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paper_id stringlengths 10 19	venue stringclasses 15 values	focused_review stringlengths 7 10.2k	point stringlengths 47 690
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.	* 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.
NIPS_2016_339	NIPS_2016	weakness of the model. How would the values in table 1 change without this extra assumption? 3. I didn't find all parameter values. What are the model parameters for task 1? What lambda was chosen for the Boltzmann policy. But more importantly: How were the parameters chosen? Maximum likelihood estimates? 4. An answer to this point may be beyond the scope of this work, but it may be interesting to think about it. It is mentioned (lines 104-106) that "the examples [...] should maximally disambiguate the concept being taught from other possible concepts". How is disambiguation measured? How can disambiguation be maximized? Could there be an information theoretic approach to these questions? Something like: the teacher chooses samples that maximally reduce the entropy of the assumed posterior of the student. Does the proposed model do that? Minor points: â¢ line 88: The optimal policy is deterministic. Hence I'm a bit confused by "the stochastic optimal policy". Is above defined "the Boltzmann policy" meant? â¢ What is d and h in equation 2? â¢ line 108: "to calculate this ..." What is meant by "this"? â¢ Algorithm 1: Require should also include epsilon. Does line 1 initialize the set of policies to an empty set? Are the policies in line 4 added to this set? Does calculateActionValues return the Q* defined in line 75? What is M in line 6? How should p_min be chosen? Why is p_min needed anyway? â¢ Experiment 2: Is the reward 10 points (line 178) or 5 points (line 196)? â¢ Experiment 2: Is 0A the condition where all tiles are dangerous? Why are the likelihoods so much larger for 0A? Is it reasonable to average over likelihoods that differ by more than an order of magnitude (0A vs 2A-C)? â¢ Text and formulas should be carefully checked for typos (e.g. line 10 in Algorithm 1: delta > epsilon; line 217: 1^-6;)	3. I didn't find all parameter values. What are the model parameters for task 1? What lambda was chosen for the Boltzmann policy. But more importantly: How were the parameters chosen? Maximum likelihood estimates?
GeFFYOCkvS	EMNLP_2023	- The authors have reproduced a well-known result in the literature--left political bias in ChatGPT and in LLMs in general--using the "coarse" (their description) methodology of passing a binary stance classifier over ChatGPT's output. The observation that language models reproduce the biases of the corpora on which they're trained has been made at each step of the evolution of these models, from word2vec to BERT to ChatGPT, and so it's unclear why this observation needs to once again be made using the authors "coarse" methodology. - The authors' decision to filter by divisive topic using introduces an unacknowledged prior: for most of the topics given in the appendix (immigration, the death penalty, etc.), the choice to bother writing about the topic itself introduces bias. This choice will be reflected in both the frequency with which such articles appear and in the language used in those articles. The existence of the death penalty, for example, might be considered unproblematic on the right and, for that reason, one will see fewer articles on the subject in right-leaning newspapers. When they do appear, neutral language will be employed. The opposite is likely true for a left-leaning publication, for whom the existence of the death penalty is a problem: the articles will occur with more frequency and will employ less neutral language. For these reasons, it's not surprising that the authors' classifier, which was annotated via distant supervision using political slant tags assigned by Wikipedia, will tend to score most content generated by an LLM as left-leaning.	- The authors have reproduced a well-known result in the literature--left political bias in ChatGPT and in LLMs in general--using the "coarse" (their description) methodology of passing a binary stance classifier over ChatGPT's output. The observation that language models reproduce the biases of the corpora on which they're trained has been made at each step of the evolution of these models, from word2vec to BERT to ChatGPT, and so it's unclear why this observation needs to once again be made using the authors "coarse" methodology.
ICLR_2023_3705	ICLR_2023	1)The main assumption is borrowed from other works but is actually rarely used in the optimization field. Moreover, the benefits of this assumption is not well investigated. For example, a) why it is more reasonable than the previous one? B) why it can add gradient norm L_1 \nabla f(w_1) in Eqn (3) or why we do not add other term? It should be mentioned that a milder condition does not mean it is better, since it may not reflect the truth. For me, problem B) is especially important in this work, since the authors do not well explain and investigate it. 2)Results in Theorem 1 show that Adam actually does not converge, since this is a constant term O(D_0^{0.5}\delta) in Eqn. (5). This is not intuitive, the authors claim it is because the learning rate may not diminish. But many previous works, e.g. [ref 1], can prove Adam-type algorithms can converge even using a constant learning rate. Of course, they use the standard smooth condition. But (L0,L1)-smoothness condition should not cause this kind of convergence, since for nonconvex problem, in most cases, we only need the learning rate to be small but does not care whether it diminishes to zero. [ref 1] Dongruo Zhou, Jinghui Chen, et al. On the Convergence of Adaptive Gradient Methods for Nonconvex Optimization 3)It is not clear what are the challenges when the authors analyze Adam under the (L0,L1)-smoothness condition. It seems one can directly apply standard analysis on the (L0,L1)-smoothness condition. So it is better to explain the challenges, especially the difference between this one and Zhang et al. 4)Under the same assumption, the authors use examples to show the advantage of Adam over GD and SGD. This is good. But one issue is that is the example reasonable or does it share similar properties with practical problems, especially for networks. This is important since both SGD and ADAM are widely used in the deep learning field. 5)In the work, when comparing SGD and ADAM, the authors explain the advantage of adam comes from the cases when the local smoothness varies drastically across the domain. It is not very clear for me why Adam could better handle this case. Maybe one intuitive example could help. 6)The most important problem is that this work does not provide new insights, since it is well known that the second order moment could help the convergence of Adam. This work does not provide any insights beyond this point and also does not give any practical solution to further improve.	3)It is not clear what are the challenges when the authors analyze Adam under the (L0,L1)-smoothness condition. It seems one can directly apply standard analysis on the (L0,L1)-smoothness condition. So it is better to explain the challenges, especially the difference between this one and Zhang et al.
ICLR_2023_1979	ICLR_2023	Weakness: 1.It seems that the method part is very similar to the related work cited in the paper: Generating Adversarial Disturbances for Controller Verification. Could the author provide more clarification on this? 2.Experimental comparison to RRT* seems not good: Even though the RRT* baseline is an oracle without partial observability, the visible region is still very large, which covers more than half of the obstacles. In this case, the naive RRT* (as mentioned in supp C1) can still outperform the proposed method by a large margin on the first task.	1.It seems that the method part is very similar to the related work cited in the paper: Generating Adversarial Disturbances for Controller Verification. Could the author provide more clarification on this?
NIPS_2018_15	NIPS_2018	- The hGRU architecture seems pretty ad-hoc and not very well motivated. - The comparison with state-of-the-art deep architectures may not be entirely fair. - Given the actual implementation, the link to biology and the interpretation in terms of excitatory and inhibitory connections seem a bit overstated. Conclusion: Overall, I think this is a really good paper. While some parts could be done a bit more principled and perhaps simpler, I think the paper makes a good contribution as it stands and may inspire a lot of interesting future work. My main concern is the comparison with state-of-the-art deep architectures, where I would like the authors to perform a better control (see below), the results of which may undermine their main claim to some extent. Details: - The comparison with state-of-the-art deep architectures seems a bit unfair. These architectures are designed for dealing with natural images and therefore have an order of magnitude more feature maps per layer, which are probably not necessary for the simple image statistics in the Pathfinder challenge. However, this difference alone increases the number of parameters by two orders of magnitude compared with hGRU or smaller CNNs. I suspect that using the same architectures with smaller number of feature maps per layer would bring the number of parameters much closer to the hGRU model without sacrificing performance on the Pathfinder task. In the author response, I would like to see the numbers for this control at least on the ResNet-152 or one of the image-to-image models. The hGRU architecture seems very ad-hoc. - It is not quite clear to me what is the feature that makes the difference between GRU and hGRU. Is it the two steps, the sharing of the weights W, the additional constants that are introduced everywhere and in each iteration (eta_t). I would have hoped for a more systematic exploration of these features. - Why are the gain and mix where they are? E.g. why is there no gain going from H^(1) to \tilde H^(2)? - I would have expected Eqs. (7) and (10) to be analogous, but instead one uses X and the other one H^(1). Why is that? - Why are both H^(1) and C^(2) multiplied by kappa in Eq. (10)? - Are alpha, mu, beta, kappa, omega constrained to be positive? Otherwise the minus and plus signs in Eqs. (7) and (10) are arbitrary, since some of these parameters could be negative and invert the sign. - The interpretation of excitatory and inhibitory horizontal connections is a bit odd. The same kernel (W) is applied twice (but on different hidden states). Once the result is subtracted and once it's added (but see the question above whether this interpretation even makes sense). Can the authors explain the logic behind this approach? Wouldn't it be much cleaner and make more sense to learn both an excitatory and an inhibitory kernel and enforce positive and negative weights, respectively? - The claim that the non-linear horizontal interactions are necessary does not appear to be supported by the experimental results: the nonlinear lesion performs only marginally worse than the full model. - I do not understand what insights the eigenconnectivity analysis provides. It shows a different model (trained on BSDS500 rather than Pathfinder) for which we have no clue how it performs on the task and the authors do not comment on what's the interpretation of the model trained on Pathfinder not showing these same patterns. Also, it's not clear to me where the authors see the "association field, with collinear excitation and orthogonal suppression." For that, we would have to know the preferred orientation of a feature and then look at its incoming horizontal weights. If that is what Fig. 4a shows, it needs to be explained better.	- The hGRU architecture seems pretty ad-hoc and not very well motivated.
