think it will strengthen our work!
**W1. Limitation**. As the reviewer has noted in Q5, we believe that TransPL may not operate optimally in cases where the heavily shifted channel contains class-discriminative information, as our pseudo-labeling method would weigh less on such channels. We will incorporate this into our Limitation Section in the updated manuscript.
**W2. Additional Analysis.** We appreciate the reviewer's valuable insight regarding channel alignment analysis. We propose the following experiment to address this concern:
**Analyzing Channel-Level Corruption.** We plan to inject random noise into high-weight channels ($w_d $) in the adaptation scenario and measure adaptation performance by tracking the reduction in $w_d $ after noise injection. A reduction would demonstrate the model's ability to downweight corrupted channels. Would the reviewer consider this a suitable approach to provide more thorough evidence of our method's capability to identify and ignore channels with large distributional shifts?
We once again thank the reviewer for providing helpful feedback to improve our work. Please let us know if there are any additional uncertainties so that we can address them. Thank you.
---
Rebuttal Comment 1.1:
Comment: Thank you for your detailed answers to my questions.
Also, thank you for the clarification to my questions on cross entropy and class conditional likelihood.
These additional experiments such as analyzing Channel level corruptions, channel importance would certainly strengthen the paper.
I also think it might be worth including experiments which do test whether the transition matrix remains similar across diffrent types of shifts. This would help readers better understand the limitations or scenarios where transition matrix could vary significantly across domains.
One additional question: Do you think is approach is scalable as the number of dimensions increase? As that would involve computing different transition matrices for each channel? Would this be scalable when there are 100 channels?
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer **fkT4**,
We sincerely thank the reviewer for the thoughtful feedback on our work. We're pleased that our clarifications regarding cross entropy and class conditional likelihood have addressed the reviewer’s earlier concerns. Below, we provide detailed responses to the remaining suggestions.
**Channel-Level Corruptions** Following the reviewer’s recommendation, we conducted channel-level corruption experiments on the UCIHAR task across all 10 source-target pairs. (We provide the experimental results through an Annonymous Github). After analyzing the data, we identified that the 6th channel consistently exhibited high $w_d$ values across most of these pairs. When we introduced increasing levels of noise (Gaussian) to this specific channel, we observed a corresponding decrease in $w_6$ values, confirming the utility of Channel-Level Adaptation. We will incorporate these experimental results and their analysis in our revised manuscript. The reviewer’s suggestion has significantly strengthened our empirical validation.
Experimental Results: https://anonymous.4open.science/r/TransPL_Anon2-C325/
**Different Types of Shifts** We appreciate the reviewer’s recommendation to examine transition matrices across various shift types. This is indeed an intriguing direction. However, we face challenges in determining appropriate shift types and methodologies for synthetically inducing diverse shifts in our time series data. We would greatly appreciate it if the reviewer could suggest relevant literature that might guide our approach to this question. We're eager to explore this direction in our ongoing work.
**Scalability to Increased Channel Dimension** Our approach demonstrates strong scalability with increased channel dimensions, as the transition matrices between limited coarse codes remain computationally efficient. While higher channel dimensionality poses less significant challenges to our TransPL framework, we acknowledge a practical tradeoff between the number of patches and the computational time required to count transitions between these patches. For time series problems with more than 100 channels, we would suggest first filtering and reducing the number of channels to those most relevant to the task at hand. TransPL can then be effectively applied to these filtered time series, maintaining computational efficiency while preserving performance.
We once again thank the reviewer for their constructive feedback, which has significantly strengthened our work. We remain available to address any additional questions or concerns.
Best Regards,
Authors. | null | null | null | null | null | null |
Leveraging Per-Instance Privacy for Machine Unlearning | Accept (poster) | Summary: This work introduces a theoretically grounded, data-dependent measure of difficulty between data privacy and unlearning. While the current analysis has limitations (scalability, group guarantees), the empirical results are compelling.
Claims And Evidence: The identification of "harder" forget sets via privacy losses and the loss barrier analysis offer actionable insights for evaluating and improving unlearning algorithms.
Methods And Evaluation Criteria: Extensive experiments on SGLD, SGD, and L1-Sparse unlearning demonstrate the practical relevance of privacy losses. The inclusion of loss barrier analysis adds a geometric perspective to unlearning efficacy.
Theoretical Claims: The paper provides a novel theoretical framework for per-instance unlearning difficulty using Renyi divergence and differential privacy. By replacing worst-case DP bounds with per-instance privacy losses, it offers a more nuanced understanding of unlearning dynamics.
Experimental Designs Or Analyses: How does varying the forget set size (e.g., 10% vs. 50% of data) affect the predictive power of privacy losses?
Supplementary Material: Additional Experimental Details are double checked.
Relation To Broader Scientific Literature: The correlation between privacy losses and established proxies (e.g., C-Proxy, EL2N) bridges theory and heuristic approaches, grounding the work in prior literature.
Essential References Not Discussed: Not any.
Other Strengths And Weaknesses: Weakness: 1) Experiments are limited to small-scale datasets (CIFAR-10, SVHN) and architectures (ResNet-18/ViT). The scalability to large models (e.g., LLMs) or massive datasets remains unverified. 2) The paper acknowledges that group unlearning guarantees are not tight but does not propose concrete steps to address this gap. This limits practical applicability for multi-point deletion. 3) For SGD experiments, privacy losses are computed under an assumed implicit noise (σ ≤ 0.1). While pragmatic, this lacks theoretical justification and may not hold in non-stochastic settings.
Other Comments Or Suggestions: The paper emphasizes correlation with existing proxies but does not rigorously establish causality between privacy losses and unlearning difficulty. The correlation seems trivial and needs more analyzed, for example, from casual effect perspective. The Monte Carlo estimation of privacy losses via checkpoints may introduce bias.
Questions For Authors: How do loss barriers correlate with adversarial robustness or membership inference attack success? Do smaller barriers imply better security post-unlearning? Were other data difficulty metrics (e.g., influence functions) considered? How do they compare to privacy losses in terms of cost and predictive power? How does the computational cost of estimating per-instance privacy losses scale with model size (e.g., transformers) and dataset size? Could gradient checkpointing or sampling mitigate this? Can you provide empirical/theoretical evidence that the implicit noise assumption in SGD holds? How sensitive are the results to the choice of σ?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your feedback. Your review raises several important points: concerns about scalability to larger models and datasets, the practical implications of group-level unlearning, assumptions around noise in SGD, and the strength of causal interpretations in our analysis. You also asked about sensitivity to experimental parameters such as forget set size.
We address these concerns below with additional experiments and clarifications. We show that privacy losses remain predictive across varying forget set sizes and are robust to assumptions on implicit SGD noise. Our method remains practical even when theoretical guarantees do not extend cleanly to group unlearning, as we demonstrate empirical effectiveness. Furthermore, we explain clearly why our causal interpretations are theoretically grounded, rather than simply correlational. Finally, we discuss computational cost in the context of scalability.
**Experimental Designs Or Analyses.Unclear effect of forget set size**
We ran additional experiments varying forget set size and found that privacy losses consistently separate easy and hard sets, even with smaller subsets. As set size increases, differences become smaller: this is intuitive as the variance in average privacy loss gets smaller. Figures for forget set sizes 100, 5,000, and 10,000 are available at:
https://files.catbox.moe/l8ky5z.png,
https://files.catbox.moe/odaa0g.png,
https://files.catbox.moe/dqxk61.png.
We will include these results and discussion in the revised draft.
**Other Strengths And Weaknesses 1. Lack of scalability to larger models and datasets**
While more large-scale experiments would strengthen our claims, we already include several evaluations across multiple models and datasets (and SGLD noise). We’d appreciate clarification on what specifically the reviewer would want to understand by using larger models.
**Other Strengths And Weaknesses 2.Group-level guarantees lack theoretical tightness**
Our experiments show that averaging per-instance privacy losses still reliably ranks groups by unlearning difficulty (see Figure.1). Though empirical, this provides a promising direction for future theoretical development on group privacy, especially as the current group analysis is too loose.
**Other Strengths And Weaknesses 3. Assumed noise in SGD lacks justification**
We ran experiments to test sensitivity to noise values used in estimating privacy losses. For SVHN with ResNet-18: (1) Spearman correlation between rankings at σ = 0.01 and σ = 0.001 was 0.70 (p = 0.0). (2) Between σ = 0.001 and σ = 0.0005 was 0.99 (p = 0.0). (3) Between σ = 0.0005 and σ = 0.0001 was 0.99 (p = 0.0). These results suggest that rankings are largely noise-invariant, as long as some noise is present. Past work has shown evidence of observable noise during training due to software and hardware non-determinism [1]. We will include this discussion in our revised version.
[1] Jia, Hengrui, et al. "Proof-of-learning: Definitions and practice." 2021 IEEE Symposium on Security and Privacy (SP). IEEE, 2021.
**Other Comments Or Suggestions. Correlation vs causality**
Our theory establishes a link between privacy loss and the number of unlearning steps, stating that small privacy loss means only a few steps are required to unlearn. We would appreciate clarification on what is meant by a “causal effect perspective,” as our goal is to measure difficulty, not to infer intervention outcomes. We welcome suggestions if there's a specific causal framework the reviewer believes is applicable here.
**Questions For Authors. Scalability of computation and checkpointing**
Our method computes privacy loss using gradients from only 35 (out of total 150 training epochs giving 47,000 steps). In contrast, C-Proxy averages predictions over all 150 epochs of checkpoints. Average Gradient Norm also averages gradients from all training epochs. EL2N is cheaper, but less predictive (see https://files.catbox.moe/uc54l5.png). Using only 35 checkpoints makes our method more efficient and scalable than most alternatives. We agree that techniques like gradient checkpointing or sampling could further reduce cost and plan to explore these in future work. | Summary: This paper presents a per-data sample approach to quantifying the difficulty of unlearning the same via fine-tuning. They do this by adapting the definition and analysis of Thudi et al. (https://arxiv.org/abs/2307.00310) on per-instance DP to the unlearning setting to produce a quantity called a “privacy loss”, which measures the difficulty of unlearning a particular sample. This privacy loss can be straightforwardly used to get a tighter estimate on the number of finetuning steps needed to unlearn a sample. They validate the usefulness of privacy losses through experiments, and introduce “loss barriers” as another empirical measure for the difficulty of unlearning.
Claims And Evidence: The paper proposes a per-sample privacy loss which they claim indicates the difficulty of unlearning the sample. They show theoretically that this privacy loss controls the finetuning steps needed to unlearn. They also show empirically that the privacy loss correlates with the number of steps needed to unlearn a set of items. These claims are supported by clear and convincing evidence.
Methods And Evaluation Criteria: The methods and evaluation criteria make sense to me.
Theoretical Claims: The theoretical claims appear to make sense. However, it was hard to understand the privacy loss definition so I could not verify it rigorously.
Experimental Designs Or Analyses: The experimental designs made sense to me. They performed five experiments:
1) Testing that privacy loss corresponds to number of steps needed to unlearn
2) Testing that privacy loss corresponds to the difficulty of privacy violating attacks
3) Testing that loss barrier also corresponds to privacy loss
4) Testing that privacy loss corresponds to other known measures of the difficulty of unlearning
5) Testing that privacy loss is a better measure of difficulty of unlearning vs C-Proxy by showing it can select harder forget sets
All of the setups made sense and showed what they were supposed to show. I think experiment 5 could be expanded upon, as it only compares against C-Proxy.
Supplementary Material: No not in much detail
Relation To Broader Scientific Literature: The paper is related to the broader unlearning literature, and takes the differential privacy approach. The paper does a good job of discussing the related work.
Essential References Not Discussed: Not that I know of
Other Strengths And Weaknesses: Strengths
- The paper is a very timely publication that combines the analysis of Chien et al. https://openreview.net/forum?id=3LKuC8rbyV which analyzes the number of steps needed to unlearn a set of data points using the DP framework, and the analysis of Thudi et al. (https://arxiv.org/abs/2307.00310) which introduces per-instance privacy. By combining these two, they can produce a tighter analysis of the difficulty of unlearning data samples.
- The claims are well-supported with theoretical analysis and experiments
- The paper produces a clear contribution to the literature: a new measure of the difficulty of unlearning data samples which appears to be the best, pending more experimental evidence.
Weaknesses
- The value of this paper in practice would be in showing that privacy losses are the most accurate way to measure the difficulty of unlearning. The only figure that tries to demonstrate this is Figure 3. However, it only compares against C-Proxy. There are other proxy metrics (as shown in Figure 2), so it is important to compare privacy losses against all of them to be sure of the value of privacy losses in practice. Related to this, it would be good to include a discussion of the relative cost of computing each of these proxies compared to their relative accuracy at predicting the difficulty of unlearning.
- From what I understand, the loss barrier computes the sharpness of the loss curve between two different models. The authors compute the sharpness of the loss between the oracle model (the perfectly unlearned model) and the model before/after unlearning. The experiments show that the sharper the curvature on a particular set of data is, the sharper the curvature is. This analysis is nice, but I'm wondering what the motivation for this is? Does this loss barrier work help us in any tangible way?
Other Comments Or Suggestions: - Nit: figure 1 should explicitly write out what UA/MIA/GUS mean
Questions For Authors: 1. Can you provide a more comprehensive experiment for Figure 3 comparing against the known ways to measure unlearning difficulty? It is critical to make this comparison comprehensive IMO.
2. What is the value of the loss barrier discussion?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your feedback. Your review raises two key concerns: the completeness of experimental comparisons between our proposed privacy loss and other proxy metrics, and the practical value of the newly introduced “loss barrier” measure. You also suggest clarifying definitions and improving the accessibility of the theoretical explanations.
In response, we have expanded our experiments to include comparisons against EL2N and Average Gradient Norm, which further confirm that privacy loss is more effective in identifying difficult-to-unlearn examples. We also clarify the purpose and practical relevance of the loss barrier metric, showing that it provides an additional, independent way to evaluate unlearning efficacy. Each of your points is addressed below, underscoring that our proposed metrics provide robust, practical, and comprehensive methods for evaluating unlearning difficulty.
**Theoretical Claims. Unclear definition of privacy loss**
Could the reviewer clarify which parts of the definition were unclear? We recognize that the current form includes several moving parts, and we will revise the explanation to improve accessibility in the final draft.
**Weaknesses 1. Need for broader comparison in Figure.3**
We agree. In addition to C-Proxy, we have now conducted comparisons with EL2N and Average Gradient Norm. Privacy loss continues to identify harder-to-unlearn examples than all alternatives. The new figure is available at https://files.catbox.moe/uc54l5.png and will be included in the revised draft.
**Weaknesses 1. No discussion on relative computational cost of different proxies**
Thank you for raising this point. We computed privacy losses using 35 evenly spaced training checkpoints (from the 47,000 steps of training). All other methods—except EL2N—require access to all training checkpoints, making them more expensive. C-Proxy averages predictions across all checkpoints, while Average Gradient Norm uses gradients computed at each checkpoint. EL2N is cheaper but less effective, as shown in the new comparison figure linked earlier.
**Weaknesses 2. Unclear motivation behind the loss barrier metric**
The loss barrier provides an additional way to assess unlearning, providing a novel membership inference (MI) attack. Specifically, discrepancies from the expected loss barrier between two oracle models can indicate whether unlearning was successful. This provides a novel way to assess whether the model has achieved the correct loss geometry after unlearning—something not captured by existing metrics, which focus only on changes in output or loss at individual points. Its contribution to the paper is to offer another metric to evaluate our main claim: that privacy losses accurately predict unlearning difficulty.
**Other Comments Or Suggestions. Clarify UA/MIA/GUS in Figure.1**
Thank you—we will revise the caption in Figure.1 to clearly define these terms. | Summary: The paper proposes a per-instance approach to quantifying the difficulty of unlearning via fine-tuning by replacing the worst-case Rényi-DP bound with per-instance privacy losses. The authors introduce loss barriers as a way for evaluation, which are significantly reduced after unlearning. Alternative cheap proxy measures of data difficulty are explored for better efficiency. Empirical results demonstrate that the privacy losses offer a precise and actionable measure of unlearning difficulty and could identify harder data.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: The reviewer did not check the correctness of the proofs.
Experimental Designs Or Analyses: The reviewer has checked all of the experimental designs.
Supplementary Material: The reviewer read the experiments part of the supplementary material.
Relation To Broader Scientific Literature: This paper presents work whose goal is to advance the field of machine unlearning, which is specifically oriented to improve the trustworthiness of machine learning.
Essential References Not Discussed: None.
Other Strengths And Weaknesses: Strengths:
1. The paper innovatively introduces per-instance privacy losses for unlearning difficulty measurement and provides theoretical unlearning guarantees.
2. The paper is well-structured. The narrative is easy to follow.
Weaknesses:
1. Computing per-instance privacy losses requires storing and processing gradients throughout training, which can be computationally expensive, especially for large-scale models and datasets. This limits the practicality of the approach. The reviewer supposes that the proposed method can serve as a strategy for model pruning before unlearning, which can then be used to design experiments on more complex datasets and models.
Other Comments Or Suggestions: Using figure illustrations aiding analysis in Section 4 and Section 5.2 would be better, as done in Chien et al,. 2024.
Questions For Authors: In the caption of Figure 1, what do you mean by "Baseline corresponds to the loss barrier between two oracles"? What are the "two oracles" here?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your feedback. Your review focuses on question around the computational efficiency of our method for computing per-instance privacy losses, especially in the context of large-scale models and datasets. You also provide suggestions for improving the clarity of figure and definitions, which we address below.
Perhaps the most important statement for us to make about efficiency is that _our approach is significantly more efficient than all alternatives we study__ with the exception of EL2N which is inferior. We require gradients from only 35 checkpoints from the 150 training epochs. At present, alternative methods currently rely on all checkpoints. We also appreciate your suggestions for improving our illustrations and definitions, and we have incorporated them into our planned revisions. Our detailed responses aim to reinforce a key point: our method efficiently and reliably quantifies unlearning difficulty, maintaining practical feasibility even for larger models and datasets.
**Weaknesses. Computational efficiency and practical applicability**
To clarify, our method requires storing 35 checkpoints and computing gradients on them for the datapoints being evaluated. Given that our full training run consists of 150 epochs, the estimation of per-instance guarantees for the whole dataset costs about 20% of training time. Other methods, such as C-Proxy and Average Gradient Norm, are more expensive: C-Proxy averages predicted probabilities across all 150 training checkpoints, and Average Gradient Norm computes gradients at every checkpoint. In contrast, we use only 35 evenly spaced checkpoints. While EL2N is cheaper, it performs worse in identifying hard-to-unlearn examples (see https://files.catbox.moe/uc54l5.png).
Regarding the idea of using privacy loss for model pruning, we weren’t entirely sure what the reviewer meant—could you clarify this suggestion further?
**Other Comments Or Suggestions. Using figure illustrations**
Thank you for the helpful suggestion. We will include a similar diagram in the revised draft, following Chien et al. (2024), but highlighting that initial divergence varies across datapoints and that many datapoints begin with near-zero divergence---indicating they require almost no steps to unlearn.
