A fundamental goal in deep learning is the characterization of trainability and generalization of neural networks as a function of their architecture and hyperparameters. In this paper, we discuss these challenging issues in the context of wide neural networks at large depths where we will see that the situation simplifies considerably. To do this, we leverage recent advances that have separately shown: (1) that in the wide network limit, random networks before training are Gaussian Processes governed by a kernel known as the Neural Network Gaussian Process (NNGP) kernel, (2) that at large depths the spectrum of the NNGP kernel simplifies considerably and becomes "weakly data-dependent", and (3) that gradient descent training of wide neural networks is described by a kernel called the Neural Tangent Kernel (NTK) that is related to the NNGP. Here we show that in the large depth limit the spectrum of the NTK simplifies in much the same way as that of the NNGP kernel. By analyzing this spectrum, we arrive at a precise characterization of trainability and a necessary condition for generalization across a range of architectures including Fully Connected Networks (FCNs) and Convolutional Neural Networks (CNNs). In particular, we find that there are large regions of hyperparameter space where networks can only memorize the training set in the sense they reach perfect training accuracy but completely fail to generalize outside the training set, in contrast with several recent results. By comparing CNNs with-and without-global average pooling, we show that CNNs without average pooling have very nearly identical learning dynamics to FCNs while CNNs with pooling contain a correction that alters its generalization performance. We perform a thorough empirical investigation of these theoretical results and finding excellent agreement on real datasets.

This paper studies the evolution of Neural Tangent Kernel (NTK) at large-depth regimes. By analyzing the conditional number and eigenvalues, they identify three phases of hyper-parameters; 1) In the chaotic phase NTK converges to an identity matrix, which is easy to train but hardly to generalize. 2) In the ordered phase NTK converges to an all-one matrix, which is hard to train but generalizes well. 3) In the critical phase the conditional number converges to a constant. Furthermore, they also analyze the influence of pooling and flattening in CNNs and identify potential regimes where pooling hurts the generalization. They conduct empirical experiments to supporting their theoretical analyses.
However, I think this paper is worth of more revisions because many theoretical analyses are unjustified. And some potential typos makes the analyses even more difficult to understand.
1) It looks to me that Eq(2) and Eq(6) are contradictory, where T already contains sigma_w and simga_b in Eq(2) but re-multiplied in eq(6).
2) The paper analyzes the dynamics by assuming the variances of inputs are q*, which is debatable. The variance q^l also evolves with the depth increases. It is unclear whether the condition number will change if you takes the evolution of q^l into considered.
3) It is unclear how Eq(9) comes directly from Eq(6), and there aren't any rigorous proofs in the Appendix. Similarly for eq(14).
4) In the paragraph below Eq(11) the paper states that \Theta* becomes an all one-matrix. However, Eq(11) states the diagonal converges to q*/(1-xi_1), but the paragraph below Eq(9) states the off-diagonal converges to q*_{ab}/(1- xi_c). Because q*=q*_{ab} as you stated nearby, do you mean xi_1 = xi_c ?
5) In the first paragraph of Section 3.3, p^l = q* and p^l=l q*.
6) In the 2nd contribution, you mentioned "eigenvector correlation", while I cannot find anywhere else introducing this.
7) The plots of Figure 1(b) should behave like convex if the kappa really evolves like x_1^l / l. However it is concave.
8) In the first experiment, you state "To confirm that the maximal feasible learning rate are ... 2/(lambda_max)". However, learning rates are never discussed in this paper. It is confusing why this experiment is useful.
Generally speaking, I think the paper needs careful revisions to support its theoretical analyses.


Deep neural networks (DNNs) have great expressive power, which can even memorize samples with wrong labels. It is vitally important to reiterate robustness and generalization in DNNs against label corruption. To this end, this paper studies the 0-1 loss, which has a monotonic relationship with empirical adversary (reweighted) risk (Hu et al., 2018). Although the 0-1 loss is robust to outliers, it is also difficult to optimize. To efficiently optimize the 0-1 loss while keeping its robust properties, we propose a very simple and efficient loss, i.e. curriculum loss (CL). Our CL is a tighter upper bound of the 0-1 loss compared with conventional summation based surrogate losses. Moreover, CL can adaptively select samples for stagewise training. As a result, our loss can be deemed as a novel perspective of curriculum sample selection strategy, which bridges a connection between curriculum learning and robust learning. Experimental results on noisy MNIST, CIFAR10 and CIFAR100 dataset validate the robustness of the proposed loss.

Summary: This paper proposes a new loss function: curriculum loss, which is a meta-loss function that we can still specify an existing surrogate loss to use this loss function. This meta-loss function guarantees to be tighter than using a traditional pointwise-sum loss function as used in the empirical risk minimization framework. Intuitively, the proposed CL loss embed the sample selection process in the objective function. The authors suggest that it is robust against label corruption because it is tighter and provided promising experimental results.
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Clarity:
The paper is well-written and easy to follow.
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Significance:
The proposed paradigm is interesting and I am convinced that it can be useful under label noise. The experiments look promising. Future work about the analysis of NPCL/CL is also interesting to consider (e.g., which surrogate loss to use, rigorous theoretical guarantee, etc.). I think the proposed method is impactful.
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Comments:
The proposed method is interesting and can give a tighter bound for any surrogate loss by using this method (CL). Moreover, the author suggested a simple extension of CL for label corruption (NPCL) and the performance is impressive. I would like to vote accept for this paper but the following point highly concerns me and I am not sure about the correctness (see the concern below). It is about the motivation not the proposed method.
Concerns about motivation:
I disagree with the original motivation of this paper. The authors used the result of Hu et al. 2018 to motivate the use of CL. To my knowledge, the main point raised by Hu et al. is as follows:
In classification, minimizing the adversarial risk yields the same solution as using the standard empirical risk. This suggests that minimizing the adversarial risk may not enhance the robustness of a classifier. Yet, it may still be useful when we consider regression (other settings but not classification). As a result, in classification, we should try other methods to make a robust classifier. Then, Hu et al. considered to utilize some kind of structural assumption to make a robust classifier. From their title: "Does Distributionally Robust Supervised Learning Give Robust Classifiers?", I think they suggested "No" as an answer and the discussion about 0-1 loss in the curriculum loss paper will be contradicted to them from the motivation perspective.
Furthermore, regarding the adversarial risk, it is not focusing on the label noise but rather the noise of the feature-label pair, i.e, perturb (x,y) adversarially within an f-divergence ball. However, in my opinion, if we randomly flip the label of the data regardless of x (as the authors and existing work did in experiments when considering label corruption: symmetric, partial, etc.), we cannot be confident to state that the f-divergence between test distribution and corrupted training distribution is small under label noise.
Another point to motivate the use of 0-1 loss that the author mentioned is when we have outliers (Masnadi-Shirazi & Vasconcelos, 2009). This makes sense and this is a famous argument to discourage the use of too steep loss functions, e.g., exponential loss. I think this motivation is fine but it is not directly related to label corruption because we do not add out-of-distribution data but rather the label noise. Furthermore, the authors did not inject any outliers in the experiments in my understanding. I think this is totally no problem because we are focusing on label noise here, but this makes the motivation about outliers less important when we are talking about label noise.
I think the most important direction both in theory and experiments about the robustness to label noise of the 0-1 loss is that 0-1 loss satisfies a "symmetric property", i.e., \ell(z)+\ell(-z) = Constant for a margin-based loss function in binary classification. Under symmetric label noise, "the minimizer of the expected symmetric noise risk (a risk that the label is corrupted by coin flipping noise) is identical to the minimizer of the clean risk (normal risk)". Although it is not empirically but the expected version, it gives a good insight about the advantage of directly minimizing 0-1 loss under label noise. This is first pointed out by
[1] Manwani et al.: Noise tolerance under risk minimization, IEEE Transactions on Cybernetics 43 (2013)
[2] Ghosh et al.: Making risk minimization tolerant to label noise Neurocomputing 160 (2015): 93-107.
([1] focused on the 0-1 loss while [2] extended it to symmetric losses.)
Then, it was extended to the multiclass loss by the following paper:
[3] Ghosh et al.: Robust loss functions under label noise for deep neural networks. AAAI2017.
The advantage of symmetric losses is also discussed in this paper that the authors already cited in the symmetric noise experiment section.
[4] van Rooyen et al.: Learning with symmetric label noise: The importance of being unhinged, NeurIPS2015
The advantage of the symmetric condition and 0-1 loss is also discussed in a more general noise scenario and more evaluation metrics:
[5] van Rooyen et. al: An average classification algorithm. arXiv:1506.01520, 2015
[6] Charoenphakdee et al.: On symmetric losses for learning from corrupted labels, ICML2019
And the following paper that was also cited in the submitted work and compared:
[7] Zhang and Sabuncu: Generalized cross-entropy loss for training deep neural networks with noisy labels, NeurIPS2018
is also inspired by the robustness of the symmetric losses (including 0-1 loss). They argued that although the symmetric loss (MAE) for multiclass proposed by Ghosh AAAI2017 is robust, it is hard to train for challenging datasets, and they try to relevate this condition while making it easier to train.  This paper outperformed [7] and I think it is clearer and better to build a story along this line.
In short, here is the key message why I think the current motivation does not feel right. When we have noisy labeled data, instead of motivating the use of 0-1 loss by suggesting that
"If we have clean labeled data, minimizing the "adversarial" ERM risk using "clean" labeled data yields the same minimizer as minimizing the "standard" ERM risk using "clean" labeled data",
I believe the story to motivate the robustness of 0-1 loss under label noise should be
"If we have noisy labeled data, minimizing the "standard" or "modified" risk using "noisy" labeled data yields the same minimizer as minimizing the "standard" ERM risk using "clean" label data"
The latter statement corresponds to the literature I suggested.
Apart from the motivation raised by the authors, as we can see from this curriculum loss paper, NPCL nicely outperformed generalized cross entropy loss in [7], which is impressive.
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Decision.
I strongly feel that motivating the noise robustness of 0-1 loss by discussing about the adversarial risk (Hu et al.) is misleading. Nevertheless, I feel the proposed method itself makes a lot of sense and I am impressed by the results. If the author can convince me that using the current motivation of the paper is suitable, I am happy to improve the score. Another way is to agree to modify the motivation part. Given the experiments were done, it is not to difficult to change the motivation of the paper. At this point, I have decided to give a weak reject.
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Questions:
1. Is it straightforward to combine NPCL with Co-teaching/Mentornet/Co-teaching+?
2. Does the traditional theory about classification-calibration (Zhang, 2004, Bartlett+, 2006) can guarantee the Bayes-optimal solution if we use NPCL?
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Minor comments:
1. Page 9: Both our NPCL and Generalized Cross Entropy(GCE) << space missing between Entropy and (
Update: I have read the rebuttal. Although I am still not fully convinced with the motivation of the paper and still doubting whether NPCL works well because of the given motivation, I still believe that the proposed NPCL should give a new perspective to deal with noisy labels. I like the idea of the paper. Thus, I change the score to Weak Accept.


