Datasets:

boda
/

review_evaluation_main_1

paper_id stringlengths 10 19	venue stringclasses 14 values	focused_review stringlengths 232 10.2k	point stringlengths 64 662
gybvlVXT6z	EMNLP_2023	1. I feel that paper has insufficiant baseline. For example, CoCoOp (https://arxiv.org/abs/2203.05557) is a widely used baseline for prompt tuning research in CLIP. Moreover, it would be nice to include the natural data shift setting as in most other prompt tuning papers for CLIP. 2. It would be nice to include the hard prompt baseline in Table 1 to see the increase in performance of each method. 3. I think the performance drop seen with respect to the prompt length (Figure 4) is a major limitation of this approach. For example, this phenomenon might make it so that using just a general hard prompt of length 4 ('a photo of a') would outperform the CBBT with length 4 or even CBBT with length 1.	2. It would be nice to include the hard prompt baseline in Table 1 to see the increase in performance of each method.
NIPS_2022_670	NIPS_2022	1. Lack of numerical results. The reviewer is curious about how to apply it to some popular algorithms and their performance compared with existing DP algorithms. 2. The presentation of this paper is hard to follow for the reviewer.	1. Lack of numerical results. The reviewer is curious about how to apply it to some popular algorithms and their performance compared with existing DP algorithms.
NIPS_2020_295	NIPS_2020	1. The experimental comparisons are not enough. Some methods like MoCo and SimCLR also test the results with wider backbones like ResNet50 (2×) and ResNet50 (4×). It would be interesting to see the results of proposed InvP with these wider backbones. 2. Some methods use epochs and pretrain epochs as 200, while the reported InvP uses 800 epochs. What are the results of InvP with epochs as 200? It would be more clear after adding these results into the tables. 3. The proposed method adopts memory bank to update vi, as detailed in the beginning of Sec.3. What the results would be when adopting momentum queue and current batch of features? As the results of SimCLR and MoCo are better than InsDis, it would be nice to have those results.	1. The experimental comparisons are not enough. Some methods like MoCo and SimCLR also test the results with wider backbones like ResNet50 (2×) and ResNet50 (4×). It would be interesting to see the results of proposed InvP with these wider backbones.
NIPS_2017_351	NIPS_2017	- As I said above, I found the writing / presentation a bit jumbled at times. - The novelty here feels a bit limited. Undoubtedly the architecture is more complex than and outperforms the MCB for VQA model [7], but much of this added complexity is simply repeating the intuition of [7] at higher (trinary) and lower (unary) orders. I don't think this is a huge problem, but I would suggest the authors clarify these contributions (and any I may have missed). - I don't think the probabilistic connection is drawn very well. It doesn't seem to be made formally enough to take it as anything more than motivational which is fine, but I would suggest the authors either cement this connection more formally or adjust the language to clarify. - Figure 2 is at an odd level of abstraction where it is not detailed enough to understand the network's functionality but also not abstract enough to easily capture the outline of the approach. I would suggest trying to simplify this figure to emphasize the unary/pairwise/trinary potential generation more clearly. - Figure 3 is never referenced unless I missed it. Some things I'm curious about: - What values were learned for the linear coefficients for combining the marginalized potentials in equations (1)? It would be interesting if different modalities took advantage of different potential orders. - I find it interesting that the 2-Modalities Unary+Pairwise model under-performs MCB [7] despite such a similar architecture. I was disappointed that there was not much discussion about this in the text. Any intuition into this result? Is it related to swap to the MCB / MCT decision computation modules? - The discussion of using sequential MCB vs a single MCT layers for the decision head was quite interesting, but no results were shown. Could the authors speak a bit about what was observed?	- I don't think the probabilistic connection is drawn very well. It doesn't seem to be made formally enough to take it as anything more than motivational which is fine, but I would suggest the authors either cement this connection more formally or adjust the language to clarify.
NIPS_2016_9	NIPS_2016	Weakness: The authors do not provide any theoretical understanding of the algorithm. The paper seems to be well written. The proposed algorithm seems to work very all on the experimental setup, using both synthetic and real-world data. The contributions of the papers are enough to be considered for a poster presentation. The following concerns if addressed properly could raise to the level of oral presentation: 1. The paper does not provide an analysis on what type of data the algorithm work best and on what type of data the algorithm may not work well. 2. The first claimed contribution of the paper is that unlike other existing algorithms, the proposed algorithm does not take as many points or does not need apriori knowledge about dimensions of subspaces. It would have been better if there were some empirical justification about this. 3. It would be good to show some empirical evidence that the proposed algorithm works better for Column Subset Selection problem too, as claimed in the third contribution of the paper.	3. It would be good to show some empirical evidence that the proposed algorithm works better for Column Subset Selection problem too, as claimed in the third contribution of the paper.
NIPS_2020_916	NIPS_2020	My major complaints can be characterized into the following bullet points: - Robustness is argued only indirectly by way of Lipschitz constants. While the authors present a novel formulation (i.e., differing from the standard low-lipschitz=>robustness claims in the ML literature) of how controlling the lipschitz function of the classifier controls sensitivity to adversarial perturbations, this setting differs slightly from standard classification settings. In the standard classification setting, where labels are 1-hot vectors in R^dim(Y), a classifier typically returns as a label the argmax of the vector-valued function. Robustness then is usually considered as whether the argmax returns the right label, rather than a strictly-convex loss applied to the one-hot-label: this work incorporates 'confidence' into the robustness evaluation. - The applicability of the robust training scheme seems unlikely to scale to practical datasets, particularly those supported on high-dimensional domains. It seems like the accuracy would scale unfavorably unless the size of V scales exponentially with the dimension. - The example data distribution could be better chosen. As it stands, a classifier with (true) loss would require a Lipschitz constant that tends to infinity. A more standard/practical dataset would admit a perfect classifier that has a valid Lipschitz constant.	- The applicability of the robust training scheme seems unlikely to scale to practical datasets, particularly those supported on high-dimensional domains. It seems like the accuracy would scale unfavorably unless the size of V scales exponentially with the dimension.
VnMfQuDSgG	EMNLP_2023	- The paper is entirely statistical. For a task like this, it is important to show the linguistic nuance that is captured by the metrics. - The choice of datasets: is 4 years sufficient period to study style shifts? what kind of style shifts happen in such a time? Without these answers, it is hard to appreciate what the model is capturing.	- The choice of datasets: is 4 years sufficient period to study style shifts? what kind of style shifts happen in such a time? Without these answers, it is hard to appreciate what the model is capturing.
NIPS_2021_442	NIPS_2021	of the paper: Strengths: 1) To the best of my knowledge, the problem investigated in the paper is original in the sense that top-m identification has not been studied in the misspecified setting. 2) The paper provides some interesting results: i) (Section 3.1) Knowing the level of misspecification ε is a key ingredient, as not knowing the same would yield sample complexity bounds which are no better than the bound obtainable from unstructured ( ε = ∞ ) stochastic bandits. ii) A single no-regret learner is used for the sampling strategy instead of assigning a learner for each of the (N choose k) answers, thus exponentially reducing the number of online learners. iii) The proposed decision rules are shown to match the prescribed lower bound asymptotically. 3) Sufficient experimental validation is provided to showcase the empirical performance of the prescribed decision rules. Weaknesses: Some of the explanations provided by the authors are a bit unclear to me. Specifically, I have the following questions: 1) IMO, a better explanation of investigating top-m identification in this setting is required. Specifically, in this setting, we could readily convert the problem to the general top-m identification by appending the constant 1 to the features (converting them into d + 1 dimensional features) and trying to estimate the misspecifications η in the higher dimensional space. Why is that disadvantageous? Can the authors explain how the lower bound in Theorem 1 explicitly captures the effect of the upper bound on misspecification ε ? The relationship could be shown, for instance, by providing an example of a particular bandit environment (say, Gaussian bandits) ala [Kaufmann2016]. Sample complexity: Theorem 2 states the sample complexity in a very abstract way; it provides an equation which needs to be solved in order to get an explicit expression of the sample complexity. In order to make a comparison, the authors then mention that the unstructured confidence interval β t , δ u n s is approximately log ⁡ ( 1 δ ) in the limit of δ → 0 , which is then used to argue that the sample complexity of MISLID is asymptotically optimal. However, β t , δ u n s also depends on t . In fact, my understanding is that as δ goes to 0 , the stopping time t goes to infinity, where it is not clear as to what value the overall expression β t , δ u n s converges. Overall, I feel that the authors need to explicate the sample complexity a bit more. My suggestions are: can the authors find a solution to equation (5) (or at least an upper bound on the solution for different regimes of ε )? Using such an upper bound, even if the authors could give an explicit expression of the (asymptotic) sample complexity and show how it compares to the lower bound, it would be a great contribution. Looking at Figure 1A (the second figure from the left, for the case of ε = 2 ), it looks like LinGapE outperforms MISLID in terms of average sample complexity. Please correct me if I’m missing something, but if what I understand is correct, then why use MISLID and not LinGapE? Probable typo: Line 211: Should it be θ instead of θ t for the self-normalized concentration? The authors have explained the limitations of the investigation in Section 6.	2) The paper provides some interesting results: i) (Section 3.1) Knowing the level of misspecification ε is a key ingredient, as not knowing the same would yield sample complexity bounds which are no better than the bound obtainable from unstructured ( ε = ∞ ) stochastic bandits. ii) A single no-regret learner is used for the sampling strategy instead of assigning a learner for each of the (N choose k) answers, thus exponentially reducing the number of online learners. iii) The proposed decision rules are shown to match the prescribed lower bound asymptotically.
