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T97kxctihq | ICLR_2024 | 1. The main claim of Section 2 is unclear. Are simple models always better than complex models for LTSF, or is it the case only to the specific framework shown in Figure 1? What if we adopt a different but still complicated framework, such as 1-dimensional CNNs? How do the results change if we include traditional models such as AR (autoregression) or ARIMA?
2. This paper is not self-contained. The experiments in Section 2 play a crucial role to motivate this work, but there is not enough description about the models and experimental setup. For example, RevIN is mentioned several times throughout the paper, but there is no definition of it. If the page limit is a problem, the authors could have added the details to Appendix.
3. Theorem 1 and 2, which are the main theoretical contributions of this work, seem trivial. If a time series can be clearly (and linearly) separated into seasonality and trend parts, I think it is obvious that a linear layer (or any linear function) is able to learn such separation. | 2. This paper is not self-contained. The experiments in Section 2 play a crucial role to motivate this work, but there is not enough description about the models and experimental setup. For example, RevIN is mentioned several times throughout the paper, but there is no definition of it. If the page limit is a problem, the authors could have added the details to Appendix. |
NIPS_2020_542 | NIPS_2020 | 1. There is no ablation study for Novel Asymmetric Transformations. It unclear whether the proposed method is better than only using Locality Sensitive Hashing (LSH). 2. The proposed Adaptive Clustering still relies on LSH. Although there is some further optimisation on E2LSH to create balanced clusters, the method is still quite similar to Re-Former work. The authors need to have some fair comparison with Re-Former or LSH. 3. The proposed method can not significantly boost the performance. I would like to see whether the method can be applied on longer sequence which can not be encoded by BERT, such as LongFormer work. For the models of BERT/RoBERTa on GLUE, it seems no need to save memory for training. 4. I would like to see some analysis of reversible Transformer/CNN (reformer) and distillation works which can also save memory for either training or inference. | 3. The proposed method can not significantly boost the performance. I would like to see whether the method can be applied on longer sequence which can not be encoded by BERT, such as LongFormer work. For the models of BERT/RoBERTa on GLUE, it seems no need to save memory for training. |
ICLR_2021_842 | ICLR_2021 | 1. Performance gains on downstream tasks of detection and instance segmentation are much lower -- how would the authors propose to improve these? 2. If the primary goal is to improve SSL performance on small models, I would have liked to see more analysis on how different design choices of setting up contrastive learning affect model performance and if these could aid performance improvement, in addition to knowledge distillation.
Questions and suggestions: 1. Adding fully-supervised baselines for small models in table 1 will be useful in understanding the gap between full supervision and SSL for these models. 2. In figure 3, does 100% (green line) represent the student network trained with 100% of labeled imagenet supervised data? It is hard to interpret what these numbers represent. 3. Minor point: Some citations, which should not be in parentheses, are in parentheses (e.g., Romero et al. page 8). Please fix this in the revision. | 2. In figure 3, does 100% (green line) represent the student network trained with 100% of labeled imagenet supervised data? It is hard to interpret what these numbers represent. |
NIPS_2022_1035 | NIPS_2022 | ] 1. The minimum patch size can be one to be added in Table 4, which can be the comparison in the per-pixel setting. 2. The experiment about time cost can be added to verify the superiority of the PAR. 3. This method is to reduce the size of the adversarial noise, but in practical applications, reducing the number of queries is a more important goal that needs to be optimized. | 3. This method is to reduce the size of the adversarial noise, but in practical applications, reducing the number of queries is a more important goal that needs to be optimized. |
ICLR_2021_2674 | ICLR_2021 | Though the training procedure is novel, a part of the algorithm is not well-justified to follow the physics and optics nature of this problem. A few key challenges in depth from defocus are missing, and the results lack a full analysis. See details below:
- the authors leverage multiple datasets, including building their own to train the model. However, different dataset is captured by different cameras, and thus the focusing distance, aperture settings, and native image resolution all affect the circle of confusion, how are those ambiguities taken into consideration during training?
- related to the point above, the paper doesn't describe the pre-processing stage, neither did it mention how the image is passed into the network. Is the native resolution preserved, or is it downsampled?
- According to Held et al "Using Blur to Affect Perceived Distance and Size", disparity and defocus can be approximated by a scalar that is related to the aperture and the focus plane distance. In the focal stack synthesis stage, how is the estimated depth map converted to a defocus map to synthesize the blur?
- the paper doesn't describe how is the focal stack synthesized, what's the forward model of using a defocus map and an image to synthesize defocused image? how do you handle the edges where depth discontinuities happen?
- in 3.4, what does “Make the original in-focus region to be more clear” mean? in-focus is defined to be sharpest region an optical system can resolve, how can it be more clear?
- the paper doesn't address handling textureless regions, which is a challenging scenario in depth from defocus. Related to this point, how are the ArUco markers placed? is it random?
- fig 8 shows images with different focusing distance, but it only shows 1m and 5m, which both exist in the training data. How about focusing distance other than those appeared in training? does it generalize well?
- what is the limit of the amount of blur presented in the input that the proposed models would fail? Are there any efforts in testing on smartphone images where the defocus is *just* noticeable by human eyes? how do the model performances differ for different defocus levels?
Minor suggestions
- figure text should be rasterized, and figures should maintain its aspect ratio.
- figure 3 is confusing as if the two nets are drawn to be independent from each other -- CNN layers are represented differently, one has output labeled while the other doesn't. It's not labeled as the notation written in the text so it's hard to reference the figure from the text, or vice versa.
- the results shown in the paper are low-resolution, it'd be helpful to have zoomed in regions of the rendered focal stack or all-in-focus images to inspect the quality.
- the sensor plane notation 's' introduced in 3.1 should be consistent in format with the other notations.
- calling 'hyper-spectral' is confusing. Hyperspectral imaging is defined as the imaging technique that obtains the spectrum for each pixel in the image of a scene. | - what is the limit of the amount of blur presented in the input that the proposed models would fail? Are there any efforts in testing on smartphone images where the defocus is *just* noticeable by human eyes? how do the model performances differ for different defocus levels? Minor suggestions - figure text should be rasterized, and figures should maintain its aspect ratio. |
NIPS_2020_1728 | NIPS_2020 | 1. While the experimental section in the paper is nice, it could be improved with some more details, please see below. 2. The paper has both a quite broad focus (on explanations in AI, for black boxes, etc.) and narrow focus (on explanations for Naive Bayes and linear classifiers). There is substantial related work in the area of explanations in Bayesian networks that is not considered. Please see below for further information about this. | 2. The paper has both a quite broad focus (on explanations in AI, for black boxes, etc.) and narrow focus (on explanations for Naive Bayes and linear classifiers). There is substantial related work in the area of explanations in Bayesian networks that is not considered. Please see below for further information about this. |
ARR_2022_24_review | ARR_2022 | - This paper brings more questions than answers -- many results are counter-intuitive or contradictory without explanation. For example: 1) Setting the vector dimension to 10 can make the entire conditional token distribution close to the Zipfian distribution. Why is that? What if the dimension is larger or smaller than 10?
2) In Figure 2(a), why do uniform and Zipfian token sampling even hurt the perplexity comparing with random weights?
3) In Figure 2(b), why does L1=nesting-parenthesis is significantly worse than L1=flat-parenthesis for Transformer?
4) In Figure 2(c), why does transferring from L1=English non-significantly worse than L1=Japanese while the task language L2=English? The flexibility of the Transformer is not a convincing explanation -- if the closeness between L1 and L2 is not a good indicator of transfer performance, then how do we conclude that a synthetic language L1 is helpful because it is closer to a real language L2?
5) In figure 3(b), why does uniform token sampling is worse than random weights by so much?
- There some technical mistakes.
1) The method of sentence-dependent token sampling can not be called "random work". In (Arora et al. 2016), $c_t$ does a slow random walk meaning that $c_{t+1}$ is obtained from $c_t$ by adding a small random displacement vector. BTW, the correct citation should be "Arora et al. 2016. A Latent Variable Model Approach to PMI-based Word Embeddings. In TACL".
2) If LSTM/Transformer models are trained with a causal (auto-regressive) LM loss, then they should be decoders, not encoders.
- Algorithm 1. How did you choose p < 0.4?
- L395. " the combination" -> "combine" - L411 "train the model with one iteration over the corpus". Why only one iteration? Is the model converged?
- After fine-tuning a LM pre-trained with conditioned token sampling (L456 "useful inductive bias"), you could check if embeddings of L2 have interpretable topological relations, such as analogy. | 2) If LSTM/Transformer models are trained with a causal (auto-regressive) LM loss, then they should be decoders, not encoders. |
y3CdSwREZl | ICLR_2025 | - The model should apply to modalities other than vision and audio, but the evaluation does not extend beyond these modalities. This is relatively minor, of course, since a paper that introduces a new method is not required to exhaust all empirical possibilities.
- The "modality separation" approach assumes minimal cross-modal information flow, which is a major oversimplification. It is not clear from an initial review to what extent removing this brick from the base of the theoretical structure collapses the rest. To a large extent this weakness is touched on in the first limitation in Sec 6.1, but it is not _addressed_. The natural interdependence between modalities, throughout the layers, should be better explained or explored. This is a more major limitation.
- It would be preferable to connect the concepts of ‘semantic telomeres’, for example, to real-world problems. What is the practical impact of this work?
- Other interpretability techniques for multimodal LLMs are not evaluated whatsoever. | - The "modality separation" approach assumes minimal cross-modal information flow, which is a major oversimplification. It is not clear from an initial review to what extent removing this brick from the base of the theoretical structure collapses the rest. To a large extent this weakness is touched on in the first limitation in Sec 6.1, but it is not _addressed_. The natural interdependence between modalities, throughout the layers, should be better explained or explored. This is a more major limitation. |
le4IoZZHy1 | ICLR_2025 | * The source(s) of the videos are not disclosed and the collection process is not described in enough detail. It would be interesting to know what website(s) the videos come from, what search queries were used. The paper says that videos were manually filtered, but filtering criteria were not mentioned. This information would be critical to understanding the composition and applicability of the benchmark.
* Evaluations on closed-source MLLMs are only performed with up to 32 / 128 frames even though ablations show that performance keeps improving as more frames are used (Fig. 7). Note: Because cost might be a prohibiting factor here, and 128 frames are enough for the provided SotA analysis, I am not considering this shortcoming in my rating. If the benchmark gets publicly released, this could easily be done by groups with sufficient resources.
* Only three examples are provided in the text. It would be good to see a few more example questions from the benchmark to get a feeling for its quality. | * Evaluations on closed-source MLLMs are only performed with up to 32 / 128 frames even though ablations show that performance keeps improving as more frames are used (Fig. 7). Note: Because cost might be a prohibiting factor here, and 128 frames are enough for the provided SotA analysis, I am not considering this shortcoming in my rating. If the benchmark gets publicly released, this could easily be done by groups with sufficient resources. |
NIPS_2021_2418 | NIPS_2021 | - The class of problems is not very well motivated. The CIFAR example is contrived and built for demonstration purposes. It is not clear what application would warrant sequentially (or in batches) and jointly selecting tasks and parameters to simultaneously optimize multiple objective functions. Although one could achieve lower regret in terms of total task-function evaluations by selecting the specific task(s) to evaluate rather than evaluating all tasks simultaneously, the regret may not be better with respect to timesteps. For example, in the assemble-to-order, even if no parameters are evaluated for task function (warehouse s) at timestep t, that warehouse is going to use some (default) set of parameters at timestep t (assuming it is in operation---if this is all on a simulator then the importance of choosing s seems even less well motivated). There are contextual BO methods (e.g. Feng et al 2020) that address the case of simultaneously tuning parameters for multiple different contexts (tasks), where all tasks are evaluated at every timestep. Compelling motivating examples would help drive home the significance of this paper. - The authors take time to discuss how KG handles the continuous task setting, but there are no experiments with continuous tasks - It’s great that entropy methods for conditional optimization are derived in Section 7 in the appendix, but why are these not included in the experiments? How does the empirical performance of these methods compare to ConBO? - The empirical performance is not that strong. EI is extremely competitive and better in low-budget regimes on ambulance and ATO - The performance evaluation procedure is bizarre: “We measure convergence of each benchmark by sampling a set of test tasks S_test ∼ P[s] ∝ W(s) which are never used during optimization”. Why are the methods evaluated on test tasks not used during the optimization since all benchmark problems have discrete (and relatively small) sets of tasks? Why not evaluate performance on the expected objective (i.e. true, weighted) across tasks? - The asymptotic convergence result for Hybrid KG is not terribly compelling - It is really buried in the appendix that approximate gradients are used to optimize KG using Adam. I would feature this more prominently. - For the global optimization study on hybrid KG, it would be interesting to see performance compared to other recent kg work (e.g. one-shot KG, since that estimator formulation can be optimized with exact gradients)
Writing: - L120: this is a run-on sentence - Figure 2: left title “poster mean” -> “posterior mean” - Figure 4: mislabeled plots. The title says validation error, but many subplots appear to show validation accuracy. Also, “hyperaparameters” -> hyperparameters - L286: “best validation error (max y)” is contradictory - L293: “We apply this trick to all algorithms in this experiment”: what is “this experiment”? - The appendix is not using NeurIPS 2021 style files - I recommend giving the appendix a proofread:
Some things that jump out
P6: “poster mean”, “peicewise-linear”
P9: “sugggest”
Limitations and societal impacts are discussed, but the potential negative societal impacts could be expounded upon. | - The empirical performance is not that strong. EI is extremely competitive and better in low-budget regimes on ambulance and ATO - The performance evaluation procedure is bizarre: “We measure convergence of each benchmark by sampling a set of test tasks S_test ∼ P[s] ∝ W(s) which are never used during optimization”. Why are the methods evaluated on test tasks not used during the optimization since all benchmark problems have discrete (and relatively small) sets of tasks? Why not evaluate performance on the expected objective (i.e. true, weighted) across tasks? |
ACL_2017_494_review | ACL_2017 | - I was hoping to see some analysis of why the morph-fitted embeddings worked better in the evaluation, and how well that corresponds with the intuitive motivation of the authors. - The authors introduce a synthetic word similarity evaluation dataset, Morph-SimLex. They create it by applying their presumably semantic-meaning-preserving morphological rules to SimLex999 to generate many more pairs with morphological variability. They do not manually annotate these new pairs, but rather use the original similarity judgements from SimLex999.
The obvious caveat with this dataset is that the similarity scores are presumed and therefore less reliable. Furthermore, the fact that this dataset was generated by the very same rules that are used in this work to morph-fit word embeddings, means that the results reported on this dataset in this work should be taken with a grain of salt. The authors should clearly state this in their paper.
- (Soricut and Och, 2015) is mentioned as a future source for morphological knowledge, but in fact it is also an alternative approach to the one proposed in this paper for generating morphologically-aware word representations. The authors should present it as such and differentiate their work.
- The evaluation does not include strong morphologically-informed embedding baselines. General Discussion: With the few exceptions noted, I like this work and I think it represents a nice contribution to the community. The authors presented a simple approach and showed that it can yield nice improvements using various common embeddings on several evaluations and four different languages. I’d be happy to see it in the conference.
Minor comments: - Line 200: I found this phrasing unclear: “We then query … of linguistic constraints”.
- Section 2.1: I suggest to elaborate a little more on what the delta is between the model used in this paper and the one it is based on in Wieting 2015. It seemed to me that this was mostly the addition of the REPEL part.
- Line 217: “The method’s cost function consists of three terms” - I suggest to spell this out in an equation.
- Line 223: x and t in this equation (and following ones) are the vector representations of the words. I suggest to denote that somehow. Also, are the vectors L2-normalized before this process? Also, when computing ‘nearest neighbor’ examples do you use cosine or dot-product? Please share these details.
- Line 297-299: I suggest to move this text to Section 3, and make the note that you did not fine-tune the params in the main text and not in a footnote.
- Line 327: (create, creates) seems like a wrong example for that rule.
- I have read the author response | - (Soricut and Och, 2015) is mentioned as a future source for morphological knowledge, but in fact it is also an alternative approach to the one proposed in this paper for generating morphologically-aware word representations. The authors should present it as such and differentiate their work. |
NIPS_2017_65 | NIPS_2017 | 1) the evaluation is weak; the baselines used in the paper are not even designed for fair classification
2) the optimization procedure used to solve the multi-objective optimization problem is not discussed in adequate detail
Detailed comments below:
Methods and Evaluation: The proposed objective is interesting and utilizes ideas from two well studied lines of research, namely, privileged learning and distribution matching to build classifiers that can incorporate multiple notions of fairness. The authors also demonstrate how some of the existing methods for learning fair classifiers are special cases of their framework. It would have been good to discuss the goal of each of the terms in the objective in more detail in Section 3.3. The part that is probably the most weakest in the entire discussion of the approach is the discussion of the optimization procedure. The authors state that there are different ways to optimize the multi-objective optimization problem they formulate without mentioning clearly which is the procedure they employ and why (in Section 3). There seems to be some discussion about the same in experiments section (first paragraph) and I think what was done is that the objective was first converted into unconstrained optimization problem and then an optimal solution from the pareto set was found using BFGS. This discussion is still quite rudimentary and it would be good to explain the pros and cons of this procedure w.r.t. other possible optimization procedures that could have been employed to optimize the objective.
The baselines used to compare the proposed approach and the evaluation in general seems a bit weak to me. Ideally, it would be good to employ baselines that learn fair classifiers based on different notions (E.g., Hardt et. al. and Zafar et. al.) and compare how well the proposed approach performs on each notion of fairness in comparison with the corresponding baseline that is designed to optimize for that notion. Furthermore, I am curious as to why k-fold cross validation was not used in generating the results. Also, was the split between train and test set done randomly? And, why are the proportions of train and test different for different datasets?
Clarity of Presentation:
The presentation is clear in general and the paper is readable. However, there are certain cases where the writing gets a bit choppy. Comments:
1. Lines 145-147 provide the reason behind x*_n being the concatenation of x_n and z_n. This is not very clear.
2. In Section 3.3, it would be good to discuss the goal of including each of the terms in the objective in the text clearly.
3. In Section 4, more details about the choice of train/test splits need to be provided (see above).
While this paper proposes a useful framework that can handle multiple notions of fairness, there is scope for improving it quite a bit in terms of its experimental evaluation and discussion of some of the technical details. | 2. In Section 3.3, it would be good to discuss the goal of including each of the terms in the objective in the text clearly. |
NIPS_2021_2131 | NIPS_2021 | - There is not much technical novelty. Given the distinct GPs modeling the function network, the acquisition function and sampling procedure are not novel - The theoretical guarantee is pretty weak (random search is asymptotically optimal).
The discussion of not requiring dense coverage to prove the method is asymptotically consistent is interesting, but the utility of proposition 2 is not clear because although dense coverage is a consideration for proving consistency, it is not really a practical reality in sample-efficient optimization—typically BO would not have dense coverage.
Questions/comments: - There is no discussion of observation noise, which is a practical concern in many of the real world use cases mentioned in the paper. The approach of using GPs to model nodes in function network can naturally handle noisy observations, so only the acquisition function would need to be adjusted to account for noisy observations since the best objective value would be unknown. I expect that the empirical performance would remain the same (e.g. using Noisy EI from Letham et al. 2019), but the computation would be much more expensive. It would be good to discuss and demonstrated performance under noisy observations. - How does the number of MC samples affect performance, empirically? How does the network structure affect this? - It would be interesting to see a head-to-head comparison with deep GPs. How different are the runtimes (including inference times) and empirical performances?
Since the core contribution is modeling each node in the function network with a distinct GP, it would be good to see more evaluation of the function network model's predictive performance compared to a alternative modeling choices (e.g. individual models with a compositional objective, vanilla global gp, deep gp)
Grammar: - L238 “out method” -> “our method” - L335 “structurre” -> “structure”
The discussion of the work's limitations is quite thorough, and it proposes interesting directions for future work. The authors have addressed potential negative societal impacts. | - There is not much technical novelty. Given the distinct GPs modeling the function network, the acquisition function and sampling procedure are not novel - The theoretical guarantee is pretty weak (random search is asymptotically optimal). The discussion of not requiring dense coverage to prove the method is asymptotically consistent is interesting, but the utility of proposition 2 is not clear because although dense coverage is a consideration for proving consistency, it is not really a practical reality in sample-efficient optimization—typically BO would not have dense coverage. Questions/comments: |
NIPS_2018_158 | NIPS_2018 | - The paper has serious clarity issues: (1) It is not clear what "unsupervised" means in the paper. The groundtruth bounding box annotations are provided and there is physics supervision. Which part is unsupervised? Does "unsupervised" mean the lack of 3D bounding box annotations? If so, how is the top part of Fig. 2 trained? (2) It is not clear how the fine-tuning is performed. I searched through the paper and supplementary material, but I couldn't find any detail about the fine-tuning procedure. (3) The details of the REINFORCE algorithm is missing (the supplementary material doesn't add much). How many samples are drawn? What are the distributions that we sample from? How is the loss computed? etc. (4) The evaluation metric is not clear. It seems the stability score is computed by averaging the stability scores of all primitives (according to line 180). Suppose only one box is predicted correctly and the stability score is 1 for that box. Does that mean the overall stability score is 1? - Another main issue is that the results are not that impressive. The physics supervision, which is the main point of this paper, does not help much. For instance, in Table 2, we have 0.200 vs 0.206 or 0.256 vs 0.261. The fine-tuning procedure is not clear so I cannot comment on those results at this point. Rebuttal Requests: Please clarify all of the items mentioned above. I will upgrade the rating if these issues are clarified. | - Another main issue is that the results are not that impressive. The physics supervision, which is the main point of this paper, does not help much. For instance, in Table 2, we have 0.200 vs 0.206 or 0.256 vs 0.261. The fine-tuning procedure is not clear so I cannot comment on those results at this point. Rebuttal Requests: Please clarify all of the items mentioned above. I will upgrade the rating if these issues are clarified. |
ICLR_2021_2627 | ICLR_2021 | Weakness:
(1) My biggest concern about this paper is the novelty of the proposed algorithms. Based on my reading, the proposed SVRG based algorithm with arbitrary sampling uses the almost same idea from Horváth & Richtarik, 2019, as well as the technical proofs (of course with minor adaptations to distributed settings). Although Horváth & Richtarik, 2019 considered the nonconvex setting and this paper considered the strongly-convex setting, the key step to handle the non-uniform distribution should not be that different. Furthermore, the extension to the mini-batch case is also standard, because there are already extensive studies on such a topic.
(2) My another concern is that the proposed algorithm heavily depend on the non-uniform sampling. However, based on their results, the chosen sampling distribution depends on the smoothness parameters of loss functions. In the experiments, the authors estimate such parameters based on some easy-to-obtain bounds on simple logistic regression objective function. However, estimating such smoothness parameters for more complicated objective function (e.g., with deep neural networks) can introduce an extra computation burden or may be infeasible in practice. For this reason, I suggest that the authors can run more experiments with more complicated objective function.
(3) The experiments are not convincing enough. First, the authors only compare the proposed algorithms to other variance-reduced methods such as SVRG and SARAH. They should also provide a comparison to SGD or ADAM types of methods if possible. Second, the authors should provide more details of the competing algorithms, i.e., SVRG and SARAH in the experiments (e.g., whether such methods also use a mini-batch sampling for the inner loop? How they choose the hyper-parameters like stepsize, batch size, etc?)
(4) Some references may be missed. Since this paper focuses on variance-reduced methods, some related papers on SPIRDER-type and SARAH-type methods should be mentioned. I provide some as follows.
1) SPIDER: Near-Optimal Non-Convex Optimization via Stochastic Path Integrated Differential Estimator.
2) SARAH: A Novel Method for Machine Learning Problems Using Stochastic Recursive Gradient.
3) SpiderBoost and Momentum: Faster Stochastic Variance Reduction Algorithms.