Generative adversarial networks (GANs) are powerful generative models, but usually suffer from instability which may lead to poor generations. Most existing works try to alleviate this problem by focusing on stabilizing the training of the discriminator, which unfortunately ignores the robustness of both generator and discriminator. In this work, we consider the robustness of GANs and propose a novel robust method called robust generative adversarial network (RGAN). Particularly, we design a robust optimization framework where the generator and discriminator compete with each other in a worst-case setting within a small Wasserstein ball. The generator tries to map the worst input distribution (rather than a specific input distribution, typically a Gaussian distribution used in most GANs) to the real data distribution, while the discriminator attempts to distinguish the real and fake distribution with the worst perturbation. We have provided theories showing that the generalization of the new robust framework can be guaranteed. A series of experiments on CIFAR-10, STL-10 and CelebA datasets indicate that our proposed robust framework can improve consistently on four baseline GAN models. We also provide ablation analysis and visualization showing the efficacy of our method on both generator and discriminator quantitatively and qualitatively.

Summary
The present work proposes to combine GANs with adversarial training replacing the original GAN lass with a mixture of the original GAN loss and an adversarial loss that applies an adversarial perturbation to both the input image of the discriminator, and to the input noise of the generator. The resulting algorithm is called robust GAN (RGAN). Existing results of [Goodfellow et al 2014] (characterizing optimal generators and discriminators in terms of the density of the true data) are adapted to the new loss functions and generalization bounds akin to [Arora et al 2017] are proved. Extensive experiments show a small but consistent improvement over a baseline method.
Decision
The authors do a thorough job at characterizing the proposed method using both theoretical analysis and wide ranging experimental studies. My main criticism of the paper in its present form is the lack of motivation for the proposed method. Why, out of the many possible ways to impose additional regularization should one use adversarial training to regularize GANs? While it is remarkable that the experimental results seem to be improving consistently, the improvement is quite small. Similarly, while theoretical results are provided, a discussion of what they mean for the performance of RGAN is sorely lacking, leaving me unconvinced that adversarial training leads to an improvement over GANs when compared with simpler methods of regularization. Therefore I vote to reject the paper in its present form.
Suggestions for improvement on the experiments
My main concern with the experiments is that a similar small improvement over the baseline could be achieved by tuning the hyperparameters in an alternative simpler regularization method. For instance, instead of using an adversarial perturbation, one could simply use a random perturbation applied to both the random noise and the discriminator input at testing time. The former would amount to a variance of the truncation trick [Brock et al 2019], while the latter would amount to using instance noise. These are established methods to improve GAN performance and to make a case for adversarial training of GANs one would need to show improvements compared to these simpler strategies, in my opinion.
My main suggestion for the theoretical part is to make a stronger case of what (if anything) these theoretical results say about the performance of RGAN compared to the usual GAN. In particular, the generalization bound does not seem to depend on lambda, (which interpolates between the original GAN and RGAN). What is to be inferred from these results regarding the performance of RGAN?
Questions to the authors
(1) I assume you perform adversarial training in practice by backpropagating in image/noise space? How does this affect performance? How would the convergence plots look like if wall-clock time, or the number of model evaluations were used on the x-axis?
(2) Did you try investing a similar computational budget to tune hyperparameters for simpler regularization methods as mentioned above and compare the resulting improvement?
(3) Is the value (I presume, standard deviation) given after each the inception score computed for different multiple iterations of the same run or multiple runs with different initialization and random seed?


We present a new method for black-box adversarial attack. Unlike previous methods that combined transfer-based and scored-based methods by using the gradient or initialization of a surrogate white-box model, this new method tries to learn a low-dimensional embedding using a pretrained model, and then performs efficient search within the embedding space to attack an unknown target network. The method produces adversarial perturbations with high level semantic patterns that are easily transferable. We show that this approach can greatly improve the query efficiency of black-box adversarial attack across different target network architectures. We evaluate our approach on MNIST, ImageNet and Google Cloud Vision API, resulting in a significant reduction on the number of queries. We also attack adversarially defended networks on CIFAR10 and ImageNet, where our method not only reduces the number of queries, but also improves the attack success rate.

This paper proposed a new method for black-box adversarial attacks which tries to learn a  low-dimensional embedding using a pretrained model and then performs efficient search within the embedding space to attack the target network. The proposed method can produce perturbation with semantic patterns are easily transferable. It can be used to improve the query efficiency in black-box attacks.
- The main idea of this paper is quite simple, i.e., using a autoencoder model to capture encoding in the embedding space and then searching over the embedding space for possible attacks. While searching for adversarial examples in the embedding space is not something new, such as manifold attack or GAN-based attack, the authors claimed that by doing so, it can help reduce the query complexity of black-box attacks. However, it is not immediately clear to me why this can help reduce the query complexity, as intuitively, restricting the attack image space to an embedding space (or a manifold) will naturally increase the difficulty for finding adversarial examples. The authors’ explanation is not quite convincing to me since many adversarial examples are not necessarily on the embedding space.
- Algorithm 1 is not clearly written and I do not understand the update rule in Algorithm 1. What is Li exactly? If Li means eq(1) or eq(2), it seems totally independent of sampled Guassian noise? Also, the update rule in Line 5 of Algorithm 1 is different from what is described in eq(4) or other black-box attack algorithms. Can the author explain the algorithm design with details?
- In experiments section, the authors miss a few important black-box attack baselines. I would suggest the authors to further comment and compare with the following black-box attacks to better demonstrate the performance of the proposed algorithm.
Ilyas, Andrew, Logan Engstrom, and Aleksander Madry. "Prior convictions: Black-box adversarial attacks with bandits and priors." ICLR 2019.
Moon, Seungyong, Gaon An, and Hyun Oh Song. "Parsimonious Black-Box Adversarial Attacks via Efficient Combinatorial Optimization." ICML 2019.
Chen, Jinghui, Jinfeng Yi, and Quanquan Gu. "A Frank-Wolfe Framework for Efficient and Effective Adversarial Attacks." arXiv preprint arXiv:1811.10828 (2018).
- Also can the authors further conduct experiments using more common choice of \epsilon to help the reader get better understandings. For example, add ImageNet experiments with \epsilon = 0.05.
Detailed comments:
- In section 3.2, the author suggests that by removing the sign function, the attacks can be more effective in (Li et al., 2019).  I didn’t find the corresponding argument in (Li et al., 2019). Can the authors be more specific on this argument?
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I have read the response and it addressed my concerns. I will increase my score


Bayesian inference offers a theoretically grounded and general way to train neural networks and can potentially give calibrated uncertainty. It is, however, challenging to specify a meaningful and tractable prior over the network parameters. More crucially, many existing inference methods assume mean-field approximate posteriors, ignoring interactions between parameters in high-dimensional weight space. To this end, this paper introduces two innovations: (i) a Gaussian process-based hierarchical model for the network parameters based on recently introduced unit embeddings that can flexibly encode weight structures, and (ii) input-dependent contextual variables for the weight prior that can provide convenient ways to regularize the function space being modeled by the network through the use of kernels. Furthermore, we develop an efficient structured variational inference scheme that alleviates the need to perform inference in the weight space whilst retaining and learning non-trivial correlations between network parameters. We show these models provide desirable test-time uncertainty estimates, demonstrate cases of modeling inductive biases for neural networks with kernels and demonstrate competitive predictive performance of the proposed model and algorithm over alternative approaches on a range of classification and active learning tasks.