ICLR_2023_977	ICLR_2023	the evaluation section has 2 experiments, but only 2 very insightful detailed examples. The paper can use a few more examples to illustrate more differences of the output sequences. This would allow the reader to internalize how the non-monotonicity in a deeper way. Questions: In details, how does the decoding algorithm actually avoid repetitions? In other way, how does other models actually degrade validation perplexity using their decoding algorithm? Typos, Grammar, etc.: Page 7, section 4.2, par. 2: the callout to table 5 should go to table 3, instead. Page 7, section 5, last par.: figure 6 callout is not directing properly	2: the callout to table 5 should go to table 3, instead. Page 7, section 5, last par.: figure 6 callout is not directing properly
NIPS_2020_1371	NIPS_2020	When reading the paper, I've got the impression that the paper is not finished with couple of key experiments missing. Some parts of the paper lack motivation. Terminology is sometimes unclear and ambiguous. 1. Terminology. The paper uses terms "animation", "generative", "interpolation". See contribution 1 in L40-42. While the paper reported some interpolation experiments, I haven't found any animation or generation experiments. It seems the authors equate interpolation and animation (Section 4.2) which is not correct. I consider animation is a physically plausible motion. Like a person opens a mouth, car moves, while interpolation is just warping one image into the other. Fig 7 shows exactly this with the end states being plausible states of the system. The authors should fix the ambiguity to avoid misunderstanding. The authors also don't report any generation results. Can I sample a random shape from the learnt distribution? If not the I don't think it's correct to say the model is generative. 2. Motivation. It's not clear why the problem is important from practical standpoint? Why one would like to interpolate between two icons? Motivation behind animation is more clear, but in my opinion, the paper doesn't do animation. I believe from a practical standpoint letting the user to input text and be able to generate an icon would also be important. Again, I have hard time understanding why shape autoencoding and interpolation is interesting. 3. Experiments. Probably the biggest concern with the paper is with the experiments. The paper reports only self comparisons. The paper also doesn't explain why this is so, which adds to the poor motivation problem. In a generative setting comparisons with SketchRNN could be performed.	3. Experiments. Probably the biggest concern with the paper is with the experiments. The paper reports only self comparisons. The paper also doesn't explain why this is so, which adds to the poor motivation problem. In a generative setting comparisons with SketchRNN could be performed.
ICLR_2022_1794	ICLR_2022	1 Medical imaging are often obtained in 3D volumes, not only limited to 2D images. So experiments should include the 3D volume data as well for the general community, rather than all on 2D images. And the lesion detection is another important task for the medical community, which has not been studied in this work. 2 More analysis and comments are recommended on the performance trending of increasing the number of parameters for ViT (DeiT) in the Figure 3. I disagree with authors' viewpoint that "Both CNNs and ViTs seem to benefit similarly from increased model capacity". In the Figure 3, the DeiT-B models does not outperform DeiT-T in APTOS2019, and it does not outperform DeiT-S on APTOS2019, ISIC2019 and CheXpert (0.1% won't be significant). However, CNNs can give more almost consistent model improvements as the capacity goes up except on the ISIC2019. 3 On the segmentation mask involved with cancer on CSAW-S, the segmentation results of DEEPLAB3-DEIT-S cannot be concluded as better than DEEPLAB3-RESNET50. The implication that ViTs outperform CNNs in this segmentation task cannot be validly drawn from an 0.2% difference with larger variance. Questions: 1 For the grid search of learning rate, is it done on the validation set? Minor problems: 1 The n number for Camelyon dataset in Table 1 is not consistent with the descriptions in the text in Page 4.	2 More analysis and comments are recommended on the performance trending of increasing the number of parameters for ViT (DeiT) in the Figure 3. I disagree with authors' viewpoint that "Both CNNs and ViTs seem to benefit similarly from increased model capacity". In the Figure 3, the DeiT-B models does not outperform DeiT-T in APTOS2019, and it does not outperform DeiT-S on APTOS2019, ISIC2019 and CheXpert (0.1% won't be significant). However, CNNs can give more almost consistent model improvements as the capacity goes up except on the ISIC2019.
ICLR_2022_3352	ICLR_2022	+ The problem studied in this paper is definitely important in many real-world applications, such as robotics decision-making and autonomous driving. Discovering the underlying causation is important for agents to make reasonable decisions, especially in dynamic environments. + The method proposed in this paper is interesting and technically correct. Intuitively, using GRU to extract sequential information helps capture the changes of causal graphs. - The main idea of causal discovery by sampling intervention set and causal graphs for masking is similar to DCDI [1]. This paper is more like using DCDI in dynamic environments, which may limit the novelty of this paper. - The paper is not difficult to follow, but there are several places that are may cause confusion. (listed in point 3). - The contribution of this paper is not fully supported by experiments. Main Questions (1) During the inference stage, why use samples instead of directly taking the argmax of Bernoulli distribution? How many samples are required? Will this sampling cause scalability problems? (2) In the experiment part, the authors only compare with one method (V-CDN). Is it possible to compare DYNOTEARS with the proposed method? (3) The authors mention that there is no ground truth to evaluate the causal discovery task. I agree with this opinion since the real world does not provide us causal graphs. However, the first experiment is conducted on a synthetic dataset, where I believe it is able to obtain the causation by checking collision conditions. In other words, I am not convinced only by the prediction results. Could the author provide the learned causal graphs and intervention sets and compare them with ground truth even on a simple synthetic dataset? Clarification questions (1) It seems the citation of NOTEARS [2] is wrongly used for DYNOTEARS [3]. This citation is important since DYNOTEARS is one of the motivations of this paper. (2) ICM part in Figure 3 is not clear. How is the Intervention set I is used? If I understand correctly, function f is a prediction model conditioned on history frames. (3) The term “Bern” in equation (3) is not defined. I assume it is the Bernoulli distribution. Then what does the symbol B e r n ( α t , β t ) mean? (4) According to equation (7), each node j has its own parameters ϕ j t and ψ j t . Could the authors explain why the parameters are related to time? (5) In equation (16), the authors mention the term “ secondary optimization”. I can’t find any reference for it. Could the author provide more information? Minor things: (1) In the caption of Figure 2, the authors say “For nonstationary causal models, (c)….”. But in figure (c) belongs to stationary methods. [1] Brouillard P, Lachapelle S, Lacoste A, et al. Differentiable causal discovery from interventional data[J]. arXiv preprint arXiv:2007.01754, 2020. [2] Zheng X, Aragam B, Ravikumar P, et al. Dags with no tears: Continuous optimization for structure learning[J]. arXiv preprint arXiv:1803.01422, 2018. [3] Pamfil R, Sriwattanaworachai N, Desai S, et al. Dynotears: Structure learning from time-series data[C]//International Conference on Artificial Intelligence and Statistics. PMLR, 2020: 1595-1605.	- The paper is not difficult to follow, but there are several places that are may cause confusion. (listed in point 3).