(5) One minor comment: Line 7 of Algorithm 1 on page 4: whether g_{\xi}(w)/Np_\xi is g_{\xi}(w)/(Np_\xi) or (g_{\xi}(w)/N)p_\xi? Based on my reading, it should be (g_{\xi}(w)/N)p_\xi? If so, I suggest the authors can write it as p_\xi g_{\xi}(w)/N.
In summary, I am not convinced by the results in this paper, and tend to reject the current version due to the limited technical novelty and the unsatisfactory experiments. However, I am open to change my mind based on the response and other reviewers’ comments. | 1) SPIDER: Near-Optimal Non-Convex Optimization via Stochastic Path Integrated Differential Estimator. |
j50c2tkQUu | ICLR_2025 | 1. The paper is not well written. It lacks derivations and the significance of each of the operations used.
For example, in Equation 4, We have not discussed how we arrived at the shown equation. Equation 5: How do we derive the 2nd line from the first line? Equation 10: The paper does not discuss how it reached that equation. More details are asked in the Questions section.
2. The use of diffusion as a hyper-network is not well motivated. Why do we want to use a diffusion model to generate weights? Does this mean given a $(e,\nu)$, there is a distribution of different $N_i$ physically accurate for location $q_i$? This requires a clear justification.
2. Line 054: How is this a generative model? The core problem is, given a 3d object and its material properties, simulate the object's motion given an external force. So, there is a single group truth simulation based on physical laws that we want to achieve. I do not see how ElastoGen is learning a distribution here. | 2. The use of diffusion as a hyper-network is not well motivated. Why do we want to use a diffusion model to generate weights? Does this mean given a $(e,\nu)$, there is a distribution of different $N_i$ physically accurate for location $q_i$? This requires a clear justification. |
NIPS_2018_265 | NIPS_2018 | in the paper. I will list them as follows. Major comments: =============== - Since face recognition/verification methods are already performing well, the great motivation for face frontalization is for applications in the wild and difficult conditions such as surveillance images where pose, resolution, lighting conditions, etc⦠vary wildly. To this effect, the paper lacks sufficient motivation for these applications. - The major drawback is the method is a collection of many existing methods and as such it is hard to draw the major technical contribution of the paper. Although a list of contributions was provided at the end of the introduction none of them are convincing enough to set this paper aside technically. Most of the techniques combined are standard existing methods and/or models. If the combination of these existing methods was carefully analyzed and there were convincing results, it could be a good application paper. But, read on below for the remaining issues I see to consider it as application paper. - The loss functions are all standard L1 and L2 losses with the exception of the adversarial loss which is also a standard in training GANs. The rationale for the formulation of these losses is little or nonexistent. - The results for face verification/recognition were mostly less than 1% and even outperformed by as much as 7% on pose angles 75 and 90 (see Table 1). The exception dataset evaluated is IJB-A, in which the proposed model performed by as much as 2% and that is not surprising given IJB-A is collected in well constrained conditions unlike LFW. These points are not discussed really well. - The visual qualities of the generated images also has a significant flaw in which it tends to produce a more warped bulged regions (see Fig. 3) than the normal side. Although, the identity preservation is better than other methods, the distortions are significant. This lack of symmetry is interesting given the dense correspondence is estimated. - Moreover, the lack of ablation analysis (in the main paper) makes it very difficult to pinpoint from which component the small performance gain is coming from. - In conclusion, due to the collection of so many existing methods to constitute the proposed methods and its lack of convincing results, the computational implications do not seem warranted. Minor comments: =============== - Minor grammatical issue need to be checked here and there. - The use of the symbol \hat for the ground truth is technically not appealing. Ground truth variables are usually represented by normal symbols while estimated variables are represented with \hat. This needs to be corrected throughout for clarity. | - The results for face verification/recognition were mostly less than 1% and even outperformed by as much as 7% on pose angles 75 and 90 (see Table 1). The exception dataset evaluated is IJB-A, in which the proposed model performed by as much as 2% and that is not surprising given IJB-A is collected in well constrained conditions unlike LFW. These points are not discussed really well. |
ICLR_2021_2892 | ICLR_2021 | - Proposition 2 seems to lack an argument why Eq 16 forms a complete basis for all functions h. The function h appears to be defined as any family of spherical signals parameterized by a parameter in [-pi/2, pi/2]. If that’s the case, why eq 16? As a concrete example, let \hat{h}^\theta_lm = 1 if l=m=1 and 0 otherwise, so constant in \theta. The only constant associated Legendre polynomial is P^0_0, so this h is not expressible in eq 16. Instead, it seems like there are additional assumptions necessary on the family of spherical functions h to let the decomposition eq 16, and thus proposition 2, work. Hence, it looks like that proposition 2 doesn’t actually characterize all azimuthal correlations. - In its discussion of SO(3) equivariant spherical convolutions, the authors do not mention the lift to SO(3) signals, which allow for more expressive filters than the ones shown in figure 1. - Can the authors clarify figure 2b? I do not understand what is shown. - The architecture used for the experiments is not clearly explained in this paper. Instead the authors refer to Jiang et al. (2019) for details. This makes the paper not self-contained. - The authors appear to not use a fast spherical Fourier transform. Why not? This could greatly help performance. Could the authors comment on the runtime cost of the experiments? - The sampling of the Fourier features to a spherical signal and then applying a point-wise non-linearity is not exactly equivariant (as noted by Kondor et al 2018). Still, the authors note at the end of Sec 6 “This limitation can be alleviated by applying fully azimuthal-rotation equivariant operations.”. Perhaps the authors can comment on that? - The experiments are limited to MNIST and a single real-world dataset. - Out of the many spherical CNNs currently in existence, the authors compare only to a single one. For example, comparisons to SO(3) equivariant methods would be interesting. Furthermore, it would be interesting to compare to SO(3) equivariant methods in which SO(3) equivariance is broken to SO(2) equivariance by adding to the spherical signal a channel that indicates the theta coordinate. - The experimental results are presented in an unclear way. A table would be much clearer. - An obvious approach to the problem of SO(2) equivariance of spherical signals, is to project the sphere to a cylinder and apply planar 2D convolutions that are periodic in one direction and not in the other. This suffers from distortion of the kernel around the poles, but perhaps this wouldn’t be too harmful. An experimental comparison to this method would benefit the paper.
Recommendation: I recommend rejection of this paper. I am not convinced of the correctness of proposition 2 and proposition 1 is similar to equivariance arguments made in prior work. The experiments are limited in their presentation, the number of datasets and the comparisons to prior work.
Suggestions for improvement: - Clarify the issue around eq 16 and proposition 2 - Improve presentation of experimental results and add experimental details - Evaluate the model of more data sets - Compare the model to other spherical convolutions
Minor points / suggestions: - When talking about the Fourier modes as numbers, perhaps clarify if these are reals or complex. - In Def 1 in the equation it is confusing to have theta twice on the left-hand side. It would be clearer if h did not have a subscript on the left-hand side. | - The experimental results are presented in an unclear way. A table would be much clearer. |
yiPtWSrBrN | ICLR_2024 | * While the motivation behind the dataset has some nice intuition, there are no concrete assessments of the presence of the properties that the authors claim the dataset has. Concretely, there are no assessments of grammaticality, factual content, vocabulary coverage, etc. and how these quantities compare to larger, human-generated corpora.
* On a similar note, there does not seem to have been any validation of the dataset, which was machine-generated.
* There are many claims about children’s language usage that are either not supported, or are not elaborated on to a degree necessary to believe the claims made by the authors. For example, what are the grammatical structures and facts used/known by a child? What checks are done to ensure that these constraints are adhered to?
* Some of the experiments seem quite ad-hoc. For example, the results of figure 6 are color-coded “according to their success (green), failure (red), or partial success (yellow),” but the criterion for success is never defined, nor is the evaluation setup provided.
* In general, text in the figures is very difficult to read | * There are many claims about children’s language usage that are either not supported, or are not elaborated on to a degree necessary to believe the claims made by the authors. For example, what are the grammatical structures and facts used/known by a child? What checks are done to ensure that these constraints are adhered to? |
ARR_2022_56_review | ARR_2022 | - The details of how to apply K-Means methods to obtain the pseudo labels when using the CCL and how the number of clusters will affect the final performance is missing.
- Given that sentence length might affect in Table 1, additional statistics of the pre-trained sentence length versus the might be good to provide. - Could the author provide a more detailed description of how to construct the pre-training phrases and how many pre-training phrases are present and how these phrases overlapped with the downstream tasks? | - Given that sentence length might affect in Table 1, additional statistics of the pre-trained sentence length versus the might be good to provide. |
NIPS_2018_753 | NIPS_2018 | weakness of the proposed method, it is just something that I believe can be useful for readers to know. == Original review == The authors propose Hamiltonian VAE, a new variational approximation building on the Hamiltonian importance sampler by Radford Neal. The paper is generally well written, and was easy to follow. The authors show improvements on a Gaussian synthetic example as well as on benchmark real data. The authors derive a lower bound on the log-marginal likelihood based on the unbiased approximation provided by a Hamiltonian importance sampler. This follows a similar line of topics in the literature (e.g. also [1,2,3] which could be combined with the current approach) that derive new variational inference procedures synthesizing ideas from the Monte Carlo literature. I had a question regarding the optimal backward kernel for HIS discussed in the paragraph between line 130-135. I was a bit confused about in what sense this is optimal? You don't actually need the backward kernel on the extended space because you can evaluate the density exactly (which is the optimal thing to use on the extended space of momentum and position). Also the authors claim on line 175-180 that evaluating parts of the ELBO analytically leads to a reduction in variance. I do not think this is true in general, for example evaluating the gradient of the entropy analytically in standard mean-field stochastic gradient VI can give higher variance when close to the optimal variational parameters compared to estimating this using Monte Carlo. Another point that I would like to see discussed is that HVAE requires access to the model-gradients when computing the approximate posterior. This is distinct from standard VAEs which does not need access to the model for computing q(z|x). Minor comments: - Regarding HVI and "arbitrary reverse Markov kernels": The reverse kernels to me don't seem to be more arbitrary than any other method that uses auxiliary variables for learning more flexible variational approximations. They are systematically learnt using a global coherent objective, which with a flexible enough reverse kernel enables learning the optimal. - Line 240-241, I was a bit confused about this sentence. Perhaps restructure a bit to make sure that the model parameters theta are not independently generated for each i \in [N]? | - Line 240-241, I was a bit confused about this sentence. Perhaps restructure a bit to make sure that the model parameters theta are not independently generated for each i \in [N]? |
EpJ7qqR0ad | EMNLP_2023 | Minor issues:
- Misspell: the first paragraph in the Introduction, `propose a multi-modal copositional problem`
- Misspell: in the first contributions, `address the domain-shift problem in compositioanl learning...`
- Misspell: the last sentence in Compositional Learning, `compptional problem`
- Misspell: Figure 2 ... `predict the masked conpositional concept conditioned`
Major issues:
- In the contribution of this paper, it is mentioned to deal with the domain-shift problem in compositional learning. Which existing works have this problem, or do all the compositional learning have it? It is not mentioned above, and it is better to explain it earlier.
- Please explain the difference between Compositional Learning and Grounded Compositional Concept Learning in one sentence.
- If the difference between the training data and the test data is too large, will the retriever still work?
- Please briefly explain the difference between the retriever and the attention mechanism in this paper. | - Please briefly explain the difference between the retriever and the attention mechanism in this paper. |
FJFVmeXusW | ICLR_2025 | 1. Even though the paper claims to successfully identify heads that can do both retrieval and reasoning for **long-context** task, which is better than the retrieval-only heads initially proposed in Wu et al. (2024), the NIAH experiment setting in the paper is not long enough (longest prompt = 8k). I believe 8k is considered to be not long enough nowadays. Can the author try longer NIAH test such as 64k or 128k to show the effectiveness of the identified R2-heads?
2. I believe there is a work called "Razorattention" [1] that is released in July which follows the same trajectory as this study, i.e. kv cache compression based on head type. Even though the paper addresses this work in their writing, I don't see any comparison in term of performance between the proposed method and that work, especially two works follow the same directory and Razorattention was released a few moths ago. It is unclear to notice the major contribution of the R2-heads from retrieval head only. Can the author benchmark and compare their performance in your experiment?
3. The estimation equation used to determine R2-head seems to be vague (or even incorrect).
- What is the first sigma, or the t-sigma, sum used for?
- The claim that this proposed estimation method can identify which head is responsible for reasoning is not convincing. Firstly, the study modifies the needle to include reasoning logics & incorrect answer, but do not consider them at all in the estimation equation. The estimation equation only considers the correct answer, c2, as the ground truth, which imo, the same as the original retrieval-identification test. What is the usage of the add-on logics and incorrect answer here if you don't consider it in the estimation?
4. I believe the paper would benefit more from ablation study showing and discussing the effect of different values of hyper-parameter alpha & beta on the performance of the methods.
[1] Hanlin Tang, Yang Lin, Jing Lin, Qingsen Han, Shikuan Hong, Yiwu Yao, and Gongyi Wang. Razorattention: Efficient kv cache compression through retrieval heads, 2024. URL https: //arxiv.org/abs/2407.15891. | 3. The estimation equation used to determine R2-head seems to be vague (or even incorrect). |
KgcuY2KIkf | EMNLP_2023 | - It's somewhat unclear whether this approach is scalable to larger models trained on more data as the kinds of sense-tagged datasets that the model is trained on are not particularly common and are relatively expensive to make.
- The paper could potentially be improved by seeing if there were performance regressions on non-figurative language tasks compared to the original language models. | - The paper could potentially be improved by seeing if there were performance regressions on non-figurative language tasks compared to the original language models. |
NIPS_2019_962 | NIPS_2019 | for exceptions. + Experiments are convincing. + To the best of my knowledge, the idea of using unsupervised keypoints for reinforcement learning is novel and promising. One can expect a variety of follow-up work. + Using keypoints as input state of a Q function is reasonable and reduces the dimensionality of the problem. + Reducing the search space to the most controllable keypoints instead of raw actions is a promising idea. Weaknesses: 1. Overstated claim on generalization In the introduction (L17-L22), the authors motivate their work by explaining that reinforcement learning approaches are limited because it is difficult to re-purpose task-specific representations, but that this is precisely what humans do. From this, one could have expected this paper to address this issue by training and applying the detector network across multiple games, re-purposing their keypoint detector. This would have be useful to verify that the learnt representations generalize to new contexts. But unfortunately, it hasn't been done, so it is a bit of an over-statement. Could this be a limitation of the method because the number of keypoints is fixed? 2. Deep RL that matters Experiments should be run multiple times. A longstanding issue with deep RL is their reproducibility and the significance of their improvements. It has been recently suggested that we need a community effort towards reproducibility [a], which should also be taken into account in this paper. Among the considerations, one critical thing is running multiple experiments and reporting the statistics. [a] Henderson, Peter, et al. "Deep reinforcement learning that matters." Thirty-Second AAAI Conference on Artificial Intelligence. 2018. 3. The choice of testing environment is not well motivated. Levels are selected without a clear rationale, with only a vague motivation in L167. This makes me suspect that they might be cherry picks. Authors should provide a more clear justification. This could be related to the next weakness that I will discuss, which is understandable. Even if this is the case, this should then be explicit with experimental evidence. 4. Keypoints are limited to moving objects A practical limitation comes from the fact that the keypoints are learnt from the moving parts of the image. As identified by the authors, the first resulting limitation is that the method assumes a fixed background, so that only meaningful objects move and can be detected as keypoints. Learning to detect keypoints based on what objects are moving has some limitations when these keypoints are supposed to be used as the input state of a Q function. One can imagine a game where some obstacles are immobile. The locations of these obstacles are important in order to make decisions but in this work, they would be ignored. It is therefore important that these limitations are also explicitly demonstrated. 5. Dealing with multiple instances. Because "PNet" generates one heatmap per keypoint, each keypoint detector "specializes" into a certain type of keypoint. This is fine for some applications (e.g. face keypoints) where only one instance of each kind of keypoint exists in each image. But there are games (e.g. Frostbite) where a lot of keypoints look exactly the same. And still, the detector is able to track them with consistency (as shown in the supplementary video). This is intriguing, as one could expect the detector to detect several keypoints at the same location, instead of distributing them almost perfectly. Is it because the receptive field is large? 6. Other issues - In section 3, the authors could improve the explanation of why the loss promotes the detection of meaningful keypoints. It is not obvious at first why the detector needs to detect keypoints to help with the reconstruction. - Figure 1: Referring to [15] as "PointNet" is confusing when this name doesn't appear anywhere in this paper ([15]) and there exists another paper with this name. See "PointNet: Deep Learning on Point Sets for 3D Classification and Segmentation", Charles R. Qi, Hao Su, Kaichun Mo, Leonidas J. Guibas. - Figure 1: The figure describes two "stop grad", but there is no mention or explanation of it in the text or caption. This is not theoretically motivated either, because most of the transported feature map comes from the source image (all the pixels that are not close from source or target keypoints). Blocking these gradients would block most of the gradients that can be used to train the "Feature CNN" and "PNet". - L93: "by marginalising the keypoint-detetor feature-maps along the image dimensions (as proposed in [15])". This would be better explained and self-contained by saying that a soft-argmax is used. - L189: "Distances above a threshold (ε) are excluded as potential matches". What threshold value is used? - What specific augmentation techniques are used during the training of the detector? - Figure 4: it is not clear what the meaning of "1-200 frames" is and how the values are computed. Why are the precision and recall changing with the trajectory length? Also, what is an "action repeat"? - Figure 6: the scores should be normalized (and maybe displayed as a plot) for easier comparison. ==== POST REBUTTAL ==== The rebuttal is quite convincing, and have addressed my concerns. I would like to raise the rating of the paper to 8 :-) I'm happy that my worries were just worries. | - What specific augmentation techniques are used during the training of the detector? |
9HbJGoe4a8 | EMNLP_2023 | * In the retrieval part, the contributions are not clear in terms of the dataset construction. The authors primarily augment two datasets by extracting the audio separately from the videos and separating into speech and non-speech components.
* Details of score computation in Eq (1) and (2) are not mentioned. Further, for the sequence to single token similarity, it is not clear how the aggregation is performed after computing similarities with multiple token elements.
* The details in Figure 4 are confusing. It might be better to define the terms associated with the similarity scores (token to sequence similarity or sequence to sequence similarities)
* For the retrieval section, experimental results should be shown with pretrained multimodal audio-visual (**wav2CLIP[1]**) or audio-text encoders (**CLAP[2]**).
* In the audio generation setup, in section **4.2.2**, it is mentioned that two separate models are trained ($SOS_{image}$ and $SOS_{image+text}$). Whereas in section **4.2.1**, it is mentioned that the text model is frozen, and then the image guidance is performed on top of it ($SOS_{image+text}$ ?). It is not clear how $SOS_{image}$ is used in this setup?
**[1]** https://arxiv.org/pdf/2110.11499.pdf
**[2]** https://arxiv.org/abs/2206.04769 | * In the retrieval part, the contributions are not clear in terms of the dataset construction. The authors primarily augment two datasets by extracting the audio separately from the videos and separating into speech and non-speech components. |
WJnciuhwyU | ICLR_2025 | - The paper introduces several assumptions that are perhaps too strong to be realistic. For example, Assumption 3.4 requires private votes to reflect the truthful utility, but it is unclear that such truthful utility exists and can be elicited easily. If such private votes exist, why not use as many private votes as possible?
- The paper lacks sufficient justification on the limitations of their proposed mechanisms. | - The paper lacks sufficient justification on the limitations of their proposed mechanisms. |
NIPS_2022_2054 | NIPS_2022 | i) The interpretations about “why PCA does not work” and “why the whitened output is not good” are not convincing. To me, the explanation could be much simpler and more intuitive: the batch whitened outputs rely on the batch statistics: an image may have different whitened representations when computed in different mini-batches.
When using PCA, the descriptor of an image relies on the eigenvectors (U in L136), which may change dramatically across mini-batches. This explains why BW-based approaches prefer large batch sizes. It explains the experimental results shown in Fig. 4. It also explains why whitened outputs are not good representations, i.e. experiments in Fig. 3.
Note that the predictors in the asymmetric methods (L197), on the other hand, do not rely on batch statistics, which I believe is a key difference.
ii) The comparisons in Table 2 may not show the full picture, e.g. baselines like BYOL/SWAV may be significantly under-trained. Here, the batch size for BYOL/SWAV is 4096. When trained for fewer epochs (e.g. 200 epochs), a large batch size may hurt the performance as it leads to significantly fewer training iterations. It would be better if baselines like BYOL/SWAV-batch-size-512-epoch-100/200 are also included.
iv) Channel whitening has been proposed before in [47] for the same task. As [47] has been published in ICLR 2022. I’m not sure if [47] could be considered a concurrent work. Compared to [47], the new content is the random group partition. This extra design may not be enough for NeurIPS. Overall, I believe [47] should at least be included as a baseline, and the ablation on the random group partition should be included.
Minor issues
i) L18-19 “two networks are trained …[8]”, I think there is only one network
ii) L286: “rand” → “random”
iii) Table 1, Simsim → SimSiam
iv) Table 1, references are included for some baselines (SimCLR, BYOL), but not all (e.g. Shuffled-DBN, W-MSE)
v) Table 2 & 3, it would be better if references are included.
Limitations are discussed in the main paper. Potential negative societal impacts are not discussed. | 3. Note that the predictors in the asymmetric methods (L197), on the other hand, do not rely on batch statistics, which I believe is a key difference. ii) The comparisons in Table 2 may not show the full picture, e.g. baselines like BYOL/SWAV may be significantly under-trained. Here, the batch size for BYOL/SWAV is 4096. When trained for fewer epochs (e.g. |
NIPS_2019_854 | NIPS_2019 | weakness I found in the paper is that the experimental results for Atari games are not significant enough. Here are my questions: - In the proposed E2W algorithm, what is the intuition behind the very specific choice of $\lambda_t$ for encouraging exploration? What if the exploration parameter $\epsilon$ is not included? Also, why is $\sum_a N(s, a)$ (but not $N(s, a)$) used for $\lambda_s$ in Equation (7)? - In Figure 3, when $d=5$, MENTS performs slightly worse than UCT at the beginning (for about 20 simulation steps) and then suddenly performs much better than UCT. Any hypothesis about this? It makes me wonder whether the algorithm scales with larger tree depth $d$. - In Table 1, what are the standard errors? Is it just one run for each algorithm? There is no learning curve showing whether each algorithm converges. What about the final performance? Itâs hard for me to justify the significance of the results without these details. - In Appendix A (experimental details), there are sentences like ``The exploration parameters for both algorithms are tuned from {}.ââ What are the exact values of all the hyperparameters used for generating the figures and tables? What hyperparameters is the algorithm sensitive to? Please make it more clear to help researchers replicate the results. To summarize based on the four review criteria: - Originality: To the best of my knowledge, the algorithm presented is original: it builds on previous work (a combination of MCTS and maximum entropy policy optimization), but comes up with a new idea for selecting actions in the tree based on the softmax value estimate. - Quality: The contribution is technically sound. The proposed method is shown to achieve an exponential convergence rate to the optimal solution, which is much faster than the polynomial convergence rate of UCT. It is also evaluated on two test domains with some good results. The experimental results for Atari games are not significant enough though. - Clarity: The paper is clear and well-written. - Significance: I think the paper is likely to be useful to those working on developing more sample efficient online planning algorithms. UPDATE: Thanks for the author's response! It addresses some of my concerns about the significance of the results. But it is still not strong enough to cause me to increase my score as it is already relatively high. | - Significance: I think the paper is likely to be useful to those working on developing more sample efficient online planning algorithms. UPDATE: Thanks for the author's response! It addresses some of my concerns about the significance of the results. But it is still not strong enough to cause me to increase my score as it is already relatively high. |
NIPS_2017_110 | NIPS_2017 | of this work include that it is a not-too-distant variation of prior work (see Schiratti et al, NIPS 2015), the search for hyperparameters for the prior distributions and sampling method do not seem to be performed on a separate test set, the simultion demonstrated that the parameters that are perhaps most critical to the model's application demonstrate the greatest relative error, and the experiments are not described with adequate detail. This last issue is particularly important as the rupture time is what clinicians would be using to determine treatment choices. In the experiments with real data, a fully Bayesian approach would have been helpful to assess the uncertainty associated with the rupture times. Paritcularly, a probabilistic evaluation of the prospective performance is warranted if that is the setting in which the authors imagine it to be most useful. Lastly, the details of the experiment are lacking. In particular, the RECIST score is a categorical score, but the authors evaluate a numerical score, the time scale is not defined in Figure 3a, and no overall statistics are reported in the evaluation, only figures with a select set of examples, and there was no mention of out-of-sample evaluation.