**Questions For Authors. Clarification on Figure.1 caption**
We appreciate the chance to clarify this. Due to stochasticity in training (e.g., minibatch sampling, GPU nondeterminism), two runs on the same dataset can result in slightly different models. To control for this noise in loss barrier evaluations, we compute the loss barrier between two models trained independently on the same retain dataset. These serve as “oracles” representing ideal retraining, and the baseline corresponds to the loss barrier between them. This gives us a reference point for how small the barrier can be when unlearning is perfect. | Summary: This paper provides a theoretical foundation to understand the relationship between per-instance privacy loss and unlearning hardness. It applies a recent per-instance privacy loss to fine-tuning-based unlearning and builds a relationship bewteen unlearning steps with the bound of Renyi divergence between a model trained with and without an individual data point. They then empirically show the relationship of the per-instance privacy loss to approximate unlearning steps.
Claims And Evidence: The paper’s contributions are primarily theoretical. While proposing a novel metric for per-instance unlearning difficulty, it lacks evidence of practical impact (e.g., would unlearning-via-fine-tuning methods with the proposed privacy loss perform better than relying on gradient norms?). Stronger empirical validation (e.g., comparative experiments) is needed to demonstrate real-world utility.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: This paper provides a better convergence analysis of $U_{k}(\alpha, \epsilon^*)$-Renyi unlearning. By directly applying the per-instance privacy loss from Thudi et al. ( 2024) into the unlearning setting, this paper builds the bound of Renyi divergence between a model trained with and without an individual data point. Then it builds a connection between the unlearning steps and the Renyi divergence bounds, which is bounded by the per-instance privacy loss. Then it is able to use per-instance privacy loss to predict per-instance unlearning hardness.
Experimental Designs Or Analyses: - All experiments focus on group unlearning; however, the theoretical analysis provides guarantees only for per-instance scenarios. Including experiments demonstrating per-instance privacy loss alignment to unlearning steps would strengthen the practical relevance of the theoretical claims.
- Figure 2: The authors claim that existing proxy privacy losses overestimate unlearning difficulty, but this may stem from scaling differences (e.g., the per-instance hardness is logarithmic with respect to the proposed loss). A fairer comparison is required. (Figure 3 partially addresses this but only contrasts with C-Proxy, which appears to underperform in Figure 2).
Supplementary Material: I read all the theoretical part and experimental details in the supplementary material.
Relation To Broader Scientific Literature: This work establishes a theoretical foundation to support prior observations that specific forget sets exhibit inherent challenges during unlearning.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: - if you could provide the distribution overlap between the constructed forget set and retain set or show any identified hard-to-forget examples, it would be helpful to understand the metric.
Questions For Authors: - I’m curious if we could use the proposed privacy loss to enhance unlearning performance or reduce unlearning time, like what Zhao et al. (2024) did. Could you show me how?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful feedback. Your review primarily raises concerns about the practical utility of our proposed privacy loss metric—specifically, whether its per-instance theoretical guarantees translate to improved empirical unlearning performance. You also highlight the focus on group-level experiments and question whether our comparisons with existing metrics fairly demonstrate superiority. We appreciate these comments and have expanded our response and experiments accordingly.
As outlined below, we clarify that our empirical results already show practical value, particularly by demonstrating that examples with low privacy loss consistently require near 0 unlearning steps. We also include new comparisons against EL2N and Average Gradient Norm, which confirm that privacy loss better identifies harder-to-unlearn datapoints. Taken together, our theoretical and empirical results reinforce the claim that our proposed privacy loss metric is valuable for explaining unlearning performance.
**Claims And Evidence. Lack of evidence for practical impact**
Figure.1 demonstrates that datapoints identified as easy by privacy loss require near-zero steps to unlearn with fine-tuning. We believe this already shows practical impact: for examples in the easiest quantiles, unlearning can be achieved with just a few fine-tuning steps. This allows privacy loss to serve as a signal for when minimal unlearning is sufficient—something existing metrics do not support as reliably.
**Experimental Designs Or Analyses 1. Including experiments demonstrating per-instance privacy loss alignment to unlearning steps**
This alignment is already shown in Figure.1, where we demonstrate that privacy loss ranks groups of datapoints by the number of steps needed to unlearn them. Our group-level results are derived by averaging per-instance privacy losses, which provides a straightforward way to extend pre-computed individual guarantees. We also tested Thudi et al.’s group privacy analysis and found it too loose to distinguish between easy and hard groups (Appendix B), further highlighting the value of our empirical approach. Future work on group privacy could study the correctness/discrepancy with averaging per-instance data points to improve the current group privacy theory.
**Experimental Designs Or Analyses 2. Claim about overestimation in Figure.2**
We agree that the original claim in Figure.2 was misleading. We now clarify that Figure.2 shows a correlation, but not necessarily overestimation due to scaling mismatches. The overestimation claim is instead supported by Figure.3, which demonstrates that datapoints identified as “hard” by other metrics are in fact easier to unlearn than those identified as hard by privacy loss. To further support this point, we’ve added new experiments comparing privacy loss against EL2N and Average Gradient Norm. Privacy loss continues to identify harder examples more effectively. These results are available at https://files.catbox.moe/uc54l5.png and will be added to our revised draft.
**Other Comments Or Suggestions. Request for overlap analysis or examples**
We have included a qualitative example showing four randomly selected images from both an easy-to-forget set (https://files.catbox.moe/2qdv6h.jpg) and a hard-to-forget set (https://files.catbox.moe/tzm6ac.jpg), each of size 1000 and constructed from the CIFAR-10 dataset. Regarding the distribution overlap, we would be happy to provide it—could the reviewer kindly clarify which specific distribution they are referring to?
**Questions For Authors. Could privacy loss help reduce unlearning time?**
Yes—this is already possible using our results. For instance, in Figure.1 we show that the easiest 50% of datapoints (as measured by privacy loss) can be unlearned in fewer than five fine-tuning steps. This suggests a simple strategy: apply lightweight fine-tuning for low-privacy-loss points, and use stronger methods (e.g., retraining or more targeted interventions) for datapoints flagged as difficult. This could easily be integrated into frameworks like RUM [1], where privacy loss can guide refinement.
[1] Zhao, Kairan, et al. "What makes unlearning hard and what to do about it." Advances in Neural Information Processing Systems 37 (2024): 12293-12333. | Summary: This paper considers the machine unlearning problem, which involves removing the influence of a subset of training data from a trained model. The authors explored a setup in which both learning and unlearning are done via noisy gradient descent and proposed to use the "per-instance privacy loss" to estimate the unlearning difficulty. theoretically demonstrate that the number of unlearning rounds depends at most logarithmically on the "per-instance privacy loss" (Corollary 4.4). Additionally, the authors presented extensive experimental results indicating that "per-instance privacy loss" provides a more accurate estimation of unlearning difficulty (i.e., time to unlearn) compared to existing proxy metrics, and it effectively identifies examples that are challenging to unlearn.
Claims And Evidence: 1. The authors stated in line 401 that "Figure 2 reveals that all these proxies overestimate the difficulty." However, Figure 2 only presents a comparison of proxies against privacy loss and does not directly relate to unlearning difficulty. To substantiate the claim that a metric overestimates difficulty, the authors should provide evidence showing that data points with relatively high metric values can be unlearned in the same (or even fewer) number of rounds as those with lower values.
2. In Section 6, the authors asserted that "privacy losses accurately predict the number of unlearning steps." While the empirical results indicate that the time to unlearn increases with privacy loss, this alone does not justify the term "accurately," as there is no established predictive rule correlating privacy loss to the exact number of unlearning rounds.
3. In Section 6.4, the authors compared privacy loss only with the C-Proxy. It is unclear why they did not include comparisons with other proxy metrics mentioned in Section 6.3. Are those other metrics demonstrated to be less effective than C-Proxy in previous work?
Methods And Evaluation Criteria: The learning and unlearning algorithms, as well as the datasets used, are appropriate for addressing the unlearning problem discussed in the article.
Theoretical Claims: I did not conduct a thorough review of the proofs, but they appear to be correct.
Experimental Designs Or Analyses: The authors provided comprehensive experiments to support their proposed "per-instance privacy loss".
1. I have raised some questions regarding the claims made based on the experimental results in the "Claims and Evidence" section.
2. I would like to inquire about the number of checkpoints ($N$) used in estimating the per-instance privacy loss.
3. While the experiments demonstrate that privacy losses can identify data that are hard to unlearn, do they also indicate which data are easy to unlearn?
Supplementary Material: N/A
Relation To Broader Scientific Literature: Unlearning has significant implications for user privacy, as it enables users to delete their data from the trained model, and it can contribute to the development of more robust machine learning models by removing malicious examples. Additionally, the proposed technique may serve as a method for detecting outliers within datasets.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
1. The idea of employing the Loss Landscape to demonstrate how geometric properties reflect unlearning difficulty is intriguing.
2. The authors conducted comprehensive experiments that effectively support their proposed method.
Weaknesses:
1. The proposed privacy loss may not accurately estimate unlearning difficulty for groups, as it focuses on per-instance loss and does not account for correlations within the group.
2. Estimating the per-instance privacy loss could be resource-intensive, as it requires gradients from multiple checkpoints.
Other Comments Or Suggestions: The definition of "5% margin" in the caption of Figure 1 is not sufficiently clear. I recommend using the definition provided in Figure 6, which is more precise, as it specifies that "5% margin" means the difference between the unlearned model’s UA and the oracle’s UA for the given forget set.
Questions For Authors: I would appreciate it if the authors could address my concerns raised in the "Claims and Evidence" section.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful feedback. Your review raises two main concerns: (1) the completeness of comparisons with alternative proxy metrics, and (2) the clarity of our empirical claims regarding how accurately privacy losses predict unlearning difficulty. To address the first concern, we have expanded our experiments to include comparisons against additional proxies—EL2N and Average Gradient Norm. These comparisons (available at https://files.catbox.moe/uc54l5.png) support our original finding: privacy loss consistently identifies harder-to-unlearn examples than existing metrics.
Regarding the second concern about the clarity of our empirical claims, we believe the ambiguities arise from our dense discussion in our original draft. Below, we describe how we have revised the text to clarify that our claims are already supported by existing figures---e.g., Figure.1 shows privacy losses can rank points by number of unlearning steps, while Figure.3 compares the "hardness" of C-proxy and our approach, as measured by training steps to unlearn. We have also clarified definitions where needed. Below we respond to individual points raised in the review.
**Claims And Evidence 1. Figure.2 does not directly relate to unlearning difficulty**
We have revised the text for clarity: Figure.2 demonstrates that past metrics correlate well with privacy losses. When discussing "overestimating difficulty" we now clearly refer to Figure.3 in our paper, which shows the hardest points identified by C-proxy take fewer steps to unlearn than the hardest points identified by privacy losses. Furthermore, we are updating Figure.3 to also include EL2N and Average Gradient Norm; we found privacy losses still identify the harder datapoints. See updated results at https://files.catbox.moe/uc54l5.png.
**Claims And Evidence 2. No predictive rule correlating privacy losses and the number of unlearning steps**
We appreciate this point. Our intended claim is not that privacy losses predict the exact number of steps, but rather that they accurately rank datapoints by how long they take to unlearn. This is shown in Figure.1, where unlearning time increases with privacy loss. We will revise the language to say: “privacy losses accurately rank datapoints according to the number of steps needed to unlearn.”
**Claims And Evidence 3. Compared privacy loss only with C-Proxy In Figure.3**
As mentioned above, we have now included EL2N and Average Gradient Norm in our experiments. Privacy loss remains more effective at identifying hard-to-unlearn examples.
**Experimental Designs Or Analyses 2.Number of checkpoints (N) used in estimating privacy loss**
We used 35 checkpoints, evenly spaced across the 150 training epochs (47,000 steps). We will add this clarification.
**Experimental Designs Or Analyses 3.Do privacy losses also identify easy-to-unlearn data?**
Yes. As shown in Figure.1, datapoints with the lowest privacy loss scores require virtually no unlearning steps. More broadly, privacy loss correlates with unlearning time across the full range of scores—higher privacy loss values generally correspond to more steps required to forget a sample. This pattern is shown in Figure.1 (middle panel) and is consistent with the trend observed in Figure.5.
**Weaknesses 1. privacy loss does not accurately estimate unlearning difficulty for groups**
We appreciate this concern. In Appendix B, we evaluated Thudi et al.’s group-based method and found it failed to distinguish between easy and hard-to-unlearn subsets. In contrast, simply averaging our per-instance privacy losses did capture group-level difficulty (see Figure.1). We believe this result is both practical and empirically sound—and it highlights a useful direction for theory to catch up with practice in deep learning.
**Weaknesses 2. Estimating privacy loss may be resource-intensive**
We estimate privacy losses using gradients from just 35 of the 47,000 training steps—only a small fraction of the training cost. By contrast, other metrics like C-Proxy and Average Gradient Norm rely on access to every training checkpoint (150 epochs). EL2N avoids this but performs worse. So our method strikes a good balance between efficiency and predictive power.
**Other Comments Or Suggestions. "5% margin" in caption of Figure.1 is unclear**
Thanks for pointing this out. We will clarify that the "5% margin" refers to the value of the unlearning metric (e.g., UA or MIA) measured on the oracle model: i.e., we're within 5% of the oracle UA (or MIA), depending on the metric being evaluated.
---
Rebuttal Comment 1.1:
Comment: Thank you for your clarification and additional result. The privacy loss does outperform other proxies and achieve a efficiency vs predictive precision tradeoff. I have increased my score to 3.
Just a minor issue about the word choice: I still think the word "overestimate" is a bit misleading, as it usually refers to obtaining something higher than the ground truth. In the context of identifying hard-to-unlearn examples, though the past metrics do classify some easy-to-unlearn examples as hard-to-learn, they also at the same time classify some hard-to-unlearn examples as easy-to-learn. This behavior is more analogous to misclassification than overestimation. That's why I felt confused when reviewing the article. Maybe something like "inaccurate" is a better choice than "overestimate".
---
Reply to Comment 1.1.1:
Comment: Thank you for your response!
> I still think the word "overestimate" is a bit misleading, as it usually refers to obtaining something higher than the ground truth. In the context of identifying hard-to-unlearn examples, though the past metrics do classify some easy-to-unlearn examples as hard-to-learn, they also at the same time classify some hard-to-unlearn examples as easy-to-learn. This behavior is more analogous to misclassification than overestimation. That's why I felt confused when reviewing the article. Maybe something like "inaccurate" is a better choice than "overestimate".
Sorry for missing this, yes we completely agree. We will change the use of “overestimating” to “inaccurate” throughout the paper. Thanks for the suggestion!
If you would permit us to be bold, if you think the paper should be accepted, we would ask you to vote "Accept", because at the moment, all of our votes are borderline, which is going to leave the decision up to the wind. | null | null | null | null |
Conditioning Diffusions Using Malliavin Calculus | Accept (poster) | Summary: In this paper, the authors propose a framework based on Malliavin Calculus to address the robustness issue associated with singular rewards. Their work focuses on the problem of diffusion bridges, a type of diffusion process with fixed endpoints. Using Doob's h-transform and Malliavin Calculus, the authors derive the Generalized Tweedie's formula. This theoretical result serves as the foundation for their proposed BEL algorithm. Additionally, the authors analyze the variance of the network's training target and select an optimal parameter to minimize this variance. Finally, they conduct experiments on simple diffusion processes and shape processes to demonstrate the empirical performance of their algorithm.
Claims And Evidence: I believe the answer is likely no. The authors explicitly state in the paper: 'Unfortunately, the singular nature of such a measure renders most existing approaches unsuitable: gradients are not well-defined, and naive strategies (e.g., approximating the Dirac measure with highly peaked Gaussians) often face numerical instability.' (lines 55–59). The primary goal of the proposed BEL algorithm is to address this issue. Therefore, I think the authors should present experiments demonstrating improvements in stability and performance for tasks such as flow matching [1] and entropic optimal transport [2] (mentioned in lines 49–55) using their method. In my opinion, the experiments conducted on simple toy examples are insufficient to support such a claim.
[1]. Lipman,Y., Chen,R.T., Ben-Hamu,H., Nickel,M., andLe,M. Flow matching for generative modeling. arXiv preprint arXiv:2210.02747, 2022.
[2]. Shi,Y., DeBortoli,V., Campbell,A., and Doucet, A. Diffusion schrodinger bridge matching. Advances in Neural Information Processing Systems, 36, 2024.
Methods And Evaluation Criteria: I think the methods is quite interesting, but the authors should conduct experiments on High-Dimensional and Large-Scale datasets (e.g. image datasets) to test the empirical performance of the method.
Theoretical Claims: I have checked the proofs of the theorems.
Experimental Designs Or Analyses: As mentioned earlier, I believe the authors should conduct experiments on high-dimensional and large-scale datasets (e.g., image datasets) to evaluate the empirical performance of the proposed method.
Supplementary Material: I didn't read all the supplementary materials.
Relation To Broader Scientific Literature: I believe that the key tool used to derive the algorithm in the paper is Malliavin Calculus. This is a powerful mathematical framework that allows the application of the integration-by-parts formula on path space. The authors leverage this tool to address the problem in this scenario, which is both innovative and novel.
Essential References Not Discussed: Nothing.
Other Strengths And Weaknesses: 1. **Lack of High-Dimensional and Large-Scale Experiments**
While I find the idea presented in the paper both interesting and novel, the current experiments are not sufficient to convince me that the BEL algorithm performs well on high-dimensional data or is scalable. These types of experiments are essential, as downstream tasks of diffusion bridges, such as flow matching, are inherently scalable and often involve high-dimensional generative tasks.
2. **Lack of Analysis on Efficiency and Complexity**
An analysis of the computational efficiency and complexity of the BEL algorithm is also necessary. Specifically, I believe that estimating the score process within the algorithm could be time-consuming, and this aspect warrants further discussion and evaluation.
Other Comments Or Suggestions: Nothing.
Questions For Authors: See the sections above.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thanks for your review! We're glad you think the method is interesting. We hope we will be able to address your concerns on the scalability and efficiency of our proposed method, which we discuss below!
### Section q3Kt.1: Larger Experiments and Flow-Matching
Thank you for the great suggestions. Initially, we mainly targeted the case of conditioning diffusion on a single endpoint, since this can be seen as the most singular, and hence in principle most challenging, reward case (a Dirac delta). However, due to the fact that our method works in these extremal cases, it is actually applicable to a wide range of settings. We followed your proposal and applied our methodology to condition a diffusion model trained on images (could be similarly done for flow matching)!
We first trained a diffusion model on Fashion-MNIST and then used our methodology to condition on the upper left corner of an image. You can see the results here:
- https://postimg.cc/bsbNgMY2
The upper left image of the right grid is the ground truth. We extracted the upper left quarter of that image as conditioning input (seen as the upper left image in the left grid). We then generated samples from the posterior distribution after conditioning on that upper left image. Training the conditioning drift for this particular problem took us about 30-60 minutes on a high-end GPU. Note that after this training time one can condition on *any* upper left corner.
In general, we can condition on any observation of the form $Y = G(X).$ Here, $Y$ can be discrete (classification) or continuous (upscaling, inpainting, ...), and $G$ can be smooth, but also non-differentiable and even non-continuous, since for diffusion bridges we have the extreme case of $G$ being a Dirac delta. We support both deterministic (noise-free) and stochastic (noisy) versions of G; adding artificial noise is not required but is possible to account for uncertain observations depending on the application. Of course, when $G$ has nice properties, like gradients, it might make sense to include these, but due to our lack of assumptions on the reward, our algorithm is quite generally applicable.
