Datasets:

boda
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review_evaluation_main_3

paper_id stringlengths 10 19	venue stringclasses 14 values	focused_review stringlengths 7 8.09k	point stringlengths 54 690
NIPS_2020_897	NIPS_2020	1. Not clear how this method can be applied outside of fully cooperative settings, as the authors claim. The authors should justify this claim theoretically or empirically, or else remove it. 2. Missing some citations to set this in context of other MARL work e.g. recent papers on self-play and population-play with respect to exploration and coordination (such as https://arxiv.org/abs/1806.10071, https://arxiv.org/abs/1812.07019). 3. The analysis is somewhat "circumstantial", need more detailed experiments to be a convincing argument in this section. For example the claim in lines 235 - 236 seems to require further evidence to be completely convincing. 4. The link with self-play could be more clearly drawn out. As far as I can tell, the advantage of this over self-play is precisely the different initialization of the separate agents. It is surprising and important that this has such a significant effect, and could potentially spur a meta-learning investigation into optimal initialization for SEAC in future work.	2. Missing some citations to set this in context of other MARL work e.g. recent papers on self-play and population-play with respect to exploration and coordination (such as https://arxiv.org/abs/1806.10071, https://arxiv.org/abs/1812.07019).
ICLR_2023_1645	ICLR_2023	1. Can this method be used on both SEEG and EEG simultaneously? 2. It would be better to compare with other self-supervised learning methods that are not based on contrastive learning.	2. It would be better to compare with other self-supervised learning methods that are not based on contrastive learning.
t8cBsT9mcg	ICLR_2024	1. The abstract should be expanded to encompass key concepts that effectively summarize the paper's contributions. In the introduction, the authors emphasize the significance of interpretability and the challenges it poses in achieving high accuracy. By including these vital points in the abstract, the paper can provide a more comprehensive overview of its content and contributions. 2. Regarding the abstention process, it appears to be based on a prediction probability threshold, where if the probability is lower than the threshold, the prediction is abstained? How does it different from a decision threshold used by the models? Can authors clarify that? 3. In the results and discussion section, there's limited exploration and commentary on the impact of the solution on system accuracy, as seen in Table 2. Notably, the confirmation budget appears to have a limited effect on datasets like "noisyconcepts25" and "warbler" compared to others. The paper can delve into the reasons behind this discrepancy. 4. In real-world applications of this solution, questions about the ease of concept approval and handling conflicting user feedback arise. While these aspects may be considered out of scope, addressing them would be beneficial for evaluating the practicality of implementing this approach in real-world scenarios. This is particularly important when considering the potential challenges of user feedback and conflicting inputs in such applications. Minor things: Page 4, confirm. we —> replace . with comma Section 4.2, Table Table 2 —> Table 2 Shouldn’t Table 2 rather be labelled as Figure 2?	2. Regarding the abstention process, it appears to be based on a prediction probability threshold, where if the probability is lower than the threshold, the prediction is abstained? How does it different from a decision threshold used by the models? Can authors clarify that?
NIPS_2021_1743	NIPS_2021	1. While the paper claim the importance of language modeling capability of pre-trained models, the authors did not conduct experments on generation tasks that are more likely to require a well-performing language model. Experiments on word similarity and SquAD in section 5.3 cannot really reflect the capability of language modeling. The authors may consider to include tasks like language modeling, machine translation or text sumarization to strenghen this part, as this is one of the main motivations of COCO-LM. 2. Analysis of SCL in section 5.2 regarding few-shot abaility looks not convincing. The paper claims that a more regularized representation space by SCL may result in better generalization ability in few-shot scenarios. However, results in Figure 7(c) and (d) do not meet our expectation such that COCO-LM achieves much more improvements with less labels and the improvements will gradually disappear with more labels. Besides, the authors may check if COCO-LM brings benefits to sentence retrieval tasks with the learned anisotropy text representations. 3. The comparison with Megatron is a little overrated. The performance of Megatron and COCO-LM is close to other approaches, for examples, RoBERTa, ELECTRA, and DeBERTa, which are with similar sizes as COCO-LM. If the author claim that COCO-LM is parameter-efficient, the conclusion is also applicable to the above related works. Questions for the Authors 1. In experimental setup, why did the authors switch the types of BPE vocabulary, i.e., uncased and cased. Will the change of BPE cause the variance of performance? 2. In Table 2, it looks like COCO-LM especially affects the performance on CoLA and RTE hence the final performance. Can the authors provide some explanation on how the proposed pre-training tasks affect the two different GLEU tasks? 3. In section 5.1, the authors say that the benefits of the stop gradient operation are more on stability. What stability, the training process? If so, are there any learning curves of COCO-LM with and without stop gradient during pre-training to support this claim? 4. In section 5.2, the term “Data Argumentation” seems wrong. Did the authors mean data augmentation? Typos 1. Check the term “Argumentation” in line 164, 252, and 314. 2. Line 283, “a unbalanced task”, should be “an unbalanced task”. 3. Line 326, “contrast pairs”, should be “contrastive pairs” to be consistent throughout the paper?	3. The comparison with Megatron is a little overrated. The performance of Megatron and COCO-LM is close to other approaches, for examples, RoBERTa, ELECTRA, and DeBERTa, which are with similar sizes as COCO-LM. If the author claim that COCO-LM is parameter-efficient, the conclusion is also applicable to the above related works. Questions for the Authors 1. In experimental setup, why did the authors switch the types of BPE vocabulary, i.e., uncased and cased. Will the change of BPE cause the variance of performance?
NIPS_2018_865	NIPS_2018	weakness of this paper are listed: 1) The proposed method is very similar to Squeeze-and-Excitation Networks [1], but there is no comparison to the related work quantitatively. 2) There is only the results on image classification task. However, one of success for deep learning is that it allows people leverage pretrained representation. To show the effectiveness of this approach that learns better representation, more tasks are needed, such as semantic segmentation. Especially, the key idea of this method is on the context propagation, and context information plays an important role in semantic segmentation, and thus it is important to know. 3) GS module is used to propagate the context information over different spatial locations. Is the effective receptive field improved, which can be computed from [2]? It is interesting to know how the effective receptive field changed after applying GS module. 4) The analysis from line 128 to 149 is not convincing enough. From the histogram as shown in Fig 3, the GS-P-50 model has smaller class selectivity score, which means GS-P-50 shares more features and ResNet-50 learns more class specific features. And authors hypothesize that additional context may allow the network to reduce its dependency. What is the reason such an observation can indicate GS-P-50 learns better representation? Reference: [1] J. Hu, L. Shen and G. Sun, Squeeze-and-Excitation Networks, CVPR, 2018. [2] W. Luo et al., Understanding the Effective Receptive Field in Deep Convolutional Neural Networks, NIPS, 2016.	4) The analysis from line 128 to 149 is not convincing enough. From the histogram as shown in Fig 3, the GS-P-50 model has smaller class selectivity score, which means GS-P-50 shares more features and ResNet-50 learns more class specific features. And authors hypothesize that additional context may allow the network to reduce its dependency. What is the reason such an observation can indicate GS-P-50 learns better representation? Reference: [1] J. Hu, L. Shen and G. Sun, Squeeze-and-Excitation Networks, CVPR, 2018. [2] W. Luo et al., Understanding the Effective Receptive Field in Deep Convolutional Neural Networks, NIPS, 2016.
kfFmqu3zQm	ICLR_2025	1. Some conclusions are not convincing. For example, the paper contends that We believe that continuous learning with unlabeled data accumulates noise, which is detrimental to representation quality. The results might come from the limited exploration of combination methods. In rehearsal-free continual learning, feature-replay methods have shown great potential, like [R1] in continual learning and [R2] (FRoST) in CCD. A more recent work [R3] also employs feature replay to continually adjust the feature space, which also obtains remarkable performance for continual category discovery. 2. The proposed method is naïve and the novelty is relatively limited. The method includes basic clustering and number estimation. I’m afraid that this method could not provide so many insights to the community. 3. The feature space (i.e., backbone) is only tuned using labeled known classes, does this manner result in overfitting? because the data is purely labeled but the number is limited. 4. The class number estimation algorithm requires a pre-defined threshold $d_{min}$, which is intractable to define in advance and could largely impact the results. Some experiments and ablations should be included. 5. Detailed results of each continual session (at least for one or two datasets) should also be presented to show the performance. References: [R1]. Prototype Augmentation and Self-Supervision for Incremental Learning. CVPR 2021. [R2]. Class-incremental Novel Class Discovery. ECCV 2022. [R3]. Happy: A Debiased Learning Framework for Continual Generalized Category Discovery. NeurIPS 2024. arXiv:2410.0653.	1. Some conclusions are not convincing. For example, the paper contends that We believe that continuous learning with unlabeled data accumulates noise, which is detrimental to representation quality. The results might come from the limited exploration of combination methods. In rehearsal-free continual learning, feature-replay methods have shown great potential, like [R1] in continual learning and [R2] (FRoST) in CCD. A more recent work [R3] also employs feature replay to continually adjust the feature space, which also obtains remarkable performance for continual category discovery.