ICLR_2021_1948	ICLR_2021	a. Anonymisation Failure in References i. A reference uncited in the manuscript body contains a non-anonymised set of author names to a paper with the same title as the system presented in this paper. This was not detected during initial review. "Shuby Deshpande and Jeff Schneider. Vizarel: A System to Help Better Understand RL Agents.arXiv:2007.05577." b. Citations i. There is egregiously missing information in almost all citations. This is quite obvious in all the missing dates in the manuscript text. c. Clarity i. There are a few unclear or misleadingly worded statements made as below: 1) "However, there is no corresponding set of tools for the reinforcement learning setting." - This is false. See references below (also some in the submitted paper). 2) "stronger feedback loop between the researcher and the agent" - This is at least confusing. In any learning setting, there is a strong interaction loop between experimentation by the researcher and resulting outcomes for the trained model. 3) "To the best of our knowledge, there do not exist visualization systems built for interpretable reinforcement learning that effectively address the broader goals we have identified" - It isn't clear what these broader goals are that have been identified. Therefore it isn't possible to evaluate this claim. 4) "For multi-dimensional action spaces, the viewport could be repurposed to display the variance of the action distribution, plot different projections of the action distribution, or use more sophisticated techniques (Huber)." - It would be clearer to actually state what the sophisticated techniques from Huber are here. ii. The framework could be clearer that it applies most directly as described on single agent RL. The same approach could be used with multi-agent RL but the observation state and visualisations around that get more confusing when there are multiple potentially different sets of observations. Is this not the case, please clarify? d. Experimental rigour i. The paper does include 3 extremely brief examples of how the tool might be used. However, it does not include any experiments to suggest that this tool would actually improve the debugging process for training RL in a real user study. Not every paper requires a user study, however, the contributions proposed by this particular manuscript require validation at some level from actual RL users (even a case study with some feedback from users would address this to some extent). e. Novelty in Related Work i. The manuscript contains references to several relevant publications that can be compared to the current work. However, the paper is also missing references to many related and relevant works in the space of debugging reinforcement learning using visualisations, especially with an eye towards explainable reinforcement learning. See a sampling below. 1) @inproceedings{ Rupprecht2020Finding, title={Finding and Visualizing Weaknesses of Deep Reinforcement Learning Agents}, author={Christian Rupprecht and Cyril Ibrahim and Christopher J. Pal}, booktitle={International Conference on Learning Representations}, year={2020}, url={https://openreview.net/forum?id=rylvYaNYDH} } 2) @inproceedings{ Atrey2020Exploratory, title={Exploratory Not Explanatory: Counterfactual Analysis of Saliency Maps for Deep Reinforcement Learning}, author={Akanksha Atrey and Kaleigh Clary and David Jensen}, booktitle={International Conference on Learning Representations}, year={2020}, url={https://openreview.net/forum?id=rkl3m1BFDB} } 3) @inproceedings{ Puri2020Explain, title={Explain Your Move: Understanding Agent Actions Using Specific and Relevant Feature Attribution}, author={Nikaash Puri and Sukriti Verma and Piyush Gupta and Dhruv Kayastha and Shripad Deshmukh and Balaji Krishnamurthy and Sameer Singh}, booktitle={International Conference on Learning Representations}, year={2020}, url={https://openreview.net/forum?id=SJgzLkBKPB} } 4) @article{reddy2019learning, title={Learning human objectives by evaluating hypothetical behavior}, author={Reddy, Siddharth and Dragan, Anca D and Levine, Sergey and Legg, Shane and Leike, Jan}, journal={arXiv preprint arXiv:1912.05652}, year={2019} } 5) @inproceedings{mcgregor2015facilitating, title={Facilitating testing and debugging of Markov Decision Processes with interactive visualization}, author={McGregor, Sean and Buckingham, Hailey and Dietterich, Thomas G and Houtman, Rachel and Montgomery, Claire and Metoyer, Ronald}, booktitle={2015 IEEE Symposium on Visual Languages and Human-Centric Computing (VL/HCC)}, pages={53--61}, year={2015}, organization={IEEE} } 6) @article{puiutta2020explainable, title={Explainable Reinforcement Learning: A Survey}, author={Puiutta, Erika and Veith, Eric}, journal={arXiv preprint arXiv:2005.06247}, year={2020} } 7) @book{calvaresi2019explainable, title={Explainable, Transparent Autonomous Agents and Multi-Agent Systems: First International Workshop, EXTRAAMAS 2019, Montreal, QC, Canada, May 13--14, 2019, Revised Selected Papers}, author={Calvaresi, Davide and Najjar, Amro and Schumacher, Michael and Fr{\"a}mling, Kary}, volume={11763}, year={2019}, publisher={Springer Nature} } 8) @inproceedings{juozapaitis2019explainable, title={Explainable reinforcement learning via reward decomposition}, author={Juozapaitis, Zoe and Koul, Anurag and Fern, Alan and Erwig, Martin and Doshi-Velez, Finale}, booktitle={IJCAI/ECAI Workshop on Explainable Artificial Intelligence}, year={2019} } 9) @misc{sundararajan2020shapley, title={The many Shapley values for model explanation}, author={Mukund Sundararajan and Amir Najmi}, year={2020}, eprint={1908.08474}, archivePrefix={arXiv}, primaryClass={cs.AI} } 10) @misc{madumal2020distal, title={Distal Explanations for Model-free Explainable Reinforcement Learning}, author={Prashan Madumal and Tim Miller and Liz Sonenberg and Frank Vetere}, year={2020}, eprint={2001.10284}, archivePrefix={arXiv}, primaryClass={cs.AI} } 11) @article{Sequeira_2020, title={Interestingness elements for explainable reinforcement learning: Understanding agents’ capabilities and limitations}, volume={288}, ISSN={0004-3702}, url={http://dx.doi.org/10.1016/j.artint.2020.103367}, DOI={10.1016/j.artint.2020.103367}, journal={Artificial Intelligence}, publisher={Elsevier BV}, author={Sequeira, Pedro and Gervasio, Melinda}, year={2020}, month={Nov}, pages={103367} } 12) @article{Fukuchi_2017, title={Autonomous Self-Explanation of Behavior for Interactive Reinforcement Learning Agents}, ISBN={9781450351133}, url={http://dx.doi.org/10.1145/3125739.3125746}, DOI={10.1145/3125739.3125746}, journal={Proceedings of the 5th International Conference on Human Agent Interaction}, publisher={ACM}, author={Fukuchi, Yosuke and Osawa, Masahiko and Yamakawa, Hiroshi and Imai, Michita}, year={2017}, month={Oct} } 4. Recommendation a. I recommend this paper for rejection as the degree of change needed to validate the contribution through a user study or other validation is likely not feasible in the time and space needed. However, the contribution is potentially valuable to RL, so with the inclusion of this missing evaluation and additions to related work/contextualisation of the contribution, I would consider increasing my score and changing my recommendation. 5. Minor Comments/Suggestions a. It is recommended to use the TensorFlow whitepaper citation for TensorBoard (https://arxiv.org/abs/1603.04467). This is the official response (https://github.com/tensorflow/tensorboard/issues/3437).	1) "However, there is no corresponding set of tools for the reinforcement learning setting." - This is false. See references below (also some in the submitted paper).
NIPS_2016_370	NIPS_2016	, and while the scores above are my best attempt to turn these strengths and weaknesses into numerical judgments, I think it's important to consider the strengths and weaknesses holistically when making a judgment. Below are my impressions. First, the strengths: 1. The idea to perform improper unsupervised learning is an interesting one, which allows one to circumvent certain NP hardness results in the unsupervised learning setting. 2. The results, while mostly based on "standard" techniques, are not obvious a priori, and require a fair degree of technical competency (i.e., the techniques are really only "standard" to a small group of experts). 3. The paper is locally well-written and the technical presentation flows easily: I can understand the statement of each theorem without having to wade through too much notation, and the authors do a good job of conveying the gist of the proofs. Second, the weaknesses: 1. The biggest weakness is some issues with the framework itself. In particular: 1a. It is not obvious that "k-bit representation" is the right notion for unsupervised learning. Presumably the idea is that if one can compress to a small number of bits, one will obtain good generalization performance from a small number of labeled samples. But in reality, this will also depend on the chosen model class used to fit this hypothetical supervised data: perhaps there is one representation which admits a linear model, while another requires a quadratic model or a kernel. It seems more desirable to have a linear model on 10,000 bits than a quadratic model on 1,000 bits. This is an issue that I felt was brushed under the rug in an otherwise clear paper. 1b. It also seems a bit clunky to work with bits (in fact, the paper basically immediately passes from bits to real numbers). 1c. Somewhat related to 1a, it wasn't obvious to me if the representations implicit in the main results would actually lead to good performance if the resulting features were then used in supervised learning. I generally felt that it would be better if the framework was (a) more tied to eventual supervised learning performance, and (b) a bit simpler to work with. 2. I thought that the introduction was a bit grandiose in comparing itself to PAC learning. 3. The main point (that improper unsupervised learning can overcome NP hardness barriers) didn't come through until I had read the paper in detail. When deciding what papers to accept into a conference, there are inevitably cases where one must decide between conservatively accepting only papers that are clearly solid, and taking risks to allow more original but higher-variance papers to reach a wide audience. I generally favor the latter approach, I think this paper is a case in point: it's hard for me to tell whether the ideas in this paper will ultimately lead to a fruitful line of work, or turn out to be flawed in the end. So the variance is high, but the expected value is high as well, and I generally get the sense from reading the paper that the authors know what they are doing. So I think it should be accepted. Some questions for the authors (please answer in rebuttal): -Do the representations implicit in Theorems 3.2 and Theorem 4.1 yield features that would be appropriate for subsequent supervised learning of a linear model (i.e., would linear combinations of the features yield a reasonable model family)? -How easy is it to handle e.g. manifolds defined by cubic constraints with the spectral decoding approach?	2. The results, while mostly based on "standard" techniques, are not obvious a priori, and require a fair degree of technical competency (i.e., the techniques are really only "standard" to a small group of experts).