We understand that our paper wasn't to clear on this, and will put more emphasis on this point in the updated version. However, nearly nothing has to change, one only needs to replace $x_T$ by a general condition $y$ in the neural network input during training and evaluation, since we never make use of the form of the observation $x_T = Id(x_T)$ in any of our steps.
### Section q3Kt.2: Schroedinger Bridges
Indeed, bridges can be used in the calculation of Schroedinger Bridges. Note that if you can solve the static Schroedinger Bridge problem (Section 3.1 of the paper you linked), and one has access to the Bridges of the reference process, one can interpolate the static coupling of the marginals with the bridges to get the dynamic Schroedinger bridge solution. Therefore, if one has already solved for the bridge process, the problem of solving Schroedinger bridges on path space reduces to just finding the optimal coupling of the marginals!
I hope we were able to dispel your concerns about the applicability of our method to different settings and high dimensional problems. Thank you for motivating us to apply the method to a diffusion model, we are very happy with the results and think this showcases the generality of our method well.
### Section q3Kt.3: Lack of Analysis on Efficiency and Complexity
We agree that it maybe was not fully clear how costly the evaluation of the score process is. Therefore we updated our paper to be more detailed on the calculation of the score process. We explain the complexity of the algorithm in the answer to reviewer 4Bsi, you can find it by searching for "Section 4Bsi.3" on this page.
We hope this answers all questions. Furthermore, we hope our experiments on problems with very high energy barries (double well) as well as high dimensions (images), showcase the applicability and efficiency of our method for different kinds of problems.
### Summary
Thanks again for the review. We believe we have managed to resolve the issues you raised, but please let us know if this is not the case! We hope you agree that the changes to the paper of including a high-dimensional image experiment alongside more details on computing the loss and its complexity will improve it!
---
Rebuttal Comment 1.1:
Comment: I'm sorry that I have sent a comment which is not visible to authors... I thank the authors for providing a detailed rebuttal, and I apologize for the delay in my response. Your clarifications have addressed some of my concerns; however, my primary concern remains unresolved. Specifically, while the proposed BEL algorithm is capable of simulating the diffusion bridge without being affected by singularities in the target distribution, it requires the trajectory of the diffusion process as input and update the score process along the jacobian process. This seems less efficient compared to existing methods such as Flow Matching [1] or Bridge Matching [2,3].
Although these existing methods [1,2,3] may encounter singularity issues, these challenges can often be mitigated through straightforward techniques such as cutoff adjustments and reparameterization of the network (also known as preconditioning). These strategies have proven sufficient for practical tasks, such as image generation. Given this, I am uncertain whether the proposed BEL method offers a significant advantage or is truly necessary for real-world applications. I'm glad to update my score if the concern is properly addressed.
[1]. Lipman, Yaron, et al. "Flow matching for generative modeling." ICLR 2023.
[2].Zhou, Linqi, et al. "Denoising diffusion bridge models." ICLR 2024.
[3]. De Bortoli, Valentin, et al. "Augmented bridge matching." arXiv:2311.06978 (2023).
---
Reply to Comment 1.1.1:
Comment: Thank you for your thoughtful feedback. We now better understand the source of the confusion. **We have quite a different use case from score-based diffusion models, bridge matching and flow matching, and these methods cannot be applied in our setting.**
## Source of confusion
The misunderstanding seems to stem from the sentence:
“Diffusion bridges … serve as building blocks for downstream tasks such as flow matching.”
We have removed this sentence in the revised version, as it may misleadingly suggest our method is an alternative to flow matching or diffusion models, or that we think that these methods are flawed. That is not the case—both are powerful tools with broad applications.
However, our method is not a generative modeling algorithm itself—it modifies a given reference process (whether physical, economic, or from a generative model) to satisfy specific constraints. In the context of generative modeling, it is most closely related to guidance, reward fine-tuning, or conditioning.
## Scope of our method
Let us clarify the scope of our method. We consider a general SDE of the form:
$$ dX_t = b_t(X_t),dt + \sigma(X_t),dW_t, $$
and aim to condition it on a final state $X_T = x$. This corresponds to a reward that assigns infinite value to trajectories ending at $x$, and zero elsewhere (and is therefore very singular).
The underlying SDE can originate from any system: weather models, molecular dynamics, stock prices, or even from generative algorithms such as diffusion models or flow matching. Our method adds a learned drift to the SDE so that the conditioned endpoint is reached, while preserving the original dynamics. The natural competitors for our method are therefore [1, 2]. The method is, for example, useful for transition path sampling in systems with high energy barriers (see Section 4.1.3 in the paper).
We hope this clears up the confusion and are happy to address any further questions.
Best regards,\
The authors
[1] Heng et al. https://arxiv.org/abs/2111.07243
[2] Baker et al. https://arxiv.org/pdf/2407.15455 | Summary: The authors propose a novel solution to tackling the interesting and challenging problem of diffusion bridges conditioned on singular rewards.
To solve this issue, they make use of theory of Malliavin calculus (essentially stochastic calculus of variations from my understanding) to handle the singularities.
Using this theory they proposed a generalization of Tweedie's formula which the conditional score function $\nabla_x \log p_{T|t}(x_T|x)$ is equal to the conditional expectation of their score process.
They then show to configure the variance of the Monte-Carlo estimator of the conditional score function.
Lastly, they use a few toy experiments to illustrate their method.
## Update after rebuttal
I agree with the other reviewers that the limited demonstration of real world applications is a shortcoming so I adjusted my score.
Claims And Evidence: * Can the claim
"recall the connection of diffusion bridges to Doob’s $h$-transform in Section 2.1, in particular the relevance of conditional score functions"
be a contribution?
The connection between Doob's $h$-transform and diffusion bridges is quite well known, see [1-4]
[1] Shi et al., *Diffusion Schrödinger Bridge Matching*, NeurIPS 2023, https://proceedings.neurips.cc/paper_files/paper/2023/file/c428adf74782c2092d254329b6b02482-Paper-Conference.pdf
[2] Somnath et al., *Aligned Diffusion Schrödinger Bridges*, UAI 2023, https://proceedings.mlr.press/v216/somnath23a/somnath23a.pdf
[3] Du et al., *Doob’s Lagrangian: A Sample-Efficient Variational Approach to Transition Path Sampling*, NeurIPS 2024, https://arxiv.org/pdf/2410.07974
[4] Brekelmans et al., *On Schrödinger Bridge Matching and Expectation Maximization*, Optimal Transport and Machine Learning Workshop at NeurIPS 2023, https://openreview.net/pdf?id=Bd4DTPzOGO
Methods And Evaluation Criteria: They make sense.
Theoretical Claims: I read the main paper thoroughly and performed a quick read of the proofs in the appendix. I could have missed details in the appendix.
Experimental Designs Or Analyses: From what I read in the main paper the experiments generally make sense, see questions below for any concerns.
Supplementary Material: I skimmed through the appendices.
Relation To Broader Scientific Literature: In section 3.2 the authors provide an excellent description of how their work connects with prior work. I have no issues with it.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: * The paper is well-written, and despite being a mathematically dense paper I found it be quite easy to read.
* I found the motivations and arguments for the proposed method to be compelling.
* I found the paper to be rigorous and easy to read, standing next to some of the seminal papers in this field in terms of general quality.
Other Comments Or Suggestions: * Footnote 1 is incomplete.
Note, I really enjoyed this paper and found it to be quite interesting. I would be happy to improve the score if the questions and concerns I raised are addressed.
Questions For Authors: 1. In Equation (6) what does $\alpha\_t'$ denote? I see $\alpha\_t$ defined in the theorem but not $\alpha\_t'$. Is it the derivative wrt $t$?
2, Wouldn't solving equation (5) amount to the continuous-time analog of forward sensitivity equations, *i.e.*, forward-mode autodiff?
The work on neural SDEs by Kidger and Li solved the adjoint equations in *reverse-time* corresponding to reverse-mode autodiff. For more details see [1, Section 5.1.4.]
3. Related to Q2 wouldn't simulating vector-matrix products be more efficient than matrix-vector products?
4. In Algorithm 1 in line 1 is $B$ and index or Brownian motion? The notation `for i = 1 to B do` seems strange to me when the next line is Sample $\{X,B\}_i$ ...
5. In Equation (17) is it supposed to be $\alpha_t$ or $\alpha_t'$?
6. In the double well experiment, (Figures 3 and 4) shouldn't samples ideally oscillate between the two wells and not just tend from 1 to -1?
7. In Figures 4 and 5 the impact of different variance schemes (choices for $\alpha_t'$ or $\alpha_t$) seems not to matter much.
8. In Sec 4.2 why does the of variance scheme seem to matter more than in Sec 4.1?
[1] Patrick Kidger, *On Neural Differential Equations*, Ph.D. thesis, https://arxiv.org/pdf/2202.02435
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks a lot for your positive review! We're very happy to hear that you really enjoyed this paper! And we were especially happy that you found the general quality to be on par with some of the seminal papers in this field.
We appreciate your detailed comments and questions, and answer them below.
### Section 4Bsi.1
_"Can the claim "recall the connection of diffusion bridges to Doob’s -transform in Section 2.1, in particular the relevance of conditional score functions" be a contribution?"_
Indeed, we agree it is well known. Our intention was to also to use this section to provide an outline to the paper, but we see how this could be confusing. To make it clearer, we will write "recall the (well-known) connection of diffusion bridges" and cite the relevant literature. We hope you agree this makes it clearer.
### Section 4Bsi.2: "Footnote 1 is incomplete."
You're right -- the footnote currently continues on the next page. We will fix this! Thank you.
### Section 4Bsi.3: Computation of the Score Process (Q2)
Thanks for the excellent questions. Indeed, the paper currently lacks some detail on how we compute the score estimator, which may have caused confusion. As you noted, vector-Jacobian products are cheaper via reverse-mode autodiff, and adjoint methods avoid computing the full Jacobian—this is exactly what we do. We simulate paths of the reference SDE (1), then compute the integral (6) in reverse, akin to adjoint ODE methods, but adapted for our setting, picking up $dB_t$ terms along the way instead of only backpropagating a final gradient. We present the full algorithm below for $\sigma = 1$ and Euler-Maruyama discretization, and will include a detailed explanation in the paper. Thank you for the helpful references—we will cite them in the revised version.
**Given**:
- $(X_0, X_{\delta t}, \ldots, X_T)$
- $(Z_0, Z_{\delta t}, \ldots, Z_T)$, which is the noise which was used to produce $X_{t + \delta t} = X_t + \delta t b(X_t) + \sqrt{\delta t}~Z_t$
**Output**:
- $(S_0, S_{\delta t}, \ldots S_T)$, the score process at all times $t$
**Method**:
_Initialize_: $S_T = 0$
_Propagate_: $S_t = S_{t+\delta t}^T (I + \delta t \nabla b(X_t))$
_At the end_: Divide $S_t$ by $T - t$ to normalize it.
We hope it's now clear that since we left-multiply with the Jacobian, we never need the full Jacobian—just one backprop pass per timestep. This yields $N = T/\delta t$ regression targets $S_t$ for gradient updates.
Note that the Jacobian in (6) is transposed before right-multiplying with $dB_t$, which is equivalent to left-multiplication. We agree this wasn’t clear and will revise it.
Thanks again for the great question—highlighting this has improved the paper. To show scalability to higher dimensions, we’ve added image experiments (see “Section q3Kt.1” in our reply to Reviewer q3Kt).
### Section 4Bsi.4: Choice of $\alpha$ (Q6 and Q7)
We found the choices "first", "optimal" and "average" all to do quite well on most problems (however, average and first are easier to implement than optimal). Which one worked the best was problem dependent. Note that "optimal" is only theoretically optimal in a specific setting (a forward process which is a Brownian motion). There are two interesting ways to study optimality:
- Getting a deeper theoretical understanding of optimal $\alpha$ choices for different classes of SDEs.
- Optimizing $\alpha$ numerically for a given problem.
However, these were out of the scope of the current work, but they are certainly very interesting for future research.
Note that in Section 4.2 we do not compare different $\alpha$ schemes. We just picked the best-performing one for shape spaces (which was "average"), and compare it to other algorithms from other publications. We observe that we outperform them. We did not observe this problem to behave very differently with regard to the choice of $\alpha$ than the other problems.
### Section Other Questions
-- 1. -- Indeed, it's the derivative with respect to $t$. We will add this to the theorem statement to make it clear!
-- 3. -- Thanks for bringing this for our attention. We have updated this to be "for $i=1$ to $N$ ...".
-- 4. -- Yes, thanks - Equation (17) should read $\alpha'_t$. We've corrected this!
-- 5. -- That's a very interesting comment. In our setting (diffusion bridges), there should be no oscillation between the wells as the conditioning "pins down" the endpoint; transitioning back and forth is highly unlikely (even more unlikely than transitioning once!) under the original dynamics. Oscillating back and forth would be expected if the dynamics were set up to equilibrate and target a (spatial) distibution of interest, for example in MCMC type sampling algorithms. Potentially our method could be modified to enhance sampling, but since this is quite different, we believe it is better reserved for future work.
Thanks again for the feedback! We hope we managed to answer your questions sufficiently and address your concerns.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for the detailed responses. My concerns on clarity were addressed and I believe the paper is a strong addition to the community. I don't hold the same reservations about experimental scope as the work is mostly theoretical. I will update my scores accordingly.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer,
Thank you for the engaging discussion and thoughtful questions regarding our paper. We appreciate your kind words and are very happy to hear that you enjoyed our article.
Best regards,
The Authors
Edit: We were happy to see that you had previously changed your score from a 4 to a 5. We noticed you have since changed it back to a 4. Could we kindly ask what the reason for this is? Thanks again for your review, and if there are still any remaining concerns please let us know! | Summary: The work develops a technique for learning the control process that
conditions a diffusion on the terminal state given the initial state.
A key advantage of their method is that it is robust to singular
rewards. They test their algorithm on multi-well toy experiments,
and show that their algorithm successfully allows conditioning on
transitions between the wells. They also test on a Shape process
and obtain better performance than previous methods.
## Update after rebuttal
The rebuttal was good, and I appreciate the additional experiment, but it still seems fairly small scale to me so was not enough to convince me to increase my score, as the extent of the importance of the results in the paper is not conveyed to me. However, I am positive about this paper and maintain my vote leaning toward accept.
Claims And Evidence: Yes, the evidence is sufficient for the claims.
Methods And Evaluation Criteria: This seems primarily a theoretical paper, so the experiments
seem appropriate. The practical usefulness of the approach
remains a bit unclear as the experiments do not seem to be
real applications.
Theoretical Claims: I did not check the proofs thoroughly.
Experimental Designs Or Analyses: I did not check them in too much detail. The plots of the
diffusion paths show that their method can condition on the transitions.
Moreover, the metrics in the tables also show improvement (they considered
metrics of distance to the target location as well as a kind of
error to the ground truth drift).
Supplementary Material: I skimmed the supplmentary materials. In particular, I checked the
parts about the metrics.
Relation To Broader Scientific Literature: Adequately discussed.
Essential References Not Discussed: None that I can think of.
Other Strengths And Weaknesses: The paper is well written.
One weakness is that the experiments are fairly toy, though checking
other related published works, it seems this is common in this field,
and the experiments may be more substantial than usual in similar papers.
Other Comments Or Suggestions: The order of the numbers of some Figures/Tables is strange.
For example, Table 1 is introduced last in the main paper, while other
tables like Table 4 are introduced earlier.
Questions For Authors: What is the computation time like?
Is this method practical?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We really appreciate your positive review and that you think our paper is well written!
***One weakness is that the experiments are fairly toy***
We based our experiments on setups from the most closely connected literature and are glad you found them more substantial than in similar papers!
We think the included experiments are good tests for our method since
1) In the double well experiment, there is a high energy barrier between transitioning between wells, meaning it happens very rarely. Therefore, conditioning to go from one well to another is challenging.
2) In the shape models, points close to one another are very correlated making transitioning to another given shape challenging.
However, we agree these are fairly toy. In order to resolve this we have now conducted an experiment on images, which we hope will convince you of the applicability of our method to numerous situations, including high dimensions!
We use the following setup:
1. As the base SDE we take a pretrained diffusion model SDE trained to go from the noise distribution to the data distribution (for this we have used Fashion MNIST).
2. We condition the SDE on the upper left corner of the image to take a given specific value. Practically, this corresponds to the task of completing partial images.
3. We link our results here: https://postimg.cc/bsbNgMY2 \
The true "left corner" is from the first image in the top left corner. We see all the samples match well, generating only images with the same left upper corner.
Strictly speaking, this experiment goes slightly beyond the considered set-up, as conditioning on a part of the image translates into "pinning down" only some of the coordinates of the endpoint. Indeed the proposed method is very flexible, and applies to conditioning on any observation $Y= G(X_T)$, with no assumptions on the function $G$ (e.g. $G$ need not be differentiable and $Y$ could be discrete or continuous). For more details, please see our answer to Reviewer q3Kt (see Section q3Kt.1). We realise this is not so clear in the paper right now and will include this discussion!
We hope we have managed to address your concern.
***The order of the numbers of some Figures/Tables is strange.***
Thanks for pointing this out! We've updated this now so that the tables and figures are named in order of appearance.
***What is the computation time like? Is this method practical?***
Training the conditioning drift for the image task took us about 30-60 minutes on a high-end GPU, so yes, this method can potentially be applied in large-scale settings. Note that after this training time one can condition on *any* upper left corner (for example jackets, shoes, etc). Please do let us know if you want anymore information on this!
For a more detailed complexity analysis of the algorithm (including the number of forward and backward passes) please refer to our answer to Reviewer 4Bsi (Section 4Bsi.3).
Thanks again for your review. We hope we have managed to resolve your concerns by including the extra experiment and an analysis on the complexity of the method. | Summary: This paper introduces a novel approach to conditioning diffusion processes using Malliavin calculus, enabling stable training of score-based diffusion bridges. By replacing the ordinary derivative by Malliavin derivative, their framework unifies and extends existing diffusion bridge methods. Through controlled experiments on Brownian motion bridges and double-well potentials, the proposed method performs better than the baselines in accurately modeling conditioned diffusions.
Claims And Evidence: Their main claim is this novel formula for conditional scores in denoising score matching in Theorem 2.1.
To the best of my knowledge, the formulation of replacing ordinary derivatives with Malliavin derivatives is new and the authors provide detailed proof for their main theorem upfront.
Methods And Evaluation Criteria: The proposed method is valid for learning the diffusion bridge problem. The evaluations are toy experiments based.
Theoretical Claims: For theorem 2.1 as \sigma(X_t) becomes singular, wouldn't you have stability issues with its inverse?
There seems to be a implicit circular dependency between S_t and u_t in your proof for showing the u_t is the unique minimizer, could you make a concise proof in your Appendix to show this is not the case?
Experimental Designs Or Analyses: The experiments are done with two toy experiments set up, given the main contribution of the paper is the theorem, the experimental designs might be acceptable.
Supplementary Material: Experimental details section of the appendix is reviewed.
Relation To Broader Scientific Literature: This paper builds on prior work in diffusion bridge learning, score-based generative modeling, and stochastic control, extending methods like Doob's h-transform by using Malliavin calculus for stable conditional score estimation.
Essential References Not Discussed: To my best knowledge, close related works are mentioned in the paper.