**Summary**: This paper proposes a hierarchical Bayesian approach to hyper-networks by placing a Gaussian process prior over the latent representation for each weight. A stochastic variational inference scheme is then proposed to infer the posterior over both the Gaussian process and the weights themselves. Experiments are performed on toy regression, classification, (edit: post rebuttal) and transfer learning tasks, as well as an uncertainty quantification experiment on MNIST.
post rebuttal (noticed recently): Many apologies for updating the review the day before the deadline; however, I recently remembered that Kronecker inference is often used in variational methods - particularly within the vein of literature of deep kernel learning. Indeed, structure exploiting SVI was proposed in Stochastic Variational Deep Kernel Learning, https://arxiv.org/pdf/1611.00336.pdf, and this method is currently the default in Gpytorch: https://github.com/cornellius-gp/gpytorch/tree/master/examples/08_Deep_Kernel_Learning .
Furthermore, Kronecker inference for non-Gaussian likelihoods for Laplace approximations was proposed back in 2015: http://proceedings.mlr.press/v37/flaxman15.pdf.
I am not updating my score because it would be unfair; however, the record should be set somewhat straight here.
post rebuttal: Thank you for the many clarifications and detailed responses. I'm now satisfied with their many changes and and tend to accept this paper despite the experimental results being somewhat limited. I would really encourage the authors to fix the color schemes (please less black and more brighter colors) on their decision boundaries plots however.
**tldr**: While I appreciate the concept of this paper, I tend to reject this paper because I find the experimental results to be on too small scale of datasets. Specifically, I would like to see either a larger scale problem being solved with this kind of approach or a tough to model applied problem that is solved with this approach.
**Originality**: As far as I can tell, this seems to be a novel approach to hyper-networks. Neural processes (Garnelo et al; 2018) propose a somewhat similar approach to training – with a latent process over some stored weight space. However, even that is quite distinct from the method proposed in this paper, and I tend to prefer this approach.
**Quality**: I really appreciate the merging of neural network and Gaussian process methods; however, tragically, I do wonder if the proposed approach combines the worst of both worlds – the necessity of architecture search for neural networks with the choice of kernel function (as illustrated in Figure 5).
If the method is truly kernel dependent, is it also architecture dependent? That is, is it robust to different settings of nonlinearities and depths?
Active learning experiment: While I appreciate the comparison here, it seems like here standard HMC should be trainable over well-designed priors on these architectures. So why not include a comparison instead of just MFVI?
**Significance**: Unfortunately, I think that the experiments section is just a bit too limited to warrant acceptance right now. This is despite the fact that I really do appreciate the thoroughness and thoughtfulness of the experiments as they are.
Specifically, in Section 6.2 why is the metaGP prior only applied to the last layer of the network? If as I suspect, it is due to the complexity and difficulty of inference, that makes the method doubly tough to use in practice. With that being said, to only have experiments on the last layer implies that one should compare to Bayesian logistic regression and linear regression on the last layer of neural networks (e.g Perrone et al, 2018 and Riquelme et al, 2018). Experiments with other methods that combine Gaussian processes with representations on the final layer (e.g. Wilson et al, 2015) are also probably worth running.
Figure 4 is a very well-done experiment, if a bit tough to read. I’d suggest that the out of distribution examples get their own figure, with the in distribution examples going into the appendix. I’d also suggest computing the expected calibration error (Naeini et al, 2015) for in and out of distribution examples on the test sets for both MNIST and K-MNIST in order to have quantitative results on the entire test set.
To recommend acceptance, I’d really have to see experiments on either a CIFAR sized dataset for classification or a larger scale regression experiment. A larger dataset on either transfer learning (after all you do have a meta-representation over functions that the NN can learn), a larger active learning experiment, or semi-supervised learning.
**Clarity**: Overall, the paper is well-written and mostly easy to follow. The meat of the paper is found in Section 4, which I found a bit difficult to follow.
(edit: post rebuttal. This concern is somewhat resolved due to the field not being well developed in this area, although it is a useful place to possibly extend the method in the future.) My primary concern here is that the prior ends up becoming Kronecker structured (after Eq. 7), so it isn’t clear to my why dense matrices and dense variational bounds have to be derived in this setting. Can one not follow the lead of the Gaussian process literature (e.g. Saatci 2012, Wilson & Nickisch, 2015) to exploit the Kronecker structure here to make computation of the log likelihoods fast?
(edit: post rebuttal. This concern is somewhat resolved.) As a result, it’s not immediately clear to me why a diagonal approximation (Eq. 10) is even necessary?
Furthermore, this may be a setting where iterative methods (e.g conjugate gradients and Lanczos decompositions as in Pleiss et al, 2018) for the predictive means and variances may shine and be fast.
I do agree that the approximation in Figure 2 does seem to be relatively accurate, although I would ask the authors to compute a relative error for that plot if possible. Additionally, what is the strange high off diagonal correlations in the marginal covariances?
(edit: post rebuttal. Thank you for the clarifications here.) Finally, I was a bit confused by the effect of adding the input dependent kernel in Section 3; this seems to make the weights much more complicated to model – now each data point has its own set of weights and therefore, we might have to store considerably more weight matrices over time. Could the authors perform a set of experiments showing the necessity of this kernel matrix in the rebuttal?
**Minor Comments**:
-	Above Eq. 9, “splitted” should be split.
-	Figure 3: could the data points be plotted in a brighter fashion? On a dark background, they are quick tough to see. Additionally, what is the difference between the two levels of classification plots?
References:
Naeini, et al. Obtaining Well Calibrated Probabilities by Bayesian Binning, AAAI, 2015. https://www.ncbi.nlm.nih.gov/pmc/articles/PMC4410090/
Perrone, V, et al. Scalable Hyperparameter Transfer Learning, NeurIPS, 2018. http://papers.nips.cc/paper/7917-scalable-hyperparameter-transfer-learning
Pleiss, G, et al. Constant Time Predictive Distributions for Gaussian Processes, ICML, 2018. https://arxiv.org/abs/1803.06058
Riquelme, C, Tucker, G, Snoek, J. Deep Bayesian Bandits Showdown, ICLR, 2018. https://arxiv.org/abs/1802.09127
Saatci, Y. Scalable Inference for Structured Gaussian process models, PhD Thesis, U. of Cambridge, 2011. http://mlg.eng.cam.ac.uk/pub/pdf/Saa11.pdf
Wilson, AG and Nickisch, H. Kernel Interpolation for Scalable Structured Gaussian Processes, ICML, 2015. http://proceedings.mlr.press/v37/wilson15.pdf
Wilson, AG, et al. Deep Kernel Learning, AISTATS, 2015. https://arxiv.org/abs/1511.02222


In this paper, we study the implicit regularization of the gradient descent algorithm in homogeneous neural networks, including fully-connected and convolutional neural networks with ReLU or LeakyReLU activations. In particular, we study the gradient descent or gradient flow (i.e., gradient descent with infinitesimal step size) optimizing the logistic loss or cross-entropy loss of any homogeneous model (possibly non-smooth), and show that if the training loss decreases below a certain threshold, then we can define a smoothed version of the normalized margin which increases over time. We also formulate a natural constrained optimization problem related to margin maximization, and prove that both the normalized margin and its smoothed version converge to the objective value at a KKT point of the optimization problem. Our results generalize the previous results for logistic regression with one-layer or multi-layer linear networks, and provide more quantitative convergence results with weaker assumptions than previous results for homogeneous smooth neural networks. We conduct several experiments to justify our theoretical finding on MNIST and CIFAR-10 datasets. Finally, as margin is closely related to robustness, we discuss potential benefits of training longer for improving the robustness of the model.

The goal of the paper is to formally prove that gradient flow / gradient descent performed on homogeneous neural network models maximizes the margin of the learnt function; assuming gradient flow/descent manages to separate the data. This is proved in two steps:
  1. Assuming that gradient descent manages to find a set of network parameters that separate the data, thereafter gradient flow/descent monotonically increases the normalized margin (rather an approximation of it).
  2. The limit points of optimization are KKT points of the margin maximization optimization problem.
While the main body of the paper presents a restricted set of results, the appendix generalizes this much further applying it to various kinds of loss functions (logistic/cross-entropy, exponential), to multi-class classification and to multi-homogeneous models. There seem to be many subtleties in the proofs and the paper seems to be quite thorough. (I must say that I'm not expert enough to assess the technical novelty of this paper over prior works.)
Recommendation:
I recommend "acceptance". The paper takes a significant step by unifying existing results on margin maximization and going beyond them.
Technical comments:
- It is clear that in order to define margin meaningfully, some form of normalization is necessary. But a priori, $\|\theta\|_2^L$ is not the *only* choice; $\|\theta\|^L$ could also work for any norm $\|\cdot\|$. But perhaps the choice of $\|\cdot\|_2$ is special (as Thm 4.4 suggests). It will be nice to have some insights/comments on why this choice of $\|\cdot\|_2$ based normalization is the right one.
- The paper argues that having a larger margin helps in obtaining better robustness to adversarial perturbations (within $\|\cdot\|$ balls for some choice of $\|\cdot\|$). However note that the notion of "margin" is not just a function of the decision boundary, but instead depends on the specific function computed by the neural network --- this is unlike margin maximization in linear models, where "margin" in determined entirely by the decision boundary. As the paper argues, if we have an upper bound on the Lipschitz constant w.r.t. $\|\cdot\|$ norm, then we get a lower bound on required adversarial perturbations for any training point. However, this does not mean that training longer is necessarily better because by doing so, we might end up with a larger Lipschitz constant (even after normalizing). So even if the "margin" is larger, the actual adversarial perturbations (in $\|\cdot\|$ norm) allowed might get smaller. So I'm not sure how relevant this result is for adversarial robustness.


Intrinsically motivated reinforcement learning aims to address the exploration challenge for sparse-reward tasks. However, the study of exploration methods in transition-dependent multi-agent settings is largely absent from the literature. We aim to take a step towards solving this problem. We present two exploration methods: exploration via information-theoretic influence (EITI) and exploration via decision-theoretic influence (EDTI), by exploiting the role of interaction in coordinated behaviors of agents. EITI uses mutual information to capture the interdependence between the transition dynamics of agents. EDTI uses a novel intrinsic reward, called Value of Interaction (VoI), to characterize and quantify the influence of one agent's behavior on expected returns of other agents. By optimizing EITI or EDTI objective as a regularizer, agents are encouraged to coordinate their exploration and learn policies to optimize the team performance. We show how to optimize these regularizers so that they can be easily integrated with policy gradient reinforcement learning. The resulting update rule draws a connection between coordinated exploration and intrinsic reward distribution. Finally, we empirically demonstrate the significant strength of our methods in a variety of multi-agent scenarios.