ICLR_2023_2851	ICLR_2023	Loss function: The proposed Decoupled Uniformity loss extends the uniformity loss in [54] and does not explicitly include the alignment loss in [54], which is elegant. The authors claimed that the proposed loss function can implicitly encourage alignment (also showed theoretically in Theorem 1 with insufficient training samples). The reviewer wonder what if you add the alignment loss similar to [54]. Would that increase or degrade the performance in practice, ie., when the number of the training samples is neither too low nor infinity? As shown in the experiment, without the prior information, the proposed method cannot beat the SOTA. Assumptions: The authors introduced the Weak-aligned encoder, which is claimed to be weaker than previous assumptions such as L-smoothness. In the implementation, how to ensure this assumption is satisfied? Assumptions: How to ensure Assumption 2 in implementation? Definition 3.7: How to find the value of \lambda? Experiments: . From the experimental results, without the prior information (the same as the benchmarks) the proposed method has no advantage compared to the SOTA. The advantage only shows when using the prior knowledge. Such comparison is a bit unfair, because in this case the proposed method essentially requires two representation models learned based on each dataset, ie., VAE/GAN + CL. Such extra complexity and cost need to be considered. . Kernel quality is crucial to the downstream performance as shown experimentally in Appendix Fig. 4. In the implementation, how to choose a proper kernel with optimal parameters? Are these parameters jointly learned or picked via the validation sets? . In Table 2, the performance of the proposed method is shown with 4 views. Do the benchmarks also use 4 views? If not, please provide results with 2 views for the fair comparison.	. From the experimental results, without the prior information (the same as the benchmarks) the proposed method has no advantage compared to the SOTA. The advantage only shows when using the prior knowledge. Such comparison is a bit unfair, because in this case the proposed method essentially requires two representation models learned based on each dataset, ie., VAE/GAN + CL. Such extra complexity and cost need to be considered.
ARR_2022_60_review	ARR_2022	- Underdefined and conflation of concepts - Several important details missing - Lack of clarity in how datasets were curated prevents one from assessing their validity - Too many results which are not fully justified or explained This is a very important, interesting, and valuable paper with many positives. First and foremost, annotators’ backgrounds are an important factor and should be taken into consideration when designing datasets for hate speech, toxicity, or related phenomena. The paper not only accounts for demographic variables as done in previous work but other attitudinal covariates like attitude towards free speech that are well-chosen. The paper presents two well-thought out experiments and presents results in a clear manner which contain several important findings. It is precisely because of the great potential and impact of this paper, I think the current manuscript requires more consideration and fine-tuning before it can reach its final stage. At this point, there seems to be a lack of important details that prevent me from fully gauging the paper’s findings and claims. Generally: - There were too many missing details (for example, what is the distribution of people with ‘free off speech’ attitudes? What is the correlation of the chosen scale item in the breadth-of-posts study?). On a minor note, many important points are relegated to the appendix. - Certain researcher choices and experiment design choices were not justified (for example, why were these particular scales used?) - The explanation of the creation of the breadth-of-posts was confusing. How accurate was the classification of AAE dialect and vulgarity? - The toxicity experiment was intriguing but there was too little space to be meaningful. More concretely, - With regard to terminology and concepts, toxicity and hate speech may be related but are not the same thing. The instructions to the annotators seem to conflate both. The paper also doesn’t present a concrete definition of either. While it might seem redundant or trivial, the wording to annotators plays an important role and can confound the results presented here. - Why were the particular scales chosen for obtaining attitudes? Particularly, for empathy there are several scale items [1], so why choose the Interpersonal Reactivity Index? - What was the distribution of the annotator’s background with respect to the attitudes? For example, if there are too few ‘free of speech’ annotators, then the results shown in Table 3, 4, etc are underpowered. - What were the correlations of the chosen attitudinal scale item for the breadth-of-posts study with the toxicity in the breadth-of-workers study? - How accurate are the automated classification in the breadth-of-posts experiment, i.e., how well does the states technique differentiate identity vs non-identity vulgarity or AAE language for that particular dataset. Particularly, how can it be ascertained whether the n-word was used as a reclaimed slur or not? - In that line, Section 6 discusses perceptions of vulgarity, but there are too many confounds here. Using b*tch in a sentence can be an indication of vulgarity and toxicity (due to sexism). - In my opinion, the perspective API experiment was interesting but rather shallow. My suggestion would be to follow up on it in more detail in a new paper rather than include it in this one. The newly created space could be used to enter the missing details mentioned in the review. - Finally, given that the paper notes that MTurk tends to be predominantly liberal and the authors (commendably) took several steps to ensure greater participation from conservatives, I was wondering if ‘typical’ hate speech datasets are annotated by more homogenous annotators compared to the sample in this paper. What could be the implications of this? Do this paper's findings then hold for existing hate speech datasets? Besides these, I also note some ethical issues in the ‘Ethical Concerns’ section. To conclude, while my rating might seem quite harsh, I believe this work has great potential and I hope to see it enriched with the required experimental details. References: [1] Gerdes, Karen E., Cynthia A. Lietz, and Elizabeth A. Segal. " Measuring empathy in the 21st century: Development of an empathy index rooted in social cognitive neuroscience and social justice." Social Work Research 35, no. 2 (2011): 83-93.	- There were too many missing details (for example, what is the distribution of people with ‘free off speech’ attitudes? What is the correlation of the chosen scale item in the breadth-of-posts study?). On a minor note, many important points are relegated to the appendix.
ICLR_2022_2323	ICLR_2022	Weakness: 1. The literature review is inaccurate, and connections to prior works are not sufficiently discussed. To be more specific, there are three connections, (i) the connection of (1) to prior works on multivariate unlabeled sensing (MUS), (ii) the connection of (1) to prior works in unlabeled sensing (US), and (iii) the connection of the paper to (Yao et al., 2021). (i) In the paper, the authors discussed this connection (i). However, the experiments shown in Figure 2 do not actually use the MUS algorithm of (Zhang & Li, 2020) to solve (1); instead the algorithm is used to solve the missing entries case. This seems to be an unfair comparison as MUS algorithms are not designed to handle missing entries. Did the authors run matrix completion prior to applying the algorithm of (Zhang & Li, 2020)? Also, the algorithm of (Zhang & Li, 2020) is expected to fail in the case of dense permutation. (ii) Similar to (i), the methods for unlabeled sensing (US) can also be applied to solve (1), using one column of B_0 at a time. There is an obvious advantage because some of the US methods can handle arbitrary permutations (sparse or dense), and they are immune to initialization. In fact, these methods were used in (Yao et al., 2021) for solving more general versions of (1) where each column of B has undergone arbitrary and usually different permutations; moreover, this can be applied to the d-correspondence problem of the paper. I kindly wish the authors consider incoporating discussions and reviews on those methods. (iii) Finally, the review on (Yao et al., 2021) is not very accurate. The framework of (Yao et al., 2021), when applied to (1), means that the subspace that contains the columns of A and B is given (when generating synthetic data the authors assume that A and B come from the same subspace). Thus the first subspace-estimation step in the pipeline of (Yao et al., 2021) is automatically done; the subspace is just the column space of A. As a result, the method of (Yao et al., 2021) can handle the situation where the rows of B are densely shuffled, as discussed above in (ii). Also, (Yao et al., 2021) did not consider only "a single unknown correspondence". In fact, (Yao et al., 2021) does not utilize the prior knowledge that each column of B is permuted by the same permutation (which is the case of (1)), instead it assumes every column of B is arbitrarily shuffled. Thus it is a more general situation of (1) and of the d-correspondence problem. Finally, (Yao et al., 2021) discusses theoretical aspects of (1) with missing entries, while an algorithm for this is missing until the present work. 2. In several places the claims of the paper are not very rigorous. For example, (i) Problem (15) can be solved via linear assignment algorithms to global optimality, why do the authors claim that "it is likely to fall into an undesirable local solution"? Also I did not find a comparison of the proposed approach with linear assignment algorithms. (ii) Problem (16) seems to be "strictly convex", not "strongly convex". Its Hessian has positive eigenvalues everywhere but the minimum eigenvalue is not lower bounded by some positive constant. This is my feeling though, as in the situation of logistic regression, please verify this. (iii) The Sinkhorn algorithm seems to use O(n^2) time per iteration, as in (17) there is a term C(hat{M_B}), which needs O(n^2) time to be computed. Experiments show that the algorithm needs > 1000 iterations to converge. Hence, in the regime where n << 1000 the algorithm might take much more time than O(n^2) (this is the regime considered in the experiments). Also I did not see any report on running times. Thus I feel uncomfortable to see the author claim in Section 5 that "we propose a highly efficient algorithm". 3. Even though an error bound is derived in Theorem 1 for the nuclear norm minimization problem, there is no guarantee of success on the alternating minimization proposal. Moreover, the algorithm requires several parameters to tune, and is sensitive to initialization. As a result, the algorithm has very lage variance, as shown in Figure 3 and Table 1. Questions: 1. In (3) the last term r+H(pi_P) and C(pi_P) is very interesting. Could you provide some intuition how it shows up, and in particular give an example? 2. I find Assumption 1 not very intuitive; and it is unclear to me why "otherwise the influence of the permutation will be less significant". Is it that the unknown permutation is less harmful if the magnitudes of A and B are close? 3. Solving the nuclear norm minimization program seems to be NP-hard as it involves optimization over permutation matrices and a complicated objective. Is there any hardness result for this problem? Suggestions: The following experiments might be useful. 1. Sensitivity to permutation sparsity: As shown in the literature of unlabeled sensing, the alternating minimization of (Abid et al., 2017) works well if the data are sparsely permuted. This might also apply to the proposed alternating minimization algorithm here. 2. Sensitivity to initialization: One could present the performance as a function of the distance of initialization M^0 to the ground-truth M^. That is for varying distance c (say from 0.01:0.01:0.1), randomly sample a matrix M^0 so that M^0 - M^ _F < c as initialization, and report the performance accordingly. One would expect that the mean error and variance increases as the quality of initialization decreases. 3. Sensitivity to other hyper-parameters. Minor Comments on language usage: (for example) 1. "we typically considers" in the above of (7) 2. "two permutation" in the above of Theorem 1 3. "until converge" in the above of (14) 4. ...... Please proofread the paper and fix all language problems.	2. Sensitivity to initialization: One could present the performance as a function of the distance of initialization M^0 to the ground-truth M^. That is for varying distance c (say from 0.01:0.01:0.1), randomly sample a matrix M^0 so that M^0 - M^ _F < c as initialization, and report the performance accordingly. One would expect that the mean error and variance increases as the quality of initialization decreases.