Other Strengths And Weaknesses: **Strengths**
Experiments on double-well potential and Brownian motion bridges showcase the effectiveness of the method in capturing rare event transitions.
The derivation of a generalized Tweedie’s formula and path-space integration by parts provides a unifying theoretical framework.
**Weaknesses**
The method assumes that the matrix A and diffusion coefficient \sigma(x_t) are always invertible, which may not hold in degenerate or low-noise regimes.
The quality of the writing sill need to be improved i.e. some of the figures are mis-referenced.
Lack of real world experiments conducted leaving applicability beyond theory uncertain.
Other Comments Or Suggestions: In section 4.1.3, some of the references to Figure 5 could be Figure 3?
Figure 1 hardly convey the message of the paper, try either include conclusion in the comments or other examples.
I would start by introducing a motivating example as mentioned by you, "(approximating the Dirac measure by highly peaked Gaussians) often face numerical instability." Then showcase that your method is able to solve the instability problem.
Questions For Authors: Some of the questions, please check the theorems section and weakness section of the review.
State-of-art diffusion based models/flow matching models all have the assumption about the highly peaked Gaussians near the t equals to 0, your method seems to circumvent this problem. With Jacobian calculation and matrix inverse in calculating S, do you think your method will be a good fit for high-dimensional task like image generation?
Some of the questions, please check the theorems section and weaknesses section of the review.
State-of-the-art diffusion-based models and flow matching models assume highly peaked Gaussians near t=0, but your method appears to circumvent this issue. With Jacobian calculations and matrix inversions involved in computing S, do you think your method is well-suited for high-dimensional tasks like image generation?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for your review! We're glad you see our method as unifying and extending diffusion bridge approaches. Below, we address your questions and concerns.
***For theorem 2.1 as $\sigma(X_t)$ becomes singular, wouldn't you have stability issues with its inverse? & The method assumes that the matrix A and diffusion coefficient $\sigma(X_t)$ are always invertible...***
Thanks for the question!
For $A$: Since $\alpha$ is user-chosen, it can always be selected to make $A$ invertible. All natural choices for $\alpha$ do so.
For $\sigma$: It is helpful to discuss two slightly different cases:
1) If $\sigma$ is small but positive definite, stability can be partly managed via small step sizes or adjusting $\alpha$. However, small noise makes the bridge problem harder in general (regardless of the method), as the dynamics become rigid; for $\sigma = 0$, the problem is ill-defined.
2) The diffusion coefficient is sometimes genuinely rank deficient, for example in the underdamped Langevin dynamics,
$\mathrm{d}q_t = p_t \, \mathrm{d}t,$
$\mathrm{d} p_t = - \nabla V(q_t) \, \mathrm{d}t - \gamma p_t \, \mathrm{d}t + \sqrt{2\gamma} \mathrm{d}W_t,$
of great interest in molecular dynamics (here the diffusion matrix would be \begin{pmatrix} 0 & 0 \\\\ 0 & \sqrt{2 \gamma}
\end{pmatrix} with noise only acting on the $p$-variable). In this case (and in similar other cases), it is possible to extend Theorem 2.1 using pseudo-inverses, and the proposed methodology generalises straightforwardly. On a technical level, this extension requires "hypoellipticity" which guarantees smooth transition probabilities of the underlying dynamics. Since underdamped Langevin dynamics is important for applications, we suggest adding a short explanation in the appendix.
***There seems to be a implicit circular dependency...***
We are a bit unsure exactly which proof you mean, but we assume you mean in Theorem 2.1. To clarify, the proof steps are as follows:
1. By Doob’s $h$-transform (Proposition 2.2) for eq (8) to coincide with the conditional law, we need to show that $u^*(x; x_T) = \nabla \log p_{T\mid t}(X_T = x_T \mid X_t = x)$.
2. By Proposition 2.3, we know $\nabla \log p_{T\mid t}(X_T = x_T \mid X_t = x) = \mathbb{E}[\mathcal{S}_t \mid X_t=x, X_T=x_T]$.
3. In the proof of Theorem 2.1 we show that the minimiser of $\mathcal{L}(u)$ is given by $\mathbb{E}[\mathcal{S}_t \mid X_t=x, X_T=x_T]$. Since this is equal to the term arising from Doob’s $h$-transform, eq (8) coincides with the SDE under the conditional law.
In particular, in equations (14) and (15), $\mathcal{S}_t$ is already fixed and does not depend on $u$, hence there is no circularity.
If this is what you mean, we’d be glad to include the above steps in proof of 2.1 making it more explicit!
***The quality of the writing still needs to be improved...***
Thanks for pointing this out! We will fix this immediately.
***Lack of real world experiments conducted leaving applicability beyond theory uncertain.***
We based our experiment setup on papers in the literature that also concentrate on similar problems [1, 2, 3, 4, 5]. Indeed, the double well experiment is a challenging problem in conditioning due to the high energy barrier between wells and therefore the transitioning events are very rare. However, we agree it is interesting to consider image generation, and have since experimented with this!
We condition a pretrained model to only generate images matching with a given top left corner. Please see our answer to Reviewer q3Kt (Section q3Kt.1) for details, and see the samples linked here: https://postimg.cc/bsbNgMY2.
We hope we've conveyed the method's applicability and flexibility! We'll include this experiment to show it scales to high-dimensional SDEs and has practical relevance beyond the theory.
[1] https://arxiv.org/abs/2111.07243\
[2] https://arxiv.org/abs/2407.15455\
[3] https://link.springer.com/article/10.1007/s42985-021-00102-x\
[4] https://arxiv.org/pdf/2312.02027v4 \
[5] https://projecteuclid.org/journals/bernoulli/volume-23/issue-4A/Guided-proposals-for-simulating-multi-dimensional-diffusion-bridges/10.3150/16-BEJ833.full.
***Figure 1 hardly convey the message...start by introducing a motivating example...***
We agree we should include more information in this first image, and update it as follows: https://postimg.cc/NK7gq2JB.
We hope you agree that this better illustrates the motivation and challenge of the paper, and it also gives us the opportunity of referring to it in the introduction when explaining the reward (and its potential singularity).
**...do you think your method will be a good fit for high-dimensional task like image generation?**
Yes, as we have seen from our experiment on images it does scale to high-dimensional tasks! The Jacobian calculation can be done very efficiently using vector-matrix products; for more details on this and on computing $\mathcal{S}$ please see our answer to Reviewer 4Bsi (Section 4Bsi.3). | null | null | null | null | null | null |
MixBridge: Heterogeneous Image-to-Image Backdoor Attack through Mixture of Schrödinger Bridges | Accept (poster) | Summary: The author proposed the MixBridge framework to conduct backdoor attacks on the Image-to-Image diffusion bridge model (called the Image-to-image Schrodinger bridge (I2SB)). Existing methods are homogeneous attacks, while MixBridge can achieve heterogeneous attacks. Specifically, MixBridge introduces the Mixture of Experts (MoE) mechanism into the backdoor trigger injection stage, and designs a Weight Reallocation Scheme to prevent the weight assignment from being too far from uniform, so as to achieve covert attacks. The author verified the effectiveness of MixBridge on two tasks: super-resolution and image inpainting.
## update after rebuttal
Although the author claims to have already discussed the relationship between the existing methods and the proposed backdoor attack, I didn't find it in the "2. Related Work" section. I will maintain my original rating.
Claims And Evidence: The author assesses the stealthiness of backdoor attacks using Entropy, and judges whether the backdoor trigger is covert through Weight Average (as shown in Figure 2). Is this a common approach? Is there any literature support? In section 5.2. Evaluation Metrics of the paper, there is no mention of relevant literature to illustrate this point.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: Yes. The author conducted a theoretical analysis of the "limitations of using a single I2SB model for heterogeneous backdoor attacks".
Experimental Designs Or Analyses: Yes.
1. It can be seen from Table 1 that compared with the benign model (I2SB), the images generated by the MixBridge attack proposed in this paper have higher quality. This advantage seems counterintuitive. Please explain the source of this performance improvement when introducing the backdoor while improving the performance of the generative model.
2. The experimental part of the paper does not compare with cutting-edge methods.
Supplementary Material: Yes. All parts.
Relation To Broader Scientific Literature: None.
Essential References Not Discussed: None.
Other Strengths And Weaknesses: None.
Other Comments Or Suggestions: 1. In section 2. Related Work of the paper, the relationship between existing methods and the method in this paper is not discussed.
2. In the caption of Figure 2, the double quotes of "Weight Average" need to be modified.
3. The meaning represented by the background color of the cells in Table 1 (optimal and suboptimal values) should be clearly explained.
4. Please add a discussion on the defense methods against the MixBridge backdoor attack by the author to address potential security issues.
Questions For Authors: 1. Add comparisons and discussions of cutting-edge methods in the experimental section.
2. Please explain why the generated image quality of the backdoored model in Table 1 is better than that of the benign model.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely express our gratitude for your acceptance and constructive comments. Due to space constraints, we include `additional_tables.pdf` and visualizations at the following link: https://anonymous.4open.science/r/ICML25-5787/. References to **Table x** and **Figure x** in our responses correspond to the materials provided in this link. The responses to your questions and weaknesses are listed below:
> Q1 Alternative evaluation methods for stealthiness
**A1:** Entropy has been widely adapted to measure privacy in the security field [1,2]. Greater entropy indicates an increasing difficulty in distinguishing between different events and thus a better "anonymity". Similarly, we use entropy to measure the anonymity of these experts. The higher the entropy, the harder it is to distinguish these experts, and thus the backdoor experts are more difficult to be detected. As another way to measure stealthiness, we evaluate the performance of each expert on benign tasks. If any expert consistently performs poorly on benign tasks, it could be easily detected and removed by the user. In particular, we input clean image $x_t^c$ to simulate the benign generation task and get the output $\epsilon_i(x_t^c,t;\theta_i)$ of each expert. Next, we predict the corresponding $x_0^{\epsilon_i}$ using Eq. 1 in our paper. Finally, we compute the MSE between $x_0^{\epsilon_i}$ and clean images. The results are as follows:
| | Entropy | Benign Expert MSE(E-02) | Backdoor Expert1 MSE(E-02) | Backdoor Expert2 MSE(E-02) | Backdoor Expert3 MSE(E-02) |
|---|---|---|---|---|---|
| MixBridge w/o WRS | 3e-05 | 0.46 | 31.87 | 33.85 | 46.35 |
| MixBridge w WRS | 1.99 | 3.80 | 1.20 | 1.45 | 1.35 |
The results show the backdoor experts generate noticeably different contents in the benign generation task if WRS is not applied. On the contrary, all experts in MixBridge with WRS produce outputs similar to the benign image. We have provided the visualization results in Figure 6 in the paper. In addition, the results of the **direct** metric (MSE) are consistent with those from the **indirect** metric (entropy).
> Q2 MixBridge has better performance
**A2:** We have noticed the MixBridge outperforms a single I2SB in the super-resolution task. The major reason is we apply a MoE mechanism to train the model, which brings much **stronger capacity**. Specifically, it helps mitigate the conflicts between the benign generation task and multiple backdoor attacks, enabling MixBridge to achieve better performance.
> Q3 Compare with cutting-edge methods
**A3:** To the best of our knowledge, there are **no** backdoor attack methods designed for I2I diffusion generation models. The setting of the unconditional diffusion model, which starts the diffusion process from a standard Gaussian noise, may not be applicable to the I2I framework. Here, we take two commonly used backdoor attack methods for standard unconditional diffusion models, BadDiffusion [3] and VillanDiffusion [4], to compare with our proposed MixBridge in the I2I setting. The results are as follows:
| | FID | PSNR | SSIM(E-02) | MSE(E-02) | CLIP(E-02) |
|---|---|---|---|---|---|
| MixBridge | **72.28** | **25.80** | **76.14** | **0.10** | **94.34** |
| BadDiffusion | 307.18 | 11.05 | 20.70 | 257.12 | 75.76 |
| VillanDiffusion | 310.58 | 11.14 | 20.83 | 135.60 | 65.65 |
The results show that the two backdoor attack methods designed for unconditional diffusion models perform significantly worse than MixBridge in both benign generation and backdoor attack tasks. This demonstrates backdoor attacks designed for unconditional models are not easily transferable to the I2I setting.
> Q4 The relationship between existing methods and the method in this paper is not discussed.
**A4:** We have already discussed the relationship between existing methods and our proposed backdoor attack. Here, we present a simple summary. Existing backdoor attacks on diffusion models can be roughly categorized into two lines: attacks on the unconditional diffusion models and attacks on the T2I diffusion models. The former injects triggers into the input Gaussian noise to generate malicious outputs, while the latter corrupts text inputs with triggers to manipulate the diffusion process. In contrast, in this paper, our method targets to conduct heterogeneous backdoor attacks against I2I bridge-based diffusion models.
We will revise the Related Work section to clearly articulate the distinctions between existing methods and our proposed backdoor attacks.
> Q5 Possible defense
**A5:** We present the discussion about defense methods in the response to the **Reviewer 8an4-Q1**.
In addition, we sincerely appreciate your meticulous review! We will revise these typos and clarify the corresponding expressions.
> Reference:
>
> [1] Quantifying and measuring anonymity
> [2] Towards measuring anonymity
> [3] How to backdoor diffusion models?
> [4] Villandiffusion: A unified backdoor attack framework for diffusion models
---
Rebuttal Comment 1.1:
Comment: Although the author claims to have already discussed the relationship between the existing methods and the proposed backdoor attack, I didn't find it in the "2. Related Work" section. I will maintain my original rating.
---
Reply to Comment 1.1.1:
Comment: We apologize for the insufficient discussion about the relationship between the existing methods and the proposed backdoor attack due to space constraints. Below, we provide a comprehensive literature review.
Backdoor attacks introduce hidden vulnerabilities into a model during training, enabling attackers to manipulate outputs at inference using a specific trigger. Early studies on backdoor attacks mainly focus on the **classification tasks** [1,2], where a backdoored model produces predefined predictions only when the input contains the trigger. The corresponding defense algorithms include backdoor detection [3] and trigger recovery [4]. More recently, researchers have investigated **backdoor attacks on generative models**. For example, [5] explores backdoor attacks in GANs, while [6] designs attacks for I2I networks.
Regarding the **diffusion model**, previous studies alter the diffusion process by injecting triggers into the input Gaussian noise. In the "2. Related Work" section of our manuscript, we have roughly discussed the two categories of existing backdoor attacks against diffusion models, the attacks on unconditional diffusion models and T2I diffusion models. Some researchers have also proposed defenses for backdoored diffusion models. [7] computes the KL divergence between the trigger and a standard Gaussian noise to detect the backdoor. [8] inverse the trigger by minimizing the gap between the triggered generation and the original trigger.
In this paper, we have proposed a novel backdoor attack for MixBridge. Our key contributions are listed as follows:
- We conduct backdoor attacks on an **I2I diffusion Schrödinger bridge model**. To the best of our knowledge, this is the first study on backdoor attacks in I2I diffusion models.
- We propose a new type of backdoor attack, **heterogeneous backdoor attack**. Unlike prior backdoor attacks, we implant multiple backdoors into the model, enabling diverse backdoor attacks.
Based on the introductions above, the **relationship** between our proposed backdoor attack and prior studies can be concluded as follows. In terms of the **similarities**, our backdoor attack method is built upon the generative diffusion framework, which solves I2I tasks in the benign case, and generates malicious outputs if the input contains a trigger. However, it differs in four key aspects. **First**, unlike early backdoor attacks that induce misclassifications, the MixBridge aims to generate target backdoor images. **Second**, the MixBridge targets the bridge-based diffusion models that directly take images as inputs, while previous studies mainly focus on unconditional or T2I diffusion models that start from a standard Gaussian noise. **Third**, we consider heterogeneous backdoor attacks against diffusion models, while previous studies consider a single backdoor attack only. **Forth**, existing defenses for diffusion models rely on the assumption that the diffusion process begins with Gaussian noise. As a result, they may not effectively mitigate our proposed I2I backdoor attack.
In conclusion, we propose a heterogeneous backdoor attack method against the I2I bridge-based diffusion model. We will incorporate this discussion into our manuscript.
> Reference:
>
> [1] Badnets: Identifying vulnerabilities in the machine learning model supply chain
> [2] Lira: Learnable, imperceptible and robust backdoor attacks
> [3] Practical detection of trojan neural networks: Data-limited and data-free cases
> [4] Neural cleanse: Identifying and mitigating backdoor attacks in neural networks
> [5] The devil is in the GAN: backdoor attacks and defenses in deep generative models
> [6] Backdoor Attacks against Image-to-Image Networks
> [7] Ufid: A unified framework for input-level backdoor detection on diffusion models
> [8] Elijah: Eliminating backdoors injected in diffusion models via distribution shift
> | Summary: This paper introduces MixBridge, a novel Diffusion Schrödinger Bridge (DSB)-based approach for enabling heterogeneous backdoor attacks on image-to-image models. The authors first demonstrate that a straightforward method—training a single DSB model with poisoned image pairs—can effectively execute such attacks. However, they identify challenges in performing heterogeneous attacks using a single DSB model. To address this, the authors propose a Mixture-of-Experts (MoE) strategy that integrates multiple DSB models, enhancing the effectiveness of heterogeneous backdoor attacks.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: I read the theoretical sections but did not examine the proofs in detail.
Experimental Designs Or Analyses: Yes. I checked the experimental sections in detail, including the normal tasks super-resolution and image inpainting, with Fake Face, NSFW, and Anime NSFW attacks.
Supplementary Material: I roughly checked Appendix D.
Relation To Broader Scientific Literature: Prior works predominantly focus on backdoor attacks on unconditional or text-to-image diffusion models. To the best of my knowledge, this work is the first to investigate backdoor attacks on image-to-image diffusion models. Moreover, heterogeneous backdoor attacks have been relatively underexplored in the literature. This study provides new insights into enabling such attacks, making a valuable contribution to the field.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: The paper is well-structured, clearly presented, and easy to follow.
The studied problem—heterogeneous attacks on image-to-image (I2I) models—is important and underexplored.
The proposed approaches are insightful, well-motivated, and thoroughly evaluated. I believe this work will provide valuable insights to the research community.
Other Comments Or Suggestions: Nan
Questions For Authors: I have no major concerns regarding the evaluation of this paper. However, I have a minor question: Can the authors provide insights on designing effective defense strategies against the proposed attack?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely thank you for accepting our work and for your constructive comments. Due to space constraints, we include `additional_tables.pdf` and visualizations at the following link: https://anonymous.4open.science/r/ICML25-5787/. References to **Table x** and **Figure x** in our responses correspond to the materials provided in this link. The responses to your questions and weaknesses are listed below:
> Q1 Possible defense
**A1:** To the best of our knowledge, existing defense mechanisms are primarily focused on T2I diffusion models and unconditional diffusion models. In addition, they mainly focus on a single expert model for backdoor attacks. In contrast, our proposed attack targets the **bridge-based I2I diffusion model** with **heterogeneous** MoE backdoor attacks. Thus, previous defense mechanisms may not be applicable to our setting.
Here, we conduct some experiments to investigate if previous defense mechanisms can be adapted to the I2I framework. We take Elijah [1] as an example to detect the trigger for a simple MixBridge model with two experts. Elijah assumes that the backdoor attack redirects the clean distribution $x_c^t\sim\mathcal{N}(\mu_c^t,\cdot)$ to the backdoor distribution $x_b^t\sim\mathcal{N}(\mu_b^t,\cdot)$ at step $t$ using a trigger $\tau$. The trigger can be optimized via the following formula.