ARR_2022_223_review	ARR_2022	The majority of the weaknesses in the paper seem to stem from confusion and inconsistencies between some of the prose and the results. 1. Figure 2, as it is, isn't totally convincing there is a gap in convergence times. The x-axis of the graph is time, when it would have been more convincing using steps. Without an efficient, factored attention for prompting implementation a la [He et al. (2022)](https://arxiv.org/abs/2110.04366) prompt tuning can cause slow downs from the increased sequence length. With time on the x-axis it is unclear if prompt tuning requires more steps or if each step just takes more time. Similarly, this work uses $0.001$ for the learning rate. This is a lot smaller than the suggested learning rate of $0.3$ in [Lester et al (2021)](https://aclanthology.org/2021.emnlp-main.243/), it would have been better to see if a larger learning rate would have closed this gap. Finally, this gap with finetuning is used as a motivating examples but the faster convergence times of things like their initialization strategy is never compared to finetuning. 2. Confusion around output space and label extraction. In the prose (and Appendix A.3) it is stated that labels are based on the predictions at `[MASK]` for RoBERTa Models and the T5 Decoder for generation. Scores in the paper, for example the random vector baseline for T5 in Table 2 suggest that the output space is restricted to only valid labels as a random vector of T5 generally produces nothing. Using this rank classification approach should be stated plainly as direct prompt reuse is unlikely to work for actual T5 generation. 3. The `laptop` and `restaurant` datasets don't seem to match their descriptions in the appendix. It is stated that they have 3 labels but their random vector performance is about 20% suggesting they actually have 5 labels? 4. Some relative performance numbers in Figure 3 are really surprising, things like $1$ for `MRPC` to `resturant` transfer seem far too low, `laptop` source to `laptop` target on T5 doesn't get 100, Are there errors in the figure or is where something going wrong with the datasets or implementation? 5. Prompt similarities are evaluated based on correlation with zero-shot performance for direct prompt transfer. Given that very few direct prompt transfers yield gain in performance, what is actually important when it comes to prompt transferability is how well the prompt works as an initialization and does that boost performance. Prompt similarity tracking zero-shot performance will be a good metric if that is in turn correlated with transfer performance. The numbers from Table 1 generally support that this as a good proxy method as 76% of datasets show small improvements when using the best zero-shot performing prompt as initialization when using T5 (although only 54% of datasets show improvement for RoBERTa). However Table 2 suggests that this zero-shot performance isn't well correlated with transfer performance. In only 38% of datasets does the best zero-shot prompt match the best prompt to use for transfer (And of these 5 successes 3 of them are based on using MNLI, a dataset well known for giving strong transfer results [(Phang et al., 2017)](https://arxiv.org/abs/1811.01088)). Given that zero-shot performance doesn't seem to be correlated with transfer performance (and that zero-shot transfer is relatively easy to compute) it seems like _ON_'s strong correlation would not be very useful in practice. 6. While recent enough that it is totally fair to call [Vu et al., (2021)](https://arxiv.org/abs/2110.07904) concurrent work, given the similarity of several approaches there should be a deeper discussion comparing the two works. Both the prompt transfer via initialization and the prompt similarity as a proxy for transferability are present in that work. Given the numerous differences (Vu et al transfer mostly focuses on large mixtures transferring to tasks and performance while this work focuses on task to task transfer with an eye towards speed. _ ON_ as an improvement over the Cosine similarities which are also present in Vu et al) it seems this section should be expanded considering how much overlap there is. 7. The majority of Model transfer results seem difficult to leverage. Compared to cross-task transfer, the gains are minimal and the convergence speed ups are small. Coupled with the extra time it takes to train the projector for _Task Tuning_ (which back propagation with the target model) it seems hard to imagine situations where this method is worth doing (that knowledge is useful). Similarly, the claim on line 109 that model transfer can significantly accelerate prompt tuning seems lie an over-claim. 8. Line 118 claims `embedding distances of prompts do not well indicate prompt transferability` but Table 4 shows that C$_{\text{average}}$ is not far behind _ON_. This claim seems over-reaching and should instead be something like "our novel method of measuring prompt similarity via model activations is better correlated with transfer performance than embedding distance based measures" 1. Line 038: They state that GPT-3 showed extremely large LM can give remarkable improvements. I think it would be correct to have one of their later citations on continually developed LM as the one that showed that. GPT-3 mostly showed promise for Few-Shot evaluation, not that it get really good performance on downstream tasks. 2. Line 148: I think it would make sense to make a distinction between hard prompt work updates the frozen model (Schick and Schütez, etc) from ones that don't. 3. Line 153: I think it makes sense to include [_Learning How to Ask: Querying LMs with Mixtures of Soft Prompts_ (Qin and Eisner, 2021)](https://aclanthology.org/2021.naacl-main.410.pdf) in the citation list for work on soft prompts. 4. Figure 3: The coloring of the PI group makes the text very hard to read in Black and White. 5. Table 1: Including the fact that the prompt used for initialization is the one that performed best in direct transfer in the caption as well as the prose would make the table more self contained. 6. Table 2: Mentioning that the prompt used as cross model initialization is from _Task Tuning_ in the caption would make the table more self contained. 7. Line 512: It is mentioned that _ON_ has a drop when applied to T$5_{\text{XXL}}$ and it is suggested this has to do with redundancy as the models grow. I think this section could be improved by highlighting that the Cosine based metrics have a similar drop (suggesting this is a fact of the model rather than the fault of the _ON_ method). Similarly, Figure 4 shows the dropping correlation as the model grows. Pointing out the that the _ON_ correlation for RoBERTA$_{\text{large}}$ would fit the tend of correlation vs model size (being between T5 Base and T5 Large) also strengths the argument but showing it isn't an artifact of _ON_ working poorly on encoder-decoder models. I think this section should also be reordered to show that this drop is correlated with model size. Then the section can be ended with hypothesizing and limited exploration of model redundancy. 8. Figure 6. It would have been interesting to see how the unified label space worked for T5 rather than RoBERTAa as the generative nature of T5's decoding is probably more vulnerable to issue stemming from different labels. 9. _ ON_ could be pushed farther. An advantage of prompt tuning is that the prompt is transformed by the models attention based on the value of the prompt. Without having an input to the model, the prompts activations are most likely dissimilar to the kind of activations one would expect when actually using the prompt. 10. Line 074: This sentence is confusing. Perhaps something like "Thus" over "Hence only"? 11. Line 165: Remove "remedy,"	2. Line 148: I think it would make sense to make a distinction between hard prompt work updates the frozen model (Schick and Schütez, etc) from ones that don't.
CEPkRTOlut	EMNLP_2023	No ethics section, but there are ethical issues that deserve discussion (see the ethics section). Also a few, mostly minor points: - When the corpus was created, participants were told to speak in such a way to make the intent of the speech unambiguous. This may lead to over-emphasis compared with natural speech. There was no mention of any evaluation of the data to avoid this. - The corpus was created with only ambiguous sentences, and the non-ambiguous content was taken from another source. There is a chance that different recording qualities between news (LSCVR) and crowdsourced data could artificially raise the ability of the model to distinguish between ambiguous (tag 1 or 2) and non-ambiguous (tag 0) sentences. - The amount of data used to train the text disambiguation model was significantly lower than the data used for training the end-to-end system. Given that the difference between the two proposed systems is only a few percentage points, it brings into question the conclusion that the direct model is clearly the better of the two (but they still are both demonstrably superior to the baseline). - It would be hard to reproduce the fine tuning of the IndoBART model without a little more information. Was it fine-tuned for a certain number of steps, for example?	- The amount of data used to train the text disambiguation model was significantly lower than the data used for training the end-to-end system. Given that the difference between the two proposed systems is only a few percentage points, it brings into question the conclusion that the direct model is clearly the better of the two (but they still are both demonstrably superior to the baseline).
pxclAomHat	ICLR_2025	1. The paper does not explicitly link the quality of the optimization landscape to convergence speed or generalization performance, which undermines its stated goal of theoretically explaining the performance of LoRA and GaLore. Many claims also lack this connection (e.g., lines 60-61, 289-291, and 301-304), making them appear weaker and less convincing. 2. The theoretical results in this paper are derived from analyses of MLPs, whereas LLMs, with their attention mechanisms, layer normalization, etc., are more complex. Since there is a gap between MLPs and LLMs, and the paper does not directly validate its theoretical results on LLMs (instead of relying only on the convergence and performance outcomes), the theoretical conclusions are less convincing. 3. The paper does not clearly motivate GaRare; it lacks evidence or justification for GaRare's advantages over GaLore based on theoretical analysis. Additionally, a more detailed algorithmic presentation is needed, particularly to clarify the process of recovering updated parameters from projected gradients, which would enhance understanding.	3. The paper does not clearly motivate GaRare; it lacks evidence or justification for GaRare's advantages over GaLore based on theoretical analysis. Additionally, a more detailed algorithmic presentation is needed, particularly to clarify the process of recovering updated parameters from projected gradients, which would enhance understanding.
NIPS_2017_356	NIPS_2017	] My major concerns about this paper is the experiment on visual dialog dataset. The authors only show the proposed model's performance on discriminative setting without any ablation studies. There is not enough experiment result to show how the proposed model works on the real dataset. If possible, please answer my following questions in the rebuttal. 1: The authors claim their model can achieve superior performance having significantly fewer parameters than baseline [1]. This is mainly achieved by using a much smaller word embedding size and LSTM size. To me, it could be authors in [1] just test model with standard parameter setting. To backup this claim, is there any improvements when the proposed model use larger word embedding, and LSTM parameters? 2: There are two test settings in visual dialog, while the Table 1 only shows the result on discriminative setting. It's known that discriminative setting can not apply on real applications, what is the result on generative setting? 3: To further backup the proposed visual reference resolution model works in real dataset, please also conduct ablation study on visDial dataset. One experiment I'm really interested is the performance of ATT(+H) (in figure 4 left). What is the result if the proposed model didn't consider the relevant attention retrieval from the attention memory.	3: To further backup the proposed visual reference resolution model works in real dataset, please also conduct ablation study on visDial dataset. One experiment I'm really interested is the performance of ATT(+H) (in figure 4 left). What is the result if the proposed model didn't consider the relevant attention retrieval from the attention memory.
NIPS_2019_220	NIPS_2019	1. Unclear experimental methodology. The paper states that 300W-LP is used to train the model, but later it is claimed same procedure is used as was used for baselines. Most baselines do not use 300W-LP dataset in their training. Is 300W-LP used in all experiments or just some? If it is used in all this would provide an unfair advantage to the proposed method. 2. Missing link to similar work on Continuous Conditional Random Fields [Ristovski 2013] and Continuous Conditional Neural Fields [Baltrusaitis 2014] that has a similar structure of the CRF and ability to perform exact inference. 3. What is Gaussian NLL? This seems to come out of nowhere and is not mentioned anywhere in the paper, besides the ablation study? Trivia: Consider replacing "difference mean" with "expected difference" between two landmarks (I believe it would be clearer)	2. Missing link to similar work on Continuous Conditional Random Fields [Ristovski 2013] and Continuous Conditional Neural Fields [Baltrusaitis 2014] that has a similar structure of the CRF and ability to perform exact inference.