TY9mstpD02	ICLR_2025	- generalizability to other models: the proposed framework is validated using gpt-4-turbo, a costly language model, which may compromise the applicability of the framework at scale. The paper could be further improved by showing how running the experiments using a cheaper model (e.g., gpt-4o) and/or open source models (e.g., Llama 3.1) would affect the obtained results. - generalizability of the results: the conducted experiments are either too simple (simple synthetic regression setting with 4 variables) or include few data-model pairs (6 in Section 4.2, 36 in Section 4.3, and 10 for the human studies), raising questions about the generalizability of the proposed framework to more complex datasets. - lack of meaningful baselines: despite mentioning various model criticism techniques in Section 2, the authors limit their comparisons to simple naive baselines. For example, the authors could compare with a chain-of-thought prompting approach. - few insights about the generated and correctness of summary statistics: while the authors provide one example in Section 4.3, the paper could be further improved by adding additional insights and contrasting the proposed discrepancies with commonly discussed discrepancies in the literature (e.g., do these resemble the ones commonly found by humans?)	- lack of meaningful baselines: despite mentioning various model criticism techniques in Section 2, the authors limit their comparisons to simple naive baselines. For example, the authors could compare with a chain-of-thought prompting approach.
ICLR_2022_2531	ICLR_2022	I have several concerns about the clinical utility of this task as well as the evaluation approach. - First of all, I think clarification is needed to describe the utility of the task setup. Why is the task framed as generation of the ECG report rather than framing the task as multi-label classification or slot-filling, especially given the known faithfulness issues with text generation? There are some existing approaches for automatic ECG interpretation. How does this work fit into the existing approaches? A portion of the ECG reports from the PTB-XL dataset are actually automatically generated (See Data Acquisition under https://physionet.org/content/ptb-xl/1.0.1/). Do you filter out those notes during evaluation? How does your method compare to those automatically generated reports? - A major claim in the paper is that RTLP generates more clinically accurate reports than MLM, yet the only analysis in the paper related to this is a qualitative analysis of a single report. A more systematic analysis of the quality of generation would be useful to support the claim made in the appendix. Can you ask clinicians to evaluate the utility of the generated reports or evaluate clinical utility by using the generated reports to predict conditions identifiable from the ECG? I think that it’s fine that the RTLP method performs comparable to existing methods, but I am not sure from the current paper what the utility of using RTLP is. - More generally, I think that this paper is trying to do two things at once – present new methods for multilingual pretraining while also developing a method of ECG captioning. If the emphasis is on the former, then I would expect to see evaluation against other multilingual pretraining setups such as the Unicoder (Huang 2019a). If the core contribution is the latter, then clinical utility of the method as well as comparison to baselines for ECG captioning (or similar methods) is especially important. - I’m a bit confused as to why the diversity of the generated reports is emphasized during evaluation. While I agree that the generated reports should be faithful to the associated ECG, diversity may not actually be necessary metric to aim for in a medical context. For instance, if many of the reports are normal, you would want similar reports for each normal ECG (i.e. low diversity). - My understanding is that reports are generated in other languages using Google Translate. While this makes sense to generate multilingual reports for training, it seems a bit strange to then evaluate your model performance on these silver-standard noisy reports. Do you have a held out set of gold standard reports in different languages for evaluation (other than German)? Other Comments: - Why do you only consider ECG segments with one label assigned to them? I would expect that the associated reports would be significantly easier than including all reports. - You might consider changing the terminology from “cardiac arrythmia” categories to something broader since hypertrophy (one of the categories) is not technically a cardiac arrythmia (although it can be detected via ECG & it does predispose you to them) - I think it’d be helpful to include an example of some of the tokens that are sampled during pretraining using your semantically similar strategy for selecting target tokens. How well does this work in languages that have very different syntactic structures compared to the source language? - Do you pretrain the cardiac signal representation learning model on the entire dataset or just the training set? If the entire set, how well does this generalize to setting where you don’t have the associated labels? - What kind of tokenization is used in the model? Which Spacy tokenizer? - It’d be helpful to reference the appendix when describing the setup in section 3/5 so that the reader knows that more detailed architecture information is there. - I’d be interested to know if other multilingual pretraining setups also struggle with Greek. - It’d be helpful to show the original ECG report with punctuation + make the ECG larger so that they are easier to read - Why do you think RTLP benefits from fine-tuning on multiple languages, but MARGE does not?	- Do you pretrain the cardiac signal representation learning model on the entire dataset or just the training set? If the entire set, how well does this generalize to setting where you don’t have the associated labels?
NIPS_2022_2152	NIPS_2022	The authors clearly addressed some potential limitations of the work: 1) Some observations and subsequent design decisions might be hardware and software dependent; 2) The NAS procedure, specifically the latency-driven slimming procedure is less involved and could be a direction for future exploration.	1) Some observations and subsequent design decisions might be hardware and software dependent;
ICLR_2021_147	ICLR_2021	the empirical validation is weak. Therefore, more new models need to be compared. For more details, please refer to “Reasons for reject” Reasons for accept: 1. The structure of this paper is clear and easy to read. Specifically, the motivation of this paper is clear and the structure is well organized; the related work is elaborated in detail; the experimental setup is complete. 2. Based on the use of replay to solve catastrophic forgetting, the current popular graph structure is introduced to capture the similarities between samples. Combined with the proposed Graph Regularization, this paper provides a new perspective for solving catastrophic forgetting. 3. The experimental results given in the paper can basically show that the proposed method is effective. The ablation study also verified the effectiveness of each component. Reasons for reject: 1. The lack of comparison of experimental effects after replacing Graph Regularization with other regularization methods mentioned in this paper, or other distance measurement methods, eg., L2. This paper compares relatively few baselines, especially recent studies. I hope to see the comparison results of some papers in the list below. The latest papers on the three types of methods (regularization, expansion, and rehearsal) for solving catastrophic forgetting are included. Therefore, if it can be compared with some of these models, it will be beneficial to the evaluation of GCL. [1] Ostapenko O , Puscas M , Klein T , et al. Learning to Remember: A Synaptic Plasticity Driven Framework for Continual Learning. ICML 2019 [2] Y Wu, Y Chen, et al. Large Scale Incremental Learning. CVPR 2019 [3] Liu Y , Liu A A , Su Y , et al. Mnemonics training: Multi-class incremental learning without forgetting. CVPR 2020 [4] Zhang J , Zhang J , Ghosh S , et al. Class-incremental learning via deep model consolidation. 2020 IEEE Winter Conference on Applications of Computer Vision (WACV) [5] Guanxiong Zeng, Yang Chen, Bo Cui, and Shan Yu. Continuous learning of context-dependent processing in neural networks. Nature Machine Intelligence, 2019. [6] Wenpeng Hu, Zhou Lin, et al. Overcoming catastrophic forgetting for continual learning via model adaptation. ICLR 2019 [7] Rao D , Visin F , Rusu A A , et al. Continual Unsupervised Representation Learning. NeurIPS 2019	1. The structure of this paper is clear and easy to read. Specifically, the motivation of this paper is clear and the structure is well organized; the related work is elaborated in detail; the experimental setup is complete.