This paper studies the problem of designing effective exploration strategies in multi-agent domains. The key idea is to define one agent's exploration in terms of its interactions with other agents. This leads to two auxiliary exploration objectives, which measure how one agent's actions affect the dynamics and value of another agent's actions. The paper does an admirable job comparing the proposed method against a number of baselines, where the proposed method performs significantly better. Visualizations and ablation experiments nicely illustrate the contributions of various components of the method.
I am leaning towards accepting the paper. To the best of my knowledge, the broad idea of applying information theory to multi-agent exploration, in addition to the specific instantiation described in the paper, is novel. I expect that this paper will encourage future work to explore more problems in this area. The experiments are quite thorough. My main reservation is a lack of comparisons to single agent exploration methods. As noted in Section 3, we can view multi-agent domains as just a special type of single agent domain. How would curiosity-based exploration, such as [Burda 2018, Pathak 17], or mutual information-based exploration, such as [Gregor 16, Eysenbach 18, Achaim 18], compare to the proposed method?
I have a few reservations about the clarity of presentation, but I think those are easily addressed. My remaining concern is that the results are on somewhat toy tasks, but I think that is par for this area of research.
Overall, I would strongly argue for accepting this paper if comparisons to single-agent exploration methods were added. I would consider decreasing my review if another reviewer found quite similar prior work, or if significant bugs were found in the mathematical derivation (I have not carefully checked all the proofs in the appendix.).
Minor comments
* "transition-dependent" -- what does this mean?
* "while tend" -- missing a subject
* "struggle in many real-world scenarios with sparse rewards" -- please add a citation
* "intrinsic value function of agent i, I_{-i|i}^\pi is \beta > 0 is a weighting" -- I think part of this sentence was accidentally deleted.
* Eq 5: What is the difference between I and MI?
* "We call …" -- What is the a_2^V0I^\pi_{-i|i} term?
* Nitpick: Use `` for the start of quotes
* Appendix B1: How is Eq 22 obtained from Eq 21?
-------------------UPDATE AFTER AUTHOR RESPONSE---------------------
The authors have done a great job address my two concerns (similarity to prior work and empirical comparisons with single-agent exploration). I therefore increase my vote to "accept."


In this paper, we present an in-depth investigation of the convolutional autoencoder (CAE) bottleneck. Autoencoders (AE), and especially their convolutional variants, play a vital role in the current deep learning toolbox. Researchers and practitioners employ CAEs for a variety of tasks, ranging from outlier detection and compression to transfer and representation learning. Despite their widespread adoption, we have limited insight into how the bottleneck shape impacts the emergent properties of the CAE. We demonstrate that increased height and width of the bottleneck drastically improves generalization, which in turn leads to better performance of the latent codes in downstream transfer learning tasks. The number of channels in the bottleneck, on the other hand, is secondary in importance. Furthermore, we show empirically that, contrary to popular belief, CAEs do not learn to copy their input, even when the bottleneck has the same number of neurons as there are pixels in the input. Copying does not occur, despite training the CAE for 1,000 epochs on a tiny (≈ 600 images) dataset. We believe that the findings in this paper are directly applicable and will lead to improvements in models that rely on CAEs.

Summary:
This paper studies some of the properties of fully convolutional autoencoders (CAE) as a function of the shape and total size of the bottleneck. They train and test CAEs with bottlenecks consisting of different ratios of spatial resolution versus number of channels, as well as different total number of neurons. The authors investigate which type of change in the bottleneck is most influential on training behavior, generalization to test set, and linear separability for classification/regression. Their first main finding is that the spatial resolution of the bottleneck is a stronger influencer of generalization to the test set than the number of channels and the total number of neurons in the bottleneck. The second main finding is that even when the total number of neurons in the bottleneck is equal to the data input size, the neural network does not appear to simply learn to copy the input image into the bottleneck.
Decision:
Weak reject: It is always refreshing to see papers that address/challenge/investigate common assumptions in deep learning. However, I find the experimental findings and discussion of borderline quality for a full conference paper. It might be more suitable as a good workshop paper.
Supporting arguments for decision:
It is unclear to me why the authors have chosen to only take a subset of the CelebA and STL-10 datasets for training and testing. It seems like dataset size is also an important factor that increases the complexity for training a model, and it certainly affects how a model can generalize. When auto-encoders are studied in other literature it is uncommon practice to restrict the dataset sizes like this, so this makes me question the applicability of this paper’s results to the literature.
It seems that the experimental validation is based on one run per CAE model with one single seed. This is on the low side of things, especially when quite extensive claims are made. An example of such a claim is on page 6 when discussing a sudden jump in training and test scores for 8x8x48 model trained on the Pokemon dataset. Because the same behavior appeared when the authors repeated the experiment with the same seed, the authors conclude “This outlier suggests, that the loss landscape might not always be as smooth towards the end of training, as some publications (Goodfellow et al., 2014) claim and that ‘cliffs” (i. e., sudden changes in loss) can occur even late in training.” Making this claim based on something that occurs with one single model for a single seed is not convincing and overstating this finding.
Another example is on page 7 under bullet point 4, where the authors discuss the obtained evidence against copying behaviour when the bottleneck is of the same size as the input. The authors state “We believe this finding to have far-reaching consequences as it directly contradicts the popular hypothesis about copying CAEs.” The paper definitely shows some empirical evidence that supports the claim that copying does not occur, but these findings are all done with a single seed and by considering small subsets of datasets (celebA and stl-10). In my opinion, it is therefore too much to state that the current findings have far reaching consequences. It has potential, but I wouldn’t go much further than that.
On page 7 in the second to last paragraph the influence of dataset complexity is discussed. The authors state “the loss curves and reconstruction samples do not appear to reflect the notion of dataset difficulty we defined in Section 2.3” and “This lack of correspondence implies that the intuitive and neural network definitions of difficulty do not align. Nevertheless, a more detailed study is required to answer this question definitively as curriculum learning research that suggests the opposite (Bengio et al., 2009) also exists.” It is unclear to me what the authors expected to find here. Moreover, the absence of major differences across the chosen datasets does not immediately make me doubt or question results from curriculum learning. My skepticism is again enhanced by the fact that the authors have taken a subset of the data for the more complex celebA and STL-10 datasets. Dataset size seems like a crucial part of dataset complexity.
An interesting smaller finding is that linear separability of the latent codes for classification is better on the test set for the pokemon dataset, even though the training and test reconstruction losses showed signs of overfitting. The authors hypothesize that overfitting might occur more in the decoder than in the encoder.
Additional feedback to improve the paper (not part of decision assessment)
- Section 2.3.1: what was the original resolution of the pokemon dataset?
- Section 3.1, c_j is used as the compression level, but in eq 3 and 4 c^i is also used to indicate the number of channels. - For clarity please use n_ci in eq 2 and 3 or choose a different all together for the compression level.
- Please increase the font size of the plots in figures 1, 3 and 4.


Learning from only partially-observed data for imputation has been an active research area. Despite promising progress on unimodal data imputation (e.g., image in-painting), models designed for multimodal data imputation are far from satisfactory. In this paper, we propose variational selective autoencoders (VSAE) for this task. Different from previous works, our proposed VSAE learns only from partially-observed data. VSAE is capable of learning the joint distribution of observed and unobserved modalities as well as the imputation mask, resulting in a unified model for various down-stream tasks including data generation and imputation. Evaluation on both synthetic high-dimensional and challenging lowdimensional multi-modality datasets shows significant improvement over the stateof-the-art data imputation models.

The paper proposes a novel training method for variational autoencoders that allows using partially-observed data with multiple modalities. A modality can be a whole block of features (e.g., a MNIST image) or just a single scalar feature. The probabilistic model contains a latent vector per modality. The key idea is to use two types of encoder networks: a unimodal encoder for every modality which is used when the modality is observed, and a shared multimodal encoder that is provided all the observed modalities and produces the latent vectors for the unobserved modalities. The whole latent vector is passed through a decoder that predicts the mask of observed modalities, and another decoder that predicts the actual values of all modalities. The “ground truth” values for the unobserved modalities are provided by sampling from the corresponding latent variables from the prior distribution once at some point of training.
While I like the premise of the paper, I feel that it needs more work. My main concern is that sampling the target values for the unobserved modalities from the prior would almost necessarily lead to blurry synthetic “ground truth” for these modalities, which in turn means that the model would produce underconfident predictions for them. The samples from MNIST in Figure 3 are indeed very blurry, supporting this. Furthermore, the claims of the model working for non-MCAR missingness are not substantiated by the experiments. I believe that the paper should currently be rejected, but I encourage the authors to revise the paper.
Pros:
* Generative modelling of partially observed data is a very important topic that would benefit from fresh ideas and new approaches
* I really like the idea of explicitly modelling the mask/missingness vector. I agree with the authors that this should help a lot with non completely random missingness.
Cons:
* The text is quite hard to read. There are many typos (see below). The text is over the 8 page limit, but I don’t think this is justified. For example, the paragraph around Eqn. (11) just says that the decoder takes in a concatenated latent vector. The MNIST+SVHN dataset setup is described in detail, yet there is no summary of the experimental results, which are presented in the appendix.
* The approach taken to train on partially-observed data is described in three sentences after the Eqn. (10). The non-observed dimensions are imputed by reconstructions from the prior from a partially trained model. I think that this is the crux of the paper that should be significantly expanded and experimentally validated. It is possible that due to this design choice the method would not produce sharper reconstructions than the original samples from the prior. Figures 3, 5 and 6 indeed show very blurry samples from the model. Furthermore, it is not obvious to me why these prior samples would be sensible at all, given that all modalities have independent latents by construction.
* The paper states multiple times that VAEAC [Ivanov et al., 2019] cannot handle partially missing data, but I don’t think this is true, since their missing features imputation experiment uses the setup of 50% truly missing features. The trick they use is adding “synthetic” missing features in addition to the real ones and only train on those. See Section 4.3.3 of that paper for more details.
* The paper states that “it can model the joint distribution of the data and the mask together and avoid limiting assumptions such as MCAR”. However, all experiments only show results in the MCAR setting, so the claim is not experimentally validated.
* The baselines in the experiments could be improved. First of all, the setup for the AE and VAE is not specified. Secondly, it would be good to include a GAN-based baseline such as GAIN, as well as some more classic feature imputation method, e.g. MICE or MissForest.
* The experiments do not demonstrate that the model learns a meaningful *conditional* distribution for the missing modalities, since the provided figures show just one sample per conditioning image.
Questions to the authors:
1. Could you comment on the differences in your setup in Section 4.1 compared to the VAEAC paper? I’ve noticed that the results you report for this method significantly differ from the original paper, e.g. for VAEAC on Phishing dataset you report PFC of 0.24, whereas the original paper reports 0.394; for Mushroom it’s 0.403 vs. 0.244. I’ve compared the experimental details yet couldn’t find any differences, for example the missing rate is 0.5 in both papers.
2. How do you explain that all methods have NRMSE > 1 on the Glass dataset (Table 1), meaning that they all most likely perform worse than a constant baseline?
Typos and minor comments:
* Contributions (1) and (2) should be merged together.
* Page 2: to literature -> to the literature
* Page 2: “This algorithm needs complete data during training cannot learn from partially-observed data only.”
* Equations (1, 2): z and \phi are not consistently boldfaced
* Equations (4, 5): you can save some space by only specifying the factorization (left column) and merging the two equations on one row
* Page 4, bottom: use Bernoulli distribution -> use factorized/independent Bernoulli distribution
* Page 5, bottom: the word “simply” is used twice
* Page 9: learn to useful -> learn useful
* Page 9: term is included -> term included
* Page 9: variable follows Bernoulli -> variable following Bernoulli
* Page 9: conditions on -> conditioning on