ICLR_2022_1923	ICLR_2022	Weakness: 1. The novelty of this paper is limited. First, the analysis of the vertex-level imbalance problem is not new, which is a reformulation of the observations in previous works [Rendle and Freudenthaler, 2014; Ding et al., 2019]. Second, the designed negative sampler uses reject sampling to increase the chance of popular items, which is similar to the proposed one in PRIS [Lian et al., 2020]. 2. The paper overclaims on its ability of debiasing sampling. The “debiased” term in the paper title is confusing. 3. The methodology detail is unclear in Sec. 4.2. The proposed design that improves sampling efficiency seems interesting but the corresponding description is hard to follow given the limited space. 4. Space complexity of the proposed VINS should also be analyzed and compared in empirical studies, given that each (u, i) corresponds to a b u f f e r u i . 5. Experiment results are not convincing enough to demonstrate the superiority of VINS on effectiveness and efficiency. - For effectiveness, the performance comparison in Table 1 is unfair. VINS sets different sample weights W u i in the training process, while most compared baselines like DNS, AOBPR, SA, PRIS set all sample weights as 1. - For efficiency, Table 2 should also include the theoretical analysis for contrast.	- For effectiveness, the performance comparison in Table 1 is unfair. VINS sets different sample weights W u i in the training process, while most compared baselines like DNS, AOBPR, SA, PRIS set all sample weights as 1.
Y4iaDU4yMi	ICLR_2025	- The paper's presentation is difficult to follow, with numerous typos and inconsistencies in notation. For example: - Line 84, "In summery" -> "In summary". - In Figure 1, "LLaVA as dicision model" -> "LLaVA as decision model." - Line 215, "donate" should be "denote"; additionally, $\pi_{ref}$ is duplicated. - The definitions of subscripts and superscripts for action (i.e., $a_t^1$ and $a_t^2$) in line 245 and in Equations (4), (6), (7), (8), and (9) are inconsistent. - Line 213 references the tuple with $o_t$, but it is unclear where $s_{1 \sim t-1}$ originates. - The authors should include a background section to introduce the basic RL framework, including elements of the MDP, trajectories, and policy, to clarify the RL context being considered. Without this, it is difficult to follow the subsequent sections. Additionally, a brief overview of the original DPO algorithm should be provided so that modifications proposed in the methods section are clearly distinguishable. - In Section 3.1, the authors state that the VLM is used as a planner; however, it is unclear how the plan is generated. It appears that the VLM functions directly as a policy, outputting final actions to step into the environment, as illustrated in Figure 1. Thus, it may be misleading to frame the proposed method as a "re-planning framework" (line 197). Can author clarify this point? - What type of action space does the paper consider? Is it continuous or discrete? If it is discrete, how is the MSE calculated in Eq. (7)? - In line 201, what does "well-fine-tuned model" refer to? Is this the VLM fine-tuned by the proposed method? - Throughout the paper, what does $\tau_t^{t-1}$ represent?	- The authors should include a background section to introduce the basic RL framework, including elements of the MDP, trajectories, and policy, to clarify the RL context being considered. Without this, it is difficult to follow the subsequent sections. Additionally, a brief overview of the original DPO algorithm should be provided so that modifications proposed in the methods section are clearly distinguishable.
NIPS_2022_389	NIPS_2022	1). Technically speaking, the contribution of this work is incremental. The proposed pipeline is not that impressive or novel; rather, it seems to be a pack of tricks to improve defense evaluation. 2). Although IoFA is well supported by cited works and described failures, its introduction lacks practical cases, where Figures 1 and 2 do not provide example failures and thus do not lead to a better understanding. 3). The reported experimental results appear to evidence the proposed methods, while there is a missing regarding the case analysis and further studies.	1). Technically speaking, the contribution of this work is incremental. The proposed pipeline is not that impressive or novel; rather, it seems to be a pack of tricks to improve defense evaluation.
ZPwX1FL4yp	ICLR_2025	1.The application of gyro-structures on SPD manifolds and correlation matrices is indeed novel, but the paper does not clearly articulate the theoretical significance or unique advantages of using Power-Euclidean (PE) geometry over existing approaches like Affine-Invariant (AI) or Log-Euclidean (LE) methods. The work seems incremental without providing substantial theoretical or empirical evidence that PE geometry offers practical improvements beyond computational convenience. Especially, while gyro-structures are presented as an extension to non-Euclidean spaces, the paper does not establish a strong need or motivation for this approach within the broader context of machine learning or geometry-based learning. It lacks a thorough discussion on why gyro-structures would fundamentally enhance SPD or correlation matrix-based learning in a way that current methods do not. 2.Some key theoretical concepts and mathematical operations, such as those in gyrovector space theory and correlation matrix manifold construction, are highly technical and lack intuitive explanations. Additional clarification or simplified summaries would improve accessibility for readers unfamiliar with advanced Riemannian geometry. 3.On the experiments part, the related discussion lacks interpretive insights that would elucidate why the proposed gyro-structures outperform existing methods. In addition, while the paper compares its methods against SPD-based models and a few gyro-structure-based approaches, it lacks comparison with other state-of-the-art methods that might not rely on gyro-structures. This omission makes it unclear whether the proposed approach actually outperforms simpler or more commonly used techniques in manifold-based learning.	3.On the experiments part, the related discussion lacks interpretive insights that would elucidate why the proposed gyro-structures outperform existing methods. In addition, while the paper compares its methods against SPD-based models and a few gyro-structure-based approaches, it lacks comparison with other state-of-the-art methods that might not rely on gyro-structures. This omission makes it unclear whether the proposed approach actually outperforms simpler or more commonly used techniques in manifold-based learning.
5BoXZXTJvL	ICLR_2024	1. The novelty of this method appears somewhat constrained. Utilizing the first-order gradient for determining parameter importance is a common approach in pruning techniques applied to CNN, BERT, and ViT. This technique is well-established within the realm of model pruning. Considering in some instances this method even falls short of those achieved by SparseGPT (e.g., 2:4 for LLaMA-1 and LLaMA-2), I cannot say the first-order gradient in pruning LLMs might be a major contribution. 2. This paper lacks experiments on different LLM families. Conducting trials with models like OPT, BLOOM, or other alternatives could provide valuable insights into the method's applicability and generalizability across various LLM families. 3. The paper doesn't provide details regarding the latency of the pruned model. In a study centered on LLM compression, including latency metrics is crucial since such information is highly important to the readers to understand the efficiency of the pruned model.	2. This paper lacks experiments on different LLM families. Conducting trials with models like OPT, BLOOM, or other alternatives could provide valuable insights into the method's applicability and generalizability across various LLM families.