ICLR_2022_2470	ICLR_2022	Weakness: The idea is a bit simple -- which in of itself is not a true weakness. ResNet as an idea is not complicated at all. I find it disheartening that the paper did not really tell readers how to construct a white paper in section 3 (if I simply missed it, please let me know). However, the code in the supplementary materials helped. White paper is constructed as follow: white_paper_gen = torch.ones(args.train_batch, 3, 32, 32) It offers another way of constructing white paper, which is white_paper_gen = 255 * np.ones((32, 32, 3), dtype=np.uint8) white_paper_gen = Image.fromarray(white_paper_gen) white_paper_gen = transforms.ToTensor()(white_paper_gen) white_paper_gen = transforms.Normalize((0.4914, 0.4822, 0.4465), (0.2023, 0.1994, 0.2010))(white_paper_gen) The code states that either version works similarly and does not affect the performance. I wonder if there are other white papers as well, for example np.zeros((32, 32, 3)) -- most CNN models add explicit bias terms in their CNN kernel. Would a different white paper reveal different bias in the model? I don't think the paper answers this question or discusses it. 2. Section 4 "Is white paper training harmful to the model?" -- the evidences do not seem to support the claim. The evidences are 1). Only projection head (CNN layers) are affected but not classification head (FCN layer); 2). Parameter changes are small. None of these constitute as a direct support that the training is not "harmful" to the model. This point can simply be illustrated by the experimental results 3. Section 5.1 and 5.2 mainly build the narrative that WPA improves the test performance (generalization performance), but they are indirect evidence to support that WPA does in fact alleviate shortcut learning. Only Section 5.3 and Table 6 directly show whether WPA does what it's designed to do. A suggestion is to discuss the result of Section 5.3 more. 4. It would be interesting to try to explain why WPA works -- with np.ones input, what is the model predicting? Would any input serve as white paper? Figure 2 seems to suggest that Gaussian noise input does not work as well as WPA. Why? Authors spend lot of time showing WPA improves the test performance of the original model, but fails to provide useful insights on how WPA works -- this is particularly important because it can spark future research directions.	4. It would be interesting to try to explain why WPA works -- with np.ones input, what is the model predicting? Would any input serve as white paper? Figure 2 seems to suggest that Gaussian noise input does not work as well as WPA. Why? Authors spend lot of time showing WPA improves the test performance of the original model, but fails to provide useful insights on how WPA works -- this is particularly important because it can spark future research directions.
ICLR_2023_1979	ICLR_2023	Weakness: 1.It seems that the method part is very similar to the related work cited in the paper: Generating Adversarial Disturbances for Controller Verification. Could the author provide more clarification on this? 2.Experimental comparison to RRT* seems not good: Even though the RRT* baseline is an oracle without partial observability, the visible region is still very large, which covers more than half of the obstacles. In this case, the naive RRT* (as mentioned in supp C1) can still outperform the proposed method by a large margin on the first task.	1.It seems that the method part is very similar to the related work cited in the paper: Generating Adversarial Disturbances for Controller Verification. Could the author provide more clarification on this?
NIPS_2022_2513	NIPS_2022	Weakness: The claim in Line 175~176 is not validated which it is valuable to see whether the proposed method could prevents potential classes from being incorrectly classified into historical classed. In Tab. 1, for VOC 2-2 (10 tasks) and VOC 19-1 (2 tasks) MicroSeg gets inferior performance compared with SSUL, the reason should be explained. It also appear in ADE 100-50 (2 tasks) in Tab. 2. The proposed method adopts a proposal generator pretrained on MSCOCO which aggregates more information. Is it fair to compared with other methods? Besides, could the proposed technique propmotes existing Class incremental semantic segmentation methods. The authors adequately addressed the limitations and potential negative societal impact of their work.	2. The proposed method adopts a proposal generator pretrained on MSCOCO which aggregates more information. Is it fair to compared with other methods? Besides, could the proposed technique propmotes existing Class incremental semantic segmentation methods. The authors adequately addressed the limitations and potential negative societal impact of their work.
NIPS_2016_287	NIPS_2016	weakness, however, is the experiment on real data where no comparison against any other method is provided. Please see the details comments below.1. While [5] is a closely related work, it is not cited or discussed at all in Section 1. I think proper credit should be given to [5] in Sec. 1 since the spacey random walk was proposed there. The difference between the random walk model in this paper and that in [5] should also be clearly stated to clarify the contributions. 2. The AAAI15 paper titled "Spectral Clustering Using Multilinear SVD: Analysis, Approximations and Applications" by Ghoshdastidar and Dukkipati seems to be a related work missed by the authors. This AAAI15 paper deals with hypergraph data with tensors as well so it should be discussed and compared against to provide a better understanding of the state-of-the-art. 3. This work combines ideas from [4], [5], and [14] so it is very important to clearly state the relationships and differences with these earlier works. 4. End of Sec. 2., there are two important parameters/thresholds to set. One is the minimum cluster size and the other is the conductance threshold. However, the experimental section (Sec. 3) did not mention or discuss how these parameters are set and how sensitive the performance is with respect to these parameters. 5. Sec. 3.2 and Sec. 3.3: The real data experiments study only the proposed method and there is no comparison against any existing method on real data. Furthermore, there is only some qualitative analysis/discussion on the real data results. Adding some quantitative studies will be more helpful to the readers and researchers in this area. 6. Possible Typo? Line 131: "wants to transition".	4. End of Sec.2., there are two important parameters/thresholds to set. One is the minimum cluster size and the other is the conductance threshold. However, the experimental section (Sec. 3) did not mention or discuss how these parameters are set and how sensitive the performance is with respect to these parameters.
NIPS_2017_330	NIPS_2017	- Section 4 is very tersely written (maybe due to limitations in space) and could have benefitted with a slower development for an easier read. - Issues of convergence, especially when applying gradient descent over a non-Euclidean space, is not addressed In all, a rather thorough paper that derives an efficient way to compute gradients for optimization on LDSs modeled using extended subspaces and kernel-based similarity. At one hand, this leads to improvements over some competing methods. Yet, at its core, the paper avoids handling of the harder topics including convergence and any analysis of the proposed optimization scheme. None the less, the derivation of the gradient computations is interesting by itself. Hence, my recommendation.	- Section 4 is very tersely written (maybe due to limitations in space) and could have benefitted with a slower development for an easier read.
NIPS_2020_257	NIPS_2020	* In terms of novelty, note that both the motivation for the model as well as the initial parts of it hold similarities to some prior works. See detailed description in the relation to prior work section. * I would be happy to see results about generalization not only for the CLEVR dataset, but also for natural images datasets where there is larger variance both in the language and visual complexity. There are multiple datasets for generalization in VQA that can be used for that such as CP-VQA and also some splits of GQA. For the CLEVR dataset, the model is basically based on using an object detector to recognize the objects and their properties and build a semantic graph that represents the image. While other approaches that are compared to for this task use object detectors as well, there are many approaches for CLEVR (such as the Neural Module Network, Relation Network, MAC and FiLM) that do not use such strong supervision and therefore the comparison between these approaches in the experimental section is not completely valid. For better comparability, I would be interested to see generalization results when these models are also being fed with at least object-based bounding-boxes representations instead of the earlier commonly used spatial features, as is very common in VQA in the last years (see bottom-up attention networks). * This can be open for debate but I personally believe that the need for reinforcement learning for a static VQA task may be a potential weakness making the approach less data efficient and harder to train the models that use gradient descent.	* This can be open for debate but I personally believe that the need for reinforcement learning for a static VQA task may be a potential weakness making the approach less data efficient and harder to train the models that use gradient descent.
BTr3PSlT0T	ICLR_2025	- I express skepticism about whether the number of videos in the benchmark can achieve a robust assessment. The CVRR-ES benchmark includes only 214 videos, with the shortest video being just 2 seconds. Upon reviewing several videos from the anonymous link, I noticed a significant proportion of short videos. I question whether such short videos can adequately cover 11 categories. Moreover, current work that focuses solely on designing Video-LLMs, without specifically constructing evaluation benchmarks, provides a much larger number of assessment videos than the 214 included in CVRR-ES, for example, Tarsier [1]. - As mentioned in the previous question, the distribution of videos of different lengths within the benchmark is crucial for the assessment of reasoning ability and robustness, and the paper does not provide relevant explanations. The authors should include a table showing the distribution of video lengths across the dataset, and explain how they ensured a balanced representation of different video lengths across the 11 categories. - In the motivation, it is mentioned that the goal is to build human-centric AI systems. Does the paper's reflection on this point merely consist of providing a human baseline? I think that offering more fine-grained visual examples would be more helpful for human-AI comparisons. - I think that the contribution of the DSCP is somewhat overstated and lacks novelty. Such prompt engineering-based methods have already been applied in many works for data generation, model evaluation, and other stages. The introduction and ablation experiments of this technology in the paper seem redundant. - The discussion on DSCP occupies a significant portion of the experimental analysis. I think that the current analysis provided in the paper lacks insight and does not fully reflect the value of CVRR-ES, especially in terms of human-machine comparison. - The phrase should be "there exist a few limitations" instead of "there exist few limitations" in line 520. - The paper does not provide prompt templates for all the closed-source and open-source Video-LLMs used, which will influence the reproducibility. The problems discussed in this paper are valuable, but the most crucial aspects of benchmark construction and evaluation are not entirely convincing. Instead, a significant amount of space is dedicated to introducing the DSCP method. I don't think it meets the acceptance standards of ICLR yet. I will consider modifying the score based on the feedback from other reviewers and the authors' responses. *** [1] Wang J, Yuan L, Zhang Y. Tarsier: Recipes for Training and Evaluating Large Video Description Models[J]. arXiv preprint arXiv:2407.00634, 2024.	- As mentioned in the previous question, the distribution of videos of different lengths within the benchmark is crucial for the assessment of reasoning ability and robustness, and the paper does not provide relevant explanations. The authors should include a table showing the distribution of video lengths across the dataset, and explain how they ensured a balanced representation of different video lengths across the 11 categories.