Explaining the prediction of deep models has gained increasing attention to increase its applicability, even spreading it to life-affecting decisions. However there has been no attempt to pinpoint only the most discriminative features contributing specifically to separating different classes in a fine-grained classification task. This paper introduces a novel notion of salient explanation and proposes a simple yet effective salient explanation method called Gaussian light and shadow (GLAS), which estimates the spatial impact of deep models by the feature perturbation inspired by light and shadow in nature. GLAS provides a useful coarseto-fine control benefiting from scalability of Gaussian mask. We also devised the ability to identify multiple instances through recursive GLAS. We prove the effectiveness of GLAS for fine-grained classification using the fine-grained classification dataset. To show the general applicability, we also illustrate that GLAS has state-of-the-art performance at high speed (about 0.5 sec per 224×224 image) via the ImageNet Large Scale Visual Recognition Challenge.

The paper introduces a new method in the family of local perturbation-based interpretations for deep networks and more specifically for fine-grained classification tasks. Compared to other saliency map methods (gradient-based, propagation-based, etc), this family has the advantage of needing only black-box access to the model. The introduced method GLAS, scans over an image and lights/shadows each part of the image to assign an importance score to different regions of the image based on the change in model's prediction. The motivation of this work is to increase the inherently low speed of (some) methods in this family and to give better explanations by
I vote for rejecting this paper as the contributions to what already exists in the literature are not clear and the provided experimental results are not convincing.
Compared to previous perturbation-based methods, the main advantage seems to be speed. There are perturbation-based methods that do not suffer from low speed e.g. Dabkowski & Gal and give real-time perturbation-based saliency maps. The authors do not mention this work (and similar works) and do not compare both their speed and their performance against it.
One important problem (probably the most important) with the perturbation-based saliency maps is the fact that the perturbations might push a given image out of the true data manifold and therefore give an invalid interpretation of the model. The authors do not discuss the matter and how their method would address this issue. Intuitively, the introduced algorithm, more specifically the RGLAS algorithm, seems to suffer from this issue not any less than other existing methods.
The experimental results seek to demonstrate the superiority of the introduced method over rival methods. The justification behind the provided visual examples is their focus on more discriminative features (in human eyes). This does not necessarily mean that a given saliency map is more "truceful"; i.e. having a more visually appealing saliency map has nothing to do with a more truthful explanation of a model's decision making. The results focused on the mistakes of the model seem more convincing and interesting.
 The objective results first focus on the target localization metric which has traditionally been used in the literature. Although it is much faster to execute, the introduced method is only marginally superior to other methods. The most important problem, however, is that as mentioned above, there are fast methods in the literature and therefore a fair objective comparison is should include other methods as well. Secondly, the IOU measure is used. GLAS is not compared to other methods in this metric.
The authors mention the effectiveness of their work for "fine-grained" classification tasks while throughout the paper there is no convincing evidence or discussion that the method is curated for such tasks. As mentioned above, changing the scale parameter for getting more visuall appealing saliency maps is not enough evidence.
All in all, the true contribution of this work to other existing methods in this family is not enough for this venue.
A few questions and suggestions:
* How should one adjust the scale parameter? In other words, what is the hyper-parameter search scheme for this method which would make it robust against the human-biased choice of hyper-parameters which would result in visually more appealing saliency maps but not necessarily explain the model?
* Explanation of RGLAS is not clear.
* For a general reader, metrics such as IOU should be explained more clearly.
* The paper has many many typing errors.


Strictly enforcing orthonormality constraints on parameter matrices has been shown advantageous in deep learning. This amounts to Riemannian optimization on the Stiefel manifold, which, however, is computationally expensive. To address this challenge, we present two main contributions: (1) A new efficient retraction map based on an iterative Cayley transform for optimization updates, and (2) An implicit vector transport mechanism based on the combination of a projection of the momentum and the Cayley transform on the Stiefel manifold. We specify two new optimization algorithms: Cayley SGD with momentum, and Cayley ADAM on the Stiefel manifold. Convergence of the Cayley SGD is theoretically analyzed. Our experiments for CNN training demonstrate that both algorithms: (a) Use less running time per iteration relative to existing approaches which also enforce orthonormality of CNN parameters; and (b) Achieve faster convergence rates than the baseline SGD and ADAM algorithms without compromising the CNN's performance. The Cayley SGD and Cayley ADAM are also shown to reduce the training time for optimizing the unitary transition matrices in RNNs.

Summary
This paper aims to improve upon current solutions for optimizing neural networks with orthonormal convolutional kernels/MLP layers. Optimizing neural networks while restricting the parameter matrices to remain orthonormal/on the Stiefel manifold is said to lead to faster convergence in terms of the number of epochs, and could reduce overfitting. One way to enforce orthonormality is to use the Cayley transform, which requires a matrix inversion that becomes expensive for large weight matrices in neural networks. The authors instead propose an iterative approximation to the Cayley transform that does not require a matrix inversion, and empirically only requires two iteration steps to lead to similar precision as a closed-form Cayley transform with numerical inverse. The authors combine this with SGD + momentum and ADAM by first performing the update step in Euclidean space and afterwards projecting the result back onto the stiefel manifold by using the iterative Cayley transform. They provide one assumption and two theorems on the convergence of the iterative approximation and its effect on optimization. The method is evaluated on classification for cifar10 and cifar100 and for modeling the hidden-to-hidden transition matrix in an RNN trained on MNIST.
Decision:
Weak reject. Although the motivation of the paper is sound. The empirical validation of the proposed method is insufficient. For instance, assumptions that are the basis of one of the theorems are violated in the experiments and converges are only shown as a function of epoch and not wall clock time.
Supporting arguments for decision:
The main issue with the paper is that the claims made are not sufficiently supported. I have the following three main issues with the evaluation:
1)  Assumption 1, which is required to prove convergence of the proposed Cayley SGD/ADAM optimizer, appears to be violated in experiments. The assumption states that the gradient of the objective function is Lipschitz continuous. However, in the VGG and wide Resnets ReLU’s are used. The derivative of a ReLU is a step function, which is not Lipschitz continuous. Therefore the objective function used in the experimental validation violates assumption 1. Now, I can imagine that perhaps in practice this does not matter too much, but surely the evaluation is not correct according to the theoretical claim. The authors should clarify this and experiments should be done with other activation functions that do not violate the assumption.
2) The paper claims to improve the convergence speed, as compared to baseline Euclidian SGD+momentum and ADAM, but learning curves are only shown as a function of epoch, and not of wall clock time. Table 3 displays per-epoch training times and clearly shows that when compared to SGD+momentum and ADAM the runtime is slowed down by a factor of 2. I am not convinced that if figure 1 would be plotted as a function of wall clock time, the proposed method would actually come out as having converged faster.
3) The learning rate decay schedule used in obtaining the results in figure 1 and table 1 seems more optimized for the proposed methods than for the baseline SGD and ADAM optimizers. ADAM and SGD have reached a plateau “earlier” (in terms of epoch number), and could have benefited from a decay in learning rate earlier on. It is also extremely hard to see what is going on after the 50th epoch due the scale of the plot in figure 1. Please zoom in on epoch 50 and onwards or also show a plot in log scale. The total number of epochs is also the same for all methods. Perhaps it would also be more fair to give every method the same total budget of wall clock time.
The following issues are more minor, but I would still like to see them addressed.
1) In the last section of the related work, the work by Wen & Yin is said to be “not suitable for training common deep neural networks”. This gives the impression that this method simply cannot be used for VGG/wide resnets. However, table 3 certainly shows results for the work by Wen & Yin for a large wide resnet with a per epoch run time that is much better than the Cayley closed form w/o momentum baseline.
2) In table 3, why is the SO training time per epoch slower than the Cayley SGD/ADAM optimization?
---- Post Rebuttal Update ----
Assumption one in the paper states that the derivative of the objective function must be Lipschitz continuous - the authors use ReLU in all experiments whose derivative is not Lipschitz continuous.
The authors address this concern with the following (page 6 in paper)
"... For some models using ReLU, the derivative of ReLU is Lipschitz continuous almost everywhere with an appropriate Lipschitz constant in Assumption 1 , except for a small neighborhood around 0, whose measure tends to 0. Such cases do not affect either analysis in theory or training in practice."
On the theory side: If the authors want to rely on the assumption that for a measure zero part of the domain the function is not Lipschitz, then the authors should adjust assumption 1 to loss functions whose derivatives are locally Lipschitz continuous, and this will require a redo of the proofs under this new assumption.
From the experimental side: they provide no direct comparison with models where assumption 1 does hold, e.g by comparing ReLU with a scaled SoftPlus as suggested in the review. So the claim that it does not matter in practice is not completely supported.
As this is an optimization paper the wall-clock convergence rates are important and was not included in the initial submission. The authors have addressed this by adding figure 2 in the appendix, which shows convergence rates from 0 - 20000 seconds. Presumably this is a subset (likely epoch 0 to 80) of the data shown in figure 1 showing 0 to 200 epochs. Why they choose not to show the full data is not completely clear to me. The authors claim that Cayley Adam catches up with Adam after 12000 seconds which might be true for cifar10 (not really visible in the figure) but is definitely not true for cifar100 where Adam seems to be better all the time.
In summary: Claims that deviating from assumption 1 does not impact theory or experiment are not supported. Important run time experiments are relegated to the appendix and only  incomplete training curves as a function of time are shown, which is potentially misleading.