Specific comments:
- l132: Consider introducing the aspects of the specific model that are specific to this example model. For example, it should be clear from the beginning that we are not operating in a setting with infinite subdivisions for \gamma^1 and \gamma^m and that certain parameters are bounded on one side (acceleration and scaling parameters).
- l81-82: Do you mean to write t_R^m or t_R^{m-1} in this unnumbered equation? If it is correct, please define t_R^m. It is used subsequently and it's meaning is unclear.
- l111: Please define the bounds for \tau_i^l because it is important for understanding the time-warp function.
- Throughout, the authors use the term constrains and should change to constraints.
- l124: What is meant by the (*)?
- l134: Do the authors mean m=2?
- l148: known, instead of know
- l156: please define \gamma_0^{***}
- Figure 1: Please specify the meaning of the colors in the caption as well as the text.
- l280: "Then we made it explicit" instead of "Then we have explicit it" | - l280: "Then we made it explicit" instead of "Then we have explicit it" |
ACL_2017_759_review | ACL_2017 | Jointly Modeling salient phrase extraction and discourse relationship labeling between speaker turns has been proposed. If intuitive explanation about their interactivity and the usefulness of considering it is fully presented.
- General Discussion: SVM-based classifier is set as a comparative method in the experiment. It would be useful to mention the validity of the setting. | -General Discussion: SVM-based classifier is set as a comparative method in the experiment. It would be useful to mention the validity of the setting. |
2JN73Z8f9Q | ICLR_2025 | - This article seems more like a prototype design rather than a complete paper, as it lacks many implementation and experimental details.
- I didn't see any examples, nor did I see any supplementary materials provided for demonstration (did I miss something?).
- How is the success rate validated? How is success defined?
- I understand A stands for audio, and V stands for video, but what does AV-V mean? What is the task? What is the goal? Does it require - - human involvement, as the paper mentions human alignment as a contribution?
- What are Plan1, Plan2, and Plan3? What are the differences?
- What do Agent1, Agent2, and Agent3 represent? What is their significance?
- What does Average steps mean? Is fewer better?
- What are the differences in the success rate between Tables 4 and 5?
- Each task seems to have different input/output formats. How are they validated separately?
- The images look very rudimentary, and some of the text is even unclear. | - The images look very rudimentary, and some of the text is even unclear. |
NIPS_2017_351 | NIPS_2017 | - As I said above, I found the writing / presentation a bit jumbled at times.
- The novelty here feels a bit limited. Undoubtedly the architecture is more complex than and outperforms the MCB for VQA model [7], but much of this added complexity is simply repeating the intuition of [7] at higher (trinary) and lower (unary) orders. I don't think this is a huge problem, but I would suggest the authors clarify these contributions (and any I may have missed).
- I don't think the probabilistic connection is drawn very well. It doesn't seem to be made formally enough to take it as anything more than motivational which is fine, but I would suggest the authors either cement this connection more formally or adjust the language to clarify.
- Figure 2 is at an odd level of abstraction where it is not detailed enough to understand the network's functionality but also not abstract enough to easily capture the outline of the approach. I would suggest trying to simplify this figure to emphasize the unary/pairwise/trinary potential generation more clearly.
- Figure 3 is never referenced unless I missed it.
Some things I'm curious about:
- What values were learned for the linear coefficients for combining the marginalized potentials in equations (1)? It would be interesting if different modalities took advantage of different potential orders.
- I find it interesting that the 2-Modalities Unary+Pairwise model under-performs MCB [7] despite such a similar architecture. I was disappointed that there was not much discussion about this in the text. Any intuition into this result? Is it related to swap to the MCB / MCT decision computation modules?
- The discussion of using sequential MCB vs a single MCT layers for the decision head was quite interesting, but no results were shown. Could the authors speak a bit about what was observed? | - I find it interesting that the 2-Modalities Unary+Pairwise model under-performs MCB [7] despite such a similar architecture. I was disappointed that there was not much discussion about this in the text. Any intuition into this result? Is it related to swap to the MCB / MCT decision computation modules? |
NIPS_2017_35 | NIPS_2017 | - The applicability of the methods to real world problems is rather limited as strong assumptions are made about the availability of camera parameters (extrinsics and intrinsics are known) and object segmentation.
- The numerical evaluation is not fully convincing as the method is only evaluated on synthetic data. The comparison with [5] is not completely fair as [5] is designed for a more complex problem, i.e., no knowledge of the camera pose parameters.
- Some explanations are a little vague. For example, the last paragraph of Section 3 (lines 207-210) on the single image case. Questions/comments:
- In the Recurrent Grid Fusion, have you tried ordering the views sequentially with respect to the camera viewing sphere?
- The main weakness to me is the numerical evaluation. I understand that the hypothesis of clean segmentation of the object and known camera pose limit the evaluation to purely synthetic settings. However, it would be interesting to see how the architecture performs when the camera pose is not perfect and/or when the segmentation is noisy. Per category results could also be useful.
- Many typos (e.g., lines 14, 102, 161, 239 ), please run a spell-check. | - The main weakness to me is the numerical evaluation. I understand that the hypothesis of clean segmentation of the object and known camera pose limit the evaluation to purely synthetic settings. However, it would be interesting to see how the architecture performs when the camera pose is not perfect and/or when the segmentation is noisy. Per category results could also be useful. |
NIPS_2016_386 | NIPS_2016 | , however. For of all, there is a lot of sloppy writing, typos and undefined notation. See the long list of minor comments below. A larger concern is that some parts of the proof I could not understand, despite trying quite hard. The authors should focus their response to this review on these technical concerns, which I mark with ** in the minor comments below. Hopefully I am missing something silly. One also has to wonder about the practicality of such algorithms. The main algorithm relies on an estimate of the payoff for the optimal policy, which can be learnt with sufficient precision in a "short" initialisation period. Some synthetic experiments might shed some light on how long the horizon needs to be before any real learning occurs. A final note. The paper is over length. Up to the two pages of references it is 10 pages, but only 9 are allowed. The appendix should have been submitted as supplementary material and the reference list cut down. Despite the weaknesses I am quite positive about this paper, although it could certainly use quite a lot of polishing. I will raise my score once the ** points are addressed in the rebuttal. Minor comments: * L75. Maybe say that pi is a function from R^m \to \Delta^{K+1} * In (2) you have X pi(X), but the dimensions do not match because you dropped the no-op action. Why not just assume the 1st column of X_t is always 0? * L177: "(OCO )" -> "(OCO)" and similar things elsewhere * L176: You might want to mention that the learner observes the whole concave function (full information setting) * L223: I would prefer to see a constant here. What does the O(.) really mean here? * L240 and L428: "is sufficient" for what? I guess you want to write that the sum of the "optimistic" hoped for rewards is close to the expected actual rewards. * L384: Could mention that you mean |Y_t - Y_{t-1}| \leq c_t almost surely. ** L431: \mu_t should be \tilde \mu_t, yes? * The algorithm only stops /after/ it has exhausted its budget. Don't you need to stop just before? (the regret is only trivially affected, so this isn't too important). * L213: \tilde \mu is undefined. I guess you mean \tilde \mu_t, but that is also not defined except in Corollary 1, where it just given as some point in the confidence ellipsoid in round t. The result holds for all points in the ellipsoid uniformly with time, so maybe just write that, or at least clarify somehow. ** L435: I do not see how this follows from Corollary 2 (I guess you meant part 1, please say so). So first of all mu_t(a_t) is not defined. Did you mean tilde mu_t(a_t)? But still I don't understand. pi^*(X_t) is (possibly random) optimal static strategy while \tilde \mu_t(a_t) is the optimistic mu for action a_t, which may not be optimistic for pi^*(X_t)? I have similar concerns about the claim on the use of budget as well. * L434: The \hat v^*_t seems like strange notation. Elsewhere the \hat is used for empirical estimates (as is standard), but here it refers to something else. * L178: Why not say what Omega is here. Also, OMD is a whole family of algorithms. It might be nice to be more explicit. What link function? Which theorem in [32] are you referring to for this regret guarantee? * L200: "for every arm a" implies there is a single optimistic parameter, but of course it depends on a ** L303: Why not choose T_0 = m Sqrt(T)? Then the condition becomes B > Sqrt(m) T^(3/4), which improves slightly on what you give. * It would be nice to have more interpretation of theta (I hope I got it right), since this is the most novel component of the proof/algorithm. | * It would be nice to have more interpretation of theta (I hope I got it right), since this is the most novel component of the proof/algorithm. |
NIPS_2021_1907 | NIPS_2021 | There is little improvement empirically. Furthermore, it is unclear if the gains in this paper are due solely to the confidence widths or if the design of the algorithm is important too. For the empirical study, it is unclear how the other experiments would perform if they had access to the same confidence widths presented in this work. This may make the algorithmic comparison fairer since the differences in performance would be solely due to the sampling procedures. Also, (and I am torn on this since the setup is nice and clear) it is worth noting that the authors are most of the way through page 5 before any results are presented.
Other comments and questions: - Does theorem 1 hold for an adaptive sequence of x_n’s or a fixed sequence? The theorem just seems to specify a set of (x,y)’s that have been collected. Ie, is this a truly anytime result or for a fixed sequence? In the case of a linear kernel, the gap in the confidence widths between an anytime and fixed confidence bound is O(\sqrt(d)) which behaves like O(sqrt(\gamma_n)) in that setting. I guess that the algorithm is using these as an adaptive sequence which is maybe okay from a Bayesian perspective. - Same question for Thm 2 - For the result in remark 2, do other works get the same factor of d since log(N^d) = dlog(N)? This work is tighter in terms of \sqrt(\gamma) but is the d dependence the same? - Why is MVR the right sampling objective? - Regarding the statement in Section 6 about simple and cumulative regret bounds, it is somewhat expected that the cumulative regret is linear if you do this well on simple regret as your objective is largely one of exploration. Take for example the SE kernel as the variance \sigma -> 0. In this setting, we recover standard multiarmed bandits where http://sbubeck.com/ALT09_BMS.pdf for instance show that there cannot be an algorithm that is simultaneously optimal in both simple and cumulative regret.
Minor comments: - Make sure that the colors chosen for the plots are colorblind friendly. There are a variety of palettes in python for this. - Some of the axes in the plots in the main body and especially Appendix G are hard to read.
The authors do a good job discussing the limitations of their work, though more consideration should be given to potential negative societal impacts than simply saying “our work is theoretical, therefore we can do no wrong.” | - Some of the axes in the plots in the main body and especially Appendix G are hard to read. The authors do a good job discussing the limitations of their work, though more consideration should be given to potential negative societal impacts than simply saying “our work is theoretical, therefore we can do no wrong.” |
NIPS_2018_288 | NIPS_2018 | . Given bellow is a list of remarks regarding these weaknesses and requests for clarifications and updates to the manuscript. - The algorithmâs O(1/(\esiplon^3 (1-\gamma)^7)) complexity is extremely high. Of course, this is not practical. Notice that as opposed to the nice recovery time O(\epsilon^{-(d+3)}) result, which is almost tight, the above complexity stems from the algorithmâs design. - Part of the intractability of the algorithm comes from the requirement of full coverage of all ball-action pairs, per each iteration. This issue is magnified by the fact that the NN effective distance, h^*, is O(\epsilon (1-\gamma)). This implies a huge discretized state set, which adds up to the above problematic complexity. The authors mention (though vaguely) that the analysis is probably loose. I wonder how much of the complexity issues originate from the analysis itself, and how much from the algorithmâs design. - In continuation to the above remark, what do you think can be done (i.e. what minimal assumptions are needed) to relax the need of visiting all ball-action pairs with each iteration? Alternatively, what would happen if you partially cover them? - Table 1 lacks two recent works [1,2] (see below) that analyze the sample complexity of parametrized TD-learning algorithms that has all âyesâ values in the columns except for the âsingle sample pathâ column. Please update accordingly. - From personal experience, I believe the Lipschitz assumption is crucial to have any guarantees. Also, this is a non-trivial assumption. Please stress it further in the introduction, and/or perhaps in the abstract itself. - There is another work [3] that should also definitely be cited. Please also explain how your work differs from it. - It is written in the abstract and in at least one more location that your O(\epsilon^{-(d+3)}) complexity is tight, but you mention a lower bound which differs by a factor of \epsilon^{-1}. So this is not really tight, right? If so, please rephrase. - p.5, l.181: âofâ is written twice. p.7, l.267: âtheâ is written twice. References: [1] Finite Sample Analyses for TD (0) with Function Approximation, G Dalal, B Szörényi, G Thoppe, S Mannor, AAAI 2018 [2] Finite Sample Analysis of Two-Timescale Stochastic Approximation with Applications to Reinforcement Learning G Dalal, B Szörényi, G Thoppe, S Mannor, COLT 2018 [3] Batch Mode Reinforcement Learning based on the Synthesis of Artificial Trajectories, Raphael Fonteneau, Susan A. Murphy, Louis Wehenkel, and Damien Ernst, Annals of Operations Research 2013 | - Part of the intractability of the algorithm comes from the requirement of full coverage of all ball-action pairs, per each iteration. This issue is magnified by the fact that the NN effective distance, h^*, is O(\epsilon (1-\gamma)). This implies a huge discretized state set, which adds up to the above problematic complexity. The authors mention (though vaguely) that the analysis is probably loose. I wonder how much of the complexity issues originate from the analysis itself, and how much from the algorithmâs design. |
NIPS_2017_560 | NIPS_2017 | weakness, but this seems not to be a problem in most examples.
3. Equation 2.6 is wrong as written; as it does not make sense to divide by a vector. (easy to fix, but I surprised at the sloppiness here given that the paper well written overall).
4. Just for clarity, in eq 1.1, state clearly that F_\theta(x) is submodular in x for every \theta.
5. Can some nonconvex constraint sets which have an easy projection be handled as well?
6. What if the projection onto set K can be computed only approximately? | 3. Equation 2.6 is wrong as written; as it does not make sense to divide by a vector. (easy to fix, but I surprised at the sloppiness here given that the paper well written overall). |
NIPS_2016_95 | NIPS_2016 | 1. The time complexity of the learning algorithm should be explicitly estimated to proof the scalability properties. 2. In Figure 4, the time complexity for TRMF-AR({1,8}) and TRMF-AR({1,2,â¦,8}) seems to be the same. The reason should be explained. | 2. In Figure 4, the time complexity for TRMF-AR({1,8}) and TRMF-AR({1,2,â¦,8}) seems to be the same. The reason should be explained. |
0TSAIUCwpp | ICLR_2025 | 1. The paper has limited innovation. Its pipeline looks like a simple combination of GLC[1] and deffeic[2], utilizing the codec framework of GLC[1] and the generative model of deffeic[2]. However, the paper does not compare performance with GLC[1].
2. This paper adopts a better performance generative model RDD instead of stable diffusion, and with the stronger generative ability of RDD, better performance is obtained. So if DiffEIC-50 also adopts RRD, will it achieve better performance?
3. The conclusions of some visualization experiments are not rigorous enough. For example, in Fig. 1, despite the obvious subjective quality improvement of RDEIC, its bit rate is 7.5% higher than deffeic[2]. A similar problem can be observed in Figure 5.
4. Some analysis needs to be included to show why RDEIC is worse than MS-ILLM on the NIQE metric.
[1] Jia Z, Li J, Li B, et al. Generative Latent Coding for Ultra-Low Bitrate Image Compression. CVPR 2024.
[2] Zhiyuan Li, Yanhui Zhou, Hao Wei, Chenyang Ge, and Jingwen Jiang. Towards extreme imagecompression with latent feature guidance and diffusion prior. IEEE Transactions on Circuits and Systems for Video Technology, 2024. | 3. The conclusions of some visualization experiments are not rigorous enough. For example, in Fig. 1, despite the obvious subjective quality improvement of RDEIC, its bit rate is 7.5% higher than deffeic[2]. A similar problem can be observed in Figure 5. |
ACL_2017_333_review | ACL_2017 | There are some few details on the implementation and on the systems to which the authors compared their work that need to be better explained. - General Discussion: - Major review: - I wonder if the summaries obtained using the proposed methods are indeed abstractive. I understand that the target vocabulary is build out of the words which appear in the summaries in the training data. But given the example shown in Figure 4, I have the impression that the summaries are rather extractive.
The authors should choose a better example for Figure 4 and give some statistics on the number of words in the output sentences which were not present in the input sentences for all test sets.
- page 2, lines 266-272: I understand the mathematical difference between the vector hi and s, but I still have the feeling that there is a great overlap between them. Both "represent the meaning". Are both indeed necessary? Did you trying using only one of them.
- Which neural network library did the authors use for implementing the system?
There is no details on the implementation.
- page 5, section 44: Which training data was used for each of the systems that the authors compare to? Diy you train any of them yourselves?
- Minor review: - page 1, line 44: Although the difference between abstractive and extractive summarization is described in section 2, this could be moved to the introduction section. At this point, some users might no be familiar with this concept.
- page 1, lines 93-96: please provide a reference for this passage: "This approach achieves huge success in tasks like neural machine translation, where alignment between all parts of the input and output are required."
- page 2, section 1, last paragraph: The contribution of the work is clear but I think the authors should emphasize that such a selective encoding model has never been proposed before (is this true?). Further, the related work section should be moved to before the methods section.
- Figure 1 vs. Table 1: the authors show two examples for abstractive summarization but I think that just one of them is enough. Further, one is called a figure while the other a table.
- Section 3.2, lines 230-234 and 234-235: please provide references for the following two passages: "In the sequence-to-sequence machine translation (MT) model, the encoder and decoder are responsible for encoding input sentence information and decoding the sentence representation to generate an output sentence"; "Some previous works apply this framework to summarization generation tasks."
- Figure 2: What is "MLP"? It seems not to be described in the paper.
- page 3, lines 289-290: the sigmoid function and the element-wise multiplication are not defined for the formulas in section 3.1.
- page 4, first column: many elements of the formulas are not defined: b (equation 11), W (equation 12, 15, 17) and U (equation 12, 15), V (equation 15).
- page 4, line 326: the readout state rt is not depicted in Figure 2 (workflow).
- Table 2: what does "#(ref)" mean?
- Section 4.3, model parameters and training. Explain how you achieved the values to the many parameters: word embedding size, GRU hidden states, alpha, beta 1 and 2, epsilon, beam size.
- Page 5, line 450: remove "the" word in this line? " SGD as our optimizing algorithms" instead of "SGD as our the optimizing algorithms."
- Page 5, beam search: please include a reference for beam search.
- Figure 4: Is there a typo in the true sentence? " council of europe again slams french prison conditions" (again or against?)
- typo "supper script" -> "superscript" (4 times) | - Figure 1 vs. Table 1: the authors show two examples for abstractive summarization but I think that just one of them is enough. Further, one is called a figure while the other a table. |
ACL_2017_216_review | ACL_2017 | 1. Compared to Balikas COLING16's work, the paper has a weaker visualization (Fig 5), which makes us doubt about the actual segmenting and assigning results of document. It could be more convincing to give a longer exemplar and make color assignment consistent with topics listed in Figure 4.
2. Since the model is more flexible than that of Balikas COLING16, it may be underfitting, could you please explain this more?
- General Discussion: The paper is well written and structured. The intuition introduced in the Abstract and again exemplified in the Introduction is quite convincing. The experiments are of a full range, solid, and achieves better quantitative results against previous works. If the visualization part is stronger, or explained why less powerful visualization, it will be more confident. Another concern is about computation efficiency, since the seminal LDA work proposed to use Variational Inference which is faster during training compared to MCMC, we wish to see the author’s future development. | 2. Since the model is more flexible than that of Balikas COLING16, it may be underfitting, could you please explain this more? |
ARR_2022_110_review | ARR_2022 | 1. My biggest concern is that the analysis doesn't provide insights on WHICH language benefits WHICH other language in a multilingual setup. The only comparison provided is mono-vs-tri-lingual, but we should also compare vs bi-lingual (For example -- comparing En+Hi, En+Te, Hi+Te vs En+Hi+Te). This analysis may point to interesting observations on which language combination is more effective. I understand that the authors want to show us that multi-lingual representations improve performance, but understanding the relationship between different languages in this context of VLN is an equally important aspect -- the experimental setting of this paper is perfectly poised to provide this analysis, but the results are tucked away in the Appendix -- this should be moved to the main paper.
2. [ presentation of results] Table 2 should also include the best result from Shen et al. 2021 (one of the baselines), so that we can compare the finegrained results on each language and metric.
3. There seems to be some discrepancy between the scores for RxR in Table 1 and the scores reported by Shen et al for RxR (see Table 4 in Shen et al.) -- could you elaborate why?
4. Sec 6.3 results are provided inline, but not as a figure/table. It is difficult to understand the improvements easily. I would strongly recommend making this a table, and also providing SOTA methods for R2R and CVDN in that table (not just the baselines). This will tell us how far away the proposed transferred model fares vs fully supervised models on the respective datasets.
5. Sec 6.3: The definition of "transfer" is unclear. Does it mean that only the navigation step is trained on R2R and CVDN while the representation step is used from RxR? Or are both steps retrained (in that case it isn't a transfer). What about zero-shot transfer from RxR to R2R? How does the CLEAR approach fare on zero-shot?
6. Sec N of the appendix includes another baseline (SimCSE, Gao et al) -- but this is missing from the tables in the main paper. Why?
7. Are LSTMs a better choice for the navigation step? Would a transformer/attention mechanism be better suited for learning longer sequences? This architectural choice should be justified.
8. In Related Work (Sec 2), other datasets/methods for V&L with multilinguality are mentioned (VQA, captioning, retrieval...) -- is your method inspired by/related to any of these methods? If not, how is it different?
1. Sec 6.3 is titled "Generalization to other V&L tasks" -- this is misleading since both eval datasets are also VLN datasets. Other tasks has the connotation of other V&L tasks such as VQA, captioning, ... 2. There seems to be a related cross-lingual VLN dataset (English-Chinese) based on R2R -- https://arxiv.org/abs/1910.11301 . You might want to test CLEAR on this benchmark if possible -- I'm not sure how practical it is, so I've not included this under "Weaknesses". At the very least, it would be prudent to include this in related work.