NIPS_2022_738	NIPS_2022	W1) The paper states that "In order to introduce epipolar constraints into attention-based feature matching while maintaining robustness to camera pose and calibration inaccuracies, we develop a Window-based Epipolar Transformer (WET), which matches reference pixels and source windows near the epipolar lines." It claims that it introduces "a window-based epipolar Transformer (WET) for enhancing patch-to-patch matching between the reference feature and corresponding windows near epipolar lines in source features". To me, taking a window around the epipolar line into account seems like an approximation to estimating the uncertainty region around the epipolar lines caused by inaccuracies in calibration and camera pose and then searching within this region (see [Förstner & Wrobel, Photogrammetric Computer Vision, Springer 2016] for a detailed derivation of how to estimate uncertainties). Is it really valid to claim this part of the proposed approach as novel? W2) I am not sure how significant the results on the DTU dataset are: a) The difference with respect to the best performing methods is less than 0.1 mm (see Tab. 1). Is the ground truth sufficiently accurate enough that such a small difference is actually noticeable / measurable or is the difference due to noise or randomness in the training process? b) Similarly, there is little difference between the results reported for the ablation study in Tab. 4. Does the claim "It can be seen from the table that our proposed modules improve in both accuracy and completeness" really hold? Why not use another dataset for the ablation study, e.g., the training set of Tanks & Temples or ETH3D? W3) I am not sure what is novel about the "novel geometric consistency loss (Geo Loss)". Looking at Eq. 10, it seems to simply combine a standard reprojection error in an image with a loss on the depth difference. I don't see how Eq. 10 provides a combination of both losses. W4) While the paper discusses prior work in Sec. 2, there is mostly no mentioning on how the paper under review is related to these existing works. In my opinion, a related work section should explain the relation of prior work to the proposed approach. This is missing. W5) There are multiple parts in the paper that are unclear to me: a) What is C in line 106? The term does not seem to be introduced. b) How are the hyperparameters in Sec. 4.1 chosen? Is their choice critical? c) Why not include UniMVSNet in Fig. 5, given that UniMVSNet also claims to generate denser point clouds (as does the paper under review)? d) Why use only N=5 images for DTU and not all available ones? e) Why is Eq. 9 a reprojection error? Eq. 9 measures the depth difference as a scalar and no projection into the image is involved. I don't see how any projection is involved in this loss. Overall, I think this is a solid paper that presents a well-engineered pipeline that represents the current state-of-the-art on a challenging benchmark. While I raised multiple concerns, most of them should be easy to address. E.g., I don't think that removing the novelty claim from W1 would make the paper weaker. The main exception is the ablation study, where I believe that the DTU dataset is too easy to provide meaningful comparisons (the relatively small differences might be explained by randomness in the training process. The following minor comments did not affect my recommendation: References are missing for Pytorch and the Adam optimizer. Post-rebuttal comments Thank you for the detailed answers. Here are my comments to the last reply: Q: Relationship to prior work. Thank you very much, this addresses my concern. A: Fig. 5 is not used to claim our method achieves the best performance among all the methods in terms of completeness, it actually indicates that our proposed method could help reconstruct complete results while keeping high accuracy (Tab. 1) compared with our baseline network [7] and the most relevant method [3]. In that context, we not only consider the quality of completeness but also the relevance to our method to perform comparison in Fig. 5. As I understand lines 228-236 in the paper, in particular "The quantitative results of DTU evaluation set are summarized in Tab. 1, where Accuracy and Completeness are a pair of official evaluation metrics. Accuracy is the percentage of generated point clouds matched in the ground truth point clouds, while Completeness measures the opposite. Overall is the mean of Accuracy and Completeness. Compared with the other methods, our proposed method shows its capability for generating denser and more complete point clouds on textureless regions, which is visualized in Fig. 5.", the paper seems to claim that the proposed method generates denser point clouds. Maybe this could be clarified? A: As a) nearly all the learning-based MVS methods (including ours) take the DTU as an important dataset for evaluation, b) the GT of DTU is approximately the most accurate GT we can obtain (compared with other datasets), c) the final results are the average across 22 test scans, we think that fewer errors could indicate better performance. However, your point about the accuracy of DTU GT is enlightening, and we think it's valuable future work. This still does not address my concern. My question is whether the ground truth is accurate enough that we can be sure that the small differences between the different components really comes from improvements provided by adding components. In this context, stating that "the GT of DTU is approximately the most accurate GT we can obtain (compared with other datasets)" does not answer this question as, even though DTU has the most accurate GT, it might not be accurate enough to measure differences at this level of accuracy (0.05 mm difference). If the GT is not accurate enough to differentiate in the 0.05 mm range, then averaging over different test scans will not really help. That "nearly all the learning-based MVS methods (including ours) take the DTU as an important dataset for evaluation" does also not address this question. Since the paper claims improvements when using the different components and uses the results to validate the components, I do not think that answering the question whether the ground truth is accurate enough to make these claims in future work is really an option. I think it would be better to run the ablation study on a dataset where improvements can be measured more clearly. Final rating I am inclined to keep my original rating ("6: Weak Accept: Technically solid, moderate-to-high impact paper, with no major concerns with respect to evaluation, resources, reproducibility, ethical considerations."). I still like the good results on the Tanks & Temples dataset and believe that the proposed approach is technically sound. However, I do not find the authors' rebuttals particularly convincing and thus do not want to increase my rating. In particular, I still have concerns about the ablation study as I am not sure whether the ground truth of the DTU dataset is accurate enough that it makes sense to claim improvements if the difference is 0.05 mm or smaller. Since this only impacts the ablation study, it is also not a reason to decrease my rating.	1). Is the ground truth sufficiently accurate enough that such a small difference is actually noticeable / measurable or is the difference due to noise or randomness in the training process? b) Similarly, there is little difference between the results reported for the ablation study in Tab.
39n570rxyO	ICLR_2025	This paper has weaknesses to address: * The major weakness of this paper is the extremely limited experiments section. There are many experiments, yet almost no explanation of how they're run or interpretation of the results. Most of the results are written like an advertisement, mostly just stating the method outperforms others. This leaves the reader unclear why the performance gains happen. Ultimately it's not clear when/why the findings would generalize. The result is that some claims appear to be quite overstated. For example, L423-L424 states "embeddings of domains with shared high-level semantics cluster together, as depicted in Appendix E.1. For example, embeddings of mono and stereo audio group closely, as do those of banking and economics." But this is cherry-picked---Temperature is way closer to Mono and Stereo Audio than Banking is to Economics. * Similarly, many important experimental details are missing or relegated to the Appendix, and the Appendix also includes almost no explanations or interpretations. For example, the PCA experiments in Figures 3, 7, and 8 aren't explained. * It's unclear how many variables actually overlap between training/testing, which seems to be a key element to make the model outperform others. Yet this isn't analyzed. Showing that others fail by ignoring other variables should be a key element of the experiments.	* Similarly, many important experimental details are missing or relegated to the Appendix, and the Appendix also includes almost no explanations or interpretations. For example, the PCA experiments in Figures 3, 7, and 8 aren't explained.
NIPS_2017_236	NIPS_2017	Weakness: 1. The real applications that the proposed method can be applied to seem to be rather restricted. It seems the proposed algorithm can only be used as a fast evaluation of residual error for 'guessing' or 'predetermining' the range of Tucker ranks, not the real ranks. 2. Since the sampling size 's' depends on the exponential term 2^[1/(e^2K-2)] (in Theorem 3.4), it could be very large if one requires the error tolerance 'e' to be relatively small and the order of tensor 'K' to be high. In that situation, there won't be much benefits to use this algorithm. Question: 1. In the Fig.1, why blue curve with large sample size 's=80' achieves the worst error compared with that of red curve with small sample size 's=20'? Overall, although proposed algorithm is theoretically sound, but appears be limited in applications for practical propose.	2. Since the sampling size 's' depends on the exponential term 2^[1/(e^2K-2)] (in Theorem 3.4), it could be very large if one requires the error tolerance 'e' to be relatively small and the order of tensor 'K' to be high. In that situation, there won't be much benefits to use this algorithm. Question:
UaZe4SwQF2	EMNLP_2023	- This paper is a bit difficult to follow. There are some unclear statements, such as motivation. - In the introduction, the summarized highlights need to be adequately elaborated, and the relevant research content of this paper needs to be detailed. - No new evaluation metrics are proposed. Only existing evaluation metrics are linearly combined. In the experimental analysis section, there needed to be an in-depth exploration of the reasons for these experimental results. - A case study should be added. - What are the advantages of your method compared to other evaluation metrics? Which needs to be emphasized in the motivation. - How do you evaluate the significance of model structure or metrics on the gender bias encoding of the model? Because you only conduct experiments in the FIBER model. Furthermore, you should conduct generalization experiments on the CLIP model or other models. - The citation format is chaotic in the paper. - There are some grammar mistakes in this paper, which could be found in “Typos, Grammar, Style, and Presentation Improvements”.	- No new evaluation metrics are proposed. Only existing evaluation metrics are linearly combined. In the experimental analysis section, there needed to be an in-depth exploration of the reasons for these experimental results.