This work proposes a closed loop, uncertainty-driven adaptive sampling framework (CLUDAS) for accelerating magnetic resonance imaging (MRI) via deep Bayesian inversion. By closed loop, we mean that our samples adapt in real-time to the incoming data. To our knowledge, we demonstrate the first generative adversarial network (GAN) based framework for posterior estimation over a continuum sampling rates of an inverse problem. We use this estimator to drive the sampling for accelerated MRI. Our numerical evidence demonstrates that the variance estimate strongly correlates with the expected mean squared error (MSE) improvement for different acceleration rates even with few posterior samples. Moreover, the resulting masks bring improvements to the state-of-the-art fixed and active mask designing approaches across MSE, posterior variance and structural similarity metric on real undersampled MRI scans.

The paper describes a method for accelerating MRI scans by proposing lines in k-space to acquire next. The proposals are based on posterior uncertainty estimates obtained from GAN-based reconstructions from parts of the k-space acquired thus far. The authors address an interesting and important problem of speeding up MRI scans and thus improving the subject's experience. The proposed method achieves better posterior uncertainty and SSIM scores than competing methods.
While the paper considers an important problem and takes a novel approach to solve it (using a GAN generative model to estimate uncertainty), I found that it may be particularly inaccessible to non-experts in the field of MRI image processing. Furthermore, several important methodology-related questions remain unanswered in the paper; and the experiments offered in the paper are insufficient for convincingly arguing the author’s claims.
Specifically, it is unclear whether GANs with their mode dropping behaviour are the right model choice for proposing reconstructions - they are likely to drop modes and by extension - yield overconfident uncertainty estimates. This can be expected to be particularly problematic for scans of images that differ from the training distribution, and is exacerbated by the fact that authors train the model only on scans from healthy subjects. Furthermore, because of the the GANs propensity to drop modes, it is also unclear whether the posterior variance numbers reported in the paper are directly comparable between the methods.
The method used for obtaining the uncertainty estimates from GAN samples implicitly makes the assumption that reconstructions follow a Guassian distribution with a diagonal covariance. This assumption is also made in a competing method of Zhang et. al (2019) that the authors do not compare against, and claim to improve upon methodologically (i.e. the authors state that the method of Zhang et. al (2019) cannot be used to produce uncertainty estimates in Fourier space). I am not convinced that the authors claims about the method differences are sufficiently substantiated (see more under major comments). And because the methods bear significant similarity to each other, an experimental comparison - which is currently missing - should be carried out (on open datasets that ideally include non-healthy subjects).
Finally, the paper teases fast(er) MRI in the title, but doesn’t touch on this topic in the text. This aspect should of the authors contribution be discussed at length, in particular comparing the Cartesian sampling strategy adopted by the authors to other strategies, as well as evaluating the feasibility of implementing the adaptive sampling strategy in an actual scanner (e.g. can the network be ran fast enough)?
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Major comments:
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1) In the proposed method the authors employ a procedure in which the currently sampled parts y of the k-space are fed to a generator network to obtain n_s reconstructions. These n_s sampled reconstructions are then averaged to obtain the empirical mean and variance, with the latter being used for estimating uncertainty. This procedure is potentially problematic for several reasons:
  a) First, taking the empirical mean and variance of the samples is in fact equivalent to assuming that the reconstructed image follows a Guassian distribution with a diagonal covariance. This is the same assumption the authors argue is not realistic when discussing the work of Zhang et al. (2019) in the end of Section 1.
  b) In case of GANs, which can model multi-modal distributions this uncertainty estimation is even more problematic in cases when the samples originate from different modes. What do the mean and variance represent then?
  c) As the authors highlight in the discussion section of the paper in the paper, GANs are prone to mode collapse. This is also potentially problematic for their estimator - in case of mode collapse their method would underestimate uncertainty. The fact that authors are able to use only two sampled reconstructions to estimate the mean and variance with acceptable accuracy is consistent with the occurrence of mode collapse in their generator. Furthermore, because mode collapse may occur in the author’s model, it is unsurprising that their method yields the smallest posterior variances in Table 1. The authors should provide evidence that mode collapse either does not occur or would not affect these numbers.
  d) Finally, the authors use the empirical mean and sampled reconstructions to obtain the empirical mean and variance in Fourier (k-) space. Specifically, they argue that “This feature is specific to generative models, as getting samples from P_{X|y_\omega} allows to transform these to a different domain [...] this is not possible with methods that only provide point-wise estimates of the mean and the variance in image space, such as the one used by Zhang et. al (2019)”. I don’t think this is true - Fourier transform is a linear transformation, thus given a mean and a variance in image space it is possible to deduce analytically what the mean and covariance in Fourier space would be. This should be elaborated in the text, and the comparison to Zhang et. al (2019) should thus be extended further.
2) The proposed method, CLUDAS, was evaluated against existing methods on a single proprietary dataset consisting of only 100 images from healthy individuals. This is potentially problematic, for several reasons:
  a) Using a proprietary dataset doesn’t allow follow-up works to compare against the author’s method; or for comparing CLUDAS to
 existing methods not considered in the paper; the methods should additionally be compared on a public dataset  and
  b) Applying the method only to a single (small) dataset does not allow for reasoning on how the method behaves in different data regimes. I strongly encourage the authors to apply their method on public datasets, for example on data used in Zhang et. al (2019) - this would then allow for comparing the two methods despite not having access to an implementation of Zhang et. al (2019).
  c) Since the data is used to train the GAN model is obtained from healthy individuals, it’s unclear whether it can be used to acquire data from subject that may potentially have aberrations in their scans - the GAN model would be expected to produce low uncertainty estimates for regions where these aberrations would lie and not propose acquiring parts of the k-space that could be used to resolve these aberrations. For similar reasons using a GAN that potentially drops modes (e.g. scans of unhealthy individuals, for example because they are less common in the training data) is also problematic. The authors should consider evaluating their method on a dataset that contains non-healthy subjects, and investigate the performance of the method when it’s evaluated on healthy subjects, but tested on unhealthy ones.
3) The title of the paper (“[...] for fast MRI”) suggests that the authors aim to accelerate the MRI data acquisition process.
  a) Yet they chose the work with the Carterian sampling (i.e. sampling lines in the k-space parallel to the x-axis), which arguably requires larger sections of the k-space to be sampled before a high-quality reconstruction can be obtained (e.g. see http://mriquestions.com/k-space-trajectories.html). Providing information on how this choice influences the speed of data acquisition (and thus subject’s comfort) is important in order to assess the applicability of the author’s method to real world scenarios. This information should be provided.
  b) The paper does not actually describe how MRI is sped up. Given that the acquisition budget (number of lines acquired in k-space) is fixed, and assuming that time per line is constant, it is unclear where the speed up comes in. More generally, the speed claims / aspect of the proposed method should be discussed in more detail - how is speed measured and evaluated? How does it compare to non-Cartesian sampling approaches.
  c) Finally, it’s unclear whether neural network inference can be made fast enough to allow for a real world application of the adaptive CLUDAS sampling - can the data be transferred fast enough from the scanner to do inference and propose the next line to scan without causing delays in the scanning process? This should be discussed in the paper.
4) Currently, the paper places a strong expectation of knowing about MRI and being familiar with MRI-specific terminology on the reader. This makes the work substantially less accessible to a wide audience with machine learning expertise as the common denominator. The authors should take steps towards making the text more accessible to non-(MRI) expert audience, for example by introducing some of the basic knowledge (e.g. the data acquisition and reconstruction processes in MRI) early on, departing from MRI-specific jargon (e.g. k-space, lines in k-space) in favour of ML terminology whenever possible, and taking care to define and possibly illustrate (strongly encouraged) the MRI-specific concepts (e.g. the k-space, lines in k-space, sampling masks). Some specific examples the authors should address follow.
  a) The k-space is defined only in passing as being the frequency domain. It’s unclear whether these lines (which correspond to sampling masks) in this domain are parallel to the x-axis. The math (e.g. Equation 1) and Figure 2 suggest that, but it’s not obvious.
x is referred to both as "model parameter" in Section 2 (and Equation 1) as well as the "ground truth image" later in the same section. This is confusing, especially because in case of GAN model parameter would typically refer parameters of the generator and discriminator.
  b) SSIM is not defined anywhere, but already used in the abstract.
  c) It could be made more clearly why undersampling is required in case of MRI. E.g. how/why does it correlation with patient comfort.
  d) “K-space sampling” is used already in the introduction, but not really defined.
  e) It’s unclear whether sampling, subsampling and undersampling all refer to the same concept or not.
  f) The term “sampling mask” is already used in the introduction, but not clear what it refers to.
  g) Use of the term “innovation” to refer v_t, which appears to be a one-hot vector marking the newly added line in k-space.
  h) The use of term “sampling decision” to refer to v_i.
  i) Unclear what eta in “Z ~ eta“ in Equation 5 refers to - it is not defined. Later in Section 2.2 it is stated that “z_i are independent samples form Z”. Is this the same as “z_i ~ eta”? If so, why the second layer of notation?
  k) In Introduction “[...] which is not feasible on a real problem without the ground truth available”. Unclear what the ground truth refers to, I assume it’s the ground truth image.
  l) In Section 2.1 data refers to x_i, with i=1,...,m; which I assume are images and thus contain real numbers. Yet Section 3 states “As our data are complex [...]”. This is confusing - is that different data?
  m) Sampling is used ambiguously in the paper - to refer to sampling in the k-space (e.g. sampling masks, sampling decisions v_1,...,v_n) and to refer to sampling reconstructions from the generator. This should be resolved to improve readability of the paper.
  n) Not entirely clear what k-space pixel-wise variances are. And what is the difference between spatial and pixels-wise variances is (Section 2.2).
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Minor comments:
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1. In the Introduction the authors argue that metrics such as MSE and SSIM “[..] do not align with what clinicians see as valuable.”, yet use these throughout the paper for evaluating and comparing methods. This decision should be explained.
2. In Section 2 (and beyond) images x are described as belonging to subspace C^p of complex numbers. While this is technically true, them to actually belong to the space of R^p. If so, this should be reflected in the text for the benefit of the readers. Furthermore, I don’t think dimensionality p is actually defined anywhere.
3. Compressive / compressed sensing abbreviations CS is defined twice in Section 1.
4. It’s not entirely clear why “The CS-inspired methods shift the burden from acquisition to reconstruction [...]”
5. Incorrect double quotes are used throughout the text (both are right quotes).
6.  In Introduction “[...] yielding an estimator which can be used to drive back the whole sampling process in a closed-loop fashion.”
it is unclear what it means to “drive back a sampling process”. Perhaps “back” should not be there?
7. In some cases it is unclear what the use of double quotes conveys, e.g.
  a) In Section 2.1 “[...] being the “full” mask [...]”
  b) In Section 2 “[...] ground truth “complete” images [...]”
  c) In Section 5 “[...] these inverse problems “depend” from each other [...]”
  d) Multiple places in Appendix B.
8. The convention of using small letters x, y for data samples / instances and capital letters X, Y for random variables could be made explicit.
9. Section mostly provides background (rather than theory) and could be named accordingly.
10. In Section 2.1, t refers to “time”. It may be clear if it were instead referred to as the step of the sampling process or something similar - the use of “time” to refer to some discrete set of actions can be a little confusing.
11. Section 2.1 refers to “[...] the online reconstruction speed of DL [...]”. This should be explained further - why are deep learning based approaches to reconstruction faster? Does this depend only on having the right hardware accelerators? Also, I don’t think the abbreviation “DL” was introduced.
12. Equation 4 is referred to both as an “Equation” and as a “Problem”.
13. In Equation 6 there is a summation over j from v_i. It is my understanding that v_i is a one-hot vector and it’s unclear what this summation means. Presumably it is the summation over pixels covered by line v_i, but the notation doesn’t convey this. It could be nice to also explain the “1D” superscript in this equation.
14. In Section 2.2 “[...] this is why the approach of (Adler & Oktem, 2018) minimizes over distance for observation in Equation 4 [...]”. I couldn’t follow the part about minimizing over the distance for an observation. Please consider making this more clear.
15. In Equation 8, what does index i run over?
16. Minor typos / textual issues:
  a) In Introduction “[...] of the our estimator [...]”
  b) In Introduction “[...] and show that even using a few samples [...]” -> even when using?
  c) In Section 2.2, after Equation 5 “[...] where t After finding the optimal”.
  d) Inconsistent use of “closed-loop” and “closed loop”.
  e) In multiple places throughout the paper a double space appears to be used instead of a single one.
  f) Section 4.1 “as can be in Figure 1”
  g) Section 4.3 “samples art random”
  h) In Section 5 “[...] “depend” from each other” should be depend on each other?
  i) In Section 5 “[...] we we found that [...]”
17. Unclear what’s meant by “[...] using the aggregated variance as a loss function” in Section 2.2
18. Section to refers to i* (integer scalar) as a line. Previously it was v_i (vector).
19. In Section 2.2 the authors state “Once the generator has been trained until convergence [...]”. The authors optimize a generator in an adversarial fashion. To my knowledge, this training procedure is not guaranteed to converge and would typically oscillate around a stable solution. Could the authors please comment on what they mean by convergence in this case and how they guarantee that the generators they train converge.
20. For the posterior variance results in Table 1 it should be discussed whether all the methods obtain / compute the variances the same way.
21. The “data consistency layer” (Section 3) should be explained briefly. How does it enforce perfect consistency and what’s meant by consistency here?
22. It should be made clear what MSE is calculated between in Figure 1 and Table 1. I assume it’s between ground truth (all frequencies sampled) and reconstructed (only some frequencies samples) images.
23. It’s not entirely clear what’s meant by consistency in Section 4.1
24. What do yellow arrows signify in Figure 2?
25. I don’t think the abbreviation UQ was defined in Figure 2.
26. The masks in Figure 2 are such that is a certain line was chosen at lower sampling rate (left on the x-axis), it would also be chosen at higher sampling rate (right on the x-axis). This is somewhat unexpected since the budget of lines v_i to be acquired differs between sampling rates. Why is there such consistency?
27. In Table 1, in the leftmost column, the number in brackets (number of posterior samples?) should be defined.
28. In Table 1 and Section 4.3: LBC-M and LBC-U - the -M and -U suffixes should be explained. What are the differences between the methods?
29. In Section 4.3: what are the FE methods?
30. Appendix A.3 is mostly a copy-paste from the main text. Unnecessary duplication?
31. Axes in Figure 4 (Appendix A.2) are not labeled or described.
32. Loss in A.4 (Equation) does not match Equation 5. In the former the discriminator takes three arguments instead of two, and the arguments z1 and z2 are not described.