$\tau=\arg\min_\tau\|\mathbb{E}_{\epsilon\sim\mathcal{N}(0,1)}[M(\epsilon+\tau,T)]-\lambda\tau\|.$
$M$ represents the model, and $\lambda$ is a hyperparameter related to the diffusion process.
However, the original Elijah defense is built upon the assumption that the generation process starts from a standard Gaussian noise (i.e., $\mu_b^T=0$). In the I2I scenario, we propose a **modified version of Elijah**. Assume the gap between the benign and backdoor distributions caused by $\tau$ to be expressed as:
$$\mu_b^t-\mu_c^t=\lambda^t\tau.$$
According to the Eq. 1 in our paper, we derive the following objective.
$\tau=\arg\min_\tau\|\sigma_1\mathbb{E}[\epsilon_{\text{Mix}}(x_1^c+\tau,t=1;\theta_{\text{Mix}})-\epsilon_{\text{Mix}}(x_1^c,t=1;\theta_{\text{Mix}})]-\lambda\tau\|.$
Ideally, one should first generate the trigger and finetune the model with the Elijah method, and perform backdoor attacks again to evaluate if the defense is effective. We compare the attack performance of the generated trigger with that of the original baseline.
| Models | MSE(E-02) | CLIP(E-02) |
|---|---|---|
| MixBridge | **0.10** | **94.34** |
| Elijah | 32.70 | 60.03 |
| Modified Elijah | 32.64 | 59.30 |
It turns out that the triggers generated by the defense methods fail to manipulate the diffusion process. In other words, they cannot inverse the trigger in the MixBridge, let alone defend against the attack. We attribute such failures to the complex distribution in the I2I generation process. In this case, the image distribution gap cannot be simply modeled by a trigger $\tau$. In addition, Elijah does not solve the **heterogeneous** backdoor. Please refer to **Figure 2** for the visualizations of triggers generated by Elijah.
> Reference:
>
> [1] Elijah: Eliminating backdoors injected in diffusion models via distribution shift
---
Rebuttal Comment 1.1:
Comment: I thank the authors for their reply. All my concerns have been addressed. I will keep my original rating.
---
Reply to Comment 1.1.1:
Comment: Thank you sincerely for your review and comments. We are deeply grateful for your recognition of our work's contributions and your acknowledgment that our responses addressed your concerns. The discussion about backdoor attack defense has significantly strengthened the paper, and we truly appreciate the time and expertise you dedicated to evaluating this research. | Summary: This paper introduces MixBridge, a novel diffusion Schrödinger bridge (DSB) framework designed to implant multiple heterogeneous backdoor triggers in bridge-based diffusion models, which accommodate complex and arbitrary input distributions. Unlike prior backdoor approaches that focus on single-attack scenarios with Gaussian noise inputs, MixBridge enables backdoor injection through direct training on poisoned image pairs, eliminating the need for complex modifications to stochastic differential equations. the authors propose a Divide-and-Merge strategy, where models are pre-trained for individual backdoors and later integrated into a unified model. Additionally, a Weight Reallocation Scheme (WRS) enhances the stealthiness of MixBridge. Empirical evaluations demonstrate the effectiveness of the proposed framework across diverse generative tasks.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes. The two metrics used in this paper, utility and specificity, are widely used in related works.
Theoretical Claims: I checked the proof in Appendix B, and do not find any issues.
Experimental Designs Or Analyses: Yes, the authors conducted extensive experiments.
Supplementary Material: Yes, I checked appendix B and D. No issues found.
Relation To Broader Scientific Literature: The key contributions of this paper build upon and extend multiple strands of existing research in backdoor attacks, diffusion models, and Schrödinger bridge frameworks. Prior work on backdoor attacks has primarily focused on single-trigger scenarios, often in classification models, with limited exploration in diffusion-based generative frameworks. Additionally, most backdoor studies have relied on Gaussian noise as the input distribution, restricting their applicability to more complex data settings. This paper broadens the scope by introducing MixBridge, which allows for backdoor implantation in bridge-based diffusion models handling arbitrary input distributions, thereby generalizing beyond previous Gaussian-based approaches.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Strength:
1. This paper propses a new backdoor attack against diffusion model.
2. Conduct extensive experiments to evaluate the proposed approach.
Weakness:
1. This authors do not evaluate the performance of the proposed approach under some defense mechanism,
Other Comments Or Suggestions: No
Questions For Authors: Could you consider some SOTA defense mechanism in the evluation section?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank you for accepting our work and for your constructive comments. Due to space constraints, we include `additional_tables.pdf` and visualizations at the following link: https://anonymous.4open.science/r/ICML25-5787/. References to **Table x** and **Figure x** in our responses correspond to the materials provided in this link. The responses to your questions and weaknesses are listed below:
> Q1 Possible defense
**A1:** To the best of our knowledge, existing defense mechanisms are primarily focused on T2I diffusion models and unconditional diffusion models. In addition, they mainly focus on a single expert model for backdoor attacks. In contrast, our proposed attack targets the **bridge-based I2I diffusion model** with **heterogeneous** MoE backdoor attacks. Thus, previous defense mechanisms may not be applicable to our setting.
Here, we conduct some experiments to investigate if previous defense mechanisms can be adapted to the I2I framework. We take Elijah [1] as an example to detect the trigger for a simple MixBridge model with two experts. Elijah assumes that the backdoor attack redirects the clean distribution $x_c^t\sim\mathcal{N}(\mu_c^t,\cdot)$ to the backdoor distribution $x_b^t\sim\mathcal{N}(\mu_b^t,\cdot)$ at step $t$ using a trigger $\tau$. The trigger can be optimized via the following formula.
$\tau=\arg\min_\tau\|\mathbb{E}_{\epsilon\sim\mathcal{N}(0,1)}[M(\epsilon+\tau,T)]-\lambda\tau\|.$
$M$ represents the model, and $\lambda$ is a hyperparameter related to the diffusion process.
However, the original Elijah defense is built upon the assumption that the generation process starts from a standard Gaussian noise (i.e., $\mu_b^T=0$). In the I2I scenario, we propose a **modified version of Elijah**. Assume the gap between the benign and backdoor distributions caused by $\tau$ to be expressed as:
$$\mu_b^t-\mu_c^t=\lambda^t\tau.$$
According to the Eq. 1 in our paper, we derive the following objective.
$\tau=\arg\min_\tau\|\sigma_1\mathbb{E}[\epsilon_{\text{Mix}}(x_1^c+\tau,t=1;\theta_{\text{Mix}})-\epsilon_{\text{Mix}}(x_1^c,t=1;\theta_{\text{Mix}})]-\lambda\tau\|.$
Ideally, one should first generate the trigger and finetune the model with the Elijah method, and perform backdoor attacks again to evaluate if the defense is effective. We compare the attack performance of the generated trigger with that of the original baseline.
| Models | MSE(E-02) | CLIP(E-02) |
|---|---|---|
| MixBridge | **0.10** | **94.34** |
| Elijah | 32.70 | 60.03 |
| Modified Elijah | 32.64 | 59.30 |
It turns out that the triggers generated by the defense methods fail to manipulate the diffusion process. In other words, they cannot inverse the trigger in the MixBridge, let alone defend against the attack. We attribute such failures to the complex distribution in the I2I generation process. In this case, the image distribution gap cannot be simply modeled by a trigger $\tau$. In addition, Elijah does not solve the **heterogeneous** backdoor. Please refer to **Figure 2** for the visualizations of triggers generated by Elijah.
> Reference:
>
> [1] Elijah: Eliminating backdoors injected in diffusion models via distribution shift | Summary: The paper presents a framework for injecting multiple heterogeneous backdoor triggers into bridge-based diffusion models. The authors propose a "Divide-and-Merge" strategy, where backdoors are trained independently and later integrated using an MoE framework. Additionally, a Weight Reallocation Scheme (WRS) is introduced to improve the stealthiness of backdoor attacks. Empirical results on ImageNet and CelebA demonstrate the effectiveness of MixBridge in both benign and backdoor generation scenarios.
Claims And Evidence: The claim “existing backdoor formulations are designed for generative models that exclusively take Gaussian noise as input” is not valid. There are existing backdoor attacks for I2I model with super-resolution images as input, such as [1].
[1] Jiang, Wenbo, et al. "Backdoor Attacks against Image-to-Image Networks." arXiv preprint arXiv:2407.10445 (2024).
Methods And Evaluation Criteria: 1. While the chosen metrics are standard in image generation and attack evaluation, the paper does not explore alternative evaluation methods that might capture stealthiness more effectively beyond entropy measurements.
2. Moreover, the stealthiness of the trigger added to images may need further consideration. If the trigger is too obvious, it could be easily detected, reducing the effectiveness of the backdoor attack in real-world scenarios.
3. It’s not clear why a two-stage approach is necessary. Could the Weight Reallocation Scheme loss L_WRS be incorporated during the router's training in the first stage?
Theoretical Claims: Proposition 4.1 argues that the natural pairing of images in I2SB facilitates backdoor training without explicit SDE modifications. Theorem 4.2 rigorously proves that a single I2SB model approximates the geometric mean of benign and backdoor distributions, leading to performance conflicts. They are aligned with their method and experiment results.
Experimental Designs Or Analyses: 1. The experimental setup is sound. However, the paper could provide more details on hyperparameter selection (e.g., trade-off parameter in Eq. 9).
2. Some backdoor defenses for T2I diffusion models such as Elijah [1] could be adapted for I2I diffusion models. The authors are encouraged to discuss possible defenses on MixBridge.
[1] An, Shengwei, et al. "Elijah: Eliminating backdoors injected in diffusion models via distribution shift." Proceedings of the AAAI Conference on Artificial Intelligence. Vol. 38. No. 10. 2024.
Supplementary Material: I went over some additional experimental results.
Relation To Broader Scientific Literature: This paper contributes to the growing literature on backdoor attacks/defenses in I2I diffusion models.
Essential References Not Discussed: The paper lacks discussion on existing backdoors for the I2I model (see Claims and Evidence). In addition, it is also encouraged to discuss possible defenses (by adapting existing ones) that may or may not defend MixBridge.
Other Strengths And Weaknesses: The paper in general is well-written with clear motivation. The method and evaluation are properly designed.
In addition to the lack of discussion on literature, I have one additional concern regarding **Attacker’s Capacity and Goal**. If the attacker is the model owner (with full control of the training process), I am not clear under which practical scenarios, the model owner would want to realize such a backdoor to make downstream users produce specific NSFW/low-quality images. As a model owner, I can understand the need to use backdoor techniques to realize some useful functions like watermarking or personalization. But here, why would a model provider want to make its users generate corrupted outputs which clearly brings it no benefit. The authors should provide more discussion on the practical significance of the proposed attack.
Other Comments Or Suggestions: None.
Questions For Authors: None.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely express our gratitude for your acceptance and constructive comments. Due to space constraints, we include `additional_tables.pdf` and visualizations at the following link: https://anonymous.4open.science/r/ICML25-5787/. References to **Table x** and **Figure x** in our responses correspond to the materials provided in this link. Below are our responses to your questions and identified weaknesses:
> Q1 Existing backdoor attacks for I2I model
**A1:** We acknowledge some previous studies have explored backdoor attacks on I2I models. However, **none** of them focus on diffusion-based models, let alone those based on the Schrödinger Bridge. We will restrict our discussion in the introduction to the diffusion-based models, and clarify the key differences from the previously mentioned I2I backdoor methods.
> Q2 Alternative evaluation methods for stealthiness
**A2:** We have included the answer in our response to **Reviewer LwZQ-Q1**.
> Q3 The stealthiness of the trigger needs further consideration
**A3:** Here, we evaluate the stealthiness based on trigger size. A **smaller** trigger is generally **harder** to detect. In particular, we conduct super-resolution task along with three heterogeneous backdoor attacks on the CelebA dataset using different trigger sizes in **Table 1**.
According to the experiments, the ASR remains 0.93 for a $16\times16$ trigger size (i.e., $1\%$ of the total image), which is a small trigger with relatively high stealthiness. In contrast, BadDiffusion [1] uses a $14\times14$ trigger on a $32\times32$ image, which occupies nearly $20\%$ of the image area. We present visualizations of different trigger sizes in **Figure 1** in the anonymous link.
> Q4 Why not one-stage WRS
**A4:** Following previous studies [2,3], we pre-train each expert separately and then finetune them jointly. Here, we conduct an ablation study for the one-stage method.
| | | FID | PSNR | SSIM(E-02) | MSE(E-02) | CLIP(E-02) | ASR | Entropy |
|:---:|:---:|:---:|:---:|:---:|:---:|:---:|:---:|:---:|
| one-stage | w/o WRS | 148.29 | 24.74 | 72.36 | 1.78 | 73.23 | 68.21 | 4e-04 |
| | WRS | 111.30 | 24.04 | 74.33 | 1.75 | 79.65 | 83.46 | **2.00** |
| two-stage (Ours) | w/o WRS | **74.67** | 25.01 | **74.64** | 0.96 | **93.68** | 98.53 | 3e-05 |
| | WRS | 92.00 | **25.43** | 74.27 | **0.64** | 93.21 | **98.73** | 1.99 |
Intuitively, the one-stage model significantly **underperforms** compared to the two-stage version. A possible reason is in one-stage training the experts might suffer from **conflicting** optimization directions across different generation tasks in the early phase, leading to poor and suboptimal solutions. By using a two-stage method, the pre-training process naturally avoids such issues, and makes the finetuning process more stable and effective.
> Q5 More details on hyperparameter
**A5:** As a trade-off hyperparameter, $\lambda$ controls the intensity of WRS. In this paper, to ensure the stealthiness of the backdoor attacks, we chose a large $\lambda$ to obtain high entropy. Here, we investigate how $\lambda$ affects the performance of the MixBridge.
| $\lambda$ | FID | PSNR | SSIM(E-02) | MSE(E-02) | CLIP(E-02) | ASR | Entropy |
|:---:|:---:|:---:|:---:|:---:|:---:|:---:|:---:|
| 1 | 92.00 | 25.43 | 74.27 | **0.64** | **93.21** | **98.73** | **1.99** |
| 0.1 | 90.47 | 25.53 | 73.73 | 0.75 | 92.61 | 98.38 | 1.93 |
| 0.07 | 87.77 | 24.90 | 73.74 | 0.70 | 92.14 | 97.98 | 1.65 |
| 0.05 | 76.38 | 25.29 | 75.01 | 0.67 | 92.86 | 98.13 | 1.24 |
| 0.03 | 75.20 | **25.85** | **75.98** | 0.90 | 92.38 | 97.73 | 0.13 |
| 0.01 | **70.45** | 25.02 | 74.92 | 1.07 | 91.24 | 98.19 | 0.01 |
The results show that a lower $\lambda$ improves benign generation but degrades the performance of backdoor attacks. We find that setting $\lambda=0.1$ or 1 leads to a relatively good tradeoff.
> Q6 Possible Defenses
**A6:** Please refer to our response to **Reviewer 8an4-Q1**.
> Q7 Attacker’s Capacity and Goal
**A7:** We apologize for the unclear explanation of the backdoor attack settings. On one hand, the model owner (or the attacker) may not be primarily motivated by financial gain. Instead, their intentions could include deliberate sabotage, reputation damage, or other non-economic incentives. For example, an attacker might aim to create chaos, undermine competitors’ credibility, or provoke legal and ethical issues to gain a strategic advantage. On the other hand, as you mentioned, backdoor techniques can be used for legitimate purposes like watermarking or personalization. Therefore, this paper can also potentially promote the studies for legitimate applications.
We will revise our corresponding claim in the paper according to your suggestion.
> Reference:
> [1] How to backdoor diffusion models?
> [2] Warm: On the benefits of weight averaged reward models
> [3] Mogu: A framework for enhancing safety of open-sourced llms while preserving their usability | null | null | null | null | null | null |
MindCustomer: Multi-Context Image Generation Blended with Brain Signal | Accept (poster) | Summary: This paper introduces MindCustomer, a novel multi-context image generation framework that integrates visual brain signals with traditional image and text modalities to enable brain-controlled image customization. The authors propose a method to blend brain semantics into the image generation process, addressing key challenges such as multi-modal integration, and context preservation.
Claims And Evidence: 1. As the first work,MindCustomer successfully implements multi context blended with brainsignal in image generation. （On the right side of line 70）
Evidence:The paper provides a thorough literature review, highlighting that previous works have focused on text-to-image generation or brain signal reconstruction but not on using brain signals to guide multi-context image generation.
2. It achieves high-quality image customization guided by cross-subject brain contexts.（On the right side of line 72）
Evidence: The paper presents qualitative results showing high-quality image outputs that faithfully represent the provided contexts.
Quantitative metrics (e.g., CLIP-I, DINOv2, CLIP-IQA) demonstrate superior performance compared to baseline methods. User studies also indicate a preference for MindCustomer's results over baselines.
3. We propose the Image-BrainTranslator(IBT) for cross-subject brain data augmentation, ensuring stable embeddings.（On the right side of line 104）
Evidence: The authors demonstrate the effectiveness of IBT through experiments showing that it can simulate brain signals from visual stimuli with moderate to high correlation to ground-truth fMRI data. Additionally, they show that IBT-augmented data improves the stability of brain embeddings.
Methods And Evaluation Criteria: Quantitative Metrics: The paper uses metrics such as CLIP-I, DINOv2, and CLIP-IQA to evaluate context similarity and image quality. These metrics are widely accepted in the field of image generation and are relevant for assessing the model's performance.
I have some concerns regarding the ablation experiments presented in Figure 8. The figure only provides two pairs of Image/Brain context examples and does not quantitatively measure the true quality of the proposed IBT, fine-tuning, and optimization methods in this paper.
The results in Table 4 appear to indicate that the fMRI image reconstruction framework proposed in this paper underperforms compared to MindBridge and UMBRAE, suggesting that there is no actual performance improvement in this study.
Theoretical Claims: The theoretical claims in the paper are primarily supported by empirical evidence rather than formal proofs. The authors provide convincing demonstrations of the effectiveness of their methods through experiments, comparisons, and user studies. However, there are potential areas for further theoretical analysis, such as:
Robustness of the IBT: Analyzing the theoretical guarantees and limitations of the IBT in simulating brain signals. The correlation metric alone may not fully capture the semantic alignment between simulated and real brain signals. Additionally, the effectiveness of the IBT may depend on the quality and diversity of the training data.
Generalization Bounds: Exploring theoretical bounds on the model's generalization ability, especially in the context of few-shot learning. The generalization ability is based on empirical results from a limited number of subjects. Theoretical analysis could further explore the conditions under which the model generalizes well and the potential limitations in more diverse populations.
Experimental Designs Or Analyses: The authors compare MindCustomer to several ablation variants, including models without IBT, without fine-tuning and optimization, and without optimization. The results are evaluated using the same metrics and qualitative analysis as in the main experiments.
The effectiveness of the IBT may vary across subjects due to inherent differences in brain signal patterns. The paper could benefit from a more detailed analysis of how well the IBT generalizes across different subjects. And while the Pearson correlation measures similarity, it does not directly assess semantic alignment. Additional metrics or qualitative analysis could provide deeper insights into the semantic fidelity of the simulated brain signals.