NIPS_2021_1759	NIPS_2021	The extension from the EH model is natural. In addition, there has been literature that proves the power of FNN from a theoretical point of view, whereas this paper fails to make a review in this regard. Among other works, Schmidt-Hieber (2020) gave an exact upper bound of the approximation error for FNNs involving the least-square loss. Since the DeepEH optimizes a likelihood-based loss, this paper builds up its asymptotic properties by following assumptions and proofs of Theorems 1 and 2 in Schmidt-Hieber (2020) as well as theories on empirical processes. Additional Feedback: 1) In the manuscript, P mostly represents a probability but sometimes for a cumulative distribution function (e.g., Eqs. (3) and (4) and L44, all in Appendix), which leads to confusion. 2). The notation K is abused too: it is used both for a known kernel function (e.g., L166) and the number of layers (e.g., L176). 3). What is K b in estimating baseline hazard (L172)?	2). The notation K is abused too: it is used both for a known kernel function (e.g., L166) and the number of layers (e.g., L176).
NIPS_2022_2005	NIPS_2022	Originality: Main Result 1 relies on known formulas for low-rank matrix factorization. It is not clearly explained what are the major technical challenges, if any, in obtaining this result. Clarity: The community labels in (3) and the model (4) are such that the E X does not have sparse columns if k is small. For this reason, I feel the paper is more about the large k version of the sparse clustering problem. Edit 08/19: After discussion with authors, the previous point is resolved. Clarity: From the main text alone, it is unclear how the information-theoretic threshold is obtained. The formula of the MSE is difficult to interpret, so I can't see if the threshold is a consequence of this. Some further explanation is needed here. Quality/Clarity: It is difficult to assess the rigour of both main results, especially Main Result 2. This is because the appendix is not organized in a conventional way with a clearly demarcated proof of Main Results 1 and 2. For Main Result 2, I do not see in the Appendix any explanation of how the asymptotic algorithmic MSE is computed. I only see plots rather than arguments. I also do not see any derivation of the Bayes-optimal MSE or reference to known (rigorous) formulas. Minor issues Line 39: Equation (2) defines vectors that are (i) standard Gaussian with probability ρ OR (ii) the zero vector with probability 1 − ρ . I think what is meant is for there to be a random subset of zero entries, with the rest of the entries being Gaussian. Main Theorem 1: Please take a careful proofread over this. Here v ∗ , u ∗ , and w have not been defined in (10). Also Z u does not appear in (10). Consider making the boundaries bolder in Figure 1. Also I found the color of λ i t to be hard on the eyes Line 70: Typo "statitiscal" Line 85: Typo "analyis" Line 91: Typo "Statistics", change to "statistics" Line 111: Change to "In particular, [10] conjectured and [11] proved..."` Line 143-144: This comment is hard to understand because (38) is in the Appendix, and then I'm having trouble seeing the connection to (6). Line 195: Typo "Invextigate" Line 261: Replace "Despite of this fact" with "Despite this fact" Summary of score My score is due to concerns mostly about the rigor and partially about the novelty of this submission. I also feel there is a lack of clarity in explaining how the main results are obtained. Update of score 08/19 The authors' rebuttal addressed my concerns about rigor and somewhat about novelty. I agree with other reviewers that the strengths and technical challenges of this paper are not highlighted enough in the main text. I also think further clarity is needed on the level of rigor and the asymptotic regime to which the results apply (which seems to be for k growing large and rho going to 0). I have raised my overall score from 3 to 4 because further serious revision is needed. I have also upgraded the soundness from 1 to 2. 1. I agree with the authors' assessment that there are no apparent potential negative societal impacts. 2. The weak recovery problem studied here is primarily of theoretical interest, and it is not clear if the AMP algorithm is useful for non-Gaussian problems. So practical impact may be limited.	2. The weak recovery problem studied here is primarily of theoretical interest, and it is not clear if the AMP algorithm is useful for non-Gaussian problems. So practical impact may be limited.
NIPS_2017_349	NIPS_2017	- The paper is not self contained Understandable given the NIPS format, but the supplementary is necessary to understand large parts of the main paper and allow reproducibility. I also hereby request the authors to release the source code of their experiments to allow reproduction of their results. - Use of deep-reinforcement learning is not well motivated The problem domain seems simple enough that a linear approximation would have likely sufficed? The network is fairly small and isn't "deep" either. - > We argue that such a mechanism is more realistic because it has an effect within the game itself, not just on the scores This is probably the most unclear part. It's not clear to me why the paper considers one to be more realistic than the other rather than just modeling different incentives? Probably not enough space in the paper but actual comparison of learning dynamics when the opportunity costs are modeled as penalties instead. As economists say: incentives matter. However, if the intention was to explicitly avoid such explicit incentives, as they _would_ affect the model-free reinforcement learning algorithm, then those reasons should be clearly stated. - Unclear whether bringing connections to human cognition makes sense As the authors themselves state that the problem is fairly reductionist and does not allow for mechanisms like bargaining and negotiation that humans use, it's unclear what the authors mean by ``Perhaps the interaction between cognitively basic adaptation mechanisms and the structure of the CPR itself has more of an effect on whether self-organization will fail or succeed than previously appreciated.'' It would be fairly surprising if any behavioral economist trying to study this problem would ignore either of these things and needs more citation for comparison against "previously appreciated". * Minor comments Line 16: > [18] found them... Consider using \citeauthor{} ? Line 167: > be the N -th agentâs should be i-th agent? Figure 3: Clarify what the `fillcolor` implies and how many runs were the results averaged over? Figure 4: Is not self contained and refers to Fig. 6 which is in the supplementary. The figure is understandably large and hard to fit in the main paper, but at least consider clarifying that it's in the supplementary (as you have clarified for other figures from the supplementary mentioned in the main paper). Figure 5: - Consider increasing the axes margins? Markers at 0 and 12 are cut off. - Increase space between the main caption and sub-caption. Line 299: From Fig 5b, it's not clear that \|R\|=7 is the maximum. To my eyes, 6 seems higher.	- Unclear whether bringing connections to human cognition makes sense As the authors themselves state that the problem is fairly reductionist and does not allow for mechanisms like bargaining and negotiation that humans use, it's unclear what the authors mean by ``Perhaps the interaction between cognitively basic adaptation mechanisms and the structure of the CPR itself has more of an effect on whether self-organization will fail or succeed than previously appreciated.'' It would be fairly surprising if any behavioral economist trying to study this problem would ignore either of these things and needs more citation for comparison against "previously appreciated".
EODzbQ2Gy4	ICLR_2024	- Wording is overly exaggerated in the conclusion: " ... our pioneering contributions herald a new era in robotic adaptability ... ". Word choice is a bit flamboyant in multiple places in the writing. - This paper seems to only be tackle in-distribution task-transfer where typically transfer is thought of as learning task A can help with a completely different task B. - Additionally, object shape transfer is mentioned as one of the applications, but only object pose transfer is considered in the experiments. - Reward function seems to be very hand-engineered. How many data points is required to fit the Q-network with the pretraining dataset? Is this dataset hard to collect? - Is there any comparison with other works that use differentiable physics for task transfer? - One of the claimed novelty in this work is the path planning algorithm for sampling new subtasks. Can you include more comparisons against other path planning algorithms in classical literature like RRT, A*, sampling-based methods, etc? Typo and writing comments: Figure 1: Sub-Task Accomplishment ... Section 5.2 MAML: repeated the word "application" Confusing last sentence in Section 5.1.4. Section 5.3, why is this transfer task considered "innovative"?	- Wording is overly exaggerated in the conclusion: " ... our pioneering contributions herald a new era in robotic adaptability ... ". Word choice is a bit flamboyant in multiple places in the writing.
Va4t6R8cGG	ICLR_2024	- This paper does not seem to be the first work of fully end-to-end spatio-temporal localization, while TubeR has proposed to directly detect an action tubelet in a video by simultaneously performing action localization and recognition before. This weakens the novelty of this paper. The authors claim the differences with TubeR but the most significant difference is that the proposed method is much less complex. - The symbols in this paper are inconsistent, e.g., b. - The authors need to perform ablation experiments to compare the proposed method with other methods (e.g., TubeR) in terms of the number of learnable parameters and GFLOPs.	- The authors need to perform ablation experiments to compare the proposed method with other methods (e.g., TubeR) in terms of the number of learnable parameters and GFLOPs.