Posterior sampling for reinforcement learning (PSRL) is a useful framework for making decisions in an unknown environment. PSRL maintains a posterior distribution of the environment and then makes planning on an environment sampled from the posterior distribution. Though PSRL works well on single-agent reinforcement learning problems, how to apply PSRL to multi-agent reinforcement learning problems is largely unexplored. In this work, we extend PSRL to twoplayer zero-sum extensive-games with imperfect information (TZIEG), which is a class of multi-agent systems. Technically, we combine PSRL with counterfactual regret minimization (CFR), which is a leading algorithm for TZIEG with a known environment. Our main contribution is a novel design of interaction strategies. With our interaction strategies, our algorithm provably converges to the Nash Equilibrium at a rate of O( √ log T /T ). Empirical results show that our algorithm works well.

PSRL
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This work considers the task of finding a Nash equilibrium in a two-player zero-sum imperfect information game, where some aspects of the game are not known to the agents (specifically, the chance node probabilities, and the reward function).
The authors propose a method based on PSRL, i.e. at each iteration a set of game parameters are sampled from the posterior of the distribution. Then, CFR is applied in the inner loop; but instead of finding the NE strategy, one player finds the strategy that basically maximizes the reward deviation between two games sampled from the posterior, given that the opponent is playing Nash in the first game.
The authors prove convergence bounds for their algorithm, and demonstrate its performance on Leduc Hold'em with game parameters randomly chosen from a Dirichlet distribution.
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I agree with the authors that standard CFR suffers from the requirement that the full game is known, so it doesn't work well in its standard form when the environment is not known. There *are* other regret minimizers that do work in the model-free setting ([1], [2], [3]), none of which are discussed by the authors.
I also find the proposed setting somewhat unconvincing. The authors are considering a situation where the environment is unknown, but it's not the RL setting because you still must control both (opposing!) agents. Of course, you can't actually find a Nash Equilibrium if you can't control the other player (because they might just never explore part of the game tree). But you would want your algorithm to be a regret minimizer regardless of your partner's strategy. Is this true of the proposed algorithm?
The proposed interaction strategy described in Eq. 5 and 6 is clever: basically, each player explores a part of the tree that maximizes the difference in payoffs between the two sampled games. This seems a bit inefficient thouggh, why doesn't the agent just find the BR to \sigma_{-i} under \tilde{d} given that the opponent plays the NE under d? I don't see why you would want to explore parameters that have a high reward uncertainty if there's a different strategy that does better than the whole confidence interval. It's like UCB: you should play a strategy not with the highest uncertainty, but with the highest optimistic payoff.
I think the work could be substantially improved by comparing against model-free baselines, e.g. fictitious self-play [2], CFR with outcome sampling [1]. The current work deosn't provide any evidence of what benefits the Bayesian approach provides over model-free regret minimization. Especially since the Bayesian approach presumably does not scale as well due to the requirement of maintaining beliefs over all possible games, and the requirement that a correct prior is provided. I would be curious to see Bayesian and model-free appraoches compared in games of different sizes to see how the different methods scale.
Nits:
- such as the private pokers in poker games (private cards)
- h_1, h_1 \in H^C, are independent
- The reference to Neil 2018 should be "Neil Burch", not "Burch Neil"
- And if you're going to say "we can directly apply the technique from [100-page PhD thesis]", please mention the page number.
[1] Lanctot, Marc, et al. "Monte Carlo sampling for regret minimization in extensive games." Advances in neural information processing systems. 2009.
[2] Heinrich, Johannes, Marc Lanctot, and David Silver. "Fictitious self-play in extensive-form games." International Conference on Machine Learning. 2015.
[3] Srinivasan, Sriram, et al. "Actor-critic policy optimization in partially observable multiagent environments." Advances in Neural Information Processing Systems. 2018.