While the ablation studies show improvements, they may not fully capture the interactions between components. More detailed analysis or additional ablation variants could provide deeper insights. For example, various indicators calculated from the reconstructed images of each part after ablation can be listed. The images displayed now are carefully selected and lack strong persuasiveness.
Supplementary Material: I have gone through all the supplementary material.
Relation To Broader Scientific Literature: The Image/Brain context-guided image generation proposed in this paper does not represent a particularly novel technology and can be viewed as a combination of existing techniques (e.g., MindEye2 (ICML 2024) and MindArtist (CVPR 2024)). It is recommended that the authors objectively evaluate the performance of the proposed methodological framework and emphasize its distinctions from previous work. This would help to highlight the contributions of this paper.
Essential References Not Discussed: See "Relation To Broader Scientific Literature".
Other Strengths And Weaknesses: The experiments in the article mainly focus on qualitative analysis, with too little emphasis on quantitative analysis. There is too little comparison with other models to fully demonstrate its effectiveness. It is strongly recommended to add quantitative indicators to key experiments such as ablation experiments, comparative experiments with image fusion, and generalization experiments. At the same time, some calculations of reconstructed image indicators can be added.
This paper proposes an Image/Brain context-guided image generation model that requires both Image and fMRI inputs during the inference process. Additionally, the textual inversion technology is not new and has been widely used. I believe that using a method similar to MindEye's [1] prior diffusion and SDXL for image generation, followed by optimization of image features, would not be inferior to the approach presented in this paper. Therefore, I am not convinced of the superiority of the proposed method over other existing methods.
References
[1] Scotti P, Banerjee A, Goode J, et al. Reconstructing the mind's eye: fmri-to-image with contrastive learning and diffusion priors[J]. Advances in Neural Information Processing Systems, 2023, 36: 24705-24728.
Other Comments Or Suggestions: After passing through Semantic Extractor, the figure points to the loss function. Suggest modifying the drawing to make it clearer.
The Method section of the article, especially the definition of variables in Brain Representation Pre training, is quite confusing. Although the author's meaning can be understood, it is difficult to read. I think it's because some variables were not used or further explained after being defined, such as EIa and eIa.
Questions For Authors: 1. Is the encoding model for predicting fMRI from images trained separately for each subject?
2. The article mentions the use of shallow subject-wise embedders and deep shared embedders to obtain two different types of embeddings. Can each embedder obtain a different type of embedding? Are they the same thing as the Shallow Layer and Shared Deep Layer in Figure 2 (1)? If so, there seems to be a sequential relationship, so how can two different types of embeddings be obtained from a shared deep layer? This part confuses me.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank you for your reviews!
***Rebuttal Link*** (https://anonymous.4open.science/r/ICML2025-Rebuttal-MindCustomer) is for supplemented results in rebuttal, please refer to it.
**Q1: Quantitative measures of ablation study and indicators of reconstructed image**
**In the submitted paper, we have presented the quantitative measures of our ablation study in the right half of Table 1**, please refer to it. Due to page limitations, we reasonably merged these results with the baseline comparison within one table and provided a table reference in the relevant text (line 437). Furthermore, **we have listed the indicators of the reconstructed images in the submitted paper, please refer to Table 4**.
**Q2: Table 4 illustration**
As the first work on multi-context (brain, image, text) blended generation, MindCustomer needs accurate context extraction. Table 4 demonstrates our method’s effectiveness in brain semantics extraction and its competitiveness with SOTA brain decoding methods. The main experiments in this paper show that our brain encoding, combined with the proposed effective cross-modal fusion pipeline, is sufficient to achieve high-quality blending. While existing fMRI reconstruction methods may offer better encoding, they introduce more conditions and complexity, making them inefficient in multi-context blended generation.
**Q3: Further theoretical analysis**
Since our proposed IBT is an MLP-based model with a relatively simple structure, we reduced some theoretical analysis in other aspects (e.g. robustness). Thank you for providing additional discussion ideas, which further enhance our theoretical analysis. We will explore the robustness of the IBT model across different data and individuals, as well as its generalization to data volume in the few-shot generation.
**Q4: Metrics or qualitative analysis of semantic fidelity of the simulated brain signals**
We have provided additional qualitative and quantitative analyses of IBT-simulated brain signals in **Figures 15 and 16 of the original Appendix**. Please refer to them.
**Q5: Comparison with other methods**
- We have described a detailed analysis and differences with references (e.g. MindEye2, MindArtist), which can be found in the paper’s introduction (Left: Line 66-109, Right: Line 55-69) and related work section (Left: Line 150-164, Right: Line 135-155). Please refer to them.
- To illustrate MindCustomer's performance, we add another baseline per the review's suggestion: using MindEye for fMRI-to-image reconstruction, followed by Versatile Diffusion (a mature image-blending model). In the baseline, VD requires no extra finetuning or optimization since it's pre-trained on large text-image datasets. In contrast, MindCustomer's finetuning adapts brain representation to diffusion's latent embedding, while optimization addresses semantic overlap between image and brain contexts—**unique innovations of our method**. As shown in the ***Rebuttal Link*** (**Rebuttal Figure 3 & Table 2**), due to the brain interpretation deviation caused by fMRI reconstruction and some semantic conflict from dual contexts resulting from the blending diffusion, the baseline shows some semantic deviation and loss. Benefiting from our unique designs, MindCustomer generates high-quality results. **We also explained this in the submitted paper (Experimental analysis: line 350-357 (right), Intro: line 091-095 & 058-065 (right)), please refer to them.** We will add the comparison results to better demonstrate MindCustomer's performance.
**Q6: Clarity**
Thank you for the suggestion. We will revise the output of the Semantic Extractor in the figure clearly. It should add the output embedding of the Semantic Extractor with the ground truth to construct the loss for model training. Besides, in the section of Brain Representation Pre-training, we will reduce some unnecessary symbols to make it simpler and easier to understand.
**Q7: Is the encoding model for predicting fMRI from images trained separately for each subject?**
IBT is subject-wise, please refer to line 181 (right). Due to the significant differences in original brain signals from different subjects, we designed the IBT for each subject. Experiments **(e.g. Figure 15 & 16, and Table 6 in Appendix)** show that even when IBT is lightweight (several layers of MLP), it can still effectively fit each subject's brain signals. Therefore, the subject-wise IBT does not increase the complexity within an acceptable range.
**Q8: Can each embedder obtain a different type of embedding?**
In line 203 (right): "We employ the shallow subjectwise embedders $E_{∫}$ and deep shared embedders $E_{⌈}$ to obtain the two types of embeddings of voxels", the two types refer to brain signal encodings supervised by CLIP-encoded **text** and **image**, respectively, as described in line 199 (right), rather than different types of encodings from different embedders. We will revise the description here for clarity. | Summary: This paper proposes a new task: image customization with brain signals, which is novel and interesting. The authors introduce the image-brain translator and brain embedded to align various modalities, including images, fMRI, and texts, together for generating new images with a versatile diffusion model.
Claims And Evidence: Claims are reasonable and supported by references and evidence.
Though, one reference mistake on ln139: "Additionally, Takagi. etc (Takagi & Nishimoto, 2023) employs Masked Autoencoders (MAE) to improve the encoding of brain signals, enabling more accurate reconstructions." Takagi & Nishimoto did not use MAE to encode brain signals in the mentioned reference. Please double-check the reference.
Methods And Evaluation Criteria: The methods and evaluation criteria make sense.
Theoretical Claims: N/A
Experimental Designs Or Analyses: Experimental designs and analysis make sense.
Supplementary Material: I reviewed the supplementary material.
Relation To Broader Scientific Literature: The proposed task is new in this area, which is interesting and could have an impact on the future application of the brain-computer interface.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: I think the quality of this paper is good in general. It presents an interesting new task with careful design for multimodal alignment. However, I have the following concerns.
- On ln185, the authors mentioned using adaptive max pooling to achieve the subject-invariant voxel sizes. However, various subjects have quite different activation regions even when viewing the same stimuli. Using adaptive max pooling as mentioned would lose or change the original position information of voxels. Therefore, this choice should be further discussed and justified.
- The baseline in Section 4.2 is not convincing enough. Ideally, the comparison should be between another fMRI blending model, rather than image bleeding models (no matter whether it is mask-free or signle-image generation or not). I would suggest using the output of an fMRI-to-image model as the input of another image-blending model as a baseline.
Other Comments Or Suggestions: Details of the user study should be introduced, such as study protocols, demographic information, etc.
Questions For Authors: See the previous sections.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank you for your reviews!
***Rebuttal Link*** (https://anonymous.4open.science/r/ICML2025-Rebuttal-MindCustomer) is for supplemented results in rebuttal, please refer to it.
**Claims And Evidence: Reference error**
Thank you for pointing out the citation error. It should be: Takagi et al.[1] reconstruct high-resolution images from brain activity while preserving rich semantic details, without the need for training or fine-tuning complex deep generative models. Mind-Vis[2] utilizes Masked Autoencoders (MAE) to enhance brain signal encoding, enabling more accurate reconstructions. We will correct this citation error.
[1] High-resolution image reconstruction with latent diffusion models from human brain activity
[2] Seeing Beyond the Brain: Conditional Diffusion Model with Sparse Masked Modeling for Vision Decoding
**Other Strengths And Weaknesses1: Choice of adaptive max pooling**
- Beyond unifying brain signals across subjects in scales, we believe adaptive max pooling helps mitigate the issue of sparse brain signal sampling, preserving critical semantic information. Additionally, reference MindBridge[3] shows that max-pooling provides better brain signal aggregation compared to average pooling or interpolation. We will further clarify this in our paper.
- Besides, in the discussion and future work sections, we will acknowledge that this is not necessarily the optimal approach. In neuroscience, effective brain signal sampling requires a comprehensive analysis of cross-subject variations in numerical values, regions, and data quantity. We will explore the strengths and limitations of different sampling methods and provide further insights. We see this as a valuable direction for future work to design more effective sampling strategies.
[3] MindBridge: A Cross-Subject Brain Decoding Framework
**Other Strengths And Weaknesses2: The reason for original baseline design and results of recommended baseline**
- The reason for us to choose the visual stimuli as the input rather than the fMRI-reconstructed image is that the images reconstructed via fMRI-to-image methods generally have lower semantic quality than the original visual stimuli. Then, using reconstructed images as inputs for blending would lead to weaker performance. Therefore, we chose to use the **higher-quality original visual stimuli** as the fusion input and set this as **a stronger baseline in our paper** to better demonstrate the effectiveness of our method.
- Additionally, we also illustrate comparison results for using the output of a SOTA fMRI-to-image model (MindEye[4]) as input for another mature image-blending model (Versatile Diffusion[5]) as a baseline (advised in review). As shown in the ***Rebuttal Link*** (**Rebuttal Figure 3 & Table 2**), we conduct both qualitative and quantitative comparisons: Due to the brain signal interpretation error caused by fMRI reconstruction and some semantic overlap between dual image contexts resulting from the blending diffusion model, this baseline shows some semantic deviation and loss. In contrast, the proposed **effective cross-modal fusing pipeline with the designed IBT model** addresses these issues. MindCustomer not only successfully blends different contexts in nature but also preserves semantics, thus generating high-quality results. **We also explained this in the submitted paper (Experimental analysis: line 350-357 (right), Intro: line 091-095 & 058-065 (right)), please refer to them.** We will also further supplement the above results and emphasize the analysis in the final version.
[4] Reconstructing the Mind's Eye: fMRI-to-Image with Contrastive Learning and Diffusion Priors
[5] Versatile Diffusion: Text, Images and Variations All in One Diffusion Model
**Others: More details of the user study**
In addition to the description of the User Study in the paper, we will provide more details about the study design in the Appendix. We randomly selected 110 pairs of comparison images, including ours and the baseline, and divided them into 11 groups. A total of 22 participants were involved, and to minimize bias caused by individual preferences, we randomly assigned every two participants to the same group, ensuring that each image received ratings from two different individuals. By comparing ours with the baseline, participants are required to score on each generated image based on the quality and consistency from 1 to 3, higher is better. Ultimately, we collected 220 answers for the 110 randomly selected image pairs from the 22 participants. The results broadly reflect the participants' consistent preference for our approach. | Summary: This paper proposes a novel framework, MindCustomer, to explore the blending of visual brain signals in multi-context image generation. This approach enables cross-subject generation, delivering unified, high-quality, and natural image generation.
Claims And Evidence: 1. This paper claims some potential for practical application. But there are no related applications introduced. It will be better that authors are able to further illustrate some specific real-world applications.
2. Part of the contribution in this paper is summarized as the introduction of Image-Brain Translator (IBT). And authors provide some qualitative and quantitative results. But there are missing comparisons with other strategies handling the multi-identities generality such as MindEye2.
Reference:
MindEye2: Shared-Subject Models Enable fMRI-To-Image With 1 Hour of Data
Methods And Evaluation Criteria: The proposed approach is intuitive but the overall methodology is kind of combinational and has limited novelty. The evaluation criteria follows previous work and is reasonable.
Theoretical Claims: There are no theoretical claims involved in this paper.
Experimental Designs Or Analyses: 1. About the figure 6, why is the proposed approach able to achieve superior performance over the baseline? Theoretically speaking, the image signal is supposed to capture more visualization information than the brain signal.
2. For the brain decoding, how is performance compared with alternative designs such as MindEye1 ?
MindEye1: Reconstructing the Mind’s Eye: fMRI-to-Image with Contrastive Learning and Diffusion Prior
Supplementary Material: Authors provide an overall implementation of their paper. I only briefly go through file structure, which seems like a reasonable project.
Relation To Broader Scientific Literature: It is a cross-domain work that combines both brain-to-image study and image generation field research. Both fields attract significant attention in the research field.
Essential References Not Discussed: It will be better if authors can also include the MindEye series of work.
MindEye2: Shared-Subject Models Enable fMRI-To-Image With 1 Hour of Data
MindEye1: Reconstructing the Mind’s Eye: fMRI-to-Image with Contrastive Learning and Diffusion Prior
Other Strengths And Weaknesses: N.A
Other Comments Or Suggestions: N.A
Questions For Authors: Please kindly resolve the issues in Claims and Evidence sections.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We sincerely thank you for your reviews!
***Rebuttal Link*** (https://anonymous.4open.science/r/ICML2025-Rebuttal-MindCustomer) is for supplemented results in rebuttal, please refer to it.
**Q1: Claim of "potential for practical application"**
- **As the first** to propose and achieve the fusion of fMRI, image, and text for customized creation, MindCustomer has demonstrated success on **the large-scale brain dataset NSD**.
- We have discussed and explained this claim of potential application in detail in our **Discussion and Limitation section (Appendix D)**, please refer to it. **Constrained by the types of existing brain signal datasets**, we think that MindCustomer presents the potential application **in future real-world scenarios**.
- Additionally, although constrained by the current types of brain signal data, we have also explored **few-shot generation for new subject in this paper**, simulating the effect of personalized generation when there is a limited amount of brain data in real-world scenarios.
In all, we believe that MindCustomer is an important foundational exploration, and in the future, more real-world data collection will be involved to promote the application of MindCustomer.
**Q2: Reference to MindEye**
- Regarding the performance of the fMRI reconstruction task, it is slightly lower compared to MindEye. We believe the reasons lie in the fact that the MindEye series used four more subjects' data for training (MindEye2) and employed additional information, such as retrieval, brain captions, and more diffusion models, to better achieve brain reconstruction tasks. In contrast, **for MindCustomer's multi-context blending task, this additional information was not needed**. As such, a direct comparison between the two **may not be fair**. Meanwhile, we **have cited and analyzed a series of brain reconstruction works, including MindEye, in our paper (line 71 in intro and line 164 in related work)**. We not only acknowledge and appreciate their contributions to brain signal decoding but also analyze the differences between our work and these previous studies in terms of tasks and challenges. Unlike prior works that focus on better decoding brain signals themselves, the core of our work lies in how to fuse brain signals with various cross-modal information to create naturally composed images. **Besides, we will also include more performance discussion of the MindEye series of work in the final version to highlight respective advantages.**
- Nevertheless, we would like to emphasize that, firstly, **we have fairly compared MindCustomer with several SOTA methods in the brain reconstruction field**. MindCustomer demonstrated strong competitiveness. Secondly, as for the task and challenges in this paper, it is not only to have a model with a certain level of brain semantic encoding ability but **more importantly**, how to integrate information from different modalities to generate natural images that preserve semantics. Our experimental results have proven that MindCustomer **is capable of effectively extracting brain signal semantics**, and **more importantly, it has demonstrated excellent performance in the personalized blending task**. Therefore, we believe that MindEye indeed makes an important contribution to the field of fMRI reconstruction, while MindCustomer also has its own merits in personalized multimodal fusion creation. We will further clarify the relation in final version.
**Q3：Figure 6 question**
- Although images may contain richer semantics, we observe that inputting two images into versatile diffusion (VD), a mature image fusion method for blended generation, often causes **semantic overlap**, making it hard to preserve distinct semantics. To address this, we designed VD fine-tuning based on image context to learn the image semantics, and more importantly, we freeze the fine-tuned VD model, and lightly optimize brain contexts with the target of image context. This helps mitigate semantic conflicts between different image and brain contexts. During the above process, we further utilize the proposed IBT to transfer image context to brain-embedding space to reduce the gap between modals. Thus, **the above-designed brain-blended cross-modal fusion** allows the final multimodal blending to better preserve each modality's semantics and produce more accurate, high-quality results. We also have explained this in the paper **(line 353, right)**: “This is likely ... ”, please refer to it.
- Therefore, as for the method design of MindCustomer, we **innovatively propose IBT to simulate the process of visual stimuli being transformed into brain signals**. This not only expands brain signal data and enhances encoding capability but also **provides the above solution of brain-blended cross-modal fusion**. Overall, MindCustomer introduces well-designed modules and a structured pipeline tailored to the task, making it a simple yet effective approach rather than a naive combination. | Summary: This paper proposes MindCustomer, an image generation method with input of image, text and brain signals. The brain signals is converted by Image-Brain Translator(IBT) into image embeding space for subsequent text-image joint generation. The diffusion model is finetuned and the embeddings is optimized to achieve more plausible visual results.
Claims And Evidence: yes
Methods And Evaluation Criteria: yes
Theoretical Claims: yes
Experimental Designs Or Analyses: yes
Supplementary Material: yes
Relation To Broader Scientific Literature: The paper builds upon previous work in brain decoding and image generation, particularly leveraging advancements in models like MindBridge.
Essential References Not Discussed: .
Other Strengths And Weaknesses: ## Strengths
1. The integration of brain signals for image editing shows successful results, surpassing baseline methods.
## Weaknesses
1. The contribution is limited to trivial fine-tuning of Versatile Diffusion and linear interpolation of two embeddings. The brain representation pre-training (IBT) and new-subject few-shot generation are largely derived from MindBridge, making the paper limited in technical contribution.
2. The introduction of ClipCap in IBT is not validated in ablation studies, making its actual contribution unclear.
3. Clarity issues in the description:
* The term "$\eta$" in equation (1) is not defined.
* The term "$e_p$" is not explained in equation (8).
Other Comments Or Suggestions: Do you have more visual results with only different text descriptions?
Questions For Authors: Please refer to weakness.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank you for your reviews!
***Rebuttal Link*** (https://anonymous.4open.science/r/ICML2025-Rebuttal-MindCustomer) is for supplemented results in rebuttal, please refer to it.