3. Overall, I would encourage the authors to re-think which analysis should go into the main paper and which in the appendix. In my opinion, every study that directly contributed to the 2 claims from the abstract, should be moved to the main paper. The main contribution of this paper seems to be the multi-lingual training -- as such ablation studies about this part of the algorithm are more important that the ablation study about visual features. (Table 9 for example) This paper makes a step in a very interesting direction -- however, I would like to see (1) re-organization of the analysis (between main and appendix), (2) focused and precise analysis of multi-lingual training, and (3) more details and exhaustive experiments in the transfer learning setup. My current score of 3.5 reflects these weaknesses + other unclear details that I've mentioned in "Weaknesses" above. In case the paper doesn't go through to your ideal *ACL venue, please address these issues before resubmitting and I'll be happy to continue as a reviewer of this paper. | 4. Sec 6.3 results are provided inline, but not as a figure/table. It is difficult to understand the improvements easily. I would strongly recommend making this a table, and also providing SOTA methods for R2R and CVDN in that table (not just the baselines). This will tell us how far away the proposed transferred model fares vs fully supervised models on the respective datasets. |
NIPS_2019_104 | NIPS_2019 | . Despite the great technical material covered in the paper, its choice of organization makes the paper hard to follow; see detailed comments below. In addition, some related and recent literature on regret minimization in RL seem to be missing. Besides, I have some technical comments, which I detail below. 1. Organization: As said earlier, despite solid theoretical content, one may find the paper hard to follow due to the choice of organization. In particular: (i) one may expect that the algorithm StrongEuler to be fully specified in the main text rather than the supplementary; (ii) The proofs in the supplementary are not well-organized, and are hard-to-follow for most readers; and (ii) there is no conclusion section. 2. About Definition 3.1. The optimism should hold âwith high probabilityâ, right? Without this, I am not sure if one can guarantee that \bar Q_{k,h} \ge Q*_{k,h} for all x, a, k, and h. Could you explain? 3. Line 218, the statement âall existing optimistic algorithmâ: the aforementioned collection of algorithms is not defined precisely. Since you are making a claim about the regret of such algorithm (which seems to be a strong one), you must specify this set clearly. Otherwise, the statement *should* be relaxed. Another vague statement of this type appears in line 212: â⦠is unavoidable for the sorts of the optimistic algorithms that we typically see in the literatureâ: again, I may ask to make the statement more precise and specific; otherwise, the claim needs to be accordingly relaxed. Minor comments: a. Theorem 2.4: \epsilon is not introduce. Does it have the same range as in Theorem 2.3? b. Line 31: The logarithmic regret bound in Jaksch et al. is an exception, as it is non-asymptotic (though it depends on the âwrong gapâ gap_*). c. Line 48: the term âalmost-gap-dependentâ does not appear to be precise enough. d. Line 96: what is \tilde S? Shouldnât it be S? e. Line 107: P(sâ|s,a) is not introduced here yet, and later it seems you use p(sâ|s,a). f. Line 107: that can be made optimal --> ⦠**uniquely** optimal (Note the uniqueness here is crucial for the proof in [15] based on change-of-measure argument to work). e. Line 897: I couldnât verify the second inequality \sqrt{a} + \sqrt{b} \precsim \sqrt{a+b}. Could you explain? Typos: Line 20: number states --> number of states Line 39: worse-case --> worst-case Line 93: discounted regret --> undiscounted regret (Isnât it correct?) Line 95: [8] give ⦠--> [8] gives Line 120: et seq. --> etc. (??) Line 129: a_{aâ} --> a_{hâ} Line 166-167: sharped --> sharpened Line 169: in right hand side --> in the right-hand side Line 196: we say than ⦠--> we say that ⦠Line 230: In the regret bound, remove extra â}â. Line 269: \sum_{t=1}^K ⦠\omega_{k,h} --> â¦\omega_{t,h} Line 268: at the end of the sentence, â)â is missing. Line 275 (and elsewhere): Cauchy-Schwartz --> Cauchy-Schwarz Line 438: the second term does not dependent --> the rest of the sentence is missing. Line 502, 590, and elsewhere: author? --> use correct referencing! Line 525: similar to ⦠--> similarly to ⦠Line 634: Then suppose that ⦠--> is it correct to begin the lemma with âthenâ? Line 656: proven Section ⦠--> proven in Section ⦠Line 668: We can with a crude comparison ⦠--> The sentence does not make sense. Line 705 â Eq. 19: gap_h --> gap_h(x,a) AND â)â is missing Line 703 â iii : â)â is missing. Line 814: similar to --> similarly to Algorithm 1: Input is not provided. Algorithm 2, Line 4: rsum --> rsum_k AND the second rsum should perhaps be rsumsq Line 1085: Lemma 6 in [6] in shows --> remove the second âinâ -- Updates (after author feedback) -- I have read the other reviews and have gone through authors' response. The response satisfactorily clarified my raised comments. In particular, the authors provided a precise plan to revise the organization of the paper. I therefore increase my score to 8. | 1. Organization: As said earlier, despite solid theoretical content, one may find the paper hard to follow due to the choice of organization. In particular: (i) one may expect that the algorithm StrongEuler to be fully specified in the main text rather than the supplementary; (ii) The proofs in the supplementary are not well-organized, and are hard-to-follow for most readers; and (ii) there is no conclusion section. |
JWwvC7As4S | ICLR_2024 | ### Theory
The main theoretical results are Theorem 2.1 and 2.2. They state that if the "average last-layer feature norm and the last-layer weight matrix norm are both bounded, then achieving near-optimal loss implies that most classes have intra-class cosine similarity near one and most pairs of classes have inter-class cosine similarity near -1/(C-1)".
Qualitatively, this result is an immediate consequence of continuity of the loss function together with the fact that bounded average last-layer feature norm and bounded last-layer weight matrices implies NC.
Quantitatively, this work proves asymptotic bounds on the proximity to NC as a function of the loss. This quantitative aspect is novel. I am not convinced of its significance however, as I will outline below.
1. The result is only asymptotic, and thus it cannot be used to estimate proximity to NC from a given loss value.
2. The bound is used as basis to argue that *"under the presence of batch normalization
and weight decay of the final layer, larger values of weight decay provide stronger NC guarantees in the sense that the intra-class cosine similarity of most classes is nearer to 1 and the inter-class cosine similarity of most pairs of classes is nearer to -1/(C-1)."*
This is backed up by the observation, that the bounds get more tight if the weight decay parameter $\lambda$ increases. To be more specific, Theorem 2.2 shows that if $L< L{min}+\epsilon$, then the average intra class cosine similarity is smaller than $-1/(C-1) + O(f(C,\lambda,\epsilon,\delta))$ and $f$ decreases with $\lambda$.
The problem with this argument is that the loss function itself depends on the regularization parameter $\lambda$ and so it is a-priori not clear whether values of $\epsilon$ are comparable for different $\lambda$. For example, apply this argument to the more simple loss function $L(x,\lambda)=\lambda x^2$. As $L$ is convex, it is clear that the value of $\lambda>0$ is irrelevant for the minimum and the near optimal solutions. Yet, $L(x,\lambda)<\epsilon$ implies $x^2<\epsilon/\lambda$ which decreases with $\lambda$. By the logic given in this work, the latter inequality suggests that minimizing a loss function with a larger value of $\lambda$ provides stronger guarantees for arriving close to the minimum at $0$. Clearly, this is not the case and an artifact of quantifying closeness to the loss minimum by $\epsilon$, when it should have been adjusted to $\lambda \epsilon$ instead.
I have doubts on how batch normalization is handled. As far as I see, batch normalization enters the proofs only through the condition $\sum_i \| h_i \|^2 =\| h_i \|^2$ (see Prop 2.1). However, this is only an implication and batch normalization induces stronger constraints. The theorems assume that the loss minimizer is a simplex ETF in the presence of batch normalization. This is not obvious, and neither proven nor discussed. It is also not accounted for in the part of the proof of Theorem 2.2, where the loss minimum $m_{reg}$ is derived.
### Experiments
- Theorems 2.1 and 2.2 are not evaluated empirically. It is not tested, whether the average intra / inter class cosine similarities of near optimal solutions follow the exponential dependency in $\lambda$ and the square (or sixth) root dependency on $\epsilon$ as suggested by the theorems.
- Instead, the dependency of cosine similarities at the end of training (200 epochs) on weight decay strength is evaluated. As presumed by the authors, the intra class cosine similarities get closer to the optimum, if the weight decay strength increases. Yet, there are problems with this experiment. It is inconsistent with the setting of the theory part and thus only provides limited insight on if the idealized theoretical results transfer to practice.
1. The theory part depends only on the weight decay strength on the last layer parameters. Yet, in the experiments, weight decay is applied to all layers and its strength varies between experiments (when instead only the strength of the last layer should change).
2. The theorems assume near optimal training loss, but training losses are not reported. Moreover, the reported cosine similarities are far from optimal (e.g. intra class is around 0.2 instead of 1) which suggests that the training loss is also far from optimal. It also suggests that the models are of too small capacity to justify the 'unconstrained-features' assumption.
3. As (suboptimally) weight decay is applied to all layers, we would expect a large training loss and thus suboptimal cosine similarities for large weight decay parameters. Conveniently, cosine similarities for such large weight decay strengths are not reported and the plots end at a weight decay strength where cosine similarities are still close to optimal.
4. On real-world data sets, the inter class cosine similarity increases with weight decay (even for batch norm models VGG11), disagreeing with the theoretical prediction. This observation is insufficiently acknowledged.
### General
The central question that this work wants to answer **What is a minimal set of conditions that would guarantee the emergence of NC?"** is already solved in the sense that it is known that minimal loss plus a norm constraint on the features (explicit via feature normalization or implicit via weight decay) implies neural collapse. The authors argue to add batch normalization to this list but that contradicts minimality.
The first contribution listed by the authors is not a contribution.
1. *"We propose the intra-class and inter-class cosine similarity measure, a simple and geometrically intuitive quantity that measures the proximity of a set of feature vectors to several core
structural properties of NC. (Section 2.2)"*
Cosine similarity (i.e. the normalized inner product) is a well known and an extensively used distance measure on the sphere. In the context of neural collapse, cosine similarities were already used in the foundational paper by Papyan et al. (2020) to empirically quantify closeness to NC (cf. Figure 3 in this reference) and many others. Minor:
- There is a grammatical error in the second sentence of the second paragraph
- There is no punctuation after formulas; In the appendix, multiple rows start with a punctuation
- intra / inter is sometimes written in italics, sometimes upright
- $\beta$ is used multiply with a different meaning
- Proposition 2.1 $N$ = batch site, Theorem 2.2 $N$ = number of samples per class.
- As a consequence, it seems that $\gamma$ needs to be rescaled to account for the number of batches | 2. The theorems assume near optimal training loss, but training losses are not reported. Moreover, the reported cosine similarities are far from optimal (e.g. intra class is around 0.2 instead of 1) which suggests that the training loss is also far from optimal. It also suggests that the models are of too small capacity to justify the 'unconstrained-features' assumption. |
NIPS_2016_93 | NIPS_2016 | / Major concerns: - It is difficult to evaluate whether the MovieQA result should be considered significant given that +10% gap exists between MemN2N on dataset with explicit answers (Task 1) and RBI + FP on dataset with other forms of supervision, especially Task 3. If I understood correctly, the different tasks are coming from the same data, but authors provide different forms of supervision. Also, Task 3 gives full supervision of the answers. Then I wonder why RBI + FP on task 3 (69%) is doing much worse than MemN2N on task 1 (80%). Is it because the supervision is presented in a more implicit way ("No, the answer is kitchen" instead of "kitchen")? - For RBI, they only train on rewarded actions. Then this means rewardless actions that get useful supervision (such as "No, the answer is Timothy Dalton." in Task 3) is ignored as well. I think this could be one significant factor that makes FP + RBI better than RBI alone. If not, I think the authors should provide stronger baseline than RBI (that is supervised by such feedback) to prove the usefulness of FP. Questions / Minor concerns: - For bAbI, it seems the model was only tested on single supporting fact dataset (Task 1 of bAbI). How about other tasks? - How is dialog dataset obtained from QA datasets? Are you using a few simple rules? - Lack of lexical / syntactic diversity of teacher feedback: assuming the teacher feedback was auto-generated, do you intend to turk the teacher feedback and / or generate a few different kinds of feedback (which is more real-life situation)? - How does other models than MemN2N do on MovieQA? | - How is dialog dataset obtained from QA datasets? Are you using a few simple rules? |
NIPS_2022_1250 | NIPS_2022 | Lacking of discussions or motivations for the importance of the proposed idea
Empirical results: Can be on toy tasks
The paper pursues an interesting research direction, which tries to unify existing POMDP formalisms. The approach looks very promising. The proposed design of the critic is very interesting. It would become very interesting if the paper can provides some basic empirical results on toy tasks to show all important claim in practice. - As the unified framework can now obtain provably efficient learning for most POMDP formalisms. Is there any limitations of its, e.g. can it do the same for any general POMDP formulations (continuous or infinite spaces)? - How can one understand agnostic learning? In Algorithm, is z just defined as historical observations? Or is it in the form of belief? | - How can one understand agnostic learning? In Algorithm, is z just defined as historical observations? Or is it in the form of belief? |
ICLR_2023_2406 | ICLR_2023 | 1. However, my major concern is that the contribution is insufficient. In general, the authors studied the connection between the complementary and the model robustness but without further studies on how to leverage such characteristics to improve model robustness. Even though this paper could be the first work to study this connection, the conclusion could be easily and intuitively obtained, i.e., when multimodal complementary is higher, the robustness is more delicate when one of the modalities is corrupted. Except for the analysis of the connection between complementary and robustness, it is expected to see more insightful findings or possible solutions. 2. The proposed metric is calculated on the features extracted by some pre-trained models. So the pre-trained models are necessary for metric computing which is contradictory to that the metric is used to measure the multimodal data complementary. In addition, in my opinion, the metric is unreliable since the model participates in the metric calculation and will inevitably affect the calculation results. 3. There are many factors that will affect the model's robustness. The multimodal data complementary is one of them. However, multimodal data complementary is not solely determined by the data itself. For example, classification on MS-COCO data is obviously less complementary than VQA on MS-COCO data. As mentioned by the author, the VQA task requires both modalities for question answering, accordingly the complementary is determined by the multimodal and the target task. However, I didn't see much further discussion about these possible factors. | 3. There are many factors that will affect the model's robustness. The multimodal data complementary is one of them. However, multimodal data complementary is not solely determined by the data itself. For example, classification on MS-COCO data is obviously less complementary than VQA on MS-COCO data. As mentioned by the author, the VQA task requires both modalities for question answering, accordingly the complementary is determined by the multimodal and the target task. However, I didn't see much further discussion about these possible factors. |
ICLR_2021_2953 | ICLR_2021 | )
The idea of incorporating the training dynamics to the Bayesian optimization tuning process to construct online BO is novel.
The experiments are conducted on two complex datasets CIFAR-10, CIFAR-100. Weaknesses:
No deep analysis is conducted to understand why the proposed method can lead to better generalization.
I feel unclear with several technical details: 1) What is the x-axis in Figures 1 & 2? Is it the number of epochs? 2) How many experiments are repeated in Figures 1&2 and Table 1? 3) How to set the search space S for GSdyn? In your experiments in Section 5, how do the authors set the search space S? 4) What is the objective function for GSdyn and FABOLAS? In Section 5.1, it is mentioned that the DNN’s accuracy is the objective function, but which accuracy? The accuracy on the validation dataset or on the test dataset? 5) To evaluate BO, the standard practice is to find the hyperparameter set with the best accuracy on the validation dataset. Why in this work, the accuracy on the test dataset (but not validation dataset) is compared between baseline methods (Figures 1 &2)? And which accuracies are there in Table 1? I understand that GSdyn leads to good generalization but the accuracy on the validation dataset is also needed to be shown as it is the objective of the vanilla BO? 6) The experiments might include different hyper-parameters, and more hyper-parameters.
Minor comments:
In the figures, the labels of each axis need to be added.
Third bullet in the summarized contributions in Section 1: Beyes --> Bayes
Line 5 of Algorithm 1: Should be either \sigma_0 or \sigma, not a mix of them?
Line 5 of Algorithm 2: What is Sample function? I understand it is the acquisition function but a rigorous formula of the acquisition function needs to be provided. | 3) How to set the search space S for GSdyn? In your experiments in Section 5, how do the authors set the search space S? |
aqlzXgXwWa | ICLR_2025 | - The proposed method is computationally heavy (line 417-420, needs 8 A100 GPUs for training), making it less accessible to possible end users. This is, however, a common issue among diffusion-based methods, not particular to the paper.
- The depth-ambiguity is not completely resolved. One can see in the supplementary video 00:44, the top-left character has their hand rendered to the back incorrectly.
- The method focuses on front-facing poses. It is unclear how it performs on extreme poses with 360-degree rotation, and also poses like handstand, etc. | - The depth-ambiguity is not completely resolved. One can see in the supplementary video 00:44, the top-left character has their hand rendered to the back incorrectly. |
ljwoQ3cvQh | ICLR_2024 | - Some of the training details are opaque in the main paper, which might lead into a simpler explanation over the observed empirical performance. For instance, could the learning algorithm or the data augmentation or the normalization impact this hypothesis?
- I am skeptical about the hypothesis formed in the following sense: even if we assume a zero input, most modern networks rely on a normalization scheme, e.g. batch or layer normalization. Then, in a trained network, the “centering” provided by the learnt means and variances of the network will not result in a zero-mean representation for the next layers. As such, I am wondering how the normalization plays into the formed hypothesis. | - Some of the training details are opaque in the main paper, which might lead into a simpler explanation over the observed empirical performance. For instance, could the learning algorithm or the data augmentation or the normalization impact this hypothesis? |
NIPS_2017_217 | NIPS_2017 | - The paper is incremental and does not have much technical substance. It just adds a new loss to [31].
- "Embedding" is an overloaded word for a scalar value that represents object ID.
- The model of [31] is used in a post-processing stage to refine the detection. Ideally, the proposed model should be end-to-end without any post-processing.
- Keypoint detection results should be included in the experiments section.
- Sometimes the predicted tag value might be in the range of tag values for two or more nearby people, how is it determined to which person the keypoint belongs?
- Line 168: It is mentioned that the anchor point changes if the neck is occluded. This makes training noisy since the distances for most examples are computed with respect to the neck.
Overall assessment: I am on the fence for this paper. The paper achieves state-of-the-art performance, but it is incremental and does not have much technical substance. Furthermore, the main improvement comes from running [31] in a post-processing stage. | - The model of [31] is used in a post-processing stage to refine the detection. Ideally, the proposed model should be end-to-end without any post-processing. |
ARR_2022_169_review | ARR_2022 | 1. The paper claims that it exploits unlabelled target language data. However, in line 363, it seems that the paper actually uses event-presence labels $e_{i}$ for each target language sample. First, $e_{i}$ is probably extracted directly from labels $y_{i}$; it is when $y_{i}$ says that some word is an event trigger that one can know that $e_{i}=1$. So, for target language data, their labels are actually used in an indirect way. Thus the method is not totally using pure "unlabelled" target language data as the paper claims. Second, I think $e_{i}$ provides super crucial information which might be responsible for most of the gain derived. To make fair comparisons with the baselines, I think baseline methods BERT-CRF in section 3.2 and the BERT-CRF+MLM in 3.4 should also see $e_{i}$ labels. 2. Also concerning $e_{i}$ in weakness point 1 above, it is not known how $e_{i}$ and $e_{i}$'s distributions look like at all. I could only guess $e_{i}$ is 0,1 binary variables? Since all SRC and TRG data comes from Cross-Lingual Event Detection datasets, maybe most samples do have an event trigger and thus most $e_{i}$s equal 1. 3. It is confusing in line 339: s$\sim$p(s) and t$\sim$p(t). Do p(s) and p(t) here the ones calculated and updated in equation (6-7) in lines 369-370? Or maybe it is fixed since each sample already has a ground truth $e_{i}$. If it is the former case, I think it might be a little weird to predict the p(s) and p(t) which the paper uses to draw samples, because p(s) and p(t) are already given since $e_{i}$s are known for all samples? 4. The authors did not justify why Optimal Transport (OT) is used and did not elaborate on what are OT's advantages. One simple substitute for OT is average euclidean distance or average cosine similarity, which can be used to replace the paper's equation (8). There are more substitutes to OT, such as the KL divergence or the Jensen-Shannon divergence (which are commonly used to make comparisons with OT). It is worth comparing OT with say, Euclidean distance, KL divergence as a side experiment. All these simple substitutes are probably super-efficient and quicker to compute than OT. 5. It is not known if the OT sample selection process in 2.4.3 only runs once or runs iteratively as EP module is updated during the training steps. Are optimizing the loss of equation (10), i.e. the training steps, and solving OT in equation (3) conducted by turns iteratively? It will be much easier for readers to know the whole process if more details and a flow chart can be added. Furthermore, what is the runtime for solving the entropic regularized discrete OT problem, and the runtime for OT sample selection?
6. It is claimed in lines 128-132 that "it would be beneficial for the LD to be trained with examples containing events". The statement in lines 137-148 also focuses only on LD. Why only LD benefits from seeing examples containing events? Do the text encoders also benefit from seeing these examples? A clue that the encoder might benefit from unlabelled data is in 3.4's result where simply MLM fine-tuning can derive considerable gains.
7. In section 3.4, the result shows that simple MLM fine-tuning on unlabelled target language data derives considerable gains against BERT-CRF baseline. I was curious if the authors could do BERT-CRF + MLM + EP like in equation (10), can the performance be better than ALA? If true, it might show that a simple MLM is better than adversarial training.
1. The writing is not fluent enough. Some typos and awkward/redundant/unnatural sentences such as lines 019, 041-043.
2. Using Optimal Transport (OT), or more specifically leveraging the Wasserstein Distance, in GAN is first seen in the Wasserstein GAN paper, i.e. WGAN (Arjovsky et al. ICML 2017). It might be beneficial to discuss WGAN a bit or even add WGAN as a baseline method.
3. The paper should elaborate on OT in both the introduction and the methodology parts and should provide more details and justifications for OT.
4. In equation (4), L2 distance is used. In OT, earth mover's distance is more common. What is the benefit of L2 distance?