NIPS_2017_53	NIPS_2017	Weakness 1. When discussing related work it is crucial to mention related work on modular networks for VQA such as [A], otherwise the introduction right now seems to paint a picture that no one does modular architectures for VQA. 2. Given that the paper uses a billinear layer to combine representations, it should mention in related work the rich line of work in VQA, starting with [B] which uses billinear pooling for learning joint question image representations. Right now the manner in which things are presented a novice reader might think this is the first application of billinear operations for question answering (based on reading till the related work section). Billinear pooling is compared to later. 3. L151: Would be interesting to have some sort of a group norm in the final part of the model (g, Fig. 1) to encourage disentanglement further. 4. It is very interesting that the approach does not use an LSTM to encode the question. This is similar to the work on a simple baseline for VQA [C] which also uses a bag of words representation. 5. () Sec. 4.2 it is not clear how the question is being used to learn an attention on the image feature since the description under Sec. 4.2 does not match with the equation in the section. Speficially the equation does not have any term for r^q which is the question representation. Would be good to clarify. Also it is not clear what \sigma means in the equation. Does it mean the sigmoid activation? If so, multiplying two sigmoid activations (with the \alpha_v computation seems to do) might be ill conditioned and numerically unstable. 6. () Is the object detection based attention being performed on the image or on some convolutional feature map V \in R^{FxWxH}? Would be good to clarify. Is some sort of rescaling done based on the receptive field to figure out which image regions belong correspond to which spatial locations in the feature map? 7. () L254: Trimming the questions after the first 10 seems like an odd design choice, especially since the question model is just a bag of words (so it is not expensive to encode longer sequences). 8. L290: it would be good to clarify how the implemented billinear layer is different from other approaches which do billinear pooling. Is the major difference the dimensionality of embeddings? How is the billinear layer swapped out with the hadarmard product and MCB approaches? Is the compression of the representations using Equation. (3) still done in this case? Minor Points: - L122: Assuming that we are multiplying in equation (1) by a dense projection matrix, it is unclear how the resulting matrix is expected to be sparse (arenât we mutliplying by a nicely-conditioned matrix to make sure everything is dense?). - Likewise, unclear why the attended image should be sparse. I can see this would happen if we did attention after the ReLU but if sparsity is an issue why not do it after the ReLU? Perliminary Evaluation The paper is a really nice contribution towards leveraging traditional vision tasks for visual question answering. Major points and clarifications for the rebuttal are marked with a (). [A] Andreas, Jacob, Marcus Rohrbach, Trevor Darrell, and Dan Klein. 2015. âNeural Module Networks.â arXiv [cs.CV]. arXiv. http://arxiv.org/abs/1511.02799. [B] Fukui, Akira, Dong Huk Park, Daylen Yang, Anna Rohrbach, Trevor Darrell, and Marcus Rohrbach. 2016. âMultimodal Compact Bilinear Pooling for Visual Question Answering and Visual Grounding.â arXiv [cs.CV]. arXiv. http://arxiv.org/abs/1606.01847. [C] Zhou, Bolei, Yuandong Tian, Sainbayar Sukhbaatar, Arthur Szlam, and Rob Fergus. 2015. âSimple Baseline for Visual Question Answering.â arXiv [cs.CV]. arXiv. http://arxiv.org/abs/1512.02167.	8.L290: it would be good to clarify how the implemented billinear layer is different from other approaches which do billinear pooling. Is the major difference the dimensionality of embeddings? How is the billinear layer swapped out with the hadarmard product and MCB approaches? Is the compression of the representations using Equation. (3) still done in this case? Minor Points:
OvoRkDRLVr	ICLR_2024	1. The paper proposes a multimodal framework built atop a frozen Large Language Model (LLM) aimed at seamlessly integrating and managing various modalities. However, this approach seems to be merely an extension of the existing InstructBLIP. 2. Additionally, the concept of extending to multiple modalities, such as the integration of audio and 3D modalities, has already been proposed in prior works like PandaGPT. Therefore, the paper appears to lack sufficient novelty in both concept and methodology. 3. In Table 1, there is a noticeable drop in performance for X-InstructBLIP. Could you please clarify the reason behind this? If this drop is due to competition among different modalities, do you propose any solutions to mitigate this issue? 4. The promised dataset has not yet been made publicly available, so a cautious approach should be taken regarding this contribution until the dataset is openly accessible.	4. The promised dataset has not yet been made publicly available, so a cautious approach should be taken regarding this contribution until the dataset is openly accessible.
ICLR_2023_3203	ICLR_2023	1. The novelty is limited. The proposed method is too similar to other attentional modules proposed in previous works [1, 2, 3]. The group attention design seems to be related to ResNeSt [4] but it is not discussed in the paper. Although these works did not evaluate their performance on object detection and instance segmentation, the overall structures between these modules and the one that this paper proposed are pretty similar. 2. Though the improvement is consistent for different frameworks and tasks, the relative gains are not very strong. For most of the baselines, the proposed methods can only achieve just about 1% gain on a relative small backbone ResNet-50. As the proposed method introduces global pooling into its structure, it might be easy to improve a relatively small backbone since it is with a smaller receptive field. I suspect whether the proposed method still works well on large backbone models like Swin-B or Swin-L. 3. Some of the baseline results do not matched with their original paper. I roughly checked the original Mask2former paper but the performance reported in this paper is much lower than the one reported in the original Mask2former paper. For example, for panoptic segmentation, Mask2former reported 51.9 but in this paper it's 50.4, and the AP for instance segmentation reported in the original paper is 43.7 but here what reported is 42.4. Meanwhile, there are some missing references about panoptic segmentation that should be included in this paper [5, 6]. Reference [1] Chen, Yunpeng, et al. "A^ 2-nets: Double attention networks." NeurIPS 2018. [2] Cao, Yue, et al. "Gcnet: Non-local networks meet squeeze-excitation networks and beyond." T-PAMI 2020 [3] Yinpeng Chen, et al. Dynamic convolution: Attention over convolution kernels. CVPR 2020. [4] Zhang, Hang, et al. "Resnest: Split-attention networks." CVPR workshop 2022. [5] Zhang, Wenwei, et al. "K-net: Towards unified image segmentation." Advances in Neural Information Processing Systems 34 (2021): 10326-10338. [6] Wang, Huiyu, et al. "Max-deeplab: End-to-end panoptic segmentation with mask transformers." CVPR 2021	1. The novelty is limited. The proposed method is too similar to other attentional modules proposed in previous works [1, 2, 3]. The group attention design seems to be related to ResNeSt [4] but it is not discussed in the paper. Although these works did not evaluate their performance on object detection and instance segmentation, the overall structures between these modules and the one that this paper proposed are pretty similar.
ICLR_2023_2283	ICLR_2023	1. 1. The symbols in Section 4.3 are not very clearly explained. 2. This paper only experiments on the very small time steps (e.g.1、2) and lack of some experiments on slightly larger time steps (e.g. 4、6) to make better comparisons with other methods. I think it is necessary to analyze the impact of the time step on the method proposed in this paper. 3. Lack of experimental results on ImageNet to verify the method. Questions: 1. Fig. 3 e. Since the preactivation values of two networks are the same membrane potentials, their output cosine similarity will be very high. Why not directly illustrate the results of the latter loss term of Eqn 13? 2. Is there any use of recurrent connections in the experiments in this paper? Apart from appendix A.5, I do not see the recurrent connections.	1. Fig. 3 e. Since the preactivation values of two networks are the same membrane potentials, their output cosine similarity will be very high. Why not directly illustrate the results of the latter loss term of Eqn 13?
eI6ajU2esa	ICLR_2024	- This paper investigates the issue of robustness in video action recognition, but it lacks comparison with test-time adaptation (TTA) methods, such as [A-B]. These TTA methods also aim to adapt to out-of-distribution data when the input data is disturbed by noise. Although these TTA methods mainly focus on updating model parameters, and this paper primarily focuses on adjusting the input data, how to prove that data processing is superior to model parameter adjustment? I believe a comparison should be made based on experimental results. - Under noisy conditions, many TTA methods can achieve desirable results, while the improvement brought by this paper's method is relatively low. - In appendix A.2.1, under noisy conditions, the average performance improvement brought by this paper's method is very low and can even be counterproductive under certain noise conditions. Does this indicate an issue with the approach of changing input data? - How to verify the reliability of the long-range photometric consistency in section 3.3? Are there any ablation study results reflecting the performance gain brought by each part? - The explanation of the formula content in Algorithm 1 in the main body is not clear enough. [A] Temporal Coherent Test-Time Optimization for Robust Video Classification. ICLR23 [B] Video Test-Time Adaptation for Action Recognition. CVPR23	- This paper investigates the issue of robustness in video action recognition, but it lacks comparison with test-time adaptation (TTA) methods, such as [A-B]. These TTA methods also aim to adapt to out-of-distribution data when the input data is disturbed by noise. Although these TTA methods mainly focus on updating model parameters, and this paper primarily focuses on adjusting the input data, how to prove that data processing is superior to model parameter adjustment? I believe a comparison should be made based on experimental results.