ICLR_2021_2804	ICLR_2021	are listed as follows. Strengths: The paper is easy to read, and the proposed idea is also easy to follow. Figure 1 can help the understanding of the proposed model. The proposed model does not need the manual labeled relationship between semantic knowledge and target categories, and this may further reduce the supervision for knowledge graph construction. Weaknesses: Incomplete comparison with existing works: the authors should list a more complete comparison table to compare the results of existing works. Some existing works can perform competitive or even superior results compared with the proposed model under the same feature backbone (ResNet-12). mini-ImageNet tiered-ImageNet 1-shot 5-shot 1-shot 5-shot Proposed 63.29+-0.71%. 80.12+-0.22% 66.69+-0.75%. 83.04+-0.61% CAN[1] 63.85+-0.48%. 79.44+-0.34% 69.89+-0.51%. 84.23+-0.37% CAN +T[1] 67.19+-0.55%. 80.64+-0.35% 73.21+-0.58%. 84.93+-0.38% Comparison with unitary modality methods is misleading, as these baseline methods do not use any external information for the training and inference. The proposed method should consider other cross-modal few-shot classification works as baseline methods. As the proposed model contains several modules, such as knowledge graph construction, graph neural network, and other few linear layers between components, this makes the reader hard to understand which module is crucial. It will be great if the authors could provide an ablation study to verify the effectiveness of each module in the next version of this paper. For example, the authors could provide studies like 1) what is the performance if the semantic information is removed in the knowledge graph, or 2) how the number of graph neural layers affects the overall performance. Overall, the paper is easy to read. The idea of integrating semantic information in few-shot classification is interesting while it has been widely explored in existing works. Given the reported results of the proposed model and lack of analyses in the proposed model, I am inclined to the score "Ok but not good enough - rejection". [1] “Cross Attention Network for Few-shot Classification”, Hou et al., NeurIPS ‘19	2) how the number of graph neural layers affects the overall performance. Overall, the paper is easy to read. The idea of integrating semantic information in few-shot classification is interesting while it has been widely explored in existing works. Given the reported results of the proposed model and lack of analyses in the proposed model, I am inclined to the score "Ok but not good enough - rejection". [1] “Cross Attention Network for Few-shot Classification”, Hou et al., NeurIPS ‘19
NIPS_2018_125	NIPS_2018	- Some missing references and somewhat weak baseline comparisons (see below) - Writing style needs some improvement, although, it is overall well written and easy to understand. Technical comments and questions: - The idea of active feature acquisition, especially in the medical domain was studied early on by Ashish Kapoor and Eric Horvitz. See https://www.microsoft.com/en-us/research/wp-content/uploads/2016/12/NIPS2009.pdf There is also a number of missing citations to work on using MDPs for acquiring information from external sources. Kanani et al, WSDM 2012, Narsimhan et al, "Improving Information Extraction by Acquiring External Evidence with Reinforcement Learning", and others. - section 3, line 131: "hyperparameter balancing the relative importances of two terms is absorbed in the predefined cost". How is this done? The predefined cost could be externally defined, so it's not clear how these two things interact. - section 3.1, line 143" "Then the state changes and environment gives a reward". This is not true of standard MDP formulations. You may not get a reward after each action, but this makes it sound like that. Also, line 154, it's not clear if each action is a single feature or the power set. Maybe make the description more clear. - The biggest weakness of the paper is that it does not compare to simple feature acquisition baselines like expected utility or some such measure to prove the effectiveness of the proposed approach. Writing style and other issues: - Line 207: I didn't find the pseudo code in the supplementary material - The results are somewhat difficult to read. It would be nice to have a more cleaner representation of results in figures 1 and 2. - Line 289: You should still include results of DWSC if it's a reasonable baseline - Line 319: your dollar numbers in the table don't match! - The paper will become more readable by fixing simple style issues like excessive use of "the" (I personally still struggle with this problem), or other grammar issues. I'll try and list most of the fixes here. 4: joint 29: only noise 47: It is worth noting that 48: pre-training is unrealistic 50: optimal learning policy 69: we cannot guarantee 70: manners meaning that => manner, that is, 86: work 123: for all data points 145: we construct an MDP (hopefully, it will be proper, so no need to mention that) 154: we assume that 174: learning is a value-based 175: from experience. To handle continuous state space, we use deep-Q learning (remove three the's) 176: has shown 180: instead of basic Q-learning 184: understood as multi-task learning 186: aim to optimize a single 208: We follow the n-step 231: versatility (?), we perform extensive 233: we use Adam optimizer 242: We assume uniform acquisition cost 245: LSTM 289: not only feature acquisition but also classification. 310: datasets 316: examination cost?	- The biggest weakness of the paper is that it does not compare to simple feature acquisition baselines like expected utility or some such measure to prove the effectiveness of the proposed approach. Writing style and other issues:
NIPS_2021_2123	NIPS_2021	This paper still existed some problems that I hope the authors could illustrate in a clearer way. The authors argued that they were the first time to directly training deep SNNs with more than 100 layers. I don’t think this is the core contribution in this paper, because of the residual block, the spiking could be deeper. In my opinion, SEW structure is the most important point in this paper, and directly training a 50-layer and 100-layer snn is not a huge breakthrough. Otherwise, if they could give a more detailed analysis about why other methods can’t train a 100-layer snn except section 3.2, it may be more reasonable. Why the RBA block can be seen as a special case of the SEW block? I mean SEW is another kind of RBA with binary input and output. Equ. 11 is wonderful, how about other bit operations? Fig. 5 a seems strange, please give more explanations. When the input is aer format, how did you deal with DVS input? If you can analyze the energy consumption as reference[15] did, this paper would be more solid.	11 is wonderful, how about other bit operations? Fig. 5 a seems strange, please give more explanations. When the input is aer format, how did you deal with DVS input? If you can analyze the energy consumption as reference[15] did, this paper would be more solid.
ICLR_2022_21	ICLR_2022	However, some key architectural details can be clarified further for full reproducibility and analysis. Specifically: 1. How are historical observations combined with inputs known over all time given differences in sequence lengths (L vs L+M)? The text mentions separate embedding and addition with positional encoding, but clarifications on how the embeddings are combined and fed into the CSCM are needed. 2. Can each node attend to its own lower-level representation? From equation 2, it seems to be that only neighbouring nodes are attended to, based on the description of N_l^(s). 3. Do the authors have any guidelines on how to select S/A/C (and consequently N) for a given receptive field L? In addition, while the ablation analysis tests the impact of changing CSCM architectures, it would be good to evaluate the base performance without the PAM to determine the value added by attention. This would also provide a simple comparison vs dilated CNNs which have been used successfully in time series forecasting applications (e.g. WaveNet). Finally, could I double check which dataset was used for the ablation analysis as well? I seem to be having some difficulty lining the numbers in Tables 4-6 up with Table 3.	1. How are historical observations combined with inputs known over all time given differences in sequence lengths (L vs L+M)? The text mentions separate embedding and addition with positional encoding, but clarifications on how the embeddings are combined and fed into the CSCM are needed.
50RNY6uM2Q	ICLR_2025	1. As mentioned in the article itself, the introduction of multi-granularity and multi-scale to enhance model performance is a common approach to convolutional networks, and merely migrating this approach to the field of MLMs is hardly an innovative contribution. Some of the algorithms used in the article from object detection only do some information enhancement on the input side, while many MLMs can already accomplish the object detection task by themselves nowadays. 2. The scores achieved on both the MMBench as well as SEEDBench datasets, while respectable, are not compared to some of the more competitive models. I identified MMB as version 1 and SEEDBench as Avg based on the scores of Qwen-VL and MiniCPM-V2, and there are a number of scores on both leaderboards that are higher than the scores of MG-LLaVA work, eg. Honeybee (Cha et al., 2024), AllSeeing-v2 (Wang et al. 2024) based on Vicuna-13b at MMB-test. and then you can also find a lot of similar models with higher scores on the same substrate. 3. In addition to Perception Benchmarks. this problem can also be found in Visual QA and Video QA. such as on the MSRVTT-QA dataset. there are already many models with very high scores in 2024. Some of them also use some methods to improve the model's ability on fine-grained tasks. eg. Flash-VStream (Zhang et al. 2024) Monkey (Li et al. 2023). The article does not seem to compare these new 2024 models. To summarize, I think the approach proposed in the article is valid, but MG-LLaVA does not do the job of making a difference, either from an innovation perspective or from a performance perspective. [1] Cha, Junbum, et al. "Honeybee: Locality-enhanced projector for multimodal llm." Proceedings of the IEEE/CVF Conference on Computer Vision and Pattern Recognition. 2024. [2] Wang, Weiyun, et al. "The all-seeing project v2: Towards general relation comprehension of the open world." arXiv preprint arXiv:2402.19474 (2024). [3] Zhang, Haoji, et al. "Flash-VStream: Memory-Based Real-Time Understanding for Long Video Streams." arXiv preprint arXiv:2406.08085 (2024). [4] Li, Zhang, et al. "Monkey: Image resolution and text label are important things for large multi-modal models." Proceedings of the IEEE/CVF Conference on Computer Vision and Pattern Recognition. 2024.	1. As mentioned in the article itself, the introduction of multi-granularity and multi-scale to enhance model performance is a common approach to convolutional networks, and merely migrating this approach to the field of MLMs is hardly an innovative contribution. Some of the algorithms used in the article from object detection only do some information enhancement on the input side, while many MLMs can already accomplish the object detection task by themselves nowadays.