**W1: Comments on contributions**
- Diffusion model fine-tuning and linear interpolation are well-established techniques widely used in many studies. While we also employ these techniques in our work, they are **not** the core contributions we claim in this paper.
- Our main contributions first lie in **as the first work, MindCustomer proposed and successfully achieved the personalized image creation task by integrating brain signals with other traditional modalities**.
- Second, we need to clarify that the designed **IBT, a model that simulates pseudo-brain signals from input images (please note that it is not a brain signal encoding model described in the review**: "The brain signals is converted by Image-Brain Translator(IBT) into image embeding space for subsequent text-image joint generation", "The brain representation pre-training (IBT)", "The introduction of ClipCap in IBT"). **IBT simulates brain signals from images to enhance subsequent brain signal semantic encoding and reduce the modal gap in the following cross-modal fusion pipeline, which is independent of MindBridge**. Specifically, based on the proposed IBT, we simulate subject-wise fMRI for each visual stimulus. In this way, we can augment the fMRI training dataset due to the stimulus for each subject is different from the original dataset. Then during brain representation pre-training, we simultaneously feed different subjects' fMRI of one stimulus for shared learning in one encoding model. **The above process is different from MindBridge**.
- Third, more importantly, we propose **an effective cross-modal information fusion pipeline**. In order to blend image context with brain context, we designed VD fine-tuning based on image context to learn the image semantics, and then we froze the fine-tuned VD model and lightly optimized brain contexts with the target of image context. **This helps mitigate semantic conflicts between different contexts**. Besides, during the above process, we further utilize the proposed IBT and brain embedding model to transfer image context to brain-embedding space to **reduce the gap between different modals**. Thus, the above-designed brain-blended cross-modal fusion enables final natural integration and semantic preservation across modalities, producing natural and high-quality blending results.
The above clarification can also be referred to the submitted paper (line 96, left - line 68, right). Therefore, **it is vital to highlight that these are our core contributions**, which fundamentally exceed simple VD fine-tuning or linear interpolation.
**W2: Ablation study of ClipCap**
In the ***Rebuttal Link*** (**Rebuttal Figure 1 & Table 1**), we include an ablation study of ClipCap. The blending results without ClipCap show lower semantic details with complete MindCustomer. Both the qualitative and quantitative results demonstrate the role of the introduced ClipCap in enhanced brain semantic extraction. Adding this experiment makes our study more comprehensive. Additionally, please note that **we have also conducted detailed numerical and visual ablation studies on the proposed *core* techniques (e.g. IBT, cross-modal information fusion pipeline) in the submitted paper**.
**W3: Clarity**
- $\eta$ in $G_{\eta}$ refers to the parameters of the IBT model $G$. Thank you for pointing out. We will add its definition.
- **We have defined $e_{p}$ in the paper (line 256) before using it in equation (8)**, "We feed the transferred image context $Bp$ into brain embedder $\epsilon$ to obtain the embeddings $e_{p}$." We will also appropriately add a further description of it in the subsequent text.
**Others: More results with only different text descriptions**
In the ***Rebuttal Link*** (**Rebuttal Figure 2**), we present more visual results with only different text contexts. As we can see, MindCustomer robustly creates multi-context images that are content-consistent and naturally integrated.
---
Rebuttal Comment 1.1:
Comment: Thank the authors for the response, which addresses most of my concerns and clarifies the technical contributions. I have therefore decided to raise my score to 3.
That said, I suggest the authors incorporate the key clarifications from the rebuttal into the revised version to make the paper clearer and more convincing to readers.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer 4Rs7,
We sincerely appreciate your recognition of our work, and we're pleased that your concerns have been resolved! Based on the rebuttal, we will make further clarifications in the revised version. | null | null | null | null | null | null |
Semi-Supervised Blind Quality Assessment with Confidence-quantifiable Pseudo-label Learning for Authentic Images | Accept (poster) | Summary: This work aims at addressing the quality assessment task for authentically disorted images from a semi-supervised learning perspective. The key idea is to leverage confidence quantifiable pseudo-label learning to confront the data insufficiency challenge. The proposed CPL-IQA can be trained on unlabeled images with an entropy-based confidence learning to mitigate the negative effects from noisy labels.
## update after rebuttal
In the rebuttal, the authors have futher verified the value of this work by leveraging unlabeled data for boost IQA model. I will keep my rating.
Claims And Evidence: Yes,
Methods And Evaluation Criteria: Yes. This work propose to leverage unlabeled data for IQA model training, which includes an neccessary module to mitigate the inevitable label noise issue. The proposed alternate learning between model training and label optimization is reasonable since the reliability of pseudo-labels progressively increase with the correctness of the model predictions.
Theoretical Claims: The proofs in the appendix is correct to the Reviewer.
Experimental Designs Or Analyses: In the experiments, existing IQA datasets with full quality annotations are manually splited into three parts: training images with labels, training images without labels (exists but not used), and test images. The experiments setup is reasonable to verify the effectiveness of the proposed semi-superivsed learning scheme. Compared with supervised learning, unsupervised learning, and other semi-supervised learning methods in the filed of IQA, the proposed method presents better performance. To the Reviewer, this work can be further improved if the authors can use the proposed method to train an IQA model on the combination of existing annotated IQA datasets and extra unlabeled images following regular setup, e.g., split KonIQ-10k with a ratio of 8:2 (training/test), training the model on the training set of KonIQ-10k and an extra unlabeled dataset, verifying that the the performance of model is improved on the test set of KonIQ-10k compared to the counterpart which is trained only on training set of KonIQ-10k.
Supplementary Material: I review the full supplementary material.
Relation To Broader Scientific Literature: In the era of deep learning, data plays a key role in developing powerful artificial intelligence models across various tasks. However, the scale of data will be limited when the cost of annotations is high, where IQA is one of such case. This work is closely related to the important topic of training artificial intelligence models using unlabeled data.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Resizing all images into 256x256 may deteriorate IQA performance, it's better to crop multiple image patches from images with their original resolution.
Other Comments Or Suggestions: No.
Questions For Authors: In Table 10, the SRCC result of HyperIQA is higher than the proposed method but not marked with bold. Is there any typo?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your affirmation and the valuable comments that help us improve our work. The following is a careful response and explanation about the weaknesses and questions.
# For Experimental Designs Or Analyses
We sincerely appreciate your recognition of our experimental design and analysis, as well as this valuable suggestion.
In fact, we have already applied the proposed method to train an IQA model using a combination of existing annotated IQA datasets and additional unlabeled images under standard experimental settings. Specifically, as shown in Appendix Table 10, we select 80% from BID,70% from KonIQ-10k, 10% from KonIQ10k,and the remaining 20% from two datasets as labeled, unlabeled, validation, and testsets, respectively. The results clearly demonstrate the superiority of our approach.
To further validate the effectiveness of our method, as suggested by the reviewer, we split KonIQ-10k into labeled training and test sets (8:2 ratio), trained the model on the labeled KonIQ-10k training set and the unlabeled LIVE-C dataset, and evaluated it on the remaining 20% KonIQ-10k test set. The results are as follows:
| training sets | 80% labeled KonIQ-10k | 80% labeled KonIQ-10k + unlabeled LIVE-C |
|-|-|-|
| PLCC | 0.879 | **0.891** |
| SRCC | 0.874 | **0.885** |
From the above results, we can observe that, after training with the extra unlabeled dataset LIVE-C, the performance of the model is improved on the test set of KonIQ-10k compared to the counterpart which is trained only on training set of KonIQ-10k. These results further validate the effectiveness of our proposed method.
In the camera-ready version, we will incorporate these additional experimental findings to further strengthen our work.
# For Other Strengths And Weaknesses
Thanks for this valuable comment. We acknowledge that resizing could theoretically alter distortion characteristics and affect quality assessment accuracy. In fact, the resize-and-crop strategy in our model is actually another choice that is widely used in many works, which can balance computational efficiency and practical applicability. Below, we provide a detailed justification for this design choice in our model from three perspectives:
1. **Preservation of Global Context:** Since the required final cropped size during training is 224×224, resizing images to 256×256 before cropping in our method ensures that the model captures relatively global regions of the image while retaining fine-grained distortion patterns. This strategy has been widely adopted in classic IQA works such as DB-CNN, NIMA, and SSL-IQA, and our approach follows this well-established practice.
2. **Trade-off Between Performance and Efficiency:** We agree with the reviewer that cropping multiple patches from original-resolution images (without resizing) is theoretically preferable. However, this requires extracting multiple patches per image, significantly increasing training overhead and computational complexity. This is because, for large original images, a small number of cropped patches may fail to cover sufficient global regions of the image. Therefore, existing models adopting this strategy (e.g., LIQE and HyperIQA) typically address this by cropping a large number of patches, which further escalates computational costs.
3. **Empirical Validation:** Following the experimental setup in Table 1, we conducted additional tests by randomly cropping 10 patches per original-resolution image (denoted as Strategy 2) and compared its performance with our default resize-and-crop approach (Strategy 1). The results show that Strategy 2 only improves PLCC and SRCC by less than 1%, but at the cost of 4× longer runtime. The cost-performance ratio is unfavorable.
| Pre-processing methods | Stategy 1 | Stategy 2 |
|-|-|-|
| PLCC | 0.873 | 0.878 |
| SRCC | 0.845 | 0.851 |
| Running time in one epoch of Stage 1 (s) | 63.24 | 238.57 |
We will emphasize in camera-ready version that our resizing-and-cropping strategy balances efficiency and performance, ensuring scalability for real-world deployment.
# For Questions
Thank you for your careful review and valuable feedback. **We are sorry for this oversight and will correct it in the camera-ready version** by bolding the SRCC result of HyperIQA in the table.
Notably, this oversight does not impact Appendix E.5's analysis, as Table 10 primarily compares our method with Semi-IQA, where ours shows superior performance. While HyperIQA achieves marginally better results on BID through computationally intensive supervised training, it underperforms significantly on KonIQ-10k compared to our method, further validating our approach's effectiveness.
In camera-ready version, we will conduct a more thorough review to eliminate any remaining typos and ensure the rigor and high standard of our research. | Summary: This paper presents a novel semi-supervised blind image quality assessment framework, named CPL-IQA, for assessing the quality of real distorted images. The method effectively utilizes a large number of unlabeled real distorted images through confidence-quantifiable pseudo-label learning, addressing the challenge of limited labeled data in the field of image quality assessment.CPL-IQA consists of two phases, namely, label transformation preprocessing and alternating model training and label optimization. Its core innovation lies in the label optimization strategy based on the streaming assumption and the confidence learning method for pseudo-labels. Experimental results show that the framework performs well on real distorted image datasets, provides a more standard semi-supervised learning paradigm, and does not require additional supervisory information or complex network structure.
## update after rebuttal
The author's response answered my questions and I will keep my score. In addition, I hope the author will finally make the code public and promote the community.
Claims And Evidence: 1) The main innovations of CPL-IQA include a label optimization strategy based on the streaming assumption and a confidence learning method for pseudo-labeling that enhances reliability and mitigates the effects of outliers. Section 3.3.3 of the paper describes the label optimization process in detail, and Section 3.3.4 describes the confidence learning method and demonstrates the effectiveness of these methods in the experimental section through ablation studies and visual analysis.
2) Experimental results show that the framework exhibits superior performance on real-world distorted image datasets. Table 1 shows the performance comparison of CPL-IQA with other traditional and deep learning BIQA methods on the KonIQ-10K dataset, and the results show that CPL-IQA achieves better performance metrics. The cross-dataset experiments in Table 2 also further validate the generalization ability of CPL-IQA.
3) The proposed confidence learning approach eliminates pseudo-label outliers and enhances the generalization capability of CPL-IQA. Section 3.3.4 describes the principle of confidence learning and the relationship between confidence and pseudo-label accuracy is supported by the visual analysis in Figure 5. The ablation study in Table 3 also shows the performance enhancement of using confidence weights.
Methods And Evaluation Criteria: 1) The paper clearly states that the problem to be addressed is semi-supervised blind image quality assessment (BIQA) in real distortion scenarios since it is difficult to obtain distortion-free reference images in practical applications and the cost of labeling real distortion images is high. The CPL-IQA framework is precisely designed to utilize limited labeled data and a large number of unlabeled real distorted images. The core idea is to enhance the performance of the model in the data sparse case through confidence quantized pseudo-label learning.
2) The paper uses a series of representative real distortion image databases as benchmark datasets, including KonIQ-10K, LIVE-C, NNID, and SPAQ. These datasets are commonly used in the field of BIQA, and in particular, KonIQ-10K and SPAQ are considered to be the most important datasets containing real-world distortions. The use of these datasets can effectively evaluate the performance of models in real-world application scenarios.
Theoretical Claims: - Assertion 3.1 claims that the sequence ${P^{(t)}}$ defined by Eq. (5) converges to $P^*$ in Eq. (6) via $\tilde{G}$ obtained by Eq. (4). The proof of this statement is given in Appendix A.1.
- Assertion 3.2 claims that the limit value of the iterative process of Eq. (5), Eq. (6), can be considered as an optimal solution of the regularization framework Eq. (13) (with $\mu > 0$ in Eq. (14)). The proof of this statement is given in Appendix A.2.
Experimental Designs Or Analyses: - CPL-IQA was compared with sixteen state-of-the-art BIQA methods, both traditional and deep learning-based, on the KonIQ-10K dataset. The experimental setup uses a 1:3:1 dataset division ratio (training labeled data: training unlabeled data: test data). The results are presented in Table 1.
- The effects of the different components of CPL-IQA were analyzed experimentally. Specifically, the effects of Label Conversion, the weight of Label Confidence, and Label Optimization in Stage 2 are investigated, and the results are presented in Table 3. In addition, the effects of the base m of the score set M and the proportion of dataset partitioning on the performance are also investigated, and the results are presented in Tables 4 and 5, respectively.
- The quality of the pseudo-labels learned by Eq. (7) in each iteration of Stage 2 was analyzed by visual means. The change in performance between pseudo-labeling and model-directly predicted labeling was compared (Fig. 3), as well as the pseudo-labeling distribution versus the true MOS labeling distribution (Fig. 4).
Supplementary Material: - Part A contains proofs of Assertion 3.1 and 3.2 in the text.
- Part B contains more detailed related works.
- E.1 Results of Different Backbones: This section (including Table 7) shows the performance of CPL-IQA trained with different backbones, including ResNet18, ResNet50, ResNet101, and Vision Transformer-base. Comparison.
- E.2 Visualization of Label Confidence: This section (including Fig. 5) visualizes the confidence of the pseudo-labels learned by the label optimization module and compares it with the L1 loss between the corresponding real MOS labels.
- E.3 Cosine Similarity-based Manifold Structure: This section (containing Fig. 6 and Fig. 7) explores the impact of using the cosine similarity-based manifold structure construction method on the experimental results.
- E.4 The Impact on CPL-IQA of The Number of Nearest Neighbors k in Eq. 3: This section (containing Table 8) experimentally analyzes the impact of different values of the number of nearest neighbors k on the performance of CPL-IQA.
- E.5 Performances of CPL-IQA Trained with Labeled and Unlabeled Samples from Different Datasets: This part (containing Tables 9 and 10) и сследует scenarios where labeled and unlabeled training data come from different datasets (BID and KonIQ-10k).
- E.6 Evaluating CPL-IQA Performance with Unlabeled Training Data from Multiple Sources: This section (containing Tables 9 and 11) compares the performance of CPL-IQA when unlabeled training data come from different datasets (BID and KonIQ-10k). This section (containing Tables 9 and 11) compares the performance of CPL-IQA on the KonIQ-10k test set when the unlabeled training data comes from different sources (KonIQ-10k, SPAQ, KADID-10k).
Relation To Broader Scientific Literature: - Semi-supervised Blind Image Quality Assessment (BIQA) Framework: The core of the CPL-IQA proposal lies in its semi-supervised learning paradigm, which aims to address the problem of scarcity of labeled data in real-world scenarios. This is in line with the recent trend of research on semi-supervised and unsupervised BIQA methods. Existing deep learning (DL)-driven BIQA methods are usually “data starved”, and thus utilizing unlabeled data to improve performance has become an important research direction.CPL-IQA efficiently utilizes unlabeled real distorted images through pseudo-label learning with quantifiable confidence. This is in line with some previous semi-supervised BIQA works such as SSLIQA (Yue et al., 2022) and SS-IQA (Pan et al., 2024), which all aim to utilize unlabeled data, but CPL-IQA differs in that it uses only a single-branch network and does not rely on additional inputs or datasets, which reduces the training cost and improves applicability, whereas SSLIQA and SS-IQA are more suitable to utilize unlabeled data, whereas CPL-IQA and SS-IQA are more suitable to utilize unlabeled data. SSLIQA and SS-IQA require multi-branch networks and additional data.
- Confidence learning method for pseudo-labeling: In order to mitigate the negative impact of inaccurate pseudo-labeling on model training, CPL-IQA proposes an entropy-based confidence learning method. The uncertainty of the predicted pseudo-labels is estimated by calculating their entropy; the higher the entropy, the lower the confidence level, and a lower weight will be assigned in subsequent model training. This is consistent with the common strategy of handling noisy pseudo-labels in semi-supervised learning.
Essential References Not Discussed: The relevant work cited in the paper is relatively comprehensive and does not suffer from missing key literature.
Other Strengths And Weaknesses: Strenghts:
- The originality lies in its novel semi-supervised BIQA framework CPL-IQA.
Originality lies in its novel semi-supervised BIQA framework, CPL-IQA, which efficiently utilizes unlabeled real distorted images through confidence-quantifiable pseudo-label learning, which directly addresses the key challenge of scarcity of labeled data in the BIQA domain.
- Uniqueness of Label Transformation Strategy: The entropy minimization-based label transformation method proposed by CPL-IQA is a key innovation in transforming scalar MOS labels into vector labels. This paves the way for applying label propagation techniques, which excel in handling vector labels, to regression tasks like MOS prediction, and draws on the idea of utilizing MOS distributions for training in NIMA, but with innovative adaptations.
- Successful application of label propagation to regression tasks: traditional label propagation methods are mainly applied to classification problems. cPL-IQA successfully extends the idea of label propagation to regression tasks (i.e., image quality assessment) and proposes a corresponding implementation via Eq. (7), which is in itself of some originality and importance.
Weaknesses:
- Although Appendix C provides the algorithm pseudo-code, the key steps of the training process, such as label transformation, graph construction, label optimization, and the iterative process of model training, can be described in more detail in the main method section, which helps readers better understand the implementation details of the algorithm.
- While the paper provides proofs of label propagation convergence and equivalence to the regularization framework (in the Appendix), a more concise exposition of the intuitive understanding of these theoretical linkages in the main body might help a broader audience understand the theoretical underpinnings of the approach. For example, it could be briefly explained how the flow shape assumption plays a role in label propagation and how the regularization framework explains the process of label propagation from an optimization perspective.
Other Comments Or Suggestions: I hope that in the future the authors will make the code public and promote the community.