ICLR_2021_2846	ICLR_2021	Weakness: There are some concerns authors should further address: 1)The transductive inference stage is essentially an ensemble of a serial of models. Especially, the proposed data perturbation can be considered as a common data augmentation. What if such an ensemble is applied to the existing transductive methods? And whether the flipping already is adopted in the data augmentation before the inputs fed to the network? 2)During meta-training, only the selected single path is used in one transductive step, what about the performance of optimizing all paths simultaneously? Given during inference all paths are utilized. 3)What about the performance of MCT (pair + instance)? 4)Why the results of Table 6 is not aligned with Table 1 (MCT-pair)? Also what about the ablation studies of MCT without the adaptive metrics. 5)Though this is not necessary, I'm curious about the performance of the SOTA method (e.g. LST) combined with the adaptive metric.	4)Why the results of Table 6 is not aligned with Table 1 (MCT-pair)? Also what about the ablation studies of MCT without the adaptive metrics.
ACL_2017_108_review	ACL_2017	The problem itself is not really well motivated. Why is it important to detect China as an entity within the entity Bank of China, to stay with the example in the introduction? I do see a point for crossing entities but what is the use case for nested entities? This could be much more motivated to make the reader interested. As for the approach itself, some important details are missing in my opinion: What is the decision criterion to include an edge or not? In lines 229--233 several different options for the I^k_t nodes are mentioned but it is never clarified which edges should be present! As for the empirical evaluation, the achieved results are better than some previous approaches but not really by a large margin. I would not really call the slight improvements as "outperformed" as is done in the paper. What is the effect size? Does it really matter to some user that there is some improvement of two percentage points in F_1? What is the actual effect one can observe? How many "important" entities are discovered, that have not been discovered by previous methods? Furthermore, what performance would some simplistic dictionary-based method achieve that could also be used to find overlapping things? And in a similar direction: what would some commercial system like Google's NLP cloud that should also be able to detect and link entities would have achieved on the datasets. Just to put the results also into contrast of existing "commercial" systems. As for the result discussion, I would have liked to see some more emphasis on actual crossing entities. How is the performance there? This in my opinion is the more interesting subset of overlapping entities than the nested ones. How many more crossing entities are detected than were possible before? Which ones were missed and maybe why? Is the performance improvement due to better nested detection only or also detecting crossing entities? Some general error discussion comparing errors made by the suggested system and previous ones would also strengthen that part. General Discussion: I like the problems related to named entity recognition and see a point for recognizing crossing entities. However, why is one interested in nested entities? The paper at hand does not really motivate the scenario and also sheds no light on that point in the evaluation. Discussing errors and maybe advantages with some example cases and an emphasis on the results on crossing entities compared to other approaches would possibly have convinced me more. So, I am only lukewarm about the paper with maybe a slight tendency to rejection. It just seems yet another try without really emphasizing the in my opinion important question of crossing entities. Minor remarks: - first mention of multigraph: some readers may benefit if the notion of a multigraph would get a short description - previously noted by ... many previous: sounds a little odd - Solving this task: which one? - e.g.: why in italics? - time linear in n: when n is sentence length, does it really matter whether it is linear or cubic? - spurious structures: in the introduction it is not clear, what is meant - regarded as _a_ chunk - NP chunking: noun phrase chunking? - Since they set: who? - pervious -> previous - of Lu and Roth~(2015) - the following five types: in sentences with no large numbers, spell out the small ones, please - types of states: what is a state in a (hyper-)graph? later state seems to be used analogous to node?! - I would place commas after the enumeration items at the end of page 2 and a period after the last one - what are child nodes in a hypergraph? - in Figure 2 it was not obvious at first glance why this is a hypergraph. colors are not visible in b/w printing. why are some nodes/edges in gray. it is also not obvious how the highlighted edges were selected and why the others are in gray ... - why should both entities be detected in the example of Figure 2? what is the difference to "just" knowing the long one? - denoting ...: sometimes in brackets, sometimes not ... why? - please place footnotes not directly in front of a punctuation mark but afterwards - footnote 2: due to the missing edge: how determined that this one should be missing? - on whether the separator defines ...: how determined? - in _the_ mention hypergraph - last paragraph before 4.1: to represent the entity separator CS: how is the CS-edge chosen algorithmically here? - comma after Equation 1? - to find out: sounds a little odd here - we extract entities_._\footnote - we make two: sounds odd; we conduct or something like that? - nested vs. crossing remark in footnote 3: why is this good? why not favor crossing? examples to clarify? - the combination of states alone do_es_ not? - the simple first order assumption: that is what? - In _the_ previous section - we see that our model: demonstrated? have shown? - used in this experiments: these - each of these distinct interpretation_s_ - published _on_ their website - The statistics of each dataset _are_ shown - allows us to use to make use: omit "to use" - tried to follow as close ... : tried to use the features suggested in previous works as close as possible? - Following (Lu and Roth, 2015): please do not use references as nouns: Following Lu and Roth (2015) - using _the_ BILOU scheme - highlighted in bold: what about the effect size? - significantly better: in what sense? effect size? - In GENIA dataset: On the GENIA dataset - outperforms by about 0.4 point_s_: I would not call that "outperform" - that _the_ GENIA dataset - this low recall: which one? - due to _an_ insufficient - Table 5: all F_1 scores seems rather similar to me ... again, "outperform" seems a bit of a stretch here ... - is more confident: why does this increase recall? - converge _than_ the mention hypergraph - References: some paper titles are lowercased, others not, why?	- first mention of multigraph: some readers may benefit if the notion of a multigraph would get a short description - previously noted by ... many previous: sounds a little odd - Solving this task: which one?
NIPS_2019_1397	NIPS_2019	weakness of the manuscript. Clarity: The manuscript is well-written in general. It does a good job in explaining many results and subtle points (e.g., blessing of dimensionality). On the other hand, I think there is still room for improvement in the structure of the manuscript. The methodology seems fully explainable by Theorem 2.2. Therefore, Theorem 2.1 doesn't seem necessary in the main paper, and can be move to the supplement as a lemma to save space. Furthermore, a few important results could be moved from the supplement back to the main paper (e.g., Algorithm 1 and Table 2). Originality: The main results seem innovative to me in general. Although optimizing information-theoretic objective functions is not new, I find the new objective function adequately novel, especially in the treatment of the Q_i's in relation to TC(Z\|X_i). Relevant lines of research are also summarized well in the related work section. Significance: The proposed methodology has many favorable features, including low computational complexity, good performance under (near) modular latent factor models, and blessing of dimensionality. I believe these will make the new method very attractive to the community. Moreover, the formulation of the objective function itself would also be of great theoretical interest. Overall, I think the manuscript would make a fairly significant contribution. Itemized comments: 1. The number of latent factors m is assumed to be constant throughout the paper. I wonder if that's necessary. The blessing of dimensionality still seems to hold if m increases slowly with p, and computational complexity can be still advantageous compared to GLASSO. 2. Line 125: For completeness, please state the final objective function (empirical version of (3)) as a function of X_i and the parameters. 3. Section 4.1: The simulation is conducted under a joint Gaussian model. Therefore, ICA should be identical with PCA, and can be removed from the comparisons. Indeed, the ICA curve is almost identical with the PCA curve in Figure 2. 4. In the covariance estimation experiments, negative log likelihood under Gaussian model is used as the performance metric for both stock market data and OpenML datasets. This seems unreasonable since the real data in the experiment may not be Gaussian. For example, there is extensive evidence that stock returns are not Gaussian. Gaussian likelihood also seems unfair as a performance metric, since it may favor methods derived under Gaussian assumptions, like the proposed method. For comparing the results under these real datasets, it might be better to focus on interpretability, or indirect metrics (e.g., portfolio performance for stock return data). 5. The equation below Line 412: the p(z) factor should be removed in the expression for p(x\|z). 6. Line 429: It seems we don't need Gaussian assumption to obtain Cov(Z_j, Z_k \| X_i) = 0. 7. Line 480: Why do we need to combine with law of total variance to obtain Cov(X_i, X_{l != i} \| Z) = 0? 8. Lines 496 and 501: It seems the Z in the denominator should be p(z). 9. The equation below Line 502: I think the '+' sign after \nu_j should be a '-' sign. In the definition of B under Line 503, there should be a '-' sign before \sum_{j=1}^m, and the '-' sign after \nu_j should be a '+' sign. In Line 504, we should have \nu_{X_i\|Z} = - B/(2A). Minor comments: 10. The manuscript could be more reader-friendly if the mathematical definitions for H(X), I(X;Y), TC(X), and TC(X\|Z) were state (in the supplementary material if no space in the main article). References to these are necessary when following the proofs/derivations. 11. Line 208: black -> block 12. Line 242: 50 real-world datasets -> 51 real-world datasets (according to Line 260 and Table 2) 13. References [7, 25, 29]: gaussian -> Gaussian Update: Thanks to the authors' for the response. A couple minor comments: - Regarding the empirical version of the objective (3), it might be appropriate to put it in the supplementary materials. - Regarding the Gaussian evaluation metric, I think it would be helpful to include the comments as a note in the paper.	50 real-world datasets -> 51 real-world datasets (according to Line 260 and Table 2) 13. References [7, 25, 29]: gaussian -> Gaussian Update: Thanks to the authors' for the response. A couple minor comments:
xNn2nq5kiy	ICLR_2024	* The plan-based method requires manually designing a plan based on the ground truth in advance, which is unrealistic in real-world scenarios. The learned plan methods are not comparable to the methods with pre-defined plans based on Table 2. It indicates that the proposed method may be difficult to generalize to a new dataset without the ground truth summary. * The novelty of the proposed method is limited. The most effective part is the manually designed plan. Based on that, they should also discuss some plan-based /outline-based prompt studies, such as [1-3]. * Some experimental details are missing. For example, * The detailed information of the proposed new data sets. For example, the size, average document length, average summary length, average citation number, training/validation/testing split, and so on. * How to choose the X (sentence number) and Y (words) in plan-based methods? * What generation configuration is used in LLaMA-2, ChatGPT-3.5, and GPT-4? For example, the greedy decoding or the sampling with temperature. * How was the human evaluation (In Section 5) conducted? The number of annotators, the inner agreement among annotators, the average compensation, the working hours, and the procedure of annotation should be described in detail. * How are Avg Rating, Avg Win Rate, and Coverage in Table 8 calculated? [1] Re3: Generating Longer Stories With Recursive Reprompting and Revision [2] Plan-and-Solve Prompting: Improving Zero-Shot Chain-of-Thought Reasoning by Large Language Models [3] Self-planning Code Generation with Large Language Models	* The plan-based method requires manually designing a plan based on the ground truth in advance, which is unrealistic in real-world scenarios. The learned plan methods are not comparable to the methods with pre-defined plans based on Table 2. It indicates that the proposed method may be difficult to generalize to a new dataset without the ground truth summary.