ICLR_2023_2286	ICLR_2023	1. The paper is poorly organized. It is hard to quickly get the motivations and main ideas of the proposed methods. 2. The thermal sensor and environment setting for data collection is not described in details. From Figure 2, why is the quality of thermal image significantly higher than RegDB and SYSU-MM01 ? Does the thermal sensor or capturing time cause it? 3. The paper presents a transformer-based network as backbone, what is the benefits over the CNN-based backbones in traditional methods? The reason using such a transformer-based method is not clearly discussed. 4. The proposed multi-task triplet loss is not clearly clarified. It is strongly to re-organize the part and make a proof-reading. In addition, It seems there is mistake in Eq. (1). I suppose a max( x,0) is lost for both terms in $L_{mtri}$. 5. The sensitivity of hyper-parameters such as $m_1$, $m_2$, $\lambda$ is not discussed. In particular, their values are not specified in the paper. 6. There are lots of grammar mistakes, typos and description blurs that makes the paper hard to follow. It is strongly to find some experts to make a proofreading.	5. The sensitivity of hyper-parameters such as $m_1$, $m_2$, $\lambda$ is not discussed. In particular, their values are not specified in the paper.
NIPS_2021_2338	NIPS_2021	Weakness: 1. Regarding the adaptive masking part, the authors' work is incremental, and there have been many papers on how to do feature augmentation, such as GraphCL[1], GCA[2]. The authors do not experiment with widely used datasets such as Cora, Citeseer, ArXiv, etc. And they did not compare with better baselines for node classification, such as GRACE[3], GCA[2], MVGRL[4], etc. I think this part of the work is shallow and not enough to constitute a contribution. The authors should focus on the main contribution, i.e., graph-level contrastive learning, and need to improve the node-level augmentation scheme. 2. In the graph classification task, the compared baseline is not sufficient, such as MVGRL[4], gpt-gnn[5] are missing. I hope the authors could add more baselines of graph contrastive learning and test them on some common datasets. 3. I am concerned whether the similarity-aware positive sample selection will accelerate GNN-based encoder over-smoothing, i.e., similar nodes or graphs will be trained with features that converge excessively and discard their own unique features. In addition, whether selecting positive samples in the same dataset without introducing some perturbation noise would lead to lower generalization performance. The authors experimented with the transfer performance of the model on the graph classification task, though it still did not allay my concerns about the model generalization. I hope there will be more experiments on different downstream tasks and across different domains. Remarks: 1. The authors seem to have over-compressed the line spacing and abused vspace. 2. Table 5 is collapsed. [1] Y. You, T. Chen, Y. Sui, T. Chen, Z. Wang, and Y. Shen, “Graph contrastive learning with augmentations,” Advances in Neural Information Processing Systems, vol. 33, 2020. [2] Y. Zhu, Y. Xu, F. Yu, Q. Liu, S. Wu, and L. Wang, “Graph contrastive learning with adaptive augmentation,” arXiv preprint arXiv:2010.14945, 2020. [3] Y. Zhu, Y. Xu, F. Yu, Q. Liu, S. Wu, and L. Wang, “Deep graph contrastive representation learning,” arXiv preprint arXiv:2006.04131, 2020. [4] Hassani, Kaveh, and Amir Hosein Khasahmadi. "Contrastive multi-view representation learning on graphs." International Conference on Machine Learning. PMLR, 2020. [5] Hu, Ziniu, et al. "Gpt-gnn: Generative pre-training of graph neural networks." Proceedings of the 26th ACM SIGKDD International Conference on Knowledge Discovery & Data Mining. 2020.	3. I am concerned whether the similarity-aware positive sample selection will accelerate GNN-based encoder over-smoothing, i.e., similar nodes or graphs will be trained with features that converge excessively and discard their own unique features. In addition, whether selecting positive samples in the same dataset without introducing some perturbation noise would lead to lower generalization performance. The authors experimented with the transfer performance of the model on the graph classification task, though it still did not allay my concerns about the model generalization. I hope there will be more experiments on different downstream tasks and across different domains. Remarks:
NIPS_2020_1185	NIPS_2020	- The theory (thm 2, cor 1) on the representational power of SMPs is only for simple unlabeled graphs. Is there any similar result for graphs with node and/or edge features ? - The experiments are quite limited. I wish to have seen SMPs in the context of graphs with node and edge features and on standard benchmarks used by GCNs/GIN/GAT models. - how good is SMP at counting cycles ? - is fast SMP less expressive than SMP ? I wish to have seen more discussion on the power of different architectures. - are, in the limit of using sufficiently many layers, all embeddings of node j at each node i becoming equal ? Can this be formally proved ? If this is not true, then isn't it a weakness that each node can learn a potentially different representation of all the nodes in the graph ? - how well is fast SMP perming on the cycle detection task ? ====================== Later edit: I agree with other reviewers' comments on the lack of powerful equivariant baselines and I do believe that the current experimental setup is limited. I am lowering my score as a consequence.	- is fast SMP less expressive than SMP ? I wish to have seen more discussion on the power of different architectures.
ICLR_2023_2163	ICLR_2023	Fully training group labels baselines could include more recent methods such as SGDRO (non-flat version of GDRO proposed in Goel et al.). There is a misleading sentence on page 3 when describing the Waterbirds dataset: “The bird images are then modified with either a water or land background.” There is no “modification” involved, in the dataset the birds are already placed either on water or land background (this is a minor note, but should be revisited). The main weaknesses are all in the “Experiments” section. 1) Although the hyperparameters are fixed, some ablation is still required (for example the regularisation in the second stage for the CivilComments dataset). 2) In Tables 1 and 2 it is not clear what the results are, is it correct to assume they are the mean and std. performances over three different initialization seeds? 3) The results in Tables 1 and 2 are not correct, CROIS is using the validation set for training in the second stage, not only for model selection. For the datasets considered, the validation set has the same distribution as the test set, it does not seem correct to talk about “group shift” anymore. 4) Table 2 should also include the average test accuracy to show the trade-off between average and worst-case performances when varying the size of the validation set. Also, why is the std. not reported here? 5) Table 3 shows promising results, but the best fraction “p” is a hyperparameter that should be tuned using the worst-group performance on the validation set, like the regularization term for GDRO. Its behaviour is not linear (e.g. the more the better) nor consistent across datasets. For example, in both text datasets, only one fraction produces better results than the GDRO baseline. Here, I disagree with the statement “In practice, p is not a parameter to choose (there’s no reason to throw away group labels) but rather is limited by the resources available to obtain group labels”: using p=0.5 is often worse than using p=0.3. 6) To obtain robust results, it would have been better to evaluate the methods across different splits of train-val-test, not simply different initialisation seeds.	6) To obtain robust results, it would have been better to evaluate the methods across different splits of train-val-test, not simply different initialisation seeds.
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.	6. The first two bullets about contributions (at the end of the intro) can be combined together.