5. I hope to see the authors' response in resubmission (if rejected) or clarifications in the camera-ready (if accepted) to remove my concern. | 3. The paper should elaborate on OT in both the introduction and the methodology parts and should provide more details and justifications for OT. |
NIPS_2018_276 | NIPS_2018 | . Strengths: * This is the first inconsistency analysis for random forests. (Verified by quick Google scholar search.) * Clearly written to make results (mostly) approachable. This is a major accomplishment for such a technical topic. * The analysis is relevant to published random forest variations; these include papers published at ICDM, AAAI, SIGKDD. Weaknesses: * Relevance to researchers and practitioners is a little on the low side because most people are using supervised random forest algorithms. * The title, abstract, introduction, and discussion do not explain that the results are for unsupervised random forests. This is a fairly serious omission, and casual readers would remember the wrong conclusions. This must be fixed for publication, but I think it would be straightforward to fix. Officially, NIPS reviewers are not required to look at the supplementary material. Because of having only three weeks to review six manuscripts, I was not able to make the time during my reviewing. So I worry that publishing this work would mean publishing results without sufficient peer review. DETAILED COMMENTS * p. 1: I'm not sure it is accurate to say that deep, unsupervised trees grown with no subsampling is a common setup for learning random forests. It appears in Geurts et al. (2006) as a special case, sometimes in mass estimation [1, 2], and sometimes in Wei Fan's random decision tree papers [3-6]. I don't think these are used very much. * You may want to draw a connection between Theorem 3 and isolation forests [7] though. I've heard some buzz around this algorithm, and it uses unsupervised, deep trees with extreme subsampling. * l. 16: "random" => "randomized" * l. 41: Would be clearer with forward pointer to definition of deep. * l. 74: "ambient" seems like wrong word choice * l. 81: Is there a typo here? Exclamation point after \thereexists is confusing. * l. 152; l. 235: I think this mischaracterizes Geurts et al. (2006), and the difference is important for the impact stated in Section 4. Geurts et al. include a completely unsupervised tree learning as a special case, when K = 1. Otherwise, K > 1 potential splits are generated randomly and unsupervised (from K features), and the best one is selected *based on the response variable*. The supervised selection is important for low error on most data sets. See Figures 2 and 3; when K = 1, the error is usually high. * l. 162: Are random projection trees really the same as oblique trees? * Section 2.2: very useful overview! * l. 192: Typo? W^2? * l. 197: No "Eq. (2)" in paper? * l. 240: "parameter setup that is widely used..." This was unclear. Can you add references? For example, Lin and Jeon (2006) study forests with adaptive splitting, which would be supervised, not unsupervised. * Based on the abstract, you might be interested in [8]. REFERENCES [1] Ting et al. (2013). Mass estimation. Machine Learning, 90(1):127-160. [2] Ting et al. (2011). Density estimation based on mass. In ICDM. [3] Fan et al. (2003). Is random model better? On its accuracy and efficiency. In ICDM. [4] Fan (2004). On the optimality of probability estimation by random decision trees. In AAAI. [5] Fan et al. (2005). Effective estimation of posterior probabilities: Explaining the accuracy of randomized decision tree approaches. In ICDM. [6] Fan el al. (2006). A general framework for accurate and fast regression by data summarization in random decision trees. In KDD. [7] Liu, Ting, and Zhou (2012). Isolation-based anomaly detection. ACM Transactions on Knowledge Discovery from Data, 6(1). [8] Wager. Asymptotic theory for random forests. https://arxiv.org/abs/1405.0352 | * Relevance to researchers and practitioners is a little on the low side because most people are using supervised random forest algorithms. |
NIPS_2018_342 | NIPS_2018 | weakness. I didn't actually have a concern on practical use cases, as the response states. I just think it would be more interesting to consider noise that appears from the types of situations described, rather than Gaussian (and the authors acknowledged this point). Overall, this was an interesting submission. I am upping my score to 7. -------------------- This paper proposes to learn an unknown graph given a subset of the effective resistances of pairs of nodes. The proposed methods can substantially out-perform random guessing in network reconstruction on a couple synthetic networks and some Facebook egonets. The main idea of the paper is interesting and original, and the proposed methods do well on the datasets considered. However, I think the choice of egonets as real-world datasets is limiting. The fact that all nodes share a common neighbor implies substantial social structure (and possibly substantial graph structure, if the ego is included --- it is not clear if the ego is included in these datasets). I would suggest to instead use a variety of social networks, or if the authors are keen on Facebook, use some of the Facebook100 graphs. Another weakness in the experimental design is the following. The noise terms for the experiments are Gaussian, but I read the motivation for the noise terms to come from using approximation algorithms to deal with computational constraints or from partial measurements (last paragraph of introduction, lines 43--48). The usefulness of the Gaussian error seems to be that the solution to the optimization problem (Problem 2) is the MLE. The experimental results would be much more convincing if the noise was closer to the motivation. For example, the authors could compute approximations to the effective resistance with an approximation algorithm (the simplest case might be to run just use a few steps of an iterative solver for computing the effective resistances). From the presentation of the introduction, I expected more theoretical results. However, the only formal theoretical statements I see in the main text are Theorem 1, which was proved in another paper, and Proposition 1, which is a gradient calculation. Overall, I think this paper would greatly benefit by tightening up all of the language around the problem formulation and including more experiments and description of the actual methodology (e.g., what is the SDP formulation?). All of that being said, I enjoyed the main idea of the paper. The problem itself opens up some interesting avenues for both theoretical and empirical future work, and the numerical experiments do show that the proposed methods can be successful. I think the experiments (namely, choice of real-world datasets and types of noise) and presentation could be updated for an improved camera version. Thus, I lean towards accepting this paper. Fianlly, perhaps I am missing a compelling reason that we should be using egonets as the main example, so please point this out to me if it is the case. Some small issues: 1. In the explanation of privacy attacks (lines 36--42), it would be useful to know some scenarios under which the node similarities would be released, but the link information would not be released. 2. "we show that, when G is a tree, exact recovery is possible for Problem 1.2 when S is a superset of G's edges" Should this be subset of edges? 3. Please include a reference to [43] in the statement of Theorem 1. Right now, it seems like the theorem is a novel contribution of this paper, which, from my reading of the text, it is not. 4. "This approach quickly converges to near global minimums for many networks." I am not sure how I am supposed to draw this conclusion from the experiments. 5. "This modified problem is convex and can be solved via an SDP." Where is the SDP formulation? 6. Why is there no \sigma^2 = 0.1 case for FB Medium A and FB Large A. 7. Typos: Appendixx E (line 186), we learn via share (line 236) | 2. "we show that, when G is a tree, exact recovery is possible for Problem 1.2 when S is a superset of G's edges" Should this be subset of edges? |
ICLR_2022_1070 | ICLR_2022 | Weakness: 1) My main concern is that the Gaussian mixture data assumption may be too strong. As shown in Eq. (7), this paper assumed the inputs are under multivariable Gaussian distribution. Many real-world datasets break this condition, such as long-tailed distribution. Moreover, the classic random features, for example random Fourier features, have no restriction on data distribution. Besides the Gaussian data assumption, Assumption 1 (iii) also seems to be strict. The authors are expected to provide more examples to illustrate the applicability of these assumptions. 2) The presented asymptotic theory requires the dimension of input space to approach infinity p → ∞
is unfamiliar in practical. Because the dimension of input space is fixed, I wonder that is there still a good approximation between K and K ~ if p
is small? For a given task with a fixed p
, is there a natural gap between K and K ~
? 3) It seems both Theorem 1 and Corollary 1 are independent from the required number of random features m
. In the existing random features literature, m
is crucial to the approximation ability and generalization ability. In general case, m = O ( n )
random features can guarantee the similar generalization ability (Rudi and Rosasco, 2017). The authors may illustrate how the number of ternary random features influence the approximation or generalization. 4) The kernel hyperparameters usually determine the performance of kernel methods, but the proposed random features approach seems to be independent from kernel hyperparameters and only depend on the kernel type. Can TRF approximate any kernel with different hyperparameters? How does TRF remove the influence of kernel hyperparameters?
Rudi A, Rosasco L. Generalization Properties of Learning with Random Features[C]//NIPS. 2017: 3215-3225. | 4) The kernel hyperparameters usually determine the performance of kernel methods, but the proposed random features approach seems to be independent from kernel hyperparameters and only depend on the kernel type. Can TRF approximate any kernel with different hyperparameters? How does TRF remove the influence of kernel hyperparameters? Rudi A, Rosasco L. Generalization Properties of Learning with Random Features[C]//NIPS. 2017: 3215-3225. |
ICLR_2023_4333 | ICLR_2023 | Weakness:
The technical novelty of the proposed framework is limited. 1) Theorem 1 is trivial (especially the proof) under some strong assumptions. The validation of applying theorem 1 to the proposed method is not properly justified. How these assumptions are reasonable to the problem settings? 2) The idea of using Noether's theorem is not new to the AI field. The only new part is applying Noether's theorem to do some mining tasks on temporal knowledge graphs.
The challenges of proposed tasks TAQ and TAM on temporal graphs are unclear. It would be helpful if the authors could elaborate challenges of these tasks. | 1) Theorem 1 is trivial (especially the proof) under some strong assumptions. The validation of applying theorem 1 to the proposed method is not properly justified. How these assumptions are reasonable to the problem settings? |
ACL_2017_148_review | ACL_2017 | - The goal of your paper is not entirely clear. I had to read the paper 4 times and I still do not understand what you are talking about!
- The article is highly ambiguous what it talks about - machine comprehension or text readability for humans - you miss important work in the readability field - Section 2.2. has completely unrelated discussion of theoretical topics.
- I have the feeling that this paper is trying to answer too many questions in the same time, by this making itself quite weak. Questions such as “does text readability have impact on RC datasets” should be analyzed separately from all these prerequisite skills.
- General Discussion: - The title is a bit ambiguous, it would be good to clarify that you are referring to machine comprehension of text, and not human reading comprehension, because “reading comprehension” and “readability” usually mean that.
- You say that your “dataset analysis suggested that the readability of RC datasets does not directly affect the question difficulty”, but this depends on the method/features used for answer detection, e.g. if you use POS/dependency parse features.
- You need to proofread the English of your paper, there are some important omissions, like “the question is easy to solve simply look..” on page 1.
- How do you annotate datasets with “metrics”??
- Here you are mixing machine reading comprehension of texts and human reading comprehension of texts, which, although somewhat similar, are also quite different, and also large areas.
- “readability of text” is not “difficulty of reading contents”. Check this: DuBay, W.H. 2004. The Principles of Readability. Costa Mesa, CA: Impact information. - it would be good if you put more pointers distinguishing your work from readability of questions for humans, because this article is highly ambiguous.
E.g. on page 1 “These two examples show that the readability of the text does not necessarily correlate with the difficulty of the questions” you should add “for machine comprehension” - Section 3.1. - Again: are you referring to such skills for humans or for machines? If for machines, why are you citing papers for humans, and how sure are you they are referring to machines too?
- How many questions the annotators had to annotate? Were the annotators clear they annotate the questions keeping in mind machines and not people? | - How many questions the annotators had to annotate? Were the annotators clear they annotate the questions keeping in mind machines and not people? |
NIPS_2020_634 | NIPS_2020 | There are, however, a few unanswered questions. 1. Are the comparative results statistically significant? 2. In the ablation study, it is indicated that larger number of sub-networks (M) would be difficult to optimize. Is this true in the multi-source DA setting as well? If so, how does the choice of M affect the performance when there are different number of domain-specific properties within each domain? 3. What are the limitations of the proposed solution? | 2. In the ablation study, it is indicated that larger number of sub-networks (M) would be difficult to optimize. Is this true in the multi-source DA setting as well? If so, how does the choice of M affect the performance when there are different number of domain-specific properties within each domain? |
NIPS_2021_2257 | NIPS_2021 | Weakness
The connection between the first part of the paper (Sec. 3) and the second part of the paper (Sec. 4) is weak. It looks like a concatenation of two papers. The reviewer expects to see how the analyses from Sec. 3 motivate the strategies proposed in Sec. 4.
Is the proposed strategies in Sec. 4 generalizable to other SSL methods? For example, a clustering-based method like SwAV.
For fine-tuning results, the reviewer suggests including baseline methods of random init for reference.
In Sec. 3.3, the experiment of BDD on linear evaluation is missing. Is it possible that training on BDD has a negative effect in the linear evaluation setting?
In Sec 4.2, the authors only explain why using AutoAugment leads to worse results. The explanations/analyses of why standard + auto-augment leads to better performance are not provided.
(copy and paste from above) Is the proposed strategies in Sec. 4 generalizable to other SSL methods? For example, a clustering-based method like SwAV.
It is still unclear what kind of feature, bias, invariance, etc, the model captures when pre-trained on different datasets given only the performance in the linear evaluation setting and the fine-tuning setting presented in Sec. 3. For example, does the model learn a more robust representation? Is the model biased to shape or to texture? | 3. For example, does the model learn a more robust representation? Is the model biased to shape or to texture? |
ICLR_2021_1213 | ICLR_2021 | weakness of the paper. Then, I present my additional comments which are related to specific expressions in the main text, proof steps in the appendix etc. I would appreciate it very much if authors could address my questions/concerns under “Additional Comments” as well, since they affect my assessment and understanding of the paper; consequently my score for the paper. Summary:
• The paper focuses on convergence of two newly-proposed versions of AdaGrad, namely AdaGrad-window and AdaGrad-truncation, for finite sum setting where each component is smooth and possibly nonconvex.
• The authors prove convergence rate with respect to number of epochs T, where in each epoch one full pass over the data is performed with respect to well-known “random shuffling” sampling strategy.
• Specifically, AdaGrad-window is shown to achieve O ~ ( T − 1 / 2 )
rate of convergence, whereas AdaGrad-truncation attains ( T − 1 / 2 )
convergence, under component-wise smoothness and bounded gradients assumptions. Additionally, authors introduce a new condition/assumption called consistency ratio which is an essential element of their analysis.
• The paper explains the proposed modification to AdaGrad and provide their intuition for such adjustments. Then, the main results are presented followed by a proof sketch, which demonstrates the main steps of the theoretical approach.
• In order to evaluate the practical performance of the modified adaptive methods in a comparative fashion, two set of experiments were provided: training logistic regression model on MNIST dataset and Resnet-18 model on CIFAR-10 dataset. In these experiments; SGD, SGD with random shuffling, AdaGrad and AdaGrad-window were compared. Additionally, authors plot the behavior of their proposed condition “consistency ratio” over epochs. Strengths:
• I think epoch-wise analysis, especially for finite sum settings, could help provide insights into behaviors of optimization algorithms. For instance, it may enable to further investigate effect of batch size or different sampling strategies with respect to progress of the algorithms after every full pass of data. This may also help with comparative analysis of deterministic and stochastic methods.
• I have checked the proof of Theorem 1 in details and had a less detailed look at Theorems 2 and 3. I appreciate some of the technically rigorous sections of the analysis as the authors bring together analytical tools from different resources and re-prove certain results with respect to their adjustments.
• Performance comparison in the paper is rather simple but the authors try to provide a perspective of their consistency condition through numerical evidence. It gives some rough idea about how to interpret this condition.
• Main text is written in a clear; authors highlight their modification to AdaGrad and also highlight what their new “consistency condition” is. Proposed contributions of the paper are stated clearly although I do not totally agree with certain claims. One of the main theorems has a proof sketch which gives an overall idea about authors’ approach to proving the results. Weaknesses:
• Although numerically the paper provides an insight into the consistency condition, it is not verifiable ahead of time. One needs to run a simulation to get some idea about this condition, although it still wouldn’t verify the correctness. Since authors did not provide any theoretical motivation for their condition, I am not fully convinced out this assumption. For instance, authors could argue about a specific problem setting in which this condition holds.
• Theorem 3 (Adagrad-truncation) sets the stepsize depends on knowledge of r
. I couldn’t figure out how it is possible to compute the value r
ahead of time. Therefore, I do not think this selection is practically applicable. Although I appreciate the theoretical rigor that goes into proving Theorem 3, I believe the concerns about computing r
weakens the importance of this result. If I am missing out some important point, I would like to kindly ask the authors to clarify it for me.
• The related work which is listed in Table 1, within the group “Adaptive Gradient Methods” prove \emph{iteration-wise} convergence rates for variants of Adam and AdaGrad, which I would call the usual practice. This paper argues about \emph{epoch-wise} convergence. The authors claim improvement over those prior papers although the convergence rate quantifications are not based on the same grounds. All of those methods consider the more general expectation minimization setting. I would suggest the authors to make this distinction clear and highlight iteration complexities of such methods while comparing previous results with theirs. In my opinion, total complexity comparison is more important that rate comparison for the setting that this paper considers.
• As a follow up to the previous comment, the related work could have highlighted related results in finite sum setting. Total complexity comparisons with respect to finite sum setting is also important. There exists results for finite-sum nonconvex optimization with variance reduction, e.g., Stochastic Variance Reduction for Nonconvex Optimization, 2016, Reddi et. al. I believe it is important to comparatively evaluate the results of this paper with that of such prior work.
• Numerically, authors only compare against AdaGrad and SGD. I would say this paper is a rather theory paper, but it claims rate improvements, for which I previously stated my doubts. Therefore, I would expect comparisons against other methods as well, which is of interest to ICLR community in my opinion.
• This is a minor comment that should be easy to address. For ICLR, supplementary material is not mandatory to check, however, this is a rather theoretical paper and the correctness/clarity of proofs is important. I would say authors could have explained some of the steps of their proof in a more open way. There are some crucial expressions which were obtained without enough explanations. Please refer to my additional comments in the following part.
Additional Comments:
• I haven’t seen the definition that x t , m + 1 = x t + 1 , 1
in the main text. It appears in the supplements. Could you please highlight this in the main text as it is important for indexing in the analysis?
• Second bullet point of your contributions claim that “[consistency] condition is easy to verify”. I do not agree with this as I cannot see how someone could guarantee/compute the value r
ahead of time or even after observing any sequence of gradients. Could you please clearly define what verification means in this context?
• In Assumption A3, I understand that G t e i = g t , i and G t e = ∑ i = 1 m g t , i
. I believe the existing notation makes it complicated for the reader to understand the implications of this condition.
• In the paragraph right above Section 4.2, authors state that presence of second moments, V t , i
enables adaptive methods to have improved rates of SGD through Lemma 3. Could the authors please explain this in details?
• In Corollary 1, authors state that “the computational complexity is nearly O ( m 5 / 2 n d 2 ϵ − 2 ) ~
”. A similar statement exists in Corollary 2. Could you please explain what “nearly” means in this context?
• In Lemma 8 in the supplements, a a T and b b T
in the main expression of the lemma are rank-1 matrices. This lemma has been used in the proof of Lemma 4. As far as I understood, Lemma 8 is used in such a way that a a T or b b T
correspond to something like g t , j 2 – g t − 1 , j 2
. I am not sure if this construction fits into Lemma 8 because, for instance, the expression g t , j 2 – g t − 1 , j 2
is difference of two rank-1 matrices, which could have rank \leq 2. Hence, there may not exist some vector a
such that a a T = g t , j 2 – g t − 1 , j 2
, hence Lemma 8 may not be applied. If I am mistaken in my judgment I am 100% open for a discussion with the authors.
• In the supplements, in section “A.1.7 PROOF OF MAIN THEOREM 1”, in the expression following the first line, I didn’t understand how you obtained the last upper bound to ∇ f ( x t , i )
. Could you please explain how this is obtained? Score:
I would like to vote for rejecting the paper. I praise the analytically rigorous proofs for the main theorems and the use of a range of tools for proving the key lemmas. Epoch-wise analysis for stochastic methods could provide insight into behavior of algorithms, especially with respect to real-life experimental setting. However, I have some concerns:
I am not convinced about the importance of consistency ratio and that it is a verifiable condition.
Related work in Table 1 has iteration-wise convergence in the general expectation-minimization setting whereas this paper considers finite sum structure with epoch-wise convergence rates. The comparison with related work is not sufficient/convincing in this perspective.
(Minor) I would suggest the authors to have a more comprehensive experimental study with comparisons against multiple adaptive/stochastic optimizers. More experimental insight might be better for demonstrating consistency ratio.
Overall, due to the reasons and concerns stated in my review, I vote for rejecting this paper. I am open for further discussions with the authors regarding my comments and their future clarifications.
======================================= Post-Discussions =======================================
I would like to thank the authors for their clarifications. After exchanging several responses with the authors and regarding other reviews, I decide to keep my score.
Although the authors come up with a more meaningful assumption, i.e., SGC, compared to their initial condition, I am not fully convinced about the contributions with respect to prior work: SGC assumption is a major factor in the improved rates and it is a very restrictive assumption to make in practice.
Although this paper proposes theoretical contributions regarding adaptive gradient methods, the experiments could have been a bit more detailed. I am not sure whether the experimental setup fully displays improvements of the proposed variants of AdaGrad. | • Main text is written in a clear; authors highlight their modification to AdaGrad and also highlight what their new “consistency condition” is. Proposed contributions of the paper are stated clearly although I do not totally agree with certain claims. One of the main theorems has a proof sketch which gives an overall idea about authors’ approach to proving the results. Weaknesses: |
ICLR_2022_3247 | ICLR_2022 | Weakness
Despite the contributions outlined above, I believe all of the following concerns need to be addressed in order for this research to be accepted.
A) A mismatch between motivation and contribution
The contributions provided by this study do not address the motivation as stated in the introduction. In the introduction, the authors raise the problems related to constructing positive and negative pairs in CL as the motivation for this study. Specifically, the following three points are mentioned as challenges in CL:
definition of semantically similar/dissimilar pair is contingent on downstream tasks,
practically data augmentation is used for a positive pair, but it still has a problem; although positive samples are valid, negative samples contain a non-negligible portion of invalid samples (class collision),
and the computation of positive and negative pairs grows quadratically with the size of the dataset.
Even though the authors state that they propose their method to examine these challenges, none of these challenges are addressed in Method/Results/Conclusion. Instead, they continue to use existing approaches that have the issues raised in the introduction. The authors should clearly state their contribution to 1) the definition of similar/dissimilar pairs independent of downstream tasks, 2) validity (especially for class collision) in negative samples, and 3) computation time issues mentioned in the motivation of this paper.
B) Derivation of the correspondence between NCA loss and contrastive loss
The derivation of Eq. 9 from Eq. 7, which is the main technical contribution of this study that leads to the correspondence between NCA loss and contrastive loss, has several concerns. The NCA uses all dataset except its own { x k : k ≠ i }
to evaluate the loss for the i
-th data. This study makes an assumption of { x k : k ≠ i } = { x j + : 1 ≤ j ≤ M } ∪ { x i − : 1 ≤ i ≤ N }
on this set to derive the contrastive loss from the NCA loss. I have two concerns about the validity of this assumption.
This assumption implies that the entire dataset can be divided into M
“positive” samples and N
“negative" samples. However, experimentally the positive/negative samples are subsampled from the entire dataset during the loss evaluation. In fact, in the numerical experiments in the second half of the paper, the authors treat M
as a hyperparameter, which is a significantly smaller number than the dataset size, so this assumption does not hold.
The assumption implicitly assumes that positive and negative samples are mutually exclusive: { x j + } ∩ { x i − } = ∅
. However, in reality, negative samples are typically taken from random samples in the same minibatch for computational simplicity, which leads to collision with positive samples. The numerical experiments in this study treat the same, and again the assumptions are not supported also from this perspective.
Since the correspondence between NCA loss and contrastive loss is the main technical contribution of this study, the validity of the assumptions for its derivation directly relates to the validity of the contribution of this study itself. The authors should address the above two concerns and clarify the validity of the assumptions made in this study.
C) Concerns about experiments
C-1) There is a gap between the technical contribution of this study (proposal of loss variant using NCA) and the experimental contribution (performance improvement including unified use of existing methods). Although this study claims to have given a unified framework for CL from the perspective of NCA and to have shown improved performance in numerical experiments, the loss variants from the perspective of NCA and the unified framework that brings together existing methods and loss variants are mutually independent. The following three effects are thought to contribute to the experimental performance improvement separately:
The effect of NCA-derived loss variants (choice of L Na ),
the effect of combining existing methods (e.g., use of adversarial examples),
and the effect of heuristics with low relevance to the main technical contribution (choice of w ( x ) ).
Because these three effects were examined at once without clearly separating them, it is not clear how large the effect of the loss variant derived through the lens of NCA is. For example, the proposed method $\mathcal{L}\mathrm{IntNaCL} h a s p a r a m e t e r s \alpha , c h o i c e o f \mathcal{L}\mathrm{Na} , M , \lambda , g^1 , g^2 , a n d
w$. By setting these parameters, loss variants, including existing methods, can be treated in a unified manner. Since there is no description of the parameter settings of the proposed algorithm in Figure 1, it is not clear which of the three effects this performance improvement depends on. The authors should examine each of these three effects independently and separate the contributions in the text.
C-2) Concern that the effect of the number of observed samples has not been removed. The authors claimed the contribution of $\mathcal{L}\mathrm{VAR} w h e n M>1 a s t h e e f f e c t o f N C A − d e r i v e d l o s s v a r i a n t . T h e a u t h o r s s t a t e d t h a t t h e \mathcal{L}\mathrm{VAR} h a s t h e p r o p e r t y o f b e i n g a b l e t o l o w e r t h e v a r i a n c e o f t h e e s t i m a t o r . H o w e v e r , i t i s n o t f a i r t o n a i v e l y c o m p a r e t h e c o n t r a s t i v e l o s s c o r r e s p o n d i n g t o M=1 a n d t h e \mathcal{L}_\mathrm{VAR} f o r M>1 i n t h e s a m e f i x e d e p o c h , b e c a u s e e x p e r i m e n t a l l y , t h e m o d e l c a n o b s e r v e d i f f e r e n t p o s i t i v e s a m p l e s i n t h e a m o u n t p r o p o r t i o n a l t o M . S u p p o s e o n e w o u l d l i k e t o h i g h l i g h t t h e e f f e c t o f t h e d i f f e r e n c e i n t h e f u n c t i o n a l f o r m o f t h e l o s s e s p u r e l y . I n t h a t c a s e , t h e a u t h o r s s h o u l d u s e l o n g e p o c h s w h e r e t h e o p t i m i z a t i o n c o n v e r g e s s u f f i c i e n t l y o r m a k e a d j u s t m e n t s s o t h a t t h e n u m b e r o f p o s i t i v e s a m p l e t y p e s o b s e r v e d d o e s n o t c h a n g e f o r d i f f e r e n t
M$ for a fair comparison. In fact, the authors have also trained the existing method with a longer epoch, and the results show that the existing method is comparable to the proposed method when trained with a longer epoch.