bIlnpVM4bc	ICLR_2025	- The main contribution of combining attention with other linear mechanisms is not novel, and, as noted in the paper, a lot of alternatives exist. - A comprehensive benchmarking against existing alternatives is lacking. Comparisons are only made to their proposed variants and Sliding Window Attention in fair setups. A thorough comparison with other models listed in Appendix A (such as MEGA, adapted to Mamba) would strengthen the findings. Additionally, selected architectures are evaluated on a very small scale and only measured by perplexity. While some models achieve lower perplexity, this alone may not suffice to establish superiority (e.g., in H3 by Dao et al., 2022b, lower perplexity is reported against transformer baselines). - Results on common benchmarks are somewhat misleading. The paper aims to showcase the architecture’s strengths, yet comparisons are often made against models trained on different data distributions, which weakens the robustness of the conclusions. - Conclusions on long-context handling remain vague, although this should be a key advantage over transformers. It would be helpful to include dataset statistics (average, median, min, max lengths) to clarify context length relevance. - The only substantial long-context experiment, the summarization task, should be included in the main paper, with clearer discussion and analysis. - Section 4, “Analysis,” could benefit from clearer motivation. Some explored dimensions may appear intuitive (e.g., l. 444, where SWA is shown to outperform full attention on larger sequence lengths than those used in training), which might limit the novelty of the findings. Other questions seems a bit unrelated to the paper topics (see Questions). - Length extrapolation, a key aspect of the paper, is barely motivated or discussed in relation to prior work. - The paper overall feels somewhat unstructured and difficult to follow. Tables present different baselines inconsistently, and messages regarding architectural advantages are interleaved with comments on training data quality (l. 229). The evaluation setup lacks consistency (performance is sometimes assessed on real benchmarks, other times by perplexity), and the rationale behind baseline choices or research questions is insufficiently explained.	- The main contribution of combining attention with other linear mechanisms is not novel, and, as noted in the paper, a lot of alternatives exist.
NIPS_2020_1274	NIPS_2020	- It would be helpful if the paper’s definition of “decentralized” is more explicitly stated in the paper, instead of in a footnote. Other ways of defining “decentralized” is where agents do not have access to the global state and actions of other agents during both training and execution which LIO seems to do. - Systematically studying the impact of the cost of incentivization on performance would have been a helpful analysis (e.g., for various values of \alpha, what are the reward incentives each agent receives, and what is the collective return?). It seems like roles between “winners” and “cooperators” emerge because the cost to reward the other agent becomes high for the cooperators. If this cost were lower, it seems like roles would be less distinguished, causing the collective return to be much lower. - In Figure 5d, more explanation as to why the Winner receives about the same incentive as the Cooperator to pull the lever would be helpful; it doesn’t match how the plot is described on lines 286-287.	- Systematically studying the impact of the cost of incentivization on performance would have been a helpful analysis (e.g., for various values of \alpha, what are the reward incentives each agent receives, and what is the collective return?). It seems like roles between “winners” and “cooperators” emerge because the cost to reward the other agent becomes high for the cooperators. If this cost were lower, it seems like roles would be less distinguished, causing the collective return to be much lower.
NIPS_2019_1377	NIPS_2019	- The proof works only under the assumption that the corresponding RNN is contractive, i.e. has no diverging directions in its eigenspace. As the authors point out (line #127), for expansive RNN there will usually be no corresponding URNN. While this is true, I think it still imposes a strong limitation a priori on the classes of problems that could be computed by an URNN. For instance chaotic attractors with at least one diverging eigendirection are ruled out to begin with. I think this needs further discussion. For instance, could URNN/ contractive RNN still efficiently solve some of the classical long-term RNN benchmarks, like the multiplication problem? Minor stuff: - Statement on line 134: Only true for standard sigmoid [1+exp(-x)]^-1, depends on max. slope - Theorem 4.1: Would be useful to elaborate a bit more in the main text why this holds (intuitively, since the RNN unlike the URNN will converge to the nearest FP). - line 199: The difference is not fundamental but only for the specific class of smooth (sigmoid) and non-smooth (ReLU) activation functions considered I think? Moreover: Is smoothness the crucial difference at all, or rather the fact that sigmoid is truly contractive while ReLU is just non-expansive? - line 223-245: Are URNN at all practical given the costly requirement to enforce the unitary matrix after each iteration?	- line 223-245: Are URNN at all practical given the costly requirement to enforce the unitary matrix after each iteration?
9RugvdmIBa	EMNLP_2023	1. Such strategy requires extra parallel data, which might not exist in many datasets/tasks especially during the pre-training stage. The authors did not consider such cases to propose some cheap ways to acquire such parallel data. Also, utilizing the parallel data for training increase the size of context window, which require larger context window for models and might be expensive. 2. The question answering requires the template mapping to transform the question into a masked statement, which might cause the poor generalization to questions that are not 'Wh-types'/transformable.	2. The question answering requires the template mapping to transform the question into a masked statement, which might cause the poor generalization to questions that are not 'Wh-types'/transformable.
NIPS_2016_117	NIPS_2016	weakness of this work is impact. The idea of "direct feedback alignment" follows fairly straightforwardly from the original FA alignment work. Its notable that it is useful in training very deep networks (e.g. 100 layers) but its not clear that this results in an advantage for function approximation (the error rate is higher for these deep networks). If the authors could demonstrate that DFA allows one to train and make use of such deep networks where BP and FA struggle on a larger dataset this would significantly enhance the impact of the paper. In terms of biological understanding, FA seems more supported by biological observations (which typically show reciprocal forward and backward connections between hierarchical brain areas, not direct connections back from one region to all others as might be expected in DFA). The paper doesn't provide support for their claim, in the final paragraph, that DFA is more biologically plausible than FA. Minor issues: - A few typos, there is no line numbers in the draft so I haven't itemized them. - Table 1, 2, 3 the legends should be longer and clarify whether the numbers are % errors, or % correct (MNIST and CIFAR respectively presumably). - Figure 2 right. I found it difficult to distinguish between the different curves. Maybe make use of styles (e.g. dashed lines) or add color. - Figure 3 is very hard to read anything on the figure. - I think this manuscript is not following the NIPS style. The citations are not by number and there are no line numbers or an "Anonymous Author" placeholder. - I might be helpful to quantify and clarify the claim "ReLU does not work very well in very deep or in convolutional networks." ReLUs were used in the AlexNet paper which, at the time, was considered deep and makes use of convolution (with pooling rather than ReLUs for the convolutional layers).	- Figure 3 is very hard to read anything on the figure.
ICLR_2023_3923	ICLR_2023	Weakness: 1: The paper focus over the metric learning approach of meta-learning, what about the optimization-based model e.g. MAML [a], Implicit-MAML [b] etc?. How the model will behave over these approaches? Does the same analysis be correct for other meta-learning model? 2: The base model is implemented based on ProtoNet (Deleu et al., 2019) with default parameters given by (Medina et al., 2020). How we can ensure there hyperparameters are optimal? 3: For the domain invariant auxiliary learning, “treat each image as its own class to form the support” how it is a valid labelling? It may be a wrong class assignment, then the result may be worse than using this, but the model works. I cannot understand the proper intuition, could you please provide the detail intuition? 4: Is it possible to add some optimization based meta-learning approach in the Table-1? like MAML/implicit-MAML? 5: What is the size of auxiliary data? [a] Model-Agnostic Meta-Learning for Fast Adaptation of Deep Networks [b] Meta-Learning with Implicit Gradients	4: Is it possible to add some optimization based meta-learning approach in the Table-1? like MAML/implicit-MAML?
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.	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.