ICLR_2021_863	ICLR_2021	Weakness 1. The presentation of the paper should be improved. Right now all the model details are placed in the appendix. This can cause confusion for readers reading the main text. 2. The necessity of using techniques includes Distributional RL and Deep Sets should be explained more thoroughly. From this paper, the illustration of Distributional RL lacks clarity. 3. The details of state representation are not explained clear. For an end-to-end method like DRL, it is crucial for state representation for training a good agent, as for network architecture. 4. The experiments are not comprehensive for validating that this algorithm works well in a wide range of scenarios. The efficiency, especially the time efficiency of the proposed algorithm, is not shown. Moreover, other DRL benchmarks, e.g., TD3 and DQN, should also be compared with. 5. There are typos and grammar errors. Detailed Comments 1. Section 3.1, first paragraph, quotation mark error for "importance". 2. Appendix A.2 does not illustrate the state space representation of the environment clearly. 3. The authors should state clearly as to why the complete state history is enough to reduce POMDP for the no-CSI case. 4. Section 3.2.1: The first expression for J ( θ ) is incorrect, which should be Q ( s t 0 , π θ ( s t 0 ) ) . 5. The paper did not explain Figure 2 clearly. In particular, what does the curve with the label "Expected" in Fig. 2(a) stand for? Not to mention there are multiple misleading curves in Fig. 2(b)&(c). The benefit of introducing distributional RL is not clearly explained. 6. In Table 1, only 4 classes of users are considered in the experiment sections, which might not be in accordance with practical situations, where there can be more classes of users in the real system and more user numbers. 7. In the experiment sections, the paper only showed the Satisfaction Probability of the proposed method is larger than conventional methods. The algorithm complexity, especially the time complexity of the proposed method in an ultra multi-user scenario, is not shown. 8. There is a large literature on wireless scheduling with latency guarantees from the networking community, e.g., Sigcomm, INFOCOM, Sigmetrics. Representative results there should also be discussed and compared with. ====== post rebuttal: My concern regarding the experiments remains. I will keep my score unchanged.	4. Section 3.2.1: The first expression for J ( θ ) is incorrect, which should be Q ( s t 0 , π θ ( s t 0 ) ) .
ICLR_2021_872	ICLR_2021	The authors push on the idea of scalable approximate inference, yet the largest experiment shown is on CIFAR-10. Given this focus on scalability, and the experiments in recent literature in this space, I think experiments on ImageNet would greatly strengthen the paper (though I sympathize with the idea that this can a high bar from a resources standpoint). As I noted down below, the experiments currently lack results for the standard variational BNN with mean-field Gaussians. More generally, I think it would be great to include the remaining models from Ovadia et al. (2019). More recent results from ICML could also useful to include (as referenced in the related works sections). Recommendation Overall, I believe this is a good paper, but the current lack of experiments on a dataset larger than CIFAR-10, while also focusing on scalability, make it somewhat difficult to fully recommend acceptance. Therefore, I am currently recommending marginal acceptance for this paper. Additional comments p. 5-7: Including tables of results for each experiment (containing NLL, ECE, accuracy, etc.) in the main text would be helpful to more easily assess p. 7: For the MNIST experiments, in Ovadia et al. (2019) they found that variational BNNs (SVI) outperformed all other methods (including deep ensembles) on all shifted and OOD experiments. How does your proposed method compare? I think this would be an interesting experiment to include, especially since the consensus in Ovadia et al. (2019) (and other related literature) is that full variational BNNs are quite promising but generally methodologically difficult to scale to large problems, with relative performance degrading even on CIFAR-10. Minor p. 6: In the phrase "for 'in-between' uncertainty", the first quotation mark on 'in-between' needs to be the forward mark rather than the backward mark (i.e., ‘ i n − b e t w e e n ′ ). p. 7: s/out of sitribution/out of distribution/ p. 8: s/expensive approaches 2) allows/expensive approaches, 2) allows/ p. 8: s/estimates 3) is/estimates, and 3) is/ In the references: Various words in many of the references need capitalization, such as "ai" in Amodei et al. (2016), "bayesian" in many of the papers, and "Advances in neural information processing systems" in several of the papers. Dusenberry et al. (2020) was published in ICML 2020 Osawa et al. (2019) was published in NeurIPS 2019 Swiatkowski et al. (2020) was published in ICML 2020 p. 13, supplement, Fig. 5: error bar regions should be upper and lowered bounded by [0, 1] for accuracy. p. 13, Table 2: Splitting this into two tables, one for MNIST and one for CIFAR-10, would be easier to read.	8: s/expensive approaches2) allows/expensive approaches,2) allows/ p.8: s/estimates3) is/estimates, and3) is/ In the references: Various words in many of the references need capitalization, such as "ai" in Amodei et al. (2016), "bayesian" in many of the papers, and "Advances in neural information processing systems" in several of the papers. Dusenberry et al. (2020) was published in ICML 2020 Osawa et al. (2019) was published in NeurIPS 2019 Swiatkowski et al. (2020) was published in ICML 2020 p. 13, supplement, Fig.
NIPS_2016_339	NIPS_2016	weakness of the model. How would the values in table 1 change without this extra assumption? 3. I didn't find all parameter values. What are the model parameters for task 1? What lambda was chosen for the Boltzmann policy. But more importantly: How were the parameters chosen? Maximum likelihood estimates? 4. An answer to this point may be beyond the scope of this work, but it may be interesting to think about it. It is mentioned (lines 104-106) that "the examples [...] should maximally disambiguate the concept being taught from other possible concepts". How is disambiguation measured? How can disambiguation be maximized? Could there be an information theoretic approach to these questions? Something like: the teacher chooses samples that maximally reduce the entropy of the assumed posterior of the student. Does the proposed model do that? Minor points: â¢ line 88: The optimal policy is deterministic. Hence I'm a bit confused by "the stochastic optimal policy". Is above defined "the Boltzmann policy" meant? â¢ What is d and h in equation 2? â¢ line 108: "to calculate this ..." What is meant by "this"? â¢ Algorithm 1: Require should also include epsilon. Does line 1 initialize the set of policies to an empty set? Are the policies in line 4 added to this set? Does calculateActionValues return the Q* defined in line 75? What is M in line 6? How should p_min be chosen? Why is p_min needed anyway? â¢ Experiment 2: Is the reward 10 points (line 178) or 5 points (line 196)? â¢ Experiment 2: Is 0A the condition where all tiles are dangerous? Why are the likelihoods so much larger for 0A? Is it reasonable to average over likelihoods that differ by more than an order of magnitude (0A vs 2A-C)? â¢ Text and formulas should be carefully checked for typos (e.g. line 10 in Algorithm 1: delta > epsilon; line 217: 1^-6;)	3. I didn't find all parameter values. What are the model parameters for task 1? What lambda was chosen for the Boltzmann policy. But more importantly: How were the parameters chosen? Maximum likelihood estimates?
NIPS_2016_313	NIPS_2016	Weakness: 1. The proposed method consists of two major components: generative shape model and the word parsing model. It is unclear which component contributes to the performance gain. Since the proposed approach follows detection-parsing paradigm, it is better to evaluate on baseline detection or parsing techniques sperately to better support the claim. 2. Lacks in detail about the techniques and make it hard to reproduce the result. For example, it is unclear about the sparsification process since it is important to extract the landmark features for following steps. And how to generate the landmark on the edge? How to decide the number of landmark used? What kind of images features? What is the fixed radius with different scales? How to achieve shape invariance, etc. 3. The authors claim to achieve state-of-the-art results on challenging scene text recognition tasks, even outperforms the deep-learning based approaches, which is not convincing. As claimed, the performance majorly come from the first step which makes it reasonable to conduct comparisons experiments with existing detection methods. 4. It is time-consuming since the shape model is trained in pixel level(though sparsity by landmark) and the model is trained independently on all font images and characters. In addition, parsing model is a high-order factor graph with four types of factors. The processing efficiency of training and testing should be described and compared with existing work. 5. For the shape model invariance study, evaluation on transformations of training images cannot fully prove the point. Are there any quantitative results on testing images?	3. The authors claim to achieve state-of-the-art results on challenging scene text recognition tasks, even outperforms the deep-learning based approaches, which is not convincing. As claimed, the performance majorly come from the first step which makes it reasonable to conduct comparisons experiments with existing detection methods.