Minor comments x adv
in Eq. 6 is not defined explicitly. “ g = g 0
” in the left-hand side for the definition of $\mathcal{L}\mathrm{VAR} , \mathcal{L}\mathrm{BIAS} , a n d \mathcal{L}_\mathrm{MIXUP} ( p .6 ) i s n o t c l e a r s i n c e “
g$” does not appear on the right-hand side of these equations.
The undefined variable x i 2 j −
is in the right-hand side of the definition of L MIXUP
in p.6. | 1 ≤ j ≤ M } ∪ { x i − : |
ICLR_2021_973 | ICLR_2021 | .
Clearly state your recommendation (accept or reject) with one or two key reasons for this choice. I recommend acceptance. The number of updates needed to learn realistic brain-like representations is a fair criticism of current models, and this paper demonstrates that this number can be greatly reduced, with moderate reduction in Brain-Score. I was surprised that it worked so well.
Ask questions you would like answered by the authors to help you clarify your understanding of the paper and provide the additional evidence you need to be confident in your assessment. - Is the third method (updating only down-sampling layers) meant to be biologically relevant? If so, can anything more specific be said about this, other than that different cortical layers learn at different rates? - Given that the brain does everything in parallel, why is the number of weight updates a better metric than the number of network updates?
Provide additional feedback with the aim to improve the paper. - Bottom of pg. 4: I think 37 bits / synapse (Zador, 2019) relates to specification of the target neuron rather than specification of the connection weight. So I’m not sure its obvious how this relates to the weight compression scheme. The target neurons are already fully specified in CORnet-S. - Pg. 5: “The training time reduction is less drastic than the parameter reduction because most gradients are still computed for early down-sampling layers (Discussion).” This seems not to have been revisited in the Discussion (which is fine, just delete “Discussion”). - Fig. 3: Did you experiment with just training the middle Conv layers (as opposed to upsample or downsample layers)? - Fig. 3: Why go to 0 trained parameters for downstream training, but minimum ~1M trained parameters for CT? - Fig. 4: On the color bar, presumably one of the labels should say “worse”. - Section B.1: How many Gaussian components were used, or how many parameters total? Or if different for each layer, what was the maximum across all layers? - Section B.3: I wasn’t clear on the numbers of parameters used in each approach. - D.1: How were CORnet-S clusters mapped to ResNet blocks? I thought different clusters were used in each layer. If not, maybe this could be highlighted in Section 4. | - Is the third method (updating only down-sampling layers) meant to be biologically relevant? If so, can anything more specific be said about this, other than that different cortical layers learn at different rates? |
rtzUW1FU3H | ICLR_2024 | - Following the promises in the abstract about the human-annotation and the cross-annotator validation, I was very disappointed to see that a large part of the benchmark's ground-truth output was generated using GPT 3.5 / 4:
>We utilize the powerful language processing and understanding capability of GPT-3.5-turbo to help generating short QA pairs from the original text.
>we employ GPT-3.5-turbo to generate factual summaries align with the source segment using with constraints
If this is indeed the case, this is disappointing, and the benchmark may be biased toward "questions that are easy for ChatGPT to answer".
- The text is very unclear in many cases. For example when describing the statistics of the benchmark, the paper says:
>Extra-long realistic documents. It contains 778 latest gathered and extremely long documents
with an average of 16.4k words. There are over 6000 test instances without distribution bias for a
more generalized assessment, many of which are exceeding 100k words.
So are there 778 examples or 6000 examples? If "many of which exceed 100k words", how many of them? what's the average? Are these two datasets? If not, why are these numbers reported separately?
- The results in Section 4.3.1 are very confusing and unclear. For example:
>In Table 3, it can be noticed that LlamaIndex obtains from the perspective of GPT4 evalution. Instead
of memorizing a shortcut of original input with a limited context window, retrieval-based context
compression technique augments the LLM by incorporating external memory, allowing relevant
information to be retrieved using a specific query.
I am not sure what such paragraphs are trying to say. What does it mean that "LlamaIndex obtains from the perspective of GPT4 evalution"? What do the authors exactly mean by "memorizing a shortcut"? Who is memorizing a shortcut?
- Measuring "GPT4 score" on GPT4's outputs is mostly meaningless. It would be better to just completely remove this column, or use another LLM that is not evaluated.
- Applicability: the paper does not mention anything about its implementation, its ease of use, its availability. As always with benchmarks, the devil is in the details, and the authors have not included the data itself, which makes it hard to really evaluate its quality.
- Presentation is poor: for example:
- the text in Figure 1 is tiny, not allowing to actually understand the overview of the new benchmark.
The entire left part of the figure contains barely any information.
I would prefer an organized and readable list of tasks and data statistics.
- The text in Table 1 tiny
- The text in Table 2 is tiny. Further, it would be helpful if these statistics would include the max/min instead of category, or a more illustrative figure of the characteristics of the examples, as in Figure 1 in the [SCROLLS paper](https://arxiv.org/pdf/2201.03533.pdf)
- The text in Figure 3 is tiny. Further, the colors are very similar, and I cannot distinguish between the different models and cannot understand anything from this figure. | - Measuring "GPT4 score" on GPT4's outputs is mostly meaningless. It would be better to just completely remove this column, or use another LLM that is not evaluated. |
NIPS_2016_93 | NIPS_2016 | / Major concerns: - It is difficult to evaluate whether the MovieQA result should be considered significant given that +10% gap exists between MemN2N on dataset with explicit answers (Task 1) and RBI + FP on dataset with other forms of supervision, especially Task 3. If I understood correctly, the different tasks are coming from the same data, but authors provide different forms of supervision. Also, Task 3 gives full supervision of the answers. Then I wonder why RBI + FP on task 3 (69%) is doing much worse than MemN2N on task 1 (80%). Is it because the supervision is presented in a more implicit way ("No, the answer is kitchen" instead of "kitchen")? - For RBI, they only train on rewarded actions. Then this means rewardless actions that get useful supervision (such as "No, the answer is Timothy Dalton." in Task 3) is ignored as well. I think this could be one significant factor that makes FP + RBI better than RBI alone. If not, I think the authors should provide stronger baseline than RBI (that is supervised by such feedback) to prove the usefulness of FP. Questions / Minor concerns: - For bAbI, it seems the model was only tested on single supporting fact dataset (Task 1 of bAbI). How about other tasks? - How is dialog dataset obtained from QA datasets? Are you using a few simple rules? - Lack of lexical / syntactic diversity of teacher feedback: assuming the teacher feedback was auto-generated, do you intend to turk the teacher feedback and / or generate a few different kinds of feedback (which is more real-life situation)? - How does other models than MemN2N do on MovieQA? | - How does other models than MemN2N do on MovieQA? |
NIPS_2020_650 | NIPS_2020 | Post rebuttal: Thanks for the authors response which clarifies most questions about the current work. I updated my score from 4 to 5 after rebuttal. My remaining concern is about the novelty part. At first glance the Algorithm 1 is like an "actor-critic" method with monotonic advantage weighting and distributional Q (with bootstrapped Q estimation)? In the introduction (line 30-32) and conclusion part (line 304-306) it seems that the point proposed is about filtered BC with advantage re-weighting. In rebuttal the point seems to be a simple and effective algorithm combined. I may suggest a major revision to restructure the work for a clear point of contribution. Minor: 1. The comparison with K-step/return-based method: The comparison in A.2 is indeed about the difference between A^{\pi_\theta} and A^{\mu_B}? Maybe a fair comparison near line 153 is a K-step/return-based estimation of A^{\pi_\theta}? There are methods can correct (to some extent) the advantage estimation from behavior policy \mu_B to the target policy \pi_\theta, e.g. Retrace and V-trace. 2. The name of A_mean and A_max may be misleading, personally I may suggest to define the truncation threshold in Eq.(3), instead of in advantage estimation. 3. And I also notice that the notation of f in Eq.(2) may need further revision. It seems that \pi will not be optimized within f(), and f is not dependent on action a if conditioned on Q_\theta(s,a). ---- I think the main contribution of this paper is a little ambiguous. I would be happier if the authors can describe this more explicitly. And I also have some detailed questions about correctness and novelty, which will be discussed in the following parts. 1. For the advantage estimation part, it seems that a constant depending on s_t will not affect the value of (2) (it cancels with the log pi part), so the difference between A_mean and A_max in Table 1 is unclear to me. 2. The convergence of the algorithm is not fully discussed. If Alg 1 converges, what would be the final Q_theta? It seems that Q will converge to Q_B instead of Q^{\pi_\theta}? With this estimation of Q, what would be the final \pi_\theta if it converges? A local optimal policy with respect to some loss function? 3. For the empirical performance, is there any possibility that the performance of MARWIL[35] BAIL[7] AWR[25] can also be compared? Since the algorithm have not been proved better theoretically, we expect stronger empirical results to demonstrate the power of the algorithm. Novelty: In Sec3 we see some ideas appeared in previous work, e.g. Eq(1) is about how to estimate Q, with distributional Q in [4], Eq(2) is about monotonic advantage term, similar to that of [35] etc. And for the estimation of advantage, the discussion of off-policy friendly methods like Retrace and V-trace is missing. Retrace: Safe and Efficient Off-Policy Reinforcement Learning V-trace: IMPALA: Scalable Distributed Deep-RL with Importance Weighted Actor-Learner Architectures | 1. For the advantage estimation part, it seems that a constant depending on s_t will not affect the value of (2) (it cancels with the log pi part), so the difference between A_mean and A_max in Table 1 is unclear to me. |
ICLR_2023_1061 | ICLR_2023 | Weakness 1.The obtained estimation error rate does not achieve the expected optimal minimax rate. Regarding to the comparison in Table 1, it looks a bit weird for me since sphere S d − 1
is a subset of the cube [ 0 , 1 ] d
, but the estimation rate on a subset Is even slower. Is there a way to fix it? Or is there a reasonable explanation?
2.Regarding to the main result in Theorem 3.1, the approximation error has basically dependence d N + d × N d / M
. This result seems also cursed by d
in numerator, otherwise one has to set a very large M
, e.g. M = d d
to get a good approximation accuracy. Please explain more on this.
3.The condition r = O ( d )
is restrictive. The author may explain more on this condition, especially it’s better to give an example on in what scenarios the condition r = O ( d )
holds. In addition, I wonder if the condition r = O ( d )
can be plugged in other existing results, e.g., Schmidt-Hieber (2020) to have a comparison with the obtained results in these d , r
varying cases. If it’s not possible, please also explain why r = O ( d )
can not directly be plugged in other results.
4.The comparison can be fairer since Schmidt-Hieber (2020) focus on the approximation on hyper-cubes instead of sphere. The authors can compare their results with Fang et al. (2020) and Feng et al. (2021) since a large part of the proof follows that of Fang et al. (2020). The most notable difference between Fang et al. (2020) and this paper is that this paper track the explicit dependence of the constant factor on d
. In addition, though Fang et al. (2020) and Feng et al. (2021) considered CNN approximations, Zhou, D.X. (2020). has shown that any CNN can be equivalently computed by a FNN with parameters at most 8 times larger than that of CNN. In light of this, the author should compare their results with Fang et al. (2020) and Feng et al. (2021).
5.Within the studies of ReLU FNN approximation, the author can also compare with more recent results which have already improved the results in Schmidt-Hieber (2020). For example, Shen, Yang, and Zhang. (2020) and Lu, Shen, Yang, and Zhang. (2021) have already demonstrated the clear dependence on dimension d
for ReLU approximation results. In line with these works, Jiao, Shen, Lin and Huang (2021) has also shown the explicit dependence of ReLU approximation results on d
as well as obtained polynomial dependence results.
Minor comment: 1.For reference, the issues about the dependence on dimension d
was also discussed in Ghorbani et al. (2020). 2.The obtained approximation results are for Sobolev function space W ∞ r
, which is actually Hölder function space. This is also mentioned in Appendix A. Reference
SCHMIDT-HIEBER, J. (2020). Nonparametric regression using deep neural networks with ReLU activation function(with discussion). Ann. Statist. 48 1875–1897.
Ding-Xuan Zhou. Theory of deep convolutional neural networks: Downsampling. Neural Networks, 124:319–327, 2020.
SHEN, Z., YANG, H. and ZHANG, S. (2020). Deep network approximation characterized by number of neurons. Commun. Comput. Phys. 28 1768–1811.
LU, J., SHEN, Z., YANG, H. and ZHANG, S. (2021). Deep network approximation for smooth functions. SIAM Journal on Mathematical Analysis 53 5465–5506.
Jiao, Y., Shen, G., Lin, Y., & Huang, J. (2021). Deep nonparametric regression on approximately low-dimensional manifolds. arXiv preprint arXiv:2104.06708.
GHORBANI, B., MEI, S., MISIAKIEWICZ, T. and MONTANARI, A. (2020). Discussion of: “Nonparametric regression using deep neural networks with ReLU activation function”. Ann. Statist. 48 1898–1901. | 1.For reference, the issues about the dependence on dimension d was also discussed in Ghorbani et al. (2020). |
BwGeIhGPgn | ICLR_2025 | 1. While some models were evaluated, there was a lack of valuable findings and insights. Specifically,
- What are the potential reasons why the existing model lacks the ability of "information gathering"? Is it data, algorithm, or other factors?
- In what direction should we work further to improve the model's ability in this aspect?
- For the failure cases of the models, we can add some statistical analysis to summarize the types and causes of failures.
Thus, I suggest adding experiments about the following points that could be helpful:
- Select a subset of failure cases, summarize the reasons for model failure, and analyze the reasons that led to the failure.
- Discuss ways to improve the model's information-gathering capability. If possible, it would be better to conduct experiments to verify the feasibility of the methods.
2. There are important details missing in the evaluation process. Specifically, assessing the model's accuracy is a non-trivial task. This is because the correct behavior is to request the missing information in the underspecific question. However, the authors don't seem to describe this point in the paper. Overall, the author needs to provide details regarding how to judge whether the question asked by the model is correct. | - For the failure cases of the models, we can add some statistical analysis to summarize the types and causes of failures. Thus, I suggest adding experiments about the following points that could be helpful: |
NIPS_2019_962 | NIPS_2019 | ** * Clarity. There are parts of this paper that are a bit unclear. The diagram and caption for KeyQN section are very helpful, but the actual text section could be fleshed out more. It would nice if the text could have a little more detail on how the outputs from the transporter are input to the KeyQN architecture and how the whole thing is trained. The exploration section was well explained for most part, but it took a bit of time to understand. Maybe would help to have an algorithm box. Also, the explanation of training process a bit confusing. Maybe a diagram of the architecture and how the transporter feeds into this would help. Also, I am confused a bit about whether the transporter is pretrained and frozen or fine-tuned. One quote from the paper in this regard confused me: âOur transporter model and all control policies simultaneuosly â so the weights of the Transporter network are not frozen during the downstream task like in KeyQN? * Experiments: They only show these results on a few games (and no error bars), so it would have been nice (but not a dealbreaker) to see results from more Atari games. They do partially justify this by saying they couldnât use a random policy on other games, but Iâd be curious just to see what happens when they try a couple more games. Would be nice to see comparisons to other exploration methods (they only show results compared to random exploration) Nitpicks/Questions * Makes sense to just refer the reader to the PointNet paper instead of re-explaining it, but a short explanation if possible of PointNet (couple sentences) might be helpful, so that one doesnât have to skim that paper to understand this paper * The diagram in figure 5 (h_psi) should show a heat map not keypoints superimposed on raw frame right? * In the appendix âK is handpicked for each game?â How? Validation loss? * The tracking experiments but the section is a bit unclear. I have a few questions on that front: * why is there a need to separating precision and recall? * why not just report overall mean average precision or F1 score? Might be a bit easier for reader to digest one number * Why bucket into diff sequence lengths? what do the different sequence lengths mean? There is no prediction-in-keypoint space model right? So there is no concept of the performance worsening as the trajectory gets longer. Arenât the keypoint guesses just the output of the PointNet at each frame, so why would the results from a 200 frame sequence be much different than 100 or something? Why not just report overall precision and recall on the test set? * In the KeyQN section What is the keypoint mask averaged feature vector? just multiply each feature map element wise by H_psi? | * why not just report overall mean average precision or F1 score? Might be a bit easier for reader to digest one number * Why bucket into diff sequence lengths? what do the different sequence lengths mean? There is no prediction-in-keypoint space model right? So there is no concept of the performance worsening as the trajectory gets longer. Arenât the keypoint guesses just the output of the PointNet at each frame, so why would the results from a 200 frame sequence be much different than 100 or something? Why not just report overall precision and recall on the test set? |
uRXxnoqDHH | ICLR_2024 | - Lack of experiments assessing whether the model performs well with scarce data, which is painted as the main motivation of MoAT. Furthermore, figure 5c does not seem to corroborate the story that MoAT performs significantly better than other methods with data scarcity (hard to say without variance). MoAT still seems to derive its main performance improvements from increasing the train ratio.
- Lack of details in the caption of the T-SNE decomposition between time series and texts.
- The remarks about information uniqueness of cross-modal vs unimodal representations are not backed up, no reason for their contained information to be unique.
- Not obvious that the text data trend-seasonal decomposition actually decomposes into trend and seasonal data, it seems like you just use two sets of attention parameters. How do you actually get these to attend to either trend or seasonal information in the texts? This just seems like it introduces more parameters into the model.
- In fact, there is no comparison of model sizes and various scaling parameters for different methods. If you don't normalize, how do you know your performance increases aren't simply due to scaling up model size?
- Unclear empirical design for hyperparameter tuning. Why default at hidden dim of 64? What does if mean dropout =0.2 "if needed"? Why is the search for optimal learning rates and decay across two values each? If you're limited by compute or have a lot of hyperparameters, random search could be better than grid search.
- Formatting needs more consistency (e.g. "Fig." vs "Figure", figure 5 before figure 4, etc.) | - Lack of experiments assessing whether the model performs well with scarce data, which is painted as the main motivation of MoAT. Furthermore, figure 5c does not seem to corroborate the story that MoAT performs significantly better than other methods with data scarcity (hard to say without variance). MoAT still seems to derive its main performance improvements from increasing the train ratio. |
ICLR_2022_540 | ICLR_2022 | /comments: - Comparison with other learning objectives. The ultimate goal of data augmentation is to improve the generalization power of a model. How does the proposed Difficult and Not Different objective compare with the objective that improves the validation performance directly like AutoAugment or TAA [1]. - Sensitivity of DND hyperparameters. Despite being an Automated Data Augmentation method, there are several important hyperparameters, e.g. λ r , λ s i m , λ s , T p
, to be tuned. How sensitive is the proposed method to these hyperparameters? Whether these hyperparameters needed to be tuned carefully? - Ablation study for extra loss terms. In the ablation study section, are the ‘Vanilla’, ‘Random’ and ‘Fixed’ baselines also being trained with the extra loss terms L s i m and L r e c o n
? While it is a motivated decision to introduce these terms during the training of f θ
, can these losses also contribute to the learning of better representations and lead to the improvement? It would be useful if the effects of these extra losses are discussed in the ablation study. - Exclusion of MixUp from the augmentation pool. Authors mention that MixUp is not included in the augmentation pool as it alters the semantics of the original sentences. However, MixUp can create difficult examples by sample and label mixing. MixUp also shows good results for some datasets under Table 1. As a learning-based data augmentation method, is it the responsibility for the search algorithm to learn the use of MixUp in a data-driven way? Can the inclusion of MixUp in the augmentation pool improves the performance? If the validity of a candidate augmentation method has to be evaluated before adding to the augmentation pool, does it contradict with the goal of fully learnable data augmentation? - Hyperparameter tuning for other baselines. Some of the baseline methods, like EDA, BERT-Aug, MixUp, Back&Adv also involve hyperparameters. According to Appendix A2, it seems that these hyperparameters are not tuned. As the hyperparameters of DND (e.g. λ s and T p
) are tuned for each dataset, it is fairer to tune the hyperparameters for the other baselines. - Formulation of the probability and magnitude for EDA. Is there a specific reason that EDA is assigned with a single probability and magnitude parameter? Can the use of different p and μ
values for synonym replacement, random insertion, random swap, and random deletion further improves the augmentation policy? - Definition of the magnitude parameters for the augmentation candidates. It is unclear how the magnitude parameters are defined for the augmentation candidates. For example, is the mask probability of BERT-Aug taken as the magnitude? What are the ranges of the magnitudes? It would be useful to include these in the appendix. Reference
[1] Shuhuai Ren, Jinchao Zhang, Lei Li, Xu Sun, Jie Zhou. Text AutoAugment: Learning Compositional Augmentation Policy for Text Classification. arXiv preprint arXiv:2109.00523, 2021 | - Hyperparameter tuning for other baselines. Some of the baseline methods, like EDA, BERT-Aug, MixUp, Back&Adv also involve hyperparameters. According to Appendix A2, it seems that these hyperparameters are not tuned. As the hyperparameters of DND (e.g. λ s and T p ) are tuned for each dataset, it is fairer to tune the hyperparameters for the other baselines. |
ICLR_2021_2330 | ICLR_2021 | Weakness
- Method on Fourier domain supervision lacks more analysis and intuition. It's unclear how the size of the grid is defined to perform FFT, from my understanding, the size is critical as local frequency will be changed using different grid size. Is it fixed throughout training? What is the effect of having different sizes?
- The generator has a recurrent structure that supports 10 frame generation, but the discriminator looks at three frames (from figure 1) at a time, which seems to limit the power of temporal consistency.
- In figure 7 result and supplemental video result, SurfGAN produces smoother results (MSE seems closer to the red ground truth in figure 7). This seems contradicts the use of Fourier components for supervision -- what causes this discrepancy?
- Figure 4 is confusing. It's not clear what the columns mean -- it is not explained in the text or caption.
- Notation is confusing. M and N are used without definition. Suggestion
- Spell out F.L.T.R in figure 4
- Figure 1 text is too small to see
- It is recommended to have notation and figure cross-referenced (e.g. M and N are not shown in the figure) | - Method on Fourier domain supervision lacks more analysis and intuition. It's unclear how the size of the grid is defined to perform FFT, from my understanding, the size is critical as local frequency will be changed using different grid size. Is it fixed throughout training? What is the effect of having different sizes? |
wWT51dSyBj | EMNLP_2023 | - the proposed approach has multiple steps which may be hard to be used or followed by future work;
- the general direction is not novel, i.e., extract sub-layers for bilingual language pairs; | - the general direction is not novel, i.e., extract sub-layers for bilingual language pairs; |
NIPS_2022_869 | NIPS_2022 | The authors distill a ViT-B/16 into a RN50. While the former takes more FLOPs than the later, ViT-B/32 is cheaper than RN50, and the CLIP version of that architecture outperforms both the author's RN50 and the CLIP RN50 model. While this doesn't totally undercut the presented results, it's a bit strange to me why the authors chose the particular distillation pair that they did --- it seems like ViT-B/32 (or even EfficientNet or MobileNet) would have been a good choice for student, and perhaps L/14-336px CLIP as the teacher would have made a more compelling setup.
The ablations suggest that the cosine similarity loss isn't really required: the best zero-shot imagenet performance is actually achieved only with the cross-modal loss, and the other datasets seem to be within a close margin. This isn't really a /negative/, per-say, but a bit contrary to the story told.
It would have been nice to see linear probe results for the other datasets like Pets37 as well.