ICLR_2022_2791	ICLR_2022	The technical contribution of this paper is limited, which is far from a decent ICLR paper. In particular, All kinds of evaluations, i.e., single-dataset setting (most of existing person re-ID methods), cross-dataset setting [1, 2,3] and live re-id setting [4], have been discussed in previous works. This paper simply makes a systematic discussion. For cross-dataset setting, this paper only evaluates standard person re-ID methods that train on one dataset and evaluate on another, but fails to evaluate the typical cross-dataset person re-ID methods, e.g., [1, 2, 3]. For live re-ID setting, this paper does not compare with the particular live re-ID baseline [4] Though some conclusions are drawn from the experiments, the novelty is limited. For example, 1) most of person re-ID methods build on the basis of pedestrian detector (two-step method), and there are also end-to-end method that combines detection and re-ID [5]; 2) It is common that distribution bias exists between datasets. It is hard to find a standard re-ID approach and a training dataset to address the problem unless the dataset is large enough that can cover as much as scenes. 3) cross-dataset methods try to mitigate the generalization problem. [1] Hu, Yang, Dong Yi, Shengcai Liao, Zhen Lei, and Stan Z. Li. "Cross dataset person re-identification." In Asian Conference on Computer Vision, pp. 650-664. Springer, Cham, 2014. [2] Lv, Jianming, Weihang Chen, Qing Li, and Can Yang. "Unsupervised cross-dataset person re-identification by transfer learning of spatial-temporal patterns." In Proceedings of the IEEE Conference on Computer Vision and Pattern Recognition, pp. 7948-7956. 2018. [3] Li, Yu-Jhe, Ci-Siang Lin, Yan-Bo Lin, and Yu-Chiang Frank Wang. "Cross-dataset person re-identification via unsupervised pose disentanglement and adaptation." In Proceedings of the IEEE/CVF International Conference on Computer Vision, pp. 7919-7929. 2019. [4] Sumari, Felix O., Luigy Machaca, Jose Huaman, Esteban WG Clua, and Joris Guérin. "Towards practical implementations of person re-identification from full video frames." Pattern Recognition Letters 138 (2020): 513-519. [5] Xiao, Tong, Shuang Li, Bochao Wang, Liang Lin, and Xiaogang Wang. "Joint detection and identification feature learning for person search." In Proceedings of the IEEE Conference on Computer Vision and Pattern Recognition, pp. 3415-3424. 2017.	1) most of person re-ID methods build on the basis of pedestrian detector (two-step method), and there are also end-to-end method that combines detection and re-ID [5];
gp5dPMBzMH	ICLR_2024	1. Figure 3 presents EEG topography plots for both the input and output during the EEG token quantization process, leading to some ambiguity in interpretation. I would recommend the authors to elucidate this procedure in greater detail. Specifically, it would be insightful to understand whether the spatial arrangement of the EEG sensors played any role in this process. 2. The manuscript introduces BELT-2 as a progression from the prior BELT-1 model. However, the discussion and distinction between the two models are somewhat scanty, especially given their apparent similarities. It would be of immense value if the authors could elaborate on the design improvements made in BELT-2 over BELT-1. A focused discussion highlighting the specific enhancements and their contribution to the performance improvements, as showcased in Table 1 and Table 4, would add depth to the paper. 3. A few inconsistencies are observed in the formatting of the tables, which might be distracting for readers. I'd kindly suggest revisiting and refining the table presentation to ensure a consistent and polished format. 4. In Figure 4 and Section 2.4, there is a mention of utilizing the mediate layer coding as 'EEG prompts'. The concept, as presented, leaves some gaps in understanding, primarily because its introduction and visualization seem absent or not explicitly labeled in the preceding figures and method sections. It would enhance coherence and clarity if the authors could revisit Figures 2 and/or 3 and annotate the specific parts illustrating this mediate layer coding.	1. Figure 3 presents EEG topography plots for both the input and output during the EEG token quantization process, leading to some ambiguity in interpretation. I would recommend the authors to elucidate this procedure in greater detail. Specifically, it would be insightful to understand whether the spatial arrangement of the EEG sensors played any role in this process.
uSiyu6CLPh	ICLR_2025	* I suggest that the authors show a more intuitive figure to visualize the framework that includes the images and labels in the original dataset and also the corrected images. This will help the readers to gain more intuition for your method. * The authors combine two existing techniques to get the framework without innovation. The adversarial attack or correction method and the domain adaptation method used by the authors are proposed by prior work. And the adopted domain adaptation method here is a very old and simple method which is proposed eight years ago. Considering there were so many effective domain adaptation methods proposed in the recent few years, why don't you use other domain adaptation methods to further improve the performance? * In Section 3.3, the authors align the features of the weak classifier on the original dataset and the synthetic dataset. Considering that the difference between the original and the synthetic datasets is the corrected part, can we omit the correctly classified samples and only minimize the covariance difference for the adversarially corrected sample and the misclassified sample? * How do you choose the hyper-parameters such as $\lambda,\epsilon$? Does your method work robustly for other choices of hyper-parameters? If not, how do you choose them?	* The authors combine two existing techniques to get the framework without innovation. The adversarial attack or correction method and the domain adaptation method used by the authors are proposed by prior work. And the adopted domain adaptation method here is a very old and simple method which is proposed eight years ago. Considering there were so many effective domain adaptation methods proposed in the recent few years, why don't you use other domain adaptation methods to further improve the performance?
eCXfUq3RDf	EMNLP_2023	1. Very limited reproducibility - Unless the authors release their training code, dialogue dataset, as well as model checkpoints, I find it very challenging to reproduce any of the claims in this paper. I encourage the authors to attach their code and datasets via anonymous repositories in the paper submission so that reviewers may verify the claims and try out the model for themselves. 2. Very high model complexity - The proposed paper employs a mathematically and computationally complex approach as compared to the textual input method. Does the proposed method outperform sending textual inputs to a large foundation model such as LLAMA or ChatGPT? The training complexity seems too high for any practical deployment of this model. 3. Dependent on the training data - I'm unsure if 44k dialogues is sufficient to capture a wide range of user traits and personalities across different content topics. LLMs are typically trained on trillions of tokens, I do not see how 44k dialogues can capture the combinations of personalities and topics. In theory, this dataset also needs to be massive to cover varied domains. 4. The paper is hard to read and often unintuitive. The mathematical complexity must be simplified and replaced with more intuitive design and modeling choice explanations so that readers may grasp core ideas faster.	3. Dependent on the training data - I'm unsure if 44k dialogues is sufficient to capture a wide range of user traits and personalities across different content topics. LLMs are typically trained on trillions of tokens, I do not see how 44k dialogues can capture the combinations of personalities and topics. In theory, this dataset also needs to be massive to cover varied domains.
NIPS_2018_914	NIPS_2018	of the paper are (i) the presentation of the proposed methodology to overcome that effect and (ii) the limitations of the proposed methods for large-scale problems, which is precisely when function approximation is required the most. While the intuition behind the two proposed algorithms is clear (to keep track of partitions of the parameter space that are consistent in successive applications of the Bellman operator), I think the authors could have formulated their idea in a more clear way, for example, using tools from Constraint Satisfaction Problems (CSPs) literature. I have the following concerns regarding both algorithms: - the authors leverage the complexity of checking on the Witness oracle, which is "polynomial time" in the tabular case. This feels like not addressing the problem in a direct way. - the required implicit call to the Witness oracle is confusing. - what happens if the policy class is not realizable? I guess the algorithm converges to an \empty partition, but that is not the optimal policy. minor: line 100 : "a2 always moves from s1 to s4 deterministically" is not true line 333 : "A number of important direction" -> "A number of important directions" line 215 : "implict" -> "implicit" - It is hard to understand the figure where all methods are compared. I suggest to move the figure to the appendix and keep a figure with less curves. - I suggest to change the name of partition function to partition value. [I am satisfied with the rebuttal and I have increased my score after the discussion]	- the required implicit call to the Witness oracle is confusing.
n7n8McETXw	ICLR_2025	1. Limitations in Model Complexity: The paper primarily analyzes a single-head attention Transformer, which may not encapsulate the full complexity and performance characteristics of multi-layer and multi-head attention models. The validation was confined to binary classification tasks, thereby restricting the generalizability of the theoretical findings. 2. Formula Accuracy: The paper requires a meticulous review of its mathematical expressions. For instance, in Example 1, the function should be denoted as \( f_2(\mu_2') = \mu_1' \) instead of \( f_1(\mu_2') = \mu_1' \), and the second matrix \( A_1^f \) should be corrected to \( A_2^f \). It is essential to verify all formulas throughout the text to ensure accuracy. 3. Theorem Validity and Clarification: The theorems presented in the article should be scrutinized for their validity, particularly the sections that substantiate reasoning, as they may induce some ambiguity. Reading the appendix is mandatory for a comprehensive understanding of the article; otherwise, it might lead to misconceptions. 4. Originality Concerns: The article's reasoning and writing logic bear similarities to those found in "How Do Nonlinear Transformers Learn and Generalize in In-Context Learning." It raises the question of whether this work is merely an extension of the previous study or if it introduces novel contributions.	4. Originality Concerns: The article's reasoning and writing logic bear similarities to those found in "How Do Nonlinear Transformers Learn and Generalize in In-Context Learning." It raises the question of whether this work is merely an extension of the previous study or if it introduces novel contributions.