vg55TCMjbC	EMNLP_2023	- Although the situations are checked by human annotators, the seed situations are generated by ChatGPT. The coverage of situation types might be limited. - The types of situations/social norms (e.g., physical/psychological safety) are not clear in the main paper. - It’s a bit hard to interpret precision on NormLens-MA, where the different labels could be considered as gold.	- The types of situations/social norms (e.g., physical/psychological safety) are not clear in the main 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?	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:
NIPS_2016_221	NIPS_2016	weakness: 1. To my understanding, two aspects which are the keys to the segmentation performance are: (1) The local DNN evaluation of shape descriptors in terms of energy, and (2) The back-end guidance of (super)voxel agglomeration. Although experiment showed gains of the proposed method over GALA, it is yet not clear enough which part is the major contributor of such gain. The original paper of GALA used methods different from this paper (3D-CNN) to generate edge probability maps. Is the edge map extraction framework in this paper + GALA a fair enough baseline? It would be great if such edge map can also be visualized. 2. The proposed method to some extent is not that novel. The idea of generating or evaluating segmentation masks with DNN has been well studied by the vision community in many general image segmentation tasks. In addition, the idea of greedily guiding the agglomeration of (super)voxels by evaluating energies pretty much resembles many bottom-up graph-theoretic merging in early segmentation methods. The authors, however, failed to mention and compare with many related works from the general vision community. Although the problem general image segmentation somewhat differs from the task of this paper, showing certain results on general image segmentation datasets (like the GALA paper) and comparing with state-of-the-art general segmentation methods may give a better view of the performance of the proposed method. 3. Certain parts did not provide enough explanation, or are flooded by too much details and fail to give the big picture clearly enough. For example in Appendix B Definition 2, when explaining the relationship between shape descriptor and connectivity region, some graphical illustrations would have helped the readers understanding the ideas in the paper much easier and better. ----------------------------------------------------------------------------- Additional Comments after Discussion Upon carefully reading the rebuttal and further reviewing some of the related literature, I decide to down-grade scores on novelty and impact. Here are some of the reasons: 1. I understand this paper targets a problem which somewhat differs from general segmentation problems. And I do very much appreciate its potential benefit to the neuroscience community. This is indeed a plus for the paper. However, an important question is how much this paper can really improve over the existing solutions. Therefore, to demonstrate that the algorithm is able to correctly find closed contours, and really show stronger robustness against weak boundaries (This is especially important for bottom up methods), the authors do need to refer to more recent trends in the vision community. 2. I noticed one reference "Maximin affinity learning of image segmentation, NIPS 2009" cited in this paper. The paper proposed a very elegant solution to affinity learning. The core ideas proposed in this paper, such as greedy merging, Rand Index like energy function show strong connections to the cited paper. The maximin affinity is basically the weakest edge along a minimum spanning tree (MST), and we know greedy region merging is also based on cutting weakest edges on a MST. The slight difference is the author proposed the energy term at a lot of positions and scales but the previous paper has a single energy term for the global image. In addition cited paper also addressed a similar problem in the experiment. However, the authors not only did not include the citation as an experimental baseline, but also failed to provide detailed discussions on the relation between the two works. 3. The authors argued for greedy strategy, claiming this is better than factorizable energies. "By sacrificing factorization, we are able to achieve the rich combinatorial modeling provided by the proposed 3d shape descriptors." I guess what the authors mean is they are putting more emphasis on local predictions. But this statement is not solidly justified by the paper. In addition, although to some extent I could understand this argument (local prediction indeed seems important because the size of cells vs volume are much smaller than segments vs whole image in general segmentation), there are significant advances on making pretty strong local predictions from the general vision community using deep learning, which the authors fail to mention and compare. I think overall the paper addressed an interesting problem and indeed showed solid research works. However it will better if the authors could better address contemporary segmentation literature and further improve the experiments.	1. I understand this paper targets a problem which somewhat differs from general segmentation problems. And I do very much appreciate its potential benefit to the neuroscience community. This is indeed a plus for the paper. However, an important question is how much this paper can really improve over the existing solutions. Therefore, to demonstrate that the algorithm is able to correctly find closed contours, and really show stronger robustness against weak boundaries (This is especially important for bottom up methods), the authors do need to refer to more recent trends in the vision community.
ICLR_2022_2754	ICLR_2022	I feel the motivation of the work is confusing. I can understand the authors want to improve CQL somehow further. But it is never made clear: what existing problems are and why they matter; Is it the lower bound on the exiting CQL is too loose? Why is improving the bound important? what is the effect you want to achieve? Is it an offline algorithm that can learn a better policy from data generated by a poor behavior policy? The contribution is incremental, and I doubt the significance. As the paper cited in section 2.2, Kumar et al. (2020) propose to penalize the actions not described by the dataset, which enables a general definition of \mu. Note that the additional weighting scheme can be essentially thought of as a new type of \mu. I don’t see a clear difference between (2) and (3). Both can be considered as the specially designed action sampling distribution. Why is theorem 1 useful? If I understand correctly, the key thing you want to say is the additional weighting can provide a tighter bound for OOD state-action pairs or those not close to the dataset? But the first step should be figuring out the effects of having a tight/loose bound. Does it hurt optimality/convergence rate/generalization…? Even partially answering this question can better motivate the reweighting approach. I believe the proof of the theorem is a simple modification from the existing CQL work. The choice of the weighting scheme lacks justification. An intuitive choice is the RBF function. Furthermore, according to theorem 1, the proposed weighting is useful only when the action is OOD, i.e., the weight is 1; when the action is ID, weight should be 0, but your weighting scheme does not give zero? Section 4.1, the proposed method comes out suddenly. Is there any reason to choose normalizing flows? Of course, normalizing flows is a good method enabling both efficient sampling and density evaluation. In your algorithm, you only need to evaluate the density but not to sample. There should be plenty of other choices. When testing ideas, it is more natural to start with some simple methods. What is the purpose of section 4.3? I expect to see how various concrete choices of the weighting scheme can affect the distance (e.g., KL divergence) between the learned policy and the behavior policy. The experiments. 1. more random seeds should be tested (figure 1) — it is hard to distinguish algorithms from the current learning curves. Readers cannot see a clear message from them. 2. I expect more baselines to be compared and more domains to be tested. As I mentioned, the choices of the weighting and the way of learning density functions are not strongly motivated. In this case, I have to ask for stronger empirical results: baselines with other design choices and more domains. 3. The experiments in Fig 2 are incomplete. Why are there no experiments for half cheetah and walker with expert data? 4. Please provide reproducing details. The abstract says, “… with a strong theoretical guarantee.” I don’t think there is any strong theory in the paper. Page 3. Last paragraph. The criticism towards using empirical dataset distribution for \hat{pi}_\beta does not make sense to me. When the state/action is continuous, the empirical estimation should be kernel density estimation, which is a consistent estimator for estimating empirical distributions. The kernel can be chosen as smooth, so the KDE should have support everywhere. Minor: there is a nontrivial number of grammar issues/typos. Please double-check. Many sentences are confusing or logically disconnected. e.g., in the abstract, “A compromise between enhancing …. To alleviate this issue, … ” what issue? “Improving the learning process.” In what sense? Higher sample efficiency? “Indeed, the lack of information … ” what information? Why does it provoke overestimation? I believe saying “based on the amount of information collected” is inaccurate because the paper does not really introduce any information measurement.	2. I expect more baselines to be compared and more domains to be tested. As I mentioned, the choices of the weighting and the way of learning density functions are not strongly motivated. In this case, I have to ask for stronger empirical results: baselines with other design choices and more domains.
NIPS_2016_153	NIPS_2016	weakness of previous models. Thus I find these results novel and exciting.Modeling studies of neural responses are usually measured on two scales: a. Their contribution to our understanding of the neural physiology, architecture or any other biological aspect. b. Model accuracy, where the aim is to provide a model which is better than the state of the art. To the best of my understanding, this study mostly focuses on the latter, i.e. provide a better than state of the art model. If I am misunderstanding, then it would probably be important to stress the biological insights gained from the study. Yet if indeed modeling accuracy is the focus, it's important to provide a fair comparison to the state of the art, and I see a few caveats in that regard: 1. The authors mention the GLM model of Pillow et al. which is pretty much state of the art, but a central point in that paper was that coupling filters between neurons are very important for the accuracy of the model. These coupling filters are omitted here which makes the comparison slightly unfair. I would strongly suggest comparing to a GLM with coupling filters. Furthermore, I suggest presenting data (like correlation coefficients) from previous studies to make sure the comparison is fair and in line with previous literature. 2. The authors note that the LN model needed regularization, but then they apply regularization (in the form of a cropped stimulus) to both LN models and GLMs. To the best of my recollection the GLM presented by pillow et al. did not crop the image but used L1 regularization for the filters and a low rank approximation to the spatial filter. To make the comparison as fair as possible I think it is important to try to reproduce the main features of previous models. Minor notes: 1. Please define the dashed lines in fig. 2A-B and 4B. 2. Why is the training correlation increasing with the amount of training data for the cutout LN model (fig. 4A)? 3. I think figure 6C is a bit awkward, it implies negative rates, which is not the case, I would suggest using a second y-axis or another visualization which is more physically accurate. 4. Please clarify how the model in fig. 7 was trained. Was it on full field flicker stimulus changing contrast with a fixed cycle? If the duration of the cycle changes (shortens, since as the authors mention the model cannot handle longer time scales), will the time scale of adaptation shorten as reported in e.g Smirnakis et al. Nature 1997.	1. Please define the dashed lines in fig. 2A-B and 4B.
ICLR_2022_2196	ICLR_2022	weakness] Modeling: The rewards are designed based on a discriminator. As we know, generative adversarial networks are not easy to train since generative networks and discriminative networks are trained alternatively. In the proposed method, the policy network and the discriminator are trained alternatively. I doubt if it is easy to train the model. I would like to see the training curves for rewards value. The detailed alignment function used in Eq. (1) and Eq. (3) need to be provided. Experiment: - The results are not satisfying. In the experiment, the generation quality of the proposed method is not good as traditional generative networks in terms of FID. In the image parsing part, the results are far behind the compared methods. - Since the results are not comparable to the existing methods, there seems not too much significance for the proposed methods.	- Since the results are not comparable to the existing methods, there seems not too much significance for the proposed methods.