Even assuming that RN50 is the best choice of student, the empirical results are somewhat unimpressive. Specifically, I believe that the authors choose anchor points to be task-specific prompts and the author's model is domain adapted to (unlabelled) dataset-specific images, i.e., there's reason to believe that the author's method is specifically tuned to the tasks described. RN50-CLIP, which is not tuned to the specific tasks described, achieves only slightly worse imagenet linear probe accuracy: 73.3 vs 74.8.
The zero shot results in table 3 are interesting, but a bit incomplete. The ViT-B/32-CLIP model smaller than the author's distilled RN50 model achieves only slightly worse performance on these tasks, but it isn't presented. Again, this observation doesn't invalidate the author's results, it's just that one really needs to buy that RN50 specifically is an interesting student model.
Overall, the authors clearly "win" on this particular architecture by a few accuracy points on linear probe imagenet, but it's not clear that this is really the best architecture to distill to (particularly because ViT-B/32 is smaller and there's already a CLIP model for that). To the author's credit, they recognize this on L288, but I would have preferred to see that the author's method generalizes to other teacher/student models, instead of just this one combination.
Overall, the authors have a promising core result: it's possible to distill the knowledge of a CLIP model into a smaller set of weights. And, the innovation that enables this distillation (that image-text distances should be preserved in addition to image-image distances) is novel. However, the empirical results are slightly underwhelming: the authors model, by virtue of the selection of the anchor points and distillation over unlabelled images from the corpora of interest, is tuned to this particular set of datasets (vs. CLIP that isn't). Their performance improvement over CLIP is somewhat small in magnitude (73.3 vs 74.8). I would have liked to have seen: 1) distillation to significantly more efficient architectures vs. RN50 (ViT-B/32 CLIP is already smaller) and with better teachers than ViT-B/16; and 2) linear probe evaluations on unseen tasks, where the images haven't been seen by the distillation model at training time.
Presentation fixes:
It should be specified that Table 3 results are all zero shot.
L71: week --> weak
The broader impact statement is a bit hollow -- I would have appreciated a fuller discussion of embedded systems and/or low resource computation
Table 4's caption has an incomplete sentence.
The authors mainly focus on making higher performance, lower-resource versions of existing CLIP models. Given that CLIP's negative impacts have been discussed in the original work and follow ups, I don't think significant additional discussion is needed here.
I did think that the "Broader impacts" section was a bit short: can more information about FLOPs/energy use/on-device computation be discussed? | 2) linear probe evaluations on unseen tasks, where the images haven't been seen by the distillation model at training time. Presentation fixes: It should be specified that Table 3 results are all zero shot. |
ARR_2022_215_review | ARR_2022 | 1. The paper raises two hypotheses in lines 078-086 about multilinguality and country/language-specific bias. While I don't think the hypotheses are phrased optimally (could they be tested as given?), their underlying ideas are valuable. However, the paper actually does not really study these hypotheses (nor are they even mentioned/discussed again). I found this not only misleading, but I would have also liked the paper to go deeper into the respective topics, at least to some extent. 2. It seemed a little disappointing to me that the 212 new pairs have _not_ been translated to English (if I'm not mistaken). To really make this dataset a bilingual resource, it would be good to have all pairs in both languages. In the given way, it seems that ultimately only the French version was of interest to the study - unlike it is claimed initially.
3. Almost no information about the reliability of the translations and the annotations is given (except for the result of the translation checking in line 285), which seems unsatisfying to me. To assess the translations, more information about the language/translation expertise of the authors would be helpful (I don't think this violates anonymity). For the annotations, I would expect some measure of inter-annotator agreement.
4. The metrics in Tables 4 and 5 need explanation, in order to make the paper self-contained. Without going to the original paper on CrowS-pairs, the values are barely understandable. Also, information on the values ranges should be given as well as whether higher or lower values are better.
- 066: social contexts >> I find this term misleading here, since the text seems to be about countries/language regions.
- 121: Deviding 1508 into 16*90 = 1440 cases cannot be fully correct. What about the remaining 68 cases?
- 241: It would also be good to state the maximum number of tasks done by any annotator.
- Table 3: Right-align the numeric columns.
- Table 4 (1): Always use the same number of decimal places, for example 61.90 instead of 61.9 to match the other values. This would increase readability. - Table 4 (2): The table exceeds the page width; that needs to be fixed.
- Tables 4+5 (1): While I undersand the layout problem, the different approaches would be much easier to compare if tables and columns were flipped (usually, one approach per row, one metric per column). - Tables 4+5 (2): What's the idea of showing the run-time? I didn't see for what this is helpful.
- 305/310: Marie/Mary >> I think these should be written the same.
- 357: The text speaks of "53", but I believe the value "52.9" from Table 4 is meant. In my view, such rounding makes understanding harder rather than helping.
- 575/577: "1/" and "2/" >> Maybe better use "(1)" and "(2)"; confused me first. | - Table 4 (1): Always use the same number of decimal places, for example 61.90 instead of 61.9 to match the other values. This would increase readability. |
ARR_2022_52_review | ARR_2022 | 1. A critical weakness of the paper is the lack of novelty and incremental nature of work. The paper addresses a particular problem of column operations in designing semantic parsers for Text-to-SQL. They design a new dataset which is a different train/test split of an existing dataset SQUALL. The other synthetic benchmark paper proposed is based on a single question template, "What was <column> in <year>?".
2. The paper assumes strong domain knowledge about the column types and assumes a domain developer first creates a set of templates based on column types. With the help of these column templates, I think many approaches (parsers) can easily solve the problem. For example, parsers utilizing the SQL grammar to generate the output SQL can use these templates to add new rules that can be used while generating the output. Few such works are 1. A Globally Normalized Neural Model for Semantic Parsing ACl 2021 2. TRANX: A Transition-based Neural Abstract Syntax Parser for Semantic Parsing and Code Generation EMNP 2018 3. GraPPa: Grammar-Augmented Pre-Training for Table Semantic Parsing, ICLR 2021.
1. It will good if the authors can learn the templates for schema expansion from source domain data.
2. Compare the proposed approach with methods which uses domain knowledge in the form of grammar. Comparing with below methods will show generality of ideas proposed in the paper in a much better way.
1. A Globally Normalized Neural Model for Semantic Parsing ACl 2021 2. TRANX: A Transition-based Neural Abstract Syntax Parser for Semantic Parsing and Code Generation EMNP 2018 3. GraPPa: Grammar-Augmented Pre-Training for Table Semantic Parsing, ICLR 2021. | 2. Compare the proposed approach with methods which uses domain knowledge in the form of grammar. Comparing with below methods will show generality of ideas proposed in the paper in a much better way. |
9aIlDR7hjq | ICLR_2025 | Points are ordered roughly according to my perceived scale, with more important points being listed first.
A) The method itself is quite simplistic from a novelty perspective (simply adding augmentations to the conditioning). I would consider this a strength, if the results were consistent (B) and strong (B, D, E, F) with a clear storyline for effective use-cases (C). However, I do not see this as being the case (see following points for details, as indicated in the corresponding parentheses).
B) The results are mixed. Examples: 1) In table 1, the random image baseline actually has the lowest FID. I do not see this discussed, with lines 323 and 339 pointing out that "the best-performing augmentation-conditioning method has one of the lowest FID scores, supporting our claim...", which is misleading. 2) In table 3, unintuitive bolding hides that your method underperforms in some categories (with LDM t&i, medium is worse and few is tied). 3) In Figure 6, by 16 shots, the novel method is already underperforming on 2 datasets. Once again, the writing does not properly address this.
C) Given the mixed results, there should be an in-depth analysis / explanation to understand when this method is most useful, but this seems to be missing. I want to stress that if done well, this could potentially make up for weakness B.
D) The comparisons with Fill-Up are not clear, as "Ours" does worse but uses less data--it would be better to compare against Fill-Up with the same amount of data as well, otherwise you have not shown that you are beating SOTA.
E) There seems to be some baselines missing in the few-shot section that could strengthen the context. 1) as the ResNet50 is pre-trained, it would be helpful to know the starting accuracy. 2) Figure 6 is missing the random-image baseline included in Table 1.
F) I do not find the CFG scale experiments as adding significant value, although they take up a page in total. They are consistent with previous work, which I don't find unsurprising. While they don't really 'hurt' anything in themselves, they overall weaken the experimental section by taking the space of what could have otherwise been more interesting / surprising / novel results, and in my opinion they water down the impact of the experimental section.
G) In the introduction, it is claimed that methods that fine-tune the diffusion model (Azizi 2023, Trabucco 2023, Shin 2023) are too expensive. However, this is never supported with numbers--it would make the claim stronger to quantify method costs. Especially because these methods have vastly different costs (e.g. in line 134, you claim that Shin 2023 uses textual inversion--this should be less expensive than full fine-tuning, correct? And what about methods that use PEFT?)
H) Table 3 is misleading. The way the sections are split, the entire lower section should be compared. However, Fill-Up is a separate class with more synthetic data, which you are not comparing against. This is not very clear by the visual, and is confusing why the highest numbers are not the ones bolded (as Fill-Up is excluded). Sometimes the bolding seems entirely wrong--e.g. in medium, "ours" is bolded, but LDM (txt and image) is clearly better, and also at comparable synthetic data counts. | 2) In table 3, unintuitive bolding hides that your method underperforms in some categories (with LDM t&i, medium is worse and few is tied). |
NIPS_2020_843 | NIPS_2020 | Major points 1. As the authors note, the stability of the feedback dynamics depends on a condition on the eigenvalues of WB - alpha*I. Without it, the feedback dynamics will yield unpredictable results and presumably not perform effective credit assignment. This condition is extremely unlikely to be satisfied generically, and is essentially the analog of sign-symmetry in forward and backward weights when one considers pseudoinverses rather than transposes. The authors manually enforce that it be satisfied at initialization, and manually adjust the backward weights if the condition is violated during training. These manual initialization choices and adjustments are doing much of the work of credit assignment in the authors' algorithm -- I can't tell from the results as presented how helpful the dynamic inversion really is. For instance, how well would it work if you used the same weight initialization and stability correction procedure but did not run any dynamics? 2. Even ignoring issue #1, the empirical results are a mixed bag. The results on the regression tasks seem good, but the fact that (the non-dynamic approximation to) the authors' algorithm performs worse than feedback alignment on MNIST classification is concerning. The initialization dependence observed in the autoencoding experiments is interesting, but probably needs further study -- it appears that in this problem, both backprop and NDI are fairly sensitive to the initialization, but with opposite preferences. Given that backprop is the workhorse of much more complex networks than these, it would require substantial evidence to show convincingly that inversion has a consistent advantage over backprop in initialization to robustness. 3. It would be good to see the actual proposed method implemented in the MNIST experiments rather than the non-dynamic "ideal" version. One of the obvious concerns with a method like this is the convergence of the dynamics, and right now it is not possible to tell how the speed of convergence will scale to harder problems. Of course, to really answer this question would require going beyond MNIST, but showing the dynamic results on MNIST would be a start. | 3. It would be good to see the actual proposed method implemented in the MNIST experiments rather than the non-dynamic "ideal" version. One of the obvious concerns with a method like this is the convergence of the dynamics, and right now it is not possible to tell how the speed of convergence will scale to harder problems. Of course, to really answer this question would require going beyond MNIST, but showing the dynamic results on MNIST would be a start. |
tCmIGJivc7 | ICLR_2025 | 1. The most critical part is using the LLM to fine-tune the token representations across languages for topic modeling. However, the issue of data ratio for topics in different languages was not introduced. How can we ensure that the training achieves the best results across multiple languages?
2. The determination of topic categories relies on clustering, how is the optimal number of topics determined?
3. The clustering process for forming training data may result in a significant portion of the data not being clustered, leading to considerable disparities in topic distribution. How well the model performs on less common topics has not been analyzed in depth.
4. There is a lack of recent comparisons with related models for demonstration selection, such as TopK + MDL, TopK + ConE, etc. | 4. There is a lack of recent comparisons with related models for demonstration selection, such as TopK + MDL, TopK + ConE, etc. |
ARR_2022_162_review | ARR_2022 | 1. It is well known that ELECTRA-style is efficient and the TLM-based model is helpful to the cross-lingual representation. It is no surprise that combining both methods would work.
2. The TLM-based pre-trained method required translation pairs. I understand most of the baseline required translation pairs, too. However, instead of using translation pairs, I would like to see more research try to achieve better cross-lingual transferability without using translation pairs.
3. There is no comparison between the usual relative position bias and gated relative position bias.
1. missing baseline in Fig.3 and Fig.4: I would like to see the comparison including InfoXLM an XLM-Align.
2. missing baseline in table 5, 6: I would like to see the comparison including InfoXLM and XLM-Align.
3. I'm interested in the difference between the results of using usual relative position bias and gated relative position bias. | 3. There is no comparison between the usual relative position bias and gated relative position bias. |
RwwM7pKGWv | ICLR_2024 | - The paper's technical novelty appears somewhat limited. In particular, it fails to adequately address the unique challenges presented by modeling EHR data compared to other sequential data. It also does not sufficiently explain the novelty in terms of model design compared to existing sequential generative models. It's important to note that in the machine learning context, several VAE-based architectures have been proposed to handle various types of sequential data, such as images, audio, and videos [1, 2].
- The model's design lacks clear explanations or motivation. For instance, it is unclear why VAE was chosen over other generative models for modeling the EHR data distribution. Furthermore, the rationale behind modeling the cluster probability distribution using a Dirichlet distribution remains unexplained.
- Connected to the previous concerns, it's uncertain whether the improvement in prediction performance stems from modeling patient subgrouping or is merely a consequence of the neural network architecture's high capacity. In other words, it is unclear whether patient subgrouping is essential, and the paper does not explore the consequences of removing patient subgrouping from DeepGC. To clarify, why did the authors not use a VAE architecture to model the temporal data (i.e., $P(X,Y)$) directly, instead of modeling $P(X,Y,\pi)$?
- The concerns raised are somewhat substantiated by the results presented in Table 1. The model with strong patient subgrouping performance (TSKM) does not perform well on downstream prediction tasks. Additionally, DeepGC's performance falls within one standard deviation of the second-best baseline models. Consequently, the paper would benefit from statistical testing to establish the significance of the proposed method.
- Several important technical details are omitted, such as the evaluation of patient subgrouping in an unsupervised setting. Furthermore, the paper does not explain how clustering metrics like SIL, DBI, and VRI were calculated. Data statistics and processing steps are also missing, including information about which clinical features were employed and how missing values were handled.
- The paper lacks the provision of code and supplementary documentation, which would enhance clarity and reproducibility. References:
[1] S3VAE: Self-Supervised Sequential VAE
for Representation Disentanglement and Data Generation. ICLR 2020
[2] Disentangled Sequential Autoencoder. ICML 2018. | - Connected to the previous concerns, it's uncertain whether the improvement in prediction performance stems from modeling patient subgrouping or is merely a consequence of the neural network architecture's high capacity. In other words, it is unclear whether patient subgrouping is essential, and the paper does not explore the consequences of removing patient subgrouping from DeepGC. To clarify, why did the authors not use a VAE architecture to model the temporal data (i.e., $P(X,Y)$) directly, instead of modeling $P(X,Y,\pi)$? |
NIPS_2022_157 | NIPS_2022 | In general i like this paper and i believe its contributions could be valuable to the ML community. To the best of my knowledge this is the first paper that analyze OGDA and EG for NC-SC and NC-C min-max problems. However i notice some issues/weaknesses that will require further clarification.
There are inconsistencies between the main paper and the appendix, in terms of notation and presentation of the results. These inconsistencies raised some questions the robustness of the theoretical results. Let me add a few details below:
In the statement of the theorems in the main paper the quantity Φ ( x 1 ) − m i n x Φ ( x )
is defined as Δ Φ
while in the appendix the same quantity is δ
. I would suggest the authors do a thorough pass and fix these issues. Statements of Theorems and their proofs need to use the same notation.
The main theoretical results in the main theorems are presented in terms of gradient complexity, however the proofs of main Theorems stop in equations (49) and (75). The authors should explain (even if this might be trivial) in more detail and provide the exact derivation of how one can obtain the main Theorem (the gradient complexity) from the end of their proofs.
As we can see for the proof to work the algorithms should be run with specific step-size selection. In the current statement of the Theorems the exact values of the step-size for OGDA and EG are hidden in the big Θ
expression. The authors should add the exact step-size values that used in the proofs (at the moment the Theorems are more abstract than what should be).
The step-sizes of the main theorems in the section 4.2 (Nonconvex-concave minimax problems) are not part of the statement of the theorems. This should be added in the updated version.
More clarifications are needed for some parts. I include a few questions about these points below.
Minor comments:
(a) Definition 3.3. and stochastic definition of in line 120 use both "g". This might be confusing for some readers. (b) Theorem 4.5 is about GDA but in the statement the author refer to Theorem 4.2which is a bit confusing. (c) The title could be updated to include "nonconvex-concave" instead of simple nonconvex as it is not. At the moment the reader expects that the methods proposed solve nonconvex nonconave problem (potentially with extra structured).
6.There are several recent closely related missing references (could be added in corresponding paragraphs of Section 2):
[1] Abernethy, J., Lai, K. A., Wibisono, A.. Last-iterate convergence rates for min-max optimization: Convergence of hamiltonian gradient descent and consensus optimization. In Algorithmic Learning Theory (pp. 3-47). PMLR
[2] Loizou, N., Berard, H., Jolicoeur-Martineau, A., Vincent, P., Lacoste-Julien, S., Mitliagkas, I. . Stochastic hamiltonian gradient methods for smooth games. In International Conference on Machine Learning (pp. 6370-6381). PMLR.
[3] Gorbunov, E., Berard, H., Gidel, G., Loizou, N. . Stochastic extragradient: General analysis and improved rates. In International Conference on Artificial Intelligence and Statistics (pp. 7865-7901). PMLR.
[4] Gorbunov, E., Loizou, N., Gidel, G.. Extragradient method: O (1/K) last-iterate convergence for monotone variational inequalities and connections with cocoercivity. In International Conference on Artificial Intelligence and Statistics (pp. 366-402). PMLR.
[5] Hsieh, Y. G., Iutzeler, F., Malick, J., Mertikopoulos, P. . Explore aggressively, update conservatively: Stochastic extragradient methods with variable stepsize scaling. Advances in Neural Information Processing Systems, 33, 16223-16234.
[6] Cai, Y., Oikonomou, A., Zheng, W.. Tight Last-Iterate Convergence of the Extragradient and the Optimistic Gradient Descent-Ascent Algorithm for Constrained Monotone Variational Inequalities. arXiv preprint arXiv:2204.09228.
[7] Loizou, N., Berard, H., Gidel, G., Mitliagkas, I., Lacoste-Julien, S.. Stochastic gradient descent-ascent and consensus optimization for smooth games: Convergence analysis under expected co-coercivity. Advances in Neural Information Processing Systems, 34, 19095-19108.
[8] Beznosikov, A., Gorbunov, E., Berard, H., Loizou, N. . Stochastic gradient descent-ascent: Unified theory and new efficient methods. arXiv preprint arXiv:2202.07262. | . Stochastic extragradient: General analysis and improved rates. In International Conference on Artificial Intelligence and Statistics (pp. 7865-7901). PMLR. [4] Gorbunov, E., Loizou, N., Gidel, G.. Extragradient method: O (1/K) last-iterate convergence for monotone variational inequalities and connections with cocoercivity. In International Conference on Artificial Intelligence and Statistics (pp. 366-402). PMLR. [5] Hsieh, Y. G., Iutzeler, F., Malick, J., Mertikopoulos, P. |
NIPS_2018_612 | NIPS_2018 | weakness is not including baselines that address the overfitting in boosting with heuristics. Ordered boosting is non-trivial, and it would be good to know how far simpler (heuristic) fixes go towards mitigating the problem. Overall, I think this paper will spur new research. As I read it, I easily came up with variations and alternatives that I wanted to see tried and compared. DETAILED COMMENTS The paper is already full of content, so the ideas for additional comparisons are really suggestions to consider. * For both model estimations, why start at example 1? Why not start at an example that is 1% of the way into the training data, to help reduce the risk of high variance estimates for early examples? * The best alternative I've seen for fixing TS leakage, while reusing the data sample, uses tools from differential privacy [1, 2]. How does this compare to Ordered TS? * Does importance-sampled voting [3] have the same target leakage problem as gradient boosting? This algorithm has a similar property of only using part of the sequence of examples for a given model. (I was very impressed by this algorithm when I used it; beat random forests hands down for our situation.) * How does ordered boosting compare to the subsampling trick mentioned in l. 150? * Yes, fixes that involve bagging (e.g., BagBoo [4]) add computational time, but so does having multiple permuted sequences. Seems worth a (future?) comparison. * Why not consider multiple permutations, and for each, split into required data subsets to avoid or mitigate leakage? Seems like it would have the same computational cost as ordered boosting. * Recommend checking out the Wilcoxon signed rank test for testing if two algorithms are significantly different over a range of data sets. See [6]. * l. 61: "A categorical feature..." * l. 73: "for each categorical *value*" ? * l. 97: For clarity, consider explaining a bit more how novel values in the test set are handled. * The approach here reminds me a bit of Dawid's prequential analysis, e.g., [5]. Could be worth checking those old papers to see if there is a useful connection. * l. 129: "we reveal" => "we describe" ? * l. 131: "called ordered boosting" * l. 135-137: The "shift" terminology seems less understandable than talking about biased estimates. * l. 174: "remind" => "recall" ? * l. 203-204: "using one tree structure"; do you mean shared \sigma? * Algorithm 1: only one random permutation? * l. 237: Don't really understand what is meant by right hand side of equality. What is 2^j subscript denoting? * l. 257: "tunning" => "tuning" * l. 268: ", what is expected." This reads awkwardly. * l. 311: This reference is incomplete. REFERENCES [1] https://www.slideshare.net/SessionsEvents/misha-bilenko-principal-researcher-microsoft [2] https://www.youtube.com/watch?v=7sZeTxIrnxs [3] Breiman (1999). Pasting small votes for classification in large databases and on-line. Machine Learning 36(1):85--103. [4] Pavlov et al. (2010). BagBoo: A scalable hybrid bagging-the-boosting model. In CIKM. [5] Dawid (1984). Present position and potential developments: Some personal views: Statistical Theory: The Prequential Approach. Journal of the Royal Stastical Society, Series A, 147(2). [6] Demsar (2006). Statistical comparisons of classifiers over multiple data sets. Journal of Machine Learning Research, 7:1--30. | * The approach here reminds me a bit of Dawid's prequential analysis, e.g., [5]. Could be worth checking those old papers to see if there is a useful connection. |
zxPDdw8koz | ICLR_2024 | - The experiment results are not convincing. The baselines are not strong. The authors should present more strong baselines, including Mask2Former. Moreover, this work dose not compare with recent state-of-the-art approach whether on semantic segmentation or depth prediction.
- Missing the frozen trained CLIP model baselines with heavier head [1], [2], [3]. What are the Frozen CLIP results of strong baselines?
- The ablation studies are not good. For example, the effects of various task heads are not explored. The effects of different task-specific experts are not explored.
The experiment details can be put into appendix.
- In abstract, “it lacks object localization capabilities” Personally, CLIP models have the localization ability. Several works [1][2] have adopted CLIP as feature extractor, which also achieve good results.
- Figure-1 (c) needs to add the baseline results for better comparison.
[1], Frozen clip models are efficient video learners, ECCV-2022
[2], Convolutions Die Hard: Open-Vocabulary Segmentation with Single Frozen Convolutional CLIP, NeurIPS-2023
[3]. F-VLM: Open-Vocabulary Object Detection upon Frozen Vision and Language Models, ICLR-2023 | - Figure-1 (c) needs to add the baseline results for better comparison. [1], Frozen clip models are efficient video learners, ECCV-2022 [2], Convolutions Die Hard: Open-Vocabulary Segmentation with Single Frozen Convolutional CLIP, NeurIPS-2023 [3]. F-VLM: Open-Vocabulary Object Detection upon Frozen Vision and Language Models, ICLR-2023 |
ARR_2022_147_review | ARR_2022 | - Lack of illustrative examples regarding the model outputs.