NIPS_2020_471	NIPS_2020	1. The descriptions in joint inference is not very clear. I cannot get how the refine process do according to Equ. 2. It would be great if the authors can clear this part during the rebuttal and polish this part in the final version. 2. I have some doubts about the definations in Table1. What's the different between anchor-based regression and the regression in RepPoints? in RetinaNet, there is also only a one-shot regression. And in ATSS, this literature has proved that the regression methods do not influence a lot. The method that directly regresses [w, h] to the center point is good enough. While RepPoints regresses distance to the location of feature maps. I think there is no obvious difference between the two methods. I hope the authors can clarify this problem. If not, the motivations here is not solid enough. 3. It would be great if the authors can analyze the computational costs and inference speeds for the proposed method.	2. I have some doubts about the definations in Table1. What's the different between anchor-based regression and the regression in RepPoints? in RetinaNet, there is also only a one-shot regression. And in ATSS, this literature has proved that the regression methods do not influence a lot. The method that directly regresses [w, h] to the center point is good enough. While RepPoints regresses distance to the location of feature maps. I think there is no obvious difference between the two methods. I hope the authors can clarify this problem. If not, the motivations here is not solid enough.
5EHI2FGf1D	EMNLP_2023	- no comparison against baselines. The functionality similarity comparison study reports only accuracy across optimization levels of binaries, but no baselines are considered. This is a widely-understood binary analysis application and many papers have developed architecture-agnostic similarity comparison (or often reported as codesearch, which is a similar task). - rebuttal promises to add this evaluation - in addition, the functionality similarity comparison methodology is questionable. The authors use cosine similarity with respect to embeddings, which to me makes the experiment rather circular. In contrast, I might have expected some type of dynamic analysis, testing, or some other reasoning to establish semantic similarity between code snippets. - rebuttal addresses this point. - vulnerability discovery methodology is also questionable. The authors consider a single vulnerability at a time, and while they acknowledge and address the data imbalance issue, I am not sure about the ecological validity of such a study. Previous work has considered multiple CVEs or CWEs at a time, and report whether or not the code contains any such vulnerability. Are the authors arguing that identifying one vulnerability at a time is an intended use case? In any case, the results are difficult to interpret (or are marginal improvements at best). - addressed in rebuttal - This paper is very similar to another accepted at Usenix 2023: Can a Deep Learning Model for One Architecture Be Used for Others? Retargeted-Architecture Binary Code Analysis. In comparison to that paper, I do not quite understand the novelty here, except perhaps for a slightly different evaluation/application domain. I certainly acknowledge that this submission was made slightly before the Usenix 2023 proceedings were made available, but I would still want to understand how this differs given the overall similarity in idea (building embeddings that help a model target a new ISA). - addressed in rebuttal - relatedly, only x86 and ARM appear to be considered in the evaluation (the authors discuss building datasets for these ISAs). There are other ISAs to consider (e.g., PPC), and validating the approach against other ISAs would be important if claiming to build models that generalize to across architectures. - author rebuttal promises a followup evaluation	- vulnerability discovery methodology is also questionable. The authors consider a single vulnerability at a time, and while they acknowledge and address the data imbalance issue, I am not sure about the ecological validity of such a study. Previous work has considered multiple CVEs or CWEs at a time, and report whether or not the code contains any such vulnerability. Are the authors arguing that identifying one vulnerability at a time is an intended use case? In any case, the results are difficult to interpret (or are marginal improvements at best).
NIPS_2021_1822	NIPS_2021	of the paper. Organization could definitely be improved and I oftentimes had a bit of a hard time following the discussed steps. But in general, I think the included background is informative and well selected. Though, I could see people having trouble understanding the state-space GP-regression when coming from the more machine-learning like perspective of function/ weight space GP-regression. Significance: I think there is definitely a significance in this work, as GP-Regression is usually a bit problematic because of the scaling, though it is still used extensively in certain areas, such as Bayesian Optimization or for modelling dynamical systems in robotics. • Background: f is a random function which describes a map e.g. f : R × R D s → R and not a function of X ∈ R N t × N s × D s as described in eq 1. At least, when one infers the inputs from the definitions of the kernel functions. • In general, the definitions are confusing and should be checked,e.g. check if f n , k = f ( X n , k ) is correct and properly define X n , k . • The operator L s is not mentioned in the text • 2.1: The description of the process f ¯ is confusing as the relationship to the original process f is established just at the end. • It would be helpful to add a bit more background on how the state space model is constructed from the kernel κ t ( ⋅ , ⋅ ) , e.g. why it induces the dimensionality d t and also describe the limitations that a finite dimensional SDE can only be established, when a suitable spectral decomposition of the kernel exist. • It should be mentioned that p ( y ∣ H f ¯ ( t n ) ) has to be chosen Gaussian, as otherwise Kalman Filtering and Smoothing and CVI is not possible. Later on in the ELBOs this is assumed anyway. • p ( u ) = N ( u ∣ 0 , K z z ) is a finite dimensional Gaussian not a Gaussian process and p(u) is not a random variable ( = not ∼ ). • The notations for the covariances, e.g. K z z are discussed in the appendix. I am fine with it; however, it should be referenced as I was confused in the beginning. • 2.2: The log is missing for the Fisher information matrix. • The acronym CVI is used in the paragraph headline before the definition. • Some figures and tables are not referenced in the text, such as figure 1. • 3.1: In line 173 the integration should be carried over f ¯ and not s , I guess? • I had a bit of a hard time establishing the connection E p ( f ) [ N ( Y ~ ∣ f , V ~ ) ] = p ( Y ~ ) which is the whole point why one part of the ELBO can be calculated using the Kalman filter. Adding this to a sentence to the text would have helped me a lot. • One question I had was that for computing the ELBO the matrix exponential is needed. When backpropagating the gradient for the hyper parameters, is this efficient? As I am used to using the adjoint method for computing gradients of the (linear) differential equation. • Reference to Appendix for the RMSE and NLPD metrics is missing.	• It should be mentioned that p ( y ∣ H f ¯ ( t n ) ) has to be chosen Gaussian, as otherwise Kalman Filtering and Smoothing and CVI is not possible. Later on in the ELBOs this is assumed anyway.
ICLR_2021_343	ICLR_2021	1. This paper is not well-organized and many parts are misleading. For example, above Eq.3, the author assumes P_{G_{0}} = P_{D}. Does the author take the samples generated by the root generator as the authentic dataset? However, in Section 2 above Eq. 4, the author claims that the authentic data does not belong to any generator. 2. In Eq.4, the key-dependent generator is obtained via adding perturbation to the output of the root model. This setting may be troublesome as :1. These generators are not actually trained. This is different from the problem which this paper tempt to solve. 2. No adversarial loss to guarantee the perturbed data being similar to the authentic data. 2. How to distinguish the samples from different generators. 3. Since Eq.4 is closely related to adversarial attack, the authors are supposed to discuss their connections in the related works. 4. The name of ‘decentralized attribution’ is misleading. Decentralized models are something like federated learning, where a ‘center’ model grasps information from ‘decentralized models’. However, the presented work is not related to such decentralization. 5. Typos: regarding the adversarial generative models ->regarding to the adversarial generative models; along the keys->along with the keys.	2. No adversarial loss to guarantee the perturbed data being similar to the authentic data.
ICLR_2023_4867	ICLR_2023	Encoder architecture is a 2-layer GCN. This has limited expressive power. Computation complexity and scalability are not analyzed theoretically, and the benchmarks used range from tiny (cora, citeseer) to medium graphs (ogb-arxiv). Missing graph contrastive baselines in experiments and review (see detailed feedback below). t-tests are not the best for evaluating statistical significance in this setting (see detailed feedback below). Detailed Feedback and Questions: This paper compares thoroughly with existing methods for handling noisy data but not nearly enough with contrastive graph learning baselines. There are several other baselines aside from GraphCL [1] that are not cited in the review and are not compared with the proposed approach in the experiments, See [2-4] ([1] is included in the paper but not its subsequent works). Well known GCL methods include perturbations in the edge set GRACE (Zhu et al., 2020), BGRL (Thakoor et al., 2021), GBT (Bielak et al., 2021)), centrality (GCA (Zhu et al., 2021)), diffusion matrix (MVGRL (Hassani & Khasahmadi, 2020)) and the original graph (GMI (Peng et al., 2020)) and DGI (Velickovic et al., 2019)). The proposed method is compared to MVGRL (Hassani & Khasahmadi, 2020) but it is not clear why it is not compared to the others. If there is a good reason why a direct comparison does not apply that can be described in the review section or a direct experimental comparison is produced, I am willing to raise my score. 2, While there is performance improvement it in the experimental results it is often quite small. The t-tests are helpful but I think using Wilcoxon signed test would be better given small sample size. t-tests require assumptions of normality that are not explicitly justified in the paper. Do the t-tests that are close to 0.05 remain under the threshold when switching to Wilcoxon test? Are the loss terms in eq. 6 added without weights? I would assume in general they are in different scales so weighting them should improve performance. This work tackles feature and label noise. What about noise in the graph topology? I understand that given extensive hyperparameter search (Table 4) gamma_0 and xi_0 can be selected. However, it would be interesting to see how selection of these values affects performance stability. How sensitive is the algorithm to xi selection in equation 2 and gamma_k selection in equation 5? Typos: p. 1 handle an2 almost infinite” -> an p. 2 Existing Methods Handing Noisy Data" -> handLing p. 3 the attributes of each node is in” -> are p. 3 following two tasks.” -> replace .” by :” References: [1] You, Yuning, et al. “Graph contrastive learning with augmentations.” Advances in Neural Inf. Proces. Syst. 33 (2020): 5812-5823. [2] You, Yuning, et al. “Graph contrastive learning automated.” Int. Conf. Machine Learning, 2021. [3] Qiu, Jiezhong, et al. “Gcc: Graph contrastive coding for graph neural network pre-training.” Proc. ACM SIGKDD Int. Conf. Knowledge Discovery & Data Mining. 2020.	3 following two tasks.” -> replace .” by :” References: [1] You, Yuning, et al. “Graph contrastive learning with augmentations.” Advances in Neural Inf. Proces. Syst.