NIPS_2017_631	NIPS_2017	1. The main contribution of the paper is CBN. But the experimental results in the paper are not advancing the state-of-art in VQA (on the VQA dataset which has been out for a while and a lot of advancement has been made on this dataset), perhaps because the VQA model used in the paper on top of which CBN is applied is not the best one out there. But in order to claim that CBN should help even the more powerful VQA models, I would like the authors to conduct experiments on more than one VQA model â favorably the ones which are closer to state-of-art (and whose codes are publicly available) such as MCB (Fukui et al., EMNLP16), HieCoAtt (Lu et al., NIPS16). It could be the case that these more powerful VQA models are already so powerful that the proposed early modulating does not help. So, it is good to know if the proposed conditional batch norm can advance the state-of-art in VQA or not. 2. L170: it would be good to know how much of performance difference this (using different image sizes and different variations of ResNets) can lead to? 3. In table 1, the results on the VQA dataset are reported on the test-dev split. However, as mentioned in the guidelines from the VQA dataset authors (http://www.visualqa.org/vqa_v1_challenge.html), numbers should be reported on test-standard split because one can overfit to test-dev split by uploading multiple entries. 4. Table 2, applying Conditional Batch Norm to layer 2 in addition to layers 3 and 4 deteriorates performance for GuessWhat?! compared to when CBN is applied to layers 4 and 3 only. Could authors please throw some light on this? Why do they think this might be happening? 5. Figure 4 visualization: the visualization in figure (a) is from ResNet which is not finetuned at all. So, it is not very surprising to see that there are not clear clusters for answer types. However, the visualization in figure (b) is using ResNet whose batch norm parameters have been finetuned with question information. So, I think a more meaningful comparison of figure (b) would be with the visualization from Ft BN ResNet in figure (a). 6. The first two bullets about contributions (at the end of the intro) can be combined together. 7. Other errors/typos: a. L14 and 15: repetition of word âimagineâ b. L42: missing reference c. L56: impact -> impacts Post-rebuttal comments: The new results of applying CBN on the MRN model are interesting and convincing that CBN helps fairly developed VQA models as well (the results have not been reported on state-of-art VQA model). So, I would like to recommend acceptance of the paper. However I still have few comments -- 1. It seems that there is still some confusion about test-standard and test-dev splits of the VQA dataset. In the rebuttal, the authors report the performance of the MCB model to be 62.5% on test-standard split. However, 62.5% seems to be the performance of the MCB model on the test-dev split as per table 1 in the MCB paper (https://arxiv.org/pdf/1606.01847.pdf). 2. The reproduced performance reported on MRN model seems close to that reported in the MRN paper when the model is trained using VQA train + val data. I would like the authors to clarify in the final version if they used train + val or just train to train the MRN and MRN + CBN models. And if train + val is being used, the performance can't be compared with 62.5% of MCB because that is when MCB is trained on train only. When MCB is trained on train + val, the performance is around 64% (table 4 in MCB paper). 3. The citation for the MRN model (in the rebuttal) is incorrect. It should be -- @inproceedings{kim2016multimodal, title={Multimodal residual learning for visual qa}, author={Kim, Jin-Hwa and Lee, Sang-Woo and Kwak, Donghyun and Heo, Min-Oh and Kim, Jeonghee and Ha, Jung-Woo and Zhang, Byoung-Tak}, booktitle={Advances in Neural Information Processing Systems}, pages={361--369}, year={2016} } 4. As AR2 and AR3, I would be interested in seeing if the findings from ResNet carry over to other CNN architectures such as VGGNet as well.	4. Table 2, applying Conditional Batch Norm to layer 2 in addition to layers 3 and 4 deteriorates performance for GuessWhat?! compared to when CBN is applied to layers 4 and 3 only. Could authors please throw some light on this? Why do they think this might be happening?
yIv4SLzO3u	ICLR_2024	- Lack of comparison with a highly relevant method. [1] also proposes to utilize the previous knowledge with ‘inter-task ensemble’, while enhancing the current task’s performance with ‘intra-task’ ensemble. Yet, the authors didn’t include the method comparison or performance comparison. - Novelty is limited. From my perspective, the submission simply applies the existing weight averaging and the bounded update to the class incremental learning problems. - No theoretical justification or interpretation. Is there any theoretical guarantee that to what extent inter-task weight averaging or bounded update counter catastrophic forgetting? - Though it shows in Table 3 that bounded model update mitigates the forgetting, the incorporation of bounded model update doesn’t seem to have enough motivation from the methodological perspective. The inter-task weight average is designed to incorporate both old and new knowledge, which is by design enough to tackle forgetting. ##### References: 1.Miao, Z., Wang, Z., Chen, W., & Qiu, Q. (2021, October). Continual learning with filter atom swapping. In International Conference on Learning Representations.	- Lack of comparison with a highly relevant method. [1] also proposes to utilize the previous knowledge with ‘inter-task ensemble’, while enhancing the current task’s performance with ‘intra-task’ ensemble. Yet, the authors didn’t include the method comparison or performance comparison.
NIPS_2018_914	NIPS_2018	of the paper are (i) the presentation of the proposed methodology to overcome that effect and (ii) the limitations of the proposed methods for large-scale problems, which is precisely when function approximation is required the most. While the intuition behind the two proposed algorithms is clear (to keep track of partitions of the parameter space that are consistent in successive applications of the Bellman operator), I think the authors could have formulated their idea in a more clear way, for example, using tools from Constraint Satisfaction Problems (CSPs) literature. I have the following concerns regarding both algorithms: - the authors leverage the complexity of checking on the Witness oracle, which is "polynomial time" in the tabular case. This feels like not addressing the problem in a direct way. - the required implicit call to the Witness oracle is confusing. - what happens if the policy class is not realizable? I guess the algorithm converges to an \empty partition, but that is not the optimal policy. minor: line 100 : "a2 always moves from s1 to s4 deterministically" is not true line 333 : "A number of important direction" -> "A number of important directions" line 215 : "implict" -> "implicit" - It is hard to understand the figure where all methods are compared. I suggest to move the figure to the appendix and keep a figure with less curves. - I suggest to change the name of partition function to partition value. [I am satisfied with the rebuttal and I have increased my score after the discussion]	- the required implicit call to the Witness oracle is confusing.
NIPS_2022_532	NIPS_2022	1. Imitation Learning: The proposed method needs to be trained by behavioral cloning, which means 1) it requires a carefully well-designed algorithm (e.g., ODA-T/B/K) to generate the supervised data set. 2) More importantly, the data generated by ODA with a time limit L is indeed not a perfect teacher for behavioral cloning. Since all the ODAs are not designed and optimized for bounded time performance, their behavior (the state-action pairs) for the first L time is not the optimal policy under time limit L. Since the generic algorithm procedure of ODA can be encoded as a MDP, is it possible to use reinforcement learning to train the model? Would the RL-based approach find a better policy for bounded time performance that is aware of the time limit T？ 2. Performance with Different Time Limits: It seems that the proposed method is both trained and tested with a single fixed time limit T = 1000s for all problems. However, in practice, the applications could have very different run time limits. Will the proposed method generalize well to different time limits (such as 1/10/100/2000/5000s)? 3. Comparison with PMOCO: PMOCO is the only learning-based approach in the comparison, but it has a very small cardinality (feasible points) for most problems. Its approximated Pareto front is also relatively sparse (which means a small set of solutions) in Figure A.3. This result is a bit counter-intuitive. In my understanding, PMOCO is a construction-based neural combinatorial optimization algorithm, of which one important advantage is the very fast run time. The PMOCO paper [1] reports it can generate 101 solutions for 100 MOKP(2-100) instances (hence 10,100 solutions in total) in only 15s, and 10,011 solutions for 100 MOTSP(3-100) instances (hence 1,001,100 solutions in total) in 33 minutes (~2000s). In this work, with a large time limit of 1,000s, I think POMO should be able to generate a dense set of solutions for each instance. In addition, while a dataset with 100 instances could provide enough supervised ODA state-action pairs (with a time limit L = 1000s for each instance) for imitation learning, it is far from enough for PMOCO's RL-based training. Since PMOCO does not require any supervised data and the MOKP instances can be easily generated on the fly, is it more suitable to train PMOCO under the same wall-clock time with the proposed method? [1] Pareto set learning for neural multi-objective combinatorial optimization. ICLR 2022. The limitations of this work are 1) the requirement of ODAs and a well-designed IP solver; 2) it loses the guarantee for finding the whole Pareto front. They have been properly discussed in the paper (see remark at the end of Section 4.1 and Conclusion). I do not see any potential negative societal impact of this work.	2) it loses the guarantee for finding the whole Pareto front. They have been properly discussed in the paper (see remark at the end of Section 4.1 and Conclusion). I do not see any potential negative societal impact of this work.
ICLR_2022_1420	ICLR_2022	Weakness: Lack of novelty. The key idea, i.e., combining foreground masks to remove the artifacts from the background, is not new. Separate handling of foreground from background is a common practice for dynamic scene novel view synthesis, and many recent methods do not even require the foreground masks for modeling dynamic scenes (they jointly model the foreground region prediction module, e.g., Tretschk et al. 2021). Lack of controllability. 1) The proposed method cannot handle the headpose. While this paper defers this problem to a future work, a previous work (e.g., Gafni et al. ICCV 2021) is already able to control both facial expression and headpose. Why is it not possible to condition the headpose parameters in the NeRF beyond the facial expression similar to [Gafni et al. ICCV 2021]? 2) Even for controlling facial expression, it is highly limited to the mouth region only. From overall qualitative results and demo video, it is not clear the method indeed can handle overall facial expression including eyes, nose, and wrinkle details, and the diversity in mouth shape that the model can deliver is significantly limited. Low quality. The results made by the proposed method are of quite low quality. 1) Low resolution: While many previous works introduce high-quality view synthesis results with high-resolution (512x512 or more), this paper shows low resolution results (256x256) for some reasons. Simply saying the problem of resources is not a convincing argument since many existing works already proved the feasibility of high resolution image synthesis using implicit function. Due to this low-resolution nature, many high-frequency details (e.g., facial wrinkles), which are the key to enabling photorealistic face image synthesis, are washed out. 2) In many cases, the conditioning facial expressions do not match that from the synthesized image. From the demo video, while mouth opening or closing are somehow synchronized with conditioning videos, there exists a mismatch in the style of the detailed mouth shape.	1) The proposed method cannot handle the headpose. While this paper defers this problem to a future work, a previous work (e.g., Gafni et al. ICCV 2021) is already able to control both facial expression and headpose. Why is it not possible to condition the headpose parameters in the NeRF beyond the facial expression similar to [Gafni et al. ICCV 2021]?