Detecting anomalies is of growing importance for various industrial applications and mission-critical infrastructures, including satellite systems. Although there have been several studies in detecting anomalies based on rule-based or machine learning-based approaches for satellite systems, a tensor-based decomposition method has not been extensively explored for anomaly detection. In this work, we introduce an Integrative Tensor-based Anomaly Detection (ITAD) framework to detect anomalies in a satellite system. Because of the high risk and cost, detecting anomalies in a satellite system is crucial. We construct 3rd-order tensors with telemetry data collected from Korea Multi-Purpose Satellite-2 (KOMPSAT-2) and calculate the anomaly score using one of the component matrices obtained by applying CANDECOMP/PARAFAC decomposition to detect anomalies. Our result shows that our tensor-based approach can be effective in achieving higher accuracy and reducing false positives in detecting anomalies as compared to other existing approaches.

The paper presents and evaluates an anomaly detection algorithm that is used for identifying anomalies in satellite data. The considered satellite data originates from multiple sensors that are divided into sensor groups. The anomaly detection algorithm roughly works as a 4 stage process:
Raw data is converted into a set of features per sensor that aggregate the last 10 min of sensor data, resulting in a tensor X with dimensions (time, features, sensors)
A tensor decomposition method is used to decompose X into matrices A,B,C.
Matrix A with dimensions (time, latent factors) is used to cluster data using k-means.
Time points are considered anomalous when the latent feature vector is too far away all cluster centres.
This algorithm is experimentally compared to baseline methods that only use one sensor at a time.
Overall, I think this paper is not fully ready for publication based on a) inconsistencies in notation that make it rather hard to read at first and b) open questions regarding the baselines, and c) missing experimental evaluations that may give insights into why the algorithm works better then the baselines. Moreover, besides those shortcomings, d) I am not convinced that ICLR is the right venue for this paper. Although the data set could provide an interesting application, the paper provides no theoretical contributions and the algorithm only pipelines known algorithms in a problem-specific way. In my view, a more application-focussed conference would be a better fit.
Detailed comments.
d) in my view is the most important issue. As mentioned above, the paper contains no theoretic contributions to the field of anomaly detection. Instead, it solves data-specific challenges for anomaly detection by pipelining a variety of methods in order to predict anomalies. While this approach is fine for solving an application, I am not convinced that it warrants a publication at ICLR, regarding in particular that the experimental evaluation does not provide any insights into why the algorithm works better than the baselines. That is,
c) I am missing experiments that show the contributions of the individual choices that were made for each stage of the detection process. E.g. how much influence does the adaptive thresholding have on the performance? (Appendix C doesn’t quantify that properly.) The same would be interesting for the other stages.
b) You state that the baseline methods are single-telemetry-based. However, you do not explain how those methods detect anomalies for multi-telemetry data as presented in Tables 3,4. Do those methods detect an anomaly whenever any of the feature/telemetry-specific methods detect one?
Also, Table 3 is not correct and doesn’t match the analysis in the text. Labels do not seem to be correct. Does Subsystem1 have 1 anomaly and Subsystem2  2?
a)
-P4: Indices for the 3 dimensions of input data X are sometimes denote I_1,I_2,I_3 and sometimes I,J,K.
-P4: the rank or number of factors is sometimes denied by lowercase r and sometimes by uppercase R, e.g. in the definition of the reconstruction error. Here, the running variable is denoted by lowercase r.
-P5, ‚Calculating anomaly score‘: Shouldn’t time samples have r dimensions instead of n?
-P5, last paragraph of Section 4: \mu should be defined by the normaliser w instead of n.


Pruning neural network parameters is often viewed as a means to compress models, but pruning has also been motivated by the desire to prevent overfitting. This motivation is particularly relevant given the perhaps surprising observation that a wide variety of pruning approaches increase test accuracy despite sometimes massive reductions in parameter counts. To better understand this phenomenon, we analyze the behavior of pruning over the course of training, finding that pruning's effect on generalization relies more on the instability it generates (defined as the drops in test accuracy immediately following pruning) than on the final size of the pruned model. We demonstrate that even the pruning of unimportant parameters can lead to such instability, and show similarities between pruning and regularizing by injecting noise, suggesting a mechanism for pruning-based generalization improvements that is compatible with the strong generalization recently observed in over-parameterized networks.

This paper mainly studies the relationship between the generalization error and mean/variance of the test accuracy. The authors first propose a new score for pruning called E[BN]. Then, the authors observe the generalization error and the test accuracy mean/variance for pruning large score weights and small score weights for VGG11, ResNet18, and Conv4 models. From these experiments, the authors observe that pruning large score weights generates instable but high test accuracy and smaller generalization gap compared to pruning small score weights. The authors additionally study some other aspects of pruning (e.g., pruning as a noise injection) and conclude the paper.
Overall, I am not sure whether the observation holds in general due to the below reasons.
- The authors proposed a new score E[BN] and all experiments are performed on this. However, how it differs from the usual magnitude-based pruning in practice is unclear. I would like to know whether similar behavior is observed for the naïve magnitude-based pruning.
- I think that the author’s observation is quite restricted and cannot extend to a general statement since the experiments are only done for pruning small score/large score weights. To verify the generalization and instability trade-off, I believe that it is necessary to examine several (artificial) pruning methods controlling the instability of test accuracies and check whether the proposed trade-off holds. For example, one can design pruning methods that disconnect (or almost disconnect) the network connection from the bottom to the top (i.e., pruned network always outputs constant) with some probability to extremely increase the instability.
- The authors did not report the results for high sparsity.
Besides, I am not sure the meaning of the instability since when the test accuracy of the pruned model is higher than that of the unpruned model, the instability could be large.
Other comments:
- The first paragraph mentions that the generalization gap might be a function of the number of parameters. However, I think that it is quite trivial that the generalization gap is not a function of the number of parameters while it only provides the upper bound.
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I have read the authors' response. Thanks for clarifying the definition of instability and additional experiments with high sparsity. However, I will maintain my score due to the following concern.
The remaining concern is that the current evidence for verifying generalization-stability tradeoff is not convincing as the authors presented only some examples having small and large instability (e.g., pruning smallest/largest weights) under the same pruning algorithm. I think that the results would be more convincing if the authors add a test accuracy plots given a fixed prune ratio, whose x-axis is controlled instabilities (e.g., from 10% to 90%) among various pruning algorithms (other than magnitude-based ones, e.g., Hessian based methods). It would be much more interesting if the same instability results same test accuracy even for different pruning algorithms.


Owing to language emergence, human beings have been able to understand the intentions of others, generate common concepts, and extend new concepts. Artificial intelligence researchers have not only predicted words and sentences statistically in machine learning, but also created a language system by communicating with the machine itself. However, strong constraints are exhibited in current studies (supervisor signals and rewards exist, or the concepts were fixed on only a point), thus hindering the emergence of real-world languages. In this study, we improved Batali (1998)  and Choi et al. (2018)'s research and attempted language emergence under conditions of low constraints such as human language generation. We included the bias that exists in humans as an "internal reflection function" into the system. Irrespective of function, messages corresponding to the label could be generated. However, through qualitative and quantitative analysis, we confirmed that the internal reflection function caused "overlearning" and different structuring of message patterns. This result suggested that the internal reflection function performed effectively in creating a grounding language from raw images with an under-restricted situation such as human language generation.

This paper proposes a framework for emergent communication system using internal reflection, similar to obverter technique in Batali 1998 and Choi et al., 2018, while not requiring explicit supervision. Despite the nice idea, the dire quality of writing makes it extremely difficult if not impossible to understand the proposed model and the results. Also, some of the experimental results seem unnecessary. In Table 3., for example, (1) in §4.4.1 the authors merely list the rules without giving an overall conclusion. (2) I'm not certain what's the significant of the results in Table 3., as these are messages from one trained instance, and I'm sure a different training run will yield different messages.
Although I am strongly leaning towards reject, I am willing to discuss with my co-reviewers if they have a different opinion.
Cons
- There doesn't seem to be a proper baseline in any of the experiments conducted.
- The writing generally is unclear, full of ungrammatical sentences and extremely hard to read: e.g. see examples below.
     - §3.2: "A language system can emerge by a pure machine, excluding the human viewpoint."
     - §3.2: "The structure, characteristics, and limitations of the messages generated by the machine can be determined."
     - §3.2: "The agents as a whole have a movement to create a system in which languages is unsupervised and one conceptual pact is formed."
     - §3.3: "Receive an image and generate a message based on self-knowledge."
     - §3.4: "This formal rule was from the human perspective".
- The evaluation section is very rambling and contains unnecessary parts that need not be included, e.g. convergence of mean squared error loss between GRU output and latent space z.
Questions
- The internal reflection function part, the core of this paper, is not properly explained until the end. For example, in §3.3, "when the comparison result is lower than the threshold value": what is the "comparison result"? How does one compare a message and another message? Please elaborate on this further.
- In the evaluation section §3.4, the authors keep referring to "dream": "correct answer rate of Dream", "We entered the message into an agent to evaluate the reconstructed Dream". But the authors don't provide a formal definition of "dream" except providing a citation to Ha and Schmidhuber, 2018. Are the readers expected to know what this means?
- In §3.4, "Jaccard coefficient were applied to test the message similarity between labels". How does one apply Jaccard index to compute similarity between labels? This seems an important part of evaluation but not explained at all.