- Some details regarding the knowledge collection process have been omitted (see "Questions" below).
QUESTIONS: - Fig. 2: Why did you discard the "anatomy" category?
- l. 221: How many query templates did you specify in total?
- l. 227: What's the size of the set of knowledge candidates?
- l. 550: Did you calculate the agreement between the annotators? Were the annotators authors of the paper?
MINOR: - Try to better align the figures with the text.
- fix punctuation: l. 336, l. 433, l. 445, l. 534 - Table 2: The highlighting of the numbers does not correspond to the caption ("highest scores are in bold, second highest scores in italic") | - Try to better align the figures with the text. |
zkzf0VkiNv | ICLR_2024 | 1. Figure 2 shows that, without employing data augmentation and similarity-based regularization, the performance of CR-OSRS is comparable to RS-GM.
2. Could acceleration be achieved by incorporating entropy regularization into the optimization process?
3. It would be beneficial if the authors could provide an analysis of the computational complexity of this method.
4. The author wants to express too much content in the article, resulting in insufficient details and incomplete content in the main text.
5. The experimental part needs to be reorganized and further improved.
Details comments
1) It is recommended to swap the positions of Sections 4.3 and 4.4. According to the diagram, 4.3 is the training section, and 4.4 aims to measure certified space. Both 4.1 and 4.2 belong to the robustness and testing sections. Therefore, putting these parts together feels more reasonable.
2) The author should emphasize "The article is a general and robust method that can be applied to various GM methods, and we only use NGMv2 as an example." at the beginning of the article, rather than just showing in the title of Method Figure 1. This can better highlight the characteristics and contribution of the method.
3) The experimental part needs to be reorganized and further improved. The experimental section has a lot of content, but the experimental content listed in the main text does not highlight the superiority of the method well, so it needs to be reorganized. Based on the characteristics of the article, the experimental suggestions in the main text should include the following: 1. Robustness comparison and accuracy analysis with other empirical robustness algorithms for the same type of perturbations, rather than just focusing on the RS method, to clarify the superiority of the method. (You should supplement this part.) 2. Suggest using ablation experiments as the second part to demonstrate the effectiveness of the method. 3. Parameter analysis, elucidating the method's dependence on parameters. 4. Consider its applications on six basic algorithms as an extension part. Afterwards, based on the importance, select the important ones to place in the main text, and show the rest in the appendix.
4) In P16, the proof of claim 2, it should be P(I \in B) not P(I \in A).
5) In Table 2 of appendix, the Summary of main existing literature in learning GM can list the related types of perturbations.
6) In Formula 8, please clarify the meaning of lower p (lower bound of unilateral confidence), and the reason and meaning of setting as 1/2. | 1. Robustness comparison and accuracy analysis with other empirical robustness algorithms for the same type of perturbations, rather than just focusing on the RS method, to clarify the superiority of the method. (You should supplement this part.) 2. Suggest using ablation experiments as the second part to demonstrate the effectiveness of the method. |
NIPS_2020_56 | NIPS_2020 | - I found some of the discussion difficult to follow. In particular, I'm not sure that I could train a BPNN given only the content of the main paper. I understand that it is difficult to trim a lot of experiments into a short page limit, but what is left in the main text leaves way more questions that answers. This is true for some of the model discussion and applies two-fold for the experimental evaluation. - Could you include some details about how to actually train this model in the main text as this seems to be the most important step of the whole process. - I'm confused a bit in the experimental section with respect to what version of BP is actually being compared against. When you say "standard BP", you mean without damping? If so, I don't think this is a fair comparison as most practitioners would not use the undamped version. Additionally, why would we expect BPNN-D to converge to better local optima than BP? Because the learned H function helps avoid local optima? If this is true, it is an interesting observation by itself. - Plots and figures should probably include variance estimates of the RMSE to give some sense of the variability of the methods. - I liked the experiments in Section 4.3, but I think that it would have been more interesting to train on one of the domains and predict one of the others. In particular, I'm very curious how overfit (if at all) these models are to the domain on which they are trained. Maybe the corrections to the message passing procedure are really only functions of the graph structure and potentials... | - Plots and figures should probably include variance estimates of the RMSE to give some sense of the variability of the methods. |
NW09xt3kvH | EMNLP_2023 | 1. The authors' construction of a hierarchical interest tree to represent user preferences in each session raises concerns about the time complexity of the overall process. To demonstrate the efficiency of the proposed framework, it would be beneficial if the paper includes a detailed analysis of the time complexity and compares it with other methods.
2. Although the framework bears similarities to [1], the paper should emphasize and better showcase the improvements and advancements achieved by the proposed approach over [1]. This clarification would add more clarity and value to the research, enabling readers to understand the novel contributions of the proposed framework.
3. For a comprehensive understanding of the proposed approach's performance, it would be valuable to include information on the success rate at each conversation turn. This data can offer insights into the framework's comparative performance throughout the recommendation process, helping readers to assess its effectiveness in a more nuanced manner.
[1] Yiming Zhang, Lingfei Wu, Qi Shen, Yitong Pang, Zhi-hua Wei, Fangli Xu, Bo Long, and Jian Pei. 2022. Multiple choice questions based multi-interest policy learning for conversational recommendation. In Proceedings of the ACM Web Conference 2022, pages 2153–2162. | 2. Although the framework bears similarities to [1], the paper should emphasize and better showcase the improvements and advancements achieved by the proposed approach over [1]. This clarification would add more clarity and value to the research, enabling readers to understand the novel contributions of the proposed framework. |
Cx6Jn6gKHz | ICLR_2024 | 1) Considering that the main contribution of the paper revolves around Eq. 6-8, there should be a formal derivation for $\hat{\delta}$ when using the first order Taylor expansion of loss $\mathcal{L}$. I would expect to see this in the supplemental for completeness, but couldn’t find any such derivation.
2) For sparse inputs on ShapeNet and Faust, it seems like NTPS (Chen 2023) evaluate on 300 points while here sparse inputs are being considered as 1024 points. Since NTPS is the other main work that does unsupervised SDF learning from sparse point clouds, it would be nice to see results on 300 points which are significantly sparser inputs then what has been presented.
3) Best values in Table 3 should be bolded to make it easier to read.
4) Figure 5 should include a comparison to NTPS as it performs the closest to the proposed method according to Table 3.
5) In Tables 4 and 5, metric $d_{C}$ is never defined. I assume this is chamfer distance.
6) DiGS seems to perform slightly better in the dense point cloud case (Table 4), but it wasn’t compared against in the sparse input case (Table 5). I would expect to see a comparison to this method for the sparse input to see if it performs worse. Additionally, NTPS should be included in both Table 4 and 5.
7) Please add the point cloud inputs to Figure 6 to have an understanding of the difference in inputs. | 2) For sparse inputs on ShapeNet and Faust, it seems like NTPS (Chen 2023) evaluate on 300 points while here sparse inputs are being considered as 1024 points. Since NTPS is the other main work that does unsupervised SDF learning from sparse point clouds, it would be nice to see results on 300 points which are significantly sparser inputs then what has been presented. |
ICLR_2023_1030 | ICLR_2023 | weakness of the current work :
The current work focusses on a simplified setup of two classes and uses Contextual Stochastic Block Model as the generative model which does not provide an accurate representation of real-world graphs.
The authors do not demonstrate how to measure over-smoothing as well as the two effects in practice. Without being able to 1) adequately measure and quantify the two effects and 2) demonstrate the authors can adequately explain over-smoothing in a general setting, the presented approach seems hypothetical.
The authors do not demonstrate the practicality of the current approach to the research community. Theoretical analysis is great however without being able to provide utility, the scope of the work is significantly reduced.
As the authors themselves point out, the current work's analysis is based on oracle classifier, however in practice, we work in a semi-supervised setting. Thus the utility associated with the current work is pretty limited. | 2) demonstrate the authors can adequately explain over-smoothing in a general setting, the presented approach seems hypothetical. The authors do not demonstrate the practicality of the current approach to the research community. Theoretical analysis is great however without being able to provide utility, the scope of the work is significantly reduced. As the authors themselves point out, the current work's analysis is based on oracle classifier, however in practice, we work in a semi-supervised setting. Thus the utility associated with the current work is pretty limited. |
ICLR_2022_1691 | ICLR_2022 | The paper does a very nice trade-off between theory and empirical analysis. However, as a potential direction for improvement, the empirical evaluation could be more on par with AT literature, for example:
analysis with different radius of the ball, i.e. plots with varying ϵ
how robust is the method to other attacks (e.g. AutoAttack), is the catastrophic overfitting improved, etc.
The main result (Thm 1) is for an ensemble of size n, while (if I understood well) the experiments are with one model. The authors mention that a single model suffices, but if I am correct there are no results with an ensemble. Verifying Thm 1 empirically, e.g. showing how n
impacts final performances would connect better the result with the experiments. Recommendations
Since Tian et al. (2021) is a very recent work I do not take this into account for my rating, but other than that it might be helpful for the audience to include a comparison with it (either theoretical insight about advantages/disadvantages, or empirical comparison on CIFAR-10).
The abstract leaves it somewhat unclear what is the online learning aspect of the method (included in the title), maybe adding a sentence would be nice.
Write the requirement C ≥ k log k
in Thm 1 more explicitly as a separate assumption before stating Thm 1.
Typo: Fig.3 noteable → notable
Since the main empirical results use temporal ensembling (TE) add a detailed description of it in the App. for completeness Questions
Fig. 1: Does the robust test accuracy of clean training (left) follow a non-uniform trend across the classes? It would be interesting to see if this observation from Fig.1 is (not) a result of AT.
If I am correct, temporal ensembling (TE) is used for all methods. This raises the question if the proposed method works well only in this setup with TE, and for completeness, it would be nice to point out this to the readers. Could the authors provide results without TE on CIFAR-10? | 1: Does the robust test accuracy of clean training (left) follow a non-uniform trend across the classes? It would be interesting to see if this observation from Fig.1 is (not) a result of AT. If I am correct, temporal ensembling (TE) is used for all methods. This raises the question if the proposed method works well only in this setup with TE, and for completeness, it would be nice to point out this to the readers. Could the authors provide results without TE on CIFAR-10? |
ICLR_2021_1181 | ICLR_2021 | 1.For domain adaptation in the NLP field, powerful pre-trained language models, e.g., BERT, XLNet, can overcome the domain-shift problem to some extent. Thus, the authors should be used as the base encoder for all methods and then compare the efficacy of the transfer parts instead of the simplest n-gram features.
2.The whole procedure is slightly complex. The author formulates the prototypical distribution as a GMM, which has high algorithm complexity. However, formal complexity analysis is absent. The author should provide an analysis of the time complexity and training time of the proposed SAUM method compared with other baselines. Besides, a statistically significant test is absent for performance improvements.
3.The motivation of learning a large margin between different classes is exactly discriminative learning, which is not novel when combined with domain adaptation methods and already proposed in the existing literature, e.g., Unified Deep Supervised Domain Adaptation and Generalization, Saeid et al., ICCV 2017. Contrastive Adaptation Network for Unsupervised Domain Adaptation, Kang et al., CVPR 2019 Joint Domain Alignment and Discriminative Feature Learning for Unsupervised Deep Domain Adaptation, Chen et al., AAAI 2019.
However, this paper lacks detailed discussions and comparisons with existing discriminative feature learning methods for domain adaptation.
4.The unlabeled data (2000) from the preprocessed Amazon review dataset (Blitzer version) is perfectly balanced, which is impractical in real-world applications. Since we cannot control the label distribution of unlabeled data during training, the author should also use a more convinced setting as did in Adaptive Semi-supervised Learning for Cross-domain Sentiment Classification, He et al., EMNLP 2018, which directly samples unlabeled data from millions of reviews.
5.The paper lacks some related work about cross-domain sentiment analysis, e.g., End-to-end adversarial memory network for cross-domain sentiment classification, Li et al., IJCAI 2017 Adaptive Semi-supervised Learning for Cross-domain Sentiment Classification, He et al., EMNLP 2018 Hierarchical attention transfer network for cross-domain sentiment classification, Li et al., AAAI 18 Questions:
1.Have the authors conducted the significance tests for the improvements?
2.How fast does this algorithm run or train compared with other baselines? | 1.Have the authors conducted the significance tests for the improvements? |
peZbJlOVAN | ICLR_2024 | * Although this paper underscores the significance of the problem within the context of retrieval augmentation, the benchmark setting does not exhibit a substantial deviation from prior work (Shi et al., 2023). It assumes that adversarial prompts are already retrieved as part of the context and does not investigate the entire retrieval-augmented LLM framework.
* The evaluation of defense against prompt injection is limited to a basic baseline, where the model adds "ignore previous prompt." Figure 2 demonstrates the significance of the injection position. This raises the natural question: "How does the model's performance change when the order of the question and the search results is swapped?" | * Although this paper underscores the significance of the problem within the context of retrieval augmentation, the benchmark setting does not exhibit a substantial deviation from prior work (Shi et al., 2023). It assumes that adversarial prompts are already retrieved as part of the context and does not investigate the entire retrieval-augmented LLM framework. |
CgAfbI4kGS | EMNLP_2023 | I think there are two reasons to consider rejecting this paper:
1) The notion of incompleteness for their KGC task is somewhat artificial; the authors obtain relations of answer entities in dev/test set, and "incomplete" them by obscuring one of the entities in the relation, and then "randomly choose a proportion P of these triplets as the final validation and test sets". This challenge here is that not all triples of answer entities are equally meaningful for QA; i.e. it is possible that some and probably likely that some, if not most, triples, are largely meaningless. As a result, obscuring them would be expected to have little/no impact on QA. This risks significantly diluting the correlation between KGC quality and downstream QA. Specifically, a KGC model might look great because it fills in lots of relations but then look bad for QA because some large percent of those relations were meaningless. This can potentially mislead the reader into thinking that a particular KGC model is strong on KGC but bad for QA, when in fact the measurement of KGC model strength on this benchmark may just be an artifact of the benchmark. I think this can be improved by applying stratified sampling over predicates to ensure that we are controlling not just for the entities we obscure but also for relative importance of the information the KGC model completes. Further motivating the need for a deeper look into this approach is Appendix D, which seems to indicate a weak correlation between KGC and KGQA. It would be interesting to see the set of questions for which there is little to no correlation, as this is where the most opportunity is to improve this benchmark. Ultimately I view this as something that dilutes, but does not invalidate, the conclusions. There is a correlation, and that correlation needs to be explored further, but unfortunately the authors don't dig into the link between KGC and KGQA much to explain this correlation.
2) Modeling techniques studied; the authors study two KGQA techniques, Pangu and DecAF. While both exhibit strong performance, these are not the most natural nor most representative baseline choices. Neither of these techniques are popular or widely cited; DecAF is somewhat popular and adopts an IR approach to KGQA, in which documents of triples are retrieved as evidence to inform answer generation, while Pangu is not and employs a neurosymbolic planner/critic pipeline. This paper would be made more sound by the inclusion of more popular and representative techniques, especially those of the semantic parsing variety, of which there are many popular approaches (citations below). The lack of semantic parsing baseline is concerning for a few reasons, including that 1) these are the most widely studied approach to KGQA and 2) semantic parsing provides a more direct means to assess KGC. W/r/t 2) specifically, these approaches would enable the authors to measure the benefit of KGC on generated parse success rate. For example, using a parsing approach trained on the complete KG and evaluated on the incomplete one would provide a realistic measurement of the impact of missing data, as parses that seek to return the obscured data would no longer be executable. The authors should give more justification behind why they chose DecAF and Pangu, beyond just "here are 2 SOTA techniques". While they discuss the lack of an LLM-only baseline in the limitation, they don't include semantic parsing. @article{Ye2021RNGKBQAGA,
title={RNG-KBQA: Generation Augmented Iterative Ranking for Knowledge Base Question Answering},
author={Xi Ye and Semih Yavuz and Kazuma Hashimoto and Yingbo Zhou and Caiming Xiong}, journal={ArXiv}, year={2021}, volume={abs/2109.08678}, url={https://api.semanticscholar.org/CorpusID:237562927} } @inproceedings{Abdelaziz2021ASP,
title={A Semantic Parsing and Reasoning-Based Approach to Knowledge Base Question Answering},
author={I. Abdelaziz and Srinivas Ravishankar and Pavan Kapanipathi and Salim Roukos and Alexander G. Gray},
booktitle={AAAI Conference on Artificial Intelligence}, year={2021}, url={https://api.semanticscholar.org/CorpusID:235363625} } | 2) semantic parsing provides a more direct means to assess KGC. W/r/t |
NIPS_2022_1699 | NIPS_2022 | 1. The exact definitions of some important notations such as Θ and Ω
are missing. 2. The authors consider a hyperparameter optimization problem on MNIST in the experiments on AID-BiO (in Line 315), while they consider another hyper-representation problem in the experiments on ITD-BiO (in Line 332). They may want to explain why they consider different problems for the two optimizers. 3. In this paper, the authors only report the losses v.s. running time and the losses v.s. the number of iterations in experiments on AID-BiO and ITD-BiO, respectively. It would be more convincing if they report MV( ϵ
)(the total number of Jacobian- and Hessian-vector product computations), Gc( ϵ
)(the total number of gradient computations) or some more metrics in the experiments to support their theoretical results on the computational complexities.
Yes, the authors adequately addressed the limitations and potential negative societal impact of their work. | 2. The authors consider a hyperparameter optimization problem on MNIST in the experiments on AID-BiO (in Line 315), while they consider another hyper-representation problem in the experiments on ITD-BiO (in Line 332). They may want to explain why they consider different problems for the two optimizers. |
ARR_2022_28_review | ARR_2022 | The main concerns with this paper is that it doesn't fully explain some choices in the model (see comments/questions section). Moreover, some parts of the paper are actually not fully clear. Finally, some details are missing, making the paper incomplete.
- Algorithm 1 is not really explained. For example, at each step (1, 2, 2a, 3, 3a) are you sampling a different batch from S and T? Is the notation L(X) meaning that you optimize only the parameters X of the architecture?
- Line 232: When you say you "mine", what do you exactly mean? Does this mean you sample P sentences from the set of sentences of S and T with similar constraints?
- Lines 237-238 and Line 262: Why would you want to use the representation from the critic last layer? - Line 239: "Ci are a set of constraints for a sentence" should be moved before.
- Table 1: It seems that the results for DRG and ARAE are not averaged over 5 runs (they're exactly the same of the previous paper version) - Table 1: How did you choose the p=0.6?
- Table 1: row=ARAE, column=POLITICAL-FL It seems this value should be the one in bold.
- Lines 349-353: It seems you're comparing results for ARAE + CONTRA, ARAE + CLF and ARAE + CONTRA + CL with respect to simple ARAE, while in the text you mention only ARAE + CONTRA and ARAE + CLF.
- Line 361: and SIM to -> and SIM with respect to - Figure 3: Please, rephrase the caption of the errors bars (or explain it in the text). It is not clear what do you mean.
- Line 389: You mention here you used different p values as in Table 1. This table doesn't report results with different values for p. - Lines 422-423: why using nucleous sampling when the best results were with greedy decoding? Where does 0.9 come from?
- In general, in the experiments, what are the source and target domains?
- Line 426-Table4: What do you want to demonstrate here? Could you add an explanation? What constraints/attributes are preserved? What is the source domain? What is the target domain?
- Lines 559-560: This is not entirely true. In Cycle Consistency loss you can iterate between two phases of the reconstructions (A-B-A and B-A-B) with two separate standard backpropagation processes.
- Line 573: works focuses -> works focus | - Algorithm 1 is not really explained. For example, at each step (1, 2, 2a, 3, 3a) are you sampling a different batch from S and T? Is the notation L(X) meaning that you optimize only the parameters X of the architecture? |
NIPS_2018_768 | NIPS_2018 | Weakness] 1: I like the paper's idea and result. However, this paper really REQUIRE the ablation study to justify the effectiveness of different compositions. For example: - In eq2, what is the number of m, and how m affect the results? - In eq3, what is the dimension of w_n? what if the use the Euclidean coordinate instead of Polar coordinate? - In eq3, how the number of Gaussian kernels changes the experiment results. 2: Based on the paper's description, I think it will be hard to replicate the result. It would be great if the authors can release the code after the acceptance of the paper. 3: There are several typos in the paper, need better proof reading. | - In eq2, what is the number of m, and how m affect the results? |
ICLR_2023_4828 | ICLR_2023 | There are some experiments results I find not consistent with authors’ claims. 1. In table 7, combining TL-Align with Mixup, CutMix is worse than TL-Align+CutMix, does this mean TL-Align will not work well with Mixup? Can authors show separate Mixup w v.s. w/o TL-Align results? 2. In Table 2, TransMix result is shown as 80.1, the actual results from TransMix paper is 80.7, which is actually higher than this paper’ results 80.6. TransMix only uses last layer’s attention map where this paper proposes to use all layers, however the comparison results are kind of confusing here, can authors comment on that? | 1. In table 7, combining TL-Align with Mixup, CutMix is worse than TL-Align+CutMix, does this mean TL-Align will not work well with Mixup? Can authors show separate Mixup w v.s. w/o TL-Align results? |
ARR_2022_40_review | ARR_2022 | - More details on how exactly the topic related chit-chat turns would have strengthened the paper. What are prompts provided to the blender bot and the impact of different prompts on the quality of generated data?
- Also, Blenderbot details for TOD simulation can be expanded in section 2.3. For instance, what is the impact of using mergeSGD vs TOD simulation on the overall quality ?
- The paper seems to lack details on performance of the intent detector model and QA models and their impact on the quality of the dialogs generated. It would be nice to have an ablation study on the quality of dialogs using different intent detectors (including the data used to train).
During the transition turn, did the process also check if the user is requesting for more information or a question before switching to TOD setting ? | - More details on how exactly the topic related chit-chat turns would have strengthened the paper. What are prompts provided to the blender bot and the impact of different prompts on the quality of generated data? |
NIPS_2021_2131 | NIPS_2021 | - There is not much technical novelty. Given the distinct GPs modeling the function network, the acquisition function and sampling procedure are not novel - The theoretical guarantee is pretty weak (random search is asymptotically optimal).
The discussion of not requiring dense coverage to prove the method is asymptotically consistent is interesting, but the utility of proposition 2 is not clear because although dense coverage is a consideration for proving consistency, it is not really a practical reality in sample-efficient optimization—typically BO would not have dense coverage.
Questions/comments: - There is no discussion of observation noise, which is a practical concern in many of the real world use cases mentioned in the paper. The approach of using GPs to model nodes in function network can naturally handle noisy observations, so only the acquisition function would need to be adjusted to account for noisy observations since the best objective value would be unknown. I expect that the empirical performance would remain the same (e.g. using Noisy EI from Letham et al. 2019), but the computation would be much more expensive. It would be good to discuss and demonstrated performance under noisy observations. - How does the number of MC samples affect performance, empirically? How does the network structure affect this? - It would be interesting to see a head-to-head comparison with deep GPs. How different are the runtimes (including inference times) and empirical performances?
Since the core contribution is modeling each node in the function network with a distinct GP, it would be good to see more evaluation of the function network model's predictive performance compared to a alternative modeling choices (e.g. individual models with a compositional objective, vanilla global gp, deep gp)
Grammar: - L238 “out method” -> “our method” - L335 “structurre” -> “structure”
The discussion of the work's limitations is quite thorough, and it proposes interesting directions for future work. The authors have addressed potential negative societal impacts. | - It would be interesting to see a head-to-head comparison with deep GPs. How different are the runtimes (including inference times) and empirical performances? Since the core contribution is modeling each node in the function network with a distinct GP, it would be good to see more evaluation of the function network model's predictive performance compared to a alternative modeling choices (e.g. individual models with a compositional objective, vanilla global gp, deep gp) Grammar: |
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