Questions For Authors: The entropy minimization-based label transformation method proposed in the paper is a key step in transforming scalar MOS labels into vector labels. Although it is explained in the paper that this is done to better model the MOS distribution and obtain higher confidence, is this conversion strategy still robust in the face of different datasets or large differences in the characteristics of the MOS distribution? Have the authors conducted relevant experiments to verify the generalization ability of this label transformation strategy, e.g., analyzing the quality of the transformed vector labels on datasets with significantly different MOS distributions? I would consider the method more practical if the authors could provide an analysis of the label transformation effect across datasets or comparative experiments to demonstrate the robustness of the strategy. If the label transformation is very sensitive to the data characteristics, it will limit the scope of its application in different scenarios in the real world.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thanks for your affirmation and the valuable comments that help us improve our work. The following is a careful response and explanation about the weaknesses and questions.
# For Weakness 1
We sincerely appreciate the constructive feedback. We would like to clarify that Sections 3.3.1 to 3.3.6 (pages 4–6) of the manuscript have already provided a comprehensive and step-by-step explanation of the algorithm’s implementation.
To further enhance clarity and ensure readers can better understand the implementation details, **in the final version**, we will include more illustrative examples or pseudocode snippets within the main text to complement the existing Algorithm 1 in Appendix C, which can further improve the readability and transparency of the method while maintaining the rigor of the technical content.
# For Weakness 2
Thank you for the insightful suggestion. **In the final version, we will add a concise discussion in Section 3.3.7 for a more concise exposition of the intuitive understanding of these theoretical linkages**, including the following two key insights:
**On the one hand**, the manifold assumption serves as the theoretical foundation for label propagation, positing that samples with similar features (i.e., neighboring nodes in the graph) should share similar labels. This fundamental assumption enables the label propagation process, where labels from annotated samples are effectively disseminated to unlabeled ones through the constructed nearest neighbor graph (Eq.4), thereby facilitating pseudo-label learning.
**On the other hand**, for the optimization perspective, the iterative propagation (Eq. 5) implicitly solves the regularization problem (Eqs. 13-14), where the first term enforces smoothness (labels vary slowly over the constructed nearest neighbor graph), and the second term fits the initial labels. The hyperparameter $\mu$ in Eq.14 balances the above two objectives.
# For Questions
Thank you for the valuable comments that help us improve our work. In fact, **both of the proposed model and label conversion strategy exhibit strong robustness across diverse datasets with varying MOS distributions**, which have been comprehensively demonstrated in our paper. Specifically:
**On the one hand**, we have conducted experiments on multiple datasets (KonIQ-10K, SPAQ, LIVE-C, and NNID) with significantly different MOS ranges and distribution characteristics (e.g., KonIQ-10K: [1,5], SPAQ: [0,100]). The consistent performance improvement (Tables 1–3) across these datasets demonstrates the generalization ability of our label conversion strategy.
Additionally, in Appendix E.5 and E.6, we explicitly tested scenarios where unlabeled training data came from different distortion types (authentic vs. synthetic) and sources (e.g., training with labeled dataset BID and unlabeled datasets KonIQ-10K in Appendix E.5, and training with labeled dataset KonIQ-10K and unlabeled datasets SPAQ/KADID-10K in Appendix E.6). Results in Tables 10 & 11 show that our method remains effective even when MOS distributions differ, as the entropy minimization inherently adapts to the input label range (Eq. 1 normalizes MOS to [1,100]) and preserves relative quality relationships. The confidence-weighted training (Eq. 8–9) further mitigates potential outliers from label conversion.
To further validate the robustness of our proposed strategy, we conducted additional experiments: we split KonIQ-10k into labeled training and test sets (8:2 ratio), trained the model on the labeled KonIQ-10k training set and the unlabeled LIVE-C dataset, and evaluated it on the remaining 20% KonIQ-10k test set. The results are as follows:
| training sets | 80% labeled KonIQ-10k | 80% labeled KonIQ-10k + unlabeled LIVE-C |
|-|-|-|
| PLCC | 0.879 | **0.891** |
| SRCC | 0.874 | **0.885** |
The above results show that our method is robust to different datasets.
**On the other hand**, **Although the label conversion process in Eq. (2) cannot be directly applied to predict MOS distributions** (since our method operates under the reasonable assumption that the labeled samples have sufficiently high confidence levels (Lines 190-192)), **the well-trained CPL-IQA model can robustly predict label distributions.** For example, using the model trained as described above, we randomly selected 10 samples each from KonIQ-10k and LIVE-C, and computed the average JS divergence and Wasserstein distance between the predicted MOS distributions and the variance-simulated normal distributions (approximating ground truth). The results are as follows:
| Samples | KonIQ-10k | LIVE-C |
|-|-|-|
| JS | 0.065 | 0.097 |
| W-Dist | 0.042 | 0.086 |
The results demonstrate that both the JS divergence and Wasserstein distance remain below 0.1, confirming the accuracy of the predicted MOS distributions and validating the robustness of our method across diverse datasets and MOS distributions.
**In final revision, we will further highlight the robustness.**
---
Rebuttal Comment 1.1:
Comment: I hope the author will finally make the code public and promote the community. The author's response answered my questions and I will keep my score.
---
Reply to Comment 1.1.1:
Comment: Thank you for your recognition and support of our work! We will make the code publicly available after the paper is accepted. | Summary: This work focuses on semi-supervised blind image quality assessment (BIQA). The method first converts MOS labels to vector labels via entropy minimization, then constructs nearest neighbor graph to help label optimization with confidence. The pseudo labels are then combined with ground truth to guide the model retraining. The experiments show a good performance of the proposed method.
------------------------- ## update after rebuttal ##-------------------------------------
comments after rebuttal:
The authors have partially addressed my concerns, but some confusions still exist.
(1) The performance of different conversion methods given in the rebuttal shows an evident fluctuation, which is somewhat weird. From a natural sense, the performance should not be that sensitive, especially for the N-D simulation with fixed variance, which is approximately a smoothed version of the proposed entropy maximization.
(2) The authors claims that "our approach maintains compatibility with any single-branch backbone architecture" in the rebuttal, which is not supported by current version of experiments.
Overall, I would keep my score unchanged.
Claims And Evidence: The authors claim that images with similar MOS values may correspond to a variety of score distributions (it is true) as shown in Fig.1, but in the label conversion, the variation is not considered, which looks like paradoxical.
Methods And Evaluation Criteria: It does make sense.
Theoretical Claims: Theoretically correct.
Experimental Designs Or Analyses: Almost sound but inadequate. It would be better to give more experiments. For example, how does the method perform if B_L and B_u varies. Further, the method requires at least two-step training, which puts more burden on the implementation, and the training cost is also questionable.
Supplementary Material: I have checked the supplementary.
Relation To Broader Scientific Literature: Increamental. The label conversion is not uncommon, which has been tried in various work in quality assessment.
Essential References Not Discussed: The references are almost adequate in a constrained page space.
Other Strengths And Weaknesses: [strength]
1) The work designs a semi-supervised BIQA method to address the limited labeled data.
2) The method introduces a nearest neighbor graph and label propagation strategy to construct pseudo labels.
3) The method is sound and easy to understand.
[weakness]
1) The label conversion is somewhat common in IQA/VQA. For example, Q-Align adopts a similar conversion method. It is also good to compare the proposed label conversion with existing MOS discretization methods to demonstrate the distinction and effectiveness.
2) The experimental result is not impressive comparing to current methods such as SSLIQA.
3) It would be better to give more experiments. For example, how does the method perform if B_L and B_u varies. I'm wondering if the performance is sensitive to the ratio of B_u/B_L, and which value is more reasonable.
4) The method requires at least two-step training, which puts more burden on the implementation, and the training cost is also questionable.
Other Comments Or Suggestions: I have put all my comments and questions in the above.
Questions For Authors: I have put all my comments and questions in the above.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We appreciate the valuable comments and will improve in final version.
# For Claims & Evidence
This is a misunderstanding. We clarify that:
1. **The purpose of Fig. 1 is to demonstrate the limitations of some existing semi-supervised BIQA methods that require full score distributions (Left Lines 61-68)**. As shown, images with similar MOS values can have divergent score distributions, making direct MOS-to-distribution conversion unreliable. Unfortunately, many datasets lack distribution information, limiting these semi-supervised methods' applicability.
2. While some datasets provide variance information, simulating a normal distribution solely based on variance is often inaccurate. Moreover, in real-world scenarios, variance information is frequently unavailable. These limitations restrict the broad applicability of these semi-supervised methods.
In addition, as shown in Left Line 95, it is confirmed that **models trained with vectorized distribution labels outperform those using scalar MOS labels**.
Therefore, the two conflict findings motivated us to **develop a more flexible solution that converts MOS labels into vector labels for training without requiring distribution and variance**.
3. Therefore, **the vectorized conversion process in our method does not depend on variance information**. To achieve this, we propse the entropy minimization (Eq.2) under the **high-confidence MOS assumption** (Left Lines 182-201), leading both better performance than scalar MOS training and broader applicability than distribution-dependent methods.
Thus, Fig. 1 and our method are logically consistent. **We will clarify this point more explicitly in final version to prevent any potential misunderstanding.**
# For Weakness 1
We acknowledge that label conversion is relatively common in IQA. However, **existing methods are designed specifically for either fully supervised or LLM-based BIQA**, including:
1. [1] discretizes the score range into five equal intervals, converting continuous scores into one-hot encoded rating levels.
2. [2] converts MOS labels into vector representations by assuming each MOS score follows a normal distribution, which is simulated using a predetermined fixed variance.
3. [3] extends [2] by incorporating sample-specific variance values.
We conduct experiments comparing our method with: (1) the one-hot conversion in [1], and (2) the normal distribution (N-D) simulation used in [2-3], using the same setting as Tab. 1.
| method | One-hot | N-D | Ours |
|-|-|-|-|
| PLCC | 0.803 | 0.832 | **0.873** |
| SRCC | 0.796 | 0.816 | **0.845** |
**Evidently, existing methods are unsuitable for semi-supervised BIQA scenarios due tofailing reliable pseudo-label confidence assessment**. In contrast, our method innovatively addresses this gap.
[1] Q-align. ICML'24
[2] BIQA with Probabilistic Representation. ICIP'18
[3] A fuzzy neural network for opinion score distribution prediction for BIQA. TCSVT'24
# For Weakness 2
While our method shows marginal improvement over SSLIQA in Tab 1, it demonstrates significantly superior performance in cross-dataset experiments on LIVE-C in Table 2, highlighting its exceptional generalization capability. Moreover, as detailed in Line 715, SSLIQA requires multi-branch network training, whereas our approach maintains compatibility with any single-branch backbone architecture, offering reduced parameters and simpler structure. These advantages substantiate the significance of our method.
# For Weakness 3
Thanks for your suggestion. In fact, the setting $B_L=8, B_U=56$ in Stage 2 is to match Stage 1's batch size $64$, i.e., $B_L+B_U=64$.
Moreover, the significantly larger size of $B_U$ compared to $B_L$ reflects the practical scenario where labeled samples are substantially fewer than unlabeled samples.
To investigate the impact of ratio $B_L / B_U$, under the settings of Tab. 1, we obtained the following results:
| $(B_L,B_U)$ | (4,60) | (8,56) | (16,48) |
|-|-|-|-|
| PLCC | 0.869 | 0.873 | 0.871 |
| SRCC | 0.841 | 0.845 | 0.848 |
The results show that while an excessively small
$B_L$ may degrade performance; **the model exhibits relative insensitivity** to variations in the ratio of $B_u / B_L$.
# For Weakness 4
This is a misunderstanding. The two-step training in our method **does not put a burden on the implementation**.
As stated in Sec. 3.2, our framework employs a two-stage approach:
**Stage 1** utilizes only labeled data for training, introducing no additional computational overhead;
**Stage 2** consists of two steps, with the pseudo-labeling process requiring merely 2.1% of the total training time **(see Response to Reviewer R7vR, Question 2)**.
Moreover, training on SPAQ, our method requires only 16.69 minutes (1 epoch in Stage 1 + 1 epoch in Stage 2) on a single 2080Ti GPU, versus SSLIQA's 18.31 minutes for 2 epochs. This efficiency gain stems from our single-branch design versus SSLIQA's dual-branch architecture, demonstrating our superior efficiency. | Summary: In this paper, an algorithm named CPL-IQA is proposed for semi-supervised BIQA task. The proposed algorithm leverages confidence-quantifiable pseudo label learning to utilize the unlabeled images for training. Specifically, it first converts MOS labels to vector labels via entropy minimization. Then, during training, it predicts the pseudo label of unlabeled images by NN graph construction. CPL-IQA alternates model training and label optimization. Extensive experimental results show that the proposed algorithm achieves the better performances than existing algorithms.
Claims And Evidence: Yes, the claims are supported by extensive experimental results including ablation studies and proofs in appendix.
Methods And Evaluation Criteria: Yes, the proposed algorithm technically sounds and the evaluation process seems fair.
Theoretical Claims: Yes, theoretical claims seem to be correct for me.
Experimental Designs Or Analyses: Yes, experimental designs and analysis process are valid and fair.
Supplementary Material: Yes, I reviewed the supplementary material, especially Section E and Algorithm 1 for more information.
Relation To Broader Scientific Literature: Most of algorithms for BIQA have been proposed for supervised learning scenario. However, the proposed algorithm is proposed for semi-supervised IQA to perform better on real-world distorted images, which are not well handled in existing IQA datasets for supervised learning scenarios. To this end, the proposed algorithm exploits pseudo label learning approach. This deep semi-supervised learning mechanism is well-studied but not common in BIQA field.
Essential References Not Discussed: Some recent papers are not addressed and compared. It would be better to compare with these algorithms as well.
- [1] Q-Align: Teaching LMMs for Visual Scoring via Discrete Text-Defined Levels, ICML24
- [2] Boosting Image Quality Assessment through Efficient Transformer Adaptation with Local Feature Enhancement, CVPR24
- [3] Blind image quality assessment based on geometric order learning. CVPR24
Other Strengths And Weaknesses: Please see questions for authors section for weakness.
Other Comments Or Suggestions: N/A
Questions For Authors: - Figure 4 compares the distribution of pseudo labels and that of corresponding GT labels. However, it would be good to have quantitative measurement such as MAE between pseudo and GT labels.
- Does the pseudo labeling process increase the training time significantly? How fast it is?
- I am curious whether adding more unlabeled data would improve performance. For example, if the KonIQ dataset with labels and the LIVE-C dataset without labels are trained together, how does the performance change when tested on the KonIQ dataset? Table 11 provides similar experimental results. However, it only uses 20% of KonIQ dataset as labeled samples.
- What is the limitation of the proposed algorithm? For example, it would be good to have failure cases.
Ethical Review Concerns: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for the affirmation and valuable suggestions. We have addressed each point below in detail.
# For Essential References Not Discussed
In fact, our method is not directly comparable with [1], [2], or [3], as they follow fundamentally different paradigms. Specifically:
* **Ours: A semi-supervised BIQA** method that leverages confidence-quantifiable pseudo-label learning to utilize unlabeled data.
* **[1]: A fully supervised LLM-based** approach trained on multiple joint datasets, requiring massive computational resources.
* **[2]: A fully supervised** method that adapts **large-scale pretrained models** with minimal trainable parameters.
* **[3]: A fully supervised** approach using **multiple comparison transformers** and score pivots to construct an embedding space.
Thus, our method is entirely incomparable with [1] and, strictly speaking, also with [2] and [3]. Nevertheless, for a fair comparison under as equal training conditions and model sizes as possible, we conducted experiments following the settings in Table 2 of our paper:
| | KonIQ-10K | KonIQ-10K |LIVE-C | LIVE-C | NNID | NNID |
|-|-|-|-|-|-|-|
| | PLCC | SRCC | PLCC | SRCC | PLCC |SRCC |
| [2] | 0.868 | 0.836 |0.742 | 0.685 |0.760 | 0.737 |
| [3] | 0.852 | 0.831 | 0.759 |0.703 |0.746 | 0.758 |
| **Ours** | **0.873** | **0.845** | **0.777** | **0.721** | **0.772** | **0.773** |
The results confirm our method's superiority. **In final version, we will cite [1], [2], [3] and expand** the experimental section to include more detailed discussions and comparisons with them, further validating the effectiveness of our approach.
# For Question 1
In fact, as mentioned in Left Lines 423-427, Figure 4 primarily serves to demonstrate that the distribution of predicted pseudo-labels closely aligns with that of the ground truth, thereby validating the effectiveness of our Label Optimizing module.
For quantitative evaluation, we have computed the two metrics between pseudo-labels and GT labels, including MAE (5.124) and RMSE (6.687). We will incorporate these results into final version for quantitative analysis.
# For Question 2
The pseudo-labeling process does not significantly increase training time, primarily due to two key innovations:
* While the label propagation is an iterative process (Eq. 5), we prove in Assertion 3.1 and Eq. 6 that its convergent solution can be obtained through simple matrix operations (Eqs. 6-7), eliminating the need for actual iterations.
* For constructing the nearest neighbor graph matrix (Sec 3.3.2), we employ FAISS (as stated in Right Line 303) - an efficient dense vector similarity search library developed by Facebook AI Research, which dramatically accelerates the pseudo-label learning process.
To further validate the efficiency of pseudo-label learning, we tested on a single 2080 Ti GPU using SPAQ with the same experimental setup as in Table 3 (SPAQ 1:8:1). The results show that: (1) Stage 1 training required 63.24 seconds per epoch (5 epochs in total); (2) In Stage 2, pseudo-label generation took 19.38 seconds while model training required 918.56 seconds per epoch (5 epochs in total). This demonstrates that the pseudo-labeling process accounts for only 2.1% of Stage 2 training time and 1.9% of the combined runtime for both stages.
# For Question 3
Indeed, incorporating additional unlabeled data enhances model performance, and the same holds true for labeled data. While the results in Tables 5 & 10 partially support this observation, we conducted the following supplementary experiments to further validate the conclusion:
**On the one hand**, to systematically validate this effect on KonIQ-10k, we varied the proportion of unlabeled data ($N_u$) following the settings in Table 1:
| $N_u$ | PLCC | SRCC |
|-|-|-|
| 0% | 0.850 | 0.822 |
| 30% | 0.865 | 0.831 |
| 60% | **0.873** | **0.845** |
**On the other hand**, following Table 11's settings, we only increased the labeled training data proportion ($N_l$) from KonIQ-10k while using SPAQ as unlabeled training data:
| $N_l$ | 20% | 50% | 80% |
|-|-|-|-|
| PLCC | 0.844 | 0.870 | **0.892** |
| SRCC | 0.833 | 0.858 | **0.883** |
The above results and Tables 5 & 10 can confirm that expanding labeled or unlabeled datasets can both improve model performance.
# For Question 4
The key limitation of our algorithm stems from the label conversion module based on entropy minimization, which inherently presumes high confidence in the annotated quality score distributions. In practice, annotation biases (such as significant labeling noise or uneven MOS distributions) may compromise pseudo-label reliability. For example, when adding Gaussian noise (μ=0.5, σ=0.5) to the MOS labels of training samples while keeping the Table 1 configuration, PLCC and SRCC decreased to 0.632 and 0.607 respectively.
Therefore, our future work will focus on developing noise-robust BIQA techniques. We will further add and analyze these limitations in **final version**.
---
Rebuttal Comment 1.1:
Comment: Thank you for the detailed response. I will keep my score.
---
Reply to Comment 1.1.1:
Comment: Thank you for your review. We sincerely appreciate your acknowledgement and recognition of our efforts. | null | null | null | null | null | null |
Subsets and Splits
No community queries yet
The top public SQL queries from the community will appear here once available.