53kW6e1uNN	ICLR_2024	1. Limited novelty. The paper seems like a straightforward application of existing literature, specifically the DeCorr [1] that focuses on general deep graph neural networks, in a specific application domain. The contribution of this study is mainly the transposition of DeCorr's insights into graph collaborative filtering, with different datasets and backbones. Although modifications like different penalty coefficients for users and items are also proposed, the whole paper still lack enough insights about what are unique challenges of overcorrelation in recommender systems. 2. It could be better if one additional figure could be illustrated, i.e., how Corr and SMV metrics evolve with the application of additional network layers—mirroring the Figure 2, but explicitly showcasing the effects of the proposed method—the authors could convincingly validate their auxiliary loss function's efficacy. 3. Presentation issues. The y-axis labels of Figure 2 lack standardization, e.g., 0.26 vs. 0.260 vs. 2600 vs. .2600. [1] Jin et al. Feature overcorrelation in deep graph neural networks: A new perspective. KDD 2022.	1. Limited novelty. The paper seems like a straightforward application of existing literature, specifically the DeCorr [1] that focuses on general deep graph neural networks, in a specific application domain. The contribution of this study is mainly the transposition of DeCorr's insights into graph collaborative filtering, with different datasets and backbones. Although modifications like different penalty coefficients for users and items are also proposed, the whole paper still lack enough insights about what are unique challenges of overcorrelation in recommender systems.
NIPS_2017_575	NIPS_2017	- While the general architecture of the model is described well and is illustrated by figures, architectural details lack mathematical definition, for example multi-head attention. Why is there a split arrow in Figure 2 right, bottom right? I assume these are the inputs for the attention layer, namely query, keys, and values. Are the same vectors used for keys and values here or different sections of them? A formal definition of this would greatly help readers understand this. - The proposed model contains lots of hyperparameters, and the most important ones are evaluated in ablation studies in the experimental section. It would have been nice to see significance tests for the various configurations in Table 3. - The complexity argument claims that self-attention models have a maximum path length of 1 which should help maintaining information flow between distant symbols (i.e. long-range dependencies). It would be good to see this empirically validated by evaluating performance on long sentences specifically. Minor comments: - Are you using dropout on the source/target embeddings? - Line 146: There seems to be dangling "2"	- The proposed model contains lots of hyperparameters, and the most important ones are evaluated in ablation studies in the experimental section. It would have been nice to see significance tests for the various configurations in Table 3.
ICLR_2021_1465	ICLR_2021	1. The complexity analysis is insufficient. In the draft, the author only provide the rough overall complexity. A better way is to show the comparison between the proposed method and some other methods, including the number of model parameter and network forwarding time. 2. In the converting of point cloud to concentric spherical signal, the Gaussian radial basis function is adopted to summarize the contribution of points. Is there any other function that can accomplish this job? The reviewer would like to the discussion about this. 3. The Figure 2 is a little ambiguous, where some symbols are not explained clearly. And the reviewer is curious about that whether there is information redundancy and interference in the multi-sphere icosahedral discretization process. 4. There are some typos in the draft. The first is the wrong use of "intra-sphere" and "inter-sphere". The second is the use of two consecutive "stacking" in the Spherical Discretization subsection. Please check the full text carefully. 5. The center choice of the concentric spheres should be discussed both theoretically and experimentally. In the opinion, the center of spheres play a important role in the representation capturing of 3D point clouds in a sphere convolution manner.	3. The Figure 2 is a little ambiguous, where some symbols are not explained clearly. And the reviewer is curious about that whether there is information redundancy and interference in the multi-sphere icosahedral discretization process.
NIPS_2017_585	NIPS_2017	weakness of the paper is in the experiments: there should be more complete comparisons in computation time, and comparisons with QMC-based methods of Yang et al (ICML2014). Without this the advantage of the proposed method remains unclear. - The limitation of the obtained results: The authors assume that the spectrum of a kernel is sub-gaussian. This is OK, as the popular Gaussian kernels are in this class. However, another popular class of kernels such as Matern kernels are not included, since their spectrum only decay polynomially. In this sense, the results of the paper could be restrictive. - Eq. (3): What is $e_l$? Corollaries 1, 2 and 3 and Theorem 4: All of these results have exponential dependence on the diameter $M$ of the domain of data: a required feature size increases exponentially as $M$ grows. While this factor does not increase as a required amount of error $\varepsilon$ decreases, the dependence on $M$ affects the constant factor of the required feature size. In fact, Figure 1 shows that the performance is more quickly getting worse than standard random features. This may exhibit the weakness of the proposed approaches (or at least of the theoretical results). - The equation in Line 170: What is $e_i$? - Subsampled dense grid: This approach is what the authors used in Section 5 on experiments. However, it looks that there is no theoretical guarantee for this method. Those having theoretical guarantees seem not to be practically useful. - Reweighted grid quadrature: (i) It looks that there is no theoretical guarantee with this method. (ii) The approach reminds me of Bayesian quadrature, which essentially obtains the weights by minimizing the worst case error in the unit ball of an RKHS. I would like to look at comparison with this approach. (iii) Would it be possible to derive a time complexity? (iv) How do you chose the regularization parameter $\lambda$ in the case of the $\ell_1$ approach? - Experiments in Section 5: (i) The authors reported the results of computation time very briefly (320 secs vs. 384 seconds for 28800 features in MNIST and "The quadrature-based features ... are about twice as fast to generate, compared to random Fourier features ..." in TIMIT). I do not they are not enough: the authors should report the results in the form of Tables, for example, varying the number of features. (ii) There should be comparison with the QMC-based methods of Yang et al. (ICML2014, JMLR2016). It is not clear what is the advantage of the proposed method over the QMC-based methods. (iii) There should be explanation on the settings of the MNIST and TIMIT classification tasks: what classifiers did you use, and how did you determine the hyper-parameters of these methods? At least such explantion should be included in the appendix.	- The limitation of the obtained results: The authors assume that the spectrum of a kernel is sub-gaussian. This is OK, as the popular Gaussian kernels are in this class. However, another popular class of kernels such as Matern kernels are not included, since their spectrum only decay polynomially. In this sense, the results of the paper could be restrictive.
ICLR_2023_4654	ICLR_2023	Weakness: 1), The proposed approach is straightforward (not a demerit), and is a native extension on how to extend the DETR into few-shot, although there exist some specific mechanism designs in this paper to facilitate such extension. However, similar ideas also can be found in existing papers such as [1], which appeared in 2021 in arXiv and published in 2022. Since [1] is already published, it should be included as a fair baseline to compare with and discuss and [1] should be the most close research reported in few-shot object detection. However, the performance reported in this manuscript seems is not as high as in [1] with a significant margin. [1] Meta-DETR: Image-Level Few-Shot Object Detection with Inter-Class Correlation Exploitation, T-PAMI, 2022. 2), From the data in Table 4, it indicates that the unsupervised pretraining is a key factor on the performance gain. However, there is no detailed discussion on the unsupervised pretraining in the main paper, which might be a problem. In fact, compared with ablation study of Table 5, the unsupervised pretraining is much more important than other modules presented in this paper. Therefore, I will suggest on focusing more on the pretraining method in the main paper. 3), I also cannot very agree with three “desiderata” claimed by the authors (although this is not a serious issue). In standard few-shot object detection, fine-tuning or re-training is not an evil. Moreover, “without re-training” is a merit to all attention-based few-shot approaches, not a unique merit of this approach. The second point, “an arbitrary number of novel objects” actually is not even an issue for those “re-training” few-shot methods. And the "re-training" based method may also have the merit that it no need to require the "queries" for the detection on both base and novel classes, and the selection of "queries" may also affect the performance of the detection performance. 4), In fact, many few-shot research is also focusing on the performance on both base and novel classes. One another important “desiderata” should be it can eliminate the performance drop as much as possible on base classes when adapting to novel classes. However, in this paper (similar for most "retraining-free" FS methods), the base class performance is not focused totally, and no experiment statistics are provided at all, this would be a problem to compare with most few-shot methods. Since the attention-based approach relying on the "queries", it's base-class performance may be worse than the "retraining" methods?	2), From the data in Table 4, it indicates that the unsupervised pretraining is a key factor on the performance gain. However, there is no detailed discussion on the unsupervised pretraining in the main paper, which might be a problem. In fact, compared with ablation study of Table 5, the unsupervised pretraining is much more important than other modules presented in this paper. Therefore, I will suggest on focusing more on the pretraining method in the main paper.