ICLR_2023_3291	ICLR_2023	although this paper uses formal data symbolic description for the proposed method, there is still no framework diagram to help the method understanding, which makes the algorithm of the article slightly inferior in the narration and implementation process. although this paper introduces various attack methods in detail, it does not show more attack methods in experimental comparison, such as ISSBA. as a novel attack method, the authors should give more experimental comparison and analysis of the attack. 3, the author mentioned in the paper the advantages of the algorithm can also be mentioned in the attack on high efficiency. But for this part, I don't seem to see more theoretical analysis (convergence) and related experimental proofs. I have reservations about this point. What is the main difference between the authors and ISSBA in terms of the formulation of the method? I would like the authors further to explain the contribution in conjunction with the formulas. Some Questions: 1.How is the computational efficiency of extracting the trigger? Unlike previous backdoor attack algorithms, the method needs to analyze and extract data from the entire training dataset. Does this result in exponential time growth as the dataset increases? 2. The effectiveness and problem of the algorithm are that it requires access to the entire training dataset. Have the authors considered how the algorithm should operate effectively when the training dataset is not fully perceptible? Overall: The trigger proposed in this paper is novel, but the related validation experiments are not comprehensive, and the time complexity of the computation and the efficiency of the algorithm are not clearly analyzed. In addition, I expect the authors to further elucidate the technical contribution rather than the form of the attack.	2. The effectiveness and problem of the algorithm are that it requires access to the entire training dataset. Have the authors considered how the algorithm should operate effectively when the training dataset is not fully perceptible? Overall: The trigger proposed in this paper is novel, but the related validation experiments are not comprehensive, and the time complexity of the computation and the efficiency of the algorithm are not clearly analyzed. In addition, I expect the authors to further elucidate the technical contribution rather than the form of the attack.
NIPS_2021_1078	NIPS_2021	weakness of this paper, I am concerned with the following two points: 1) The assumption for termination states of instructions are quite strong. In the general case, it is very expensive to label a large number of data manually. 2) It seems that performance and sample efficiency are sensitive to λ parameters. (Page 9, lines 310-313) I don't understand how the process of calculating the λ is done. How is λ computed from step here? (Page 8 lines 281-285) The authors explain why ELLA does not increase sample efficiency in a COMBO environment, but I don't quite understand what it means. [1] Yuri Burda et al, Exploration by Random Network Distillation, ICLR 2019 [2] Deepak Pathak et al, Curiosity-driven Exploration by Self-supervised Prediction, ICML 2017 [3] Roberta Raileanu et al, RIDE: Rewarding Impact-Driven Exploration for Procedurally-Generated Environments, ICLR 2020	1) The assumption for termination states of instructions are quite strong. In the general case, it is very expensive to label a large number of data manually.
sXErPfdA7Q	EMNLP_2023	UPDATE: The authors addressed most of my concerns however, I believe that the first and second points are still valid and should be discussed as potential limitations (i.e., there are too many confounding variables to claim that one is investigating an impact of different training methods; and the datasets might have been - and probably were - used for RLHF). UPDATE 2: the concerns were addressed by the authors to the extend it was possible with the current design. - The authors claim to investigate the effect of different training methods on the processing of discourse-level information (as one of three main experiments), however, it is questionable whether what we see is the effect of different training methods, different training data, or perhaps the data used for RLHF (rather than RLHF alone, that is it is possible that the MT datasets used in this study were used to create RLHF examples). Since the authors research black box models behind an API, I do not think we can make any claims about the effect of the training method (of which we know little) on the model's performance. - Data contamination might have influenced the evaluation - The authors employ various existing datasets. While two of these datasets do have publication date past the openAI's models' training cutoff point (made public in August 2022), this seems not to be the case for the other datasets employed in this study (including the dataset with contextual errors). It is likely that these were included in the training data of the LLMs being evaluated. Furthermore, with the RLHF models, it is also possible (and quite likely) that MT datasets published post-training were employed to create the RLHF data. For instance the WMT22 dataset was made public in August 2022, which gives companies like OpenAI plenty of time to retrieve it, reformulate it into training examples, and use for RLHF. - The authors discuss how certain methods are significantly different from others, yet no significance testing is done to support these claims. For example, in line 486 the authors write "The conversational ability of ChatGPT and GPT-4 significantly boosts translation quality and discourse awareness" -- the difference between zh->en ChatGPT (17.4 d-BLEU; 2.8/2.9 humeval) and GPT-4 (18.8 d-BLEU; 2.6/2.8 humeval) and the scores for FeedME-2 (16.1 d-BLEU; 2.2/2.3 humeval) and PPO (17.2 d-BLEU; 2.6/2.7 humeval) is minimal and it's hard to say whether it is significant without proper testing (including checking the distribution and accounting for multiple comparisons). - The main automatic method used throughout this paper is d-BLEU, which works best with multiple references, yet I believe only one is given. I understand that there are limited automatic options for document level evaluation where the sentences cannot be aligned. Some researchers used sliding windows for COMET, but that's not ideal (yet worth trying?). That is why the human evaluation is so important, and the one in this paper is lacking. - Human evaluation - many important details are missing so it is hard to judge the research design (more questions below); however what bothers me most is that the authors construct an ordinal scale with a clear cutoff point between 2 and 3 (for general quality especially), yet they present only average scores. I do believe that "5: Translation passes quality control; the overall translation is excellent (...)" minus "4: Translation passes quality control; the overall translation is very good" is not the same "one" as "3: Translation passes quality control; the overall translation is ok. (...)" minus "2: Translation does not pass quality control; the overall translation is poor. (...)". It is clear that the difference between 5 and 4 is minimal, while between 3 and 2 is much bigger. Simple average is not a proper way to analyze this data (a proper analysis would include histograms of scores, possibly a stacked bar with proportion of choices, statistical testing). - Another issue with the human evaluation is that it appears that the evaluators were asked to evaluate an entire document by assigning it one score. Note that this is a cognitively demanding and difficult task for the evaluators. The results are likely to be unreliable (please see Sheila Castilho's work on this topic). There is also no indication that the annotators were at least given some practice items. - "Discourse-aware prompts" - I am not sure what this experiment was about. It seems that the idea was to evaluated how the availability of discourse information can improve the translation, but if that is so, then all three setups did have discourse level information (hence this evaluation is impossible). The only thing this seems to be doing is checking in which way the information should be presented (one sentence at a time in a chat, all sentences at once but clearly marked, or the entire document at once without sentence boundaries).	- The authors discuss how certain methods are significantly different from others, yet no significance testing is done to support these claims. For example, in line 486 the authors write "The conversational ability of ChatGPT and GPT-4 significantly boosts translation quality and discourse awareness" -- the difference between zh->en ChatGPT (17.4 d-BLEU; 2.8/2.9 humeval) and GPT-4 (18.8 d-BLEU; 2.6/2.8 humeval) and the scores for FeedME-2 (16.1 d-BLEU; 2.2/2.3 humeval) and PPO (17.2 d-BLEU; 2.6/2.7 humeval) is minimal and it's hard to say whether it is significant without proper testing (including checking the distribution and accounting for multiple comparisons).
NIPS_2020_867	NIPS_2020	- As someone without a linguistics background, it was at times difficult for me to follow some parts of the paper. For example, it’s not clear to me why we care about the speaker payoff and listener payoff (separate from listener accuracy), rather than just a means to obtain higher accuracy --- is it important that the behavior of the speaker at test time stay close to its behavior during training? - I think more emphasis could be placed on the fact that the proposed methods require the speaker to have a model (in fact, in most of the experiments it’s an exact model) of the listener’s conditional probability p(t\|m), and vice-versa. - I would have liked more description of the Starcraft environment (potentially in an Appendix?)	- I would have liked more description of the Starcraft environment (potentially in an Appendix?)