How many training data are needed to learn a supervised task? It is often observed that the generalization error decreases as n −β where n is the number of training examples and β an exponent that depends on both data and algorithm. In this work we measure β when applying kernel methods to real datasets. For MNIST we find β ≈ 0.4 and for CIFAR10 β ≈ 0.1. Remarkably, β is the same for regression and classification tasks, and for Gaussian or Laplace kernels. To rationalize the existence of non-trivial exponents that can be independent of the specific kernel used, we introduce the Teacher-Student framework for kernels. In this scheme, a Teacher generates data according to a Gaussian random field, and a Student learns them via kernel regression. With a simplifying assumption -namely that the data are sampled from a regular lattice -we derive analytically β for translation invariant kernels, using previous results from the kriging literature. Provided that the Student is not too sensitive to high frequencies, β depends only on the training data and their dimension. We confirm numerically that these predictions hold when the training points are sampled at random on a hypersphere. Overall, our results quantify how smooth Gaussian data should be to avoid the curse of dimensionality, and indicate that for kernel learning the relevant dimension of the data should be defined in terms of how the distance between nearest data points depends on n. With this definition one obtains reasonable effective smoothness estimates for MNIST and CIFAR10.

This paper studies, empirically and theoretically, the learning rates of (shift-invariant) kernel learners in a misspecified setting. In the well-specified setting, the rate of kernel learners is at least $n^{-1/2}$, and in a misspecified setting assuming only Lipschitz targets, the rate is $n^{-1/d}$. Neither seems to match the experimental rate on MNIST and CIFAR-10; this paper proposes a theoretical model that can more-or-less match the experimental rate with essentially-reasonable assumptions.
My main complaint is on the basic setting of the work: in your motivation, you say "it is nowadays part of the lore that there exist kernels whose performance is nearly comparable to deep networks." The main such kernel, though, is the (convolutional) neural tangent kernel of Arora et al. (2019), which unlike the kernels you study here is not shift-invariant, and your theorems do not at all apply to this kernel. This is fine, but should probably be clearer in the description.
A related comment on your main theorem: your target function evaluated at every conceivable point (not just on a grid) is a sample from a Gaussian process. Samples from GPs with mean zero and covariance kernel $K_T$ almost surely are not in the RKHS $\mathcal H_T$, but they *are* almost surely in the RKHS of any kernel $K_R$ which nuclearly dominates $K_T$ (see Lukic and Beder, "Stochastic Processes with Sample Paths in Reproducing Kernel Hilbert Spaces", Trans. AMS 2001). If such a kernel exists, using it as the "student" kernel should give us a rate of at least $n^{-1/2}$ with standard results (with some slight details still to be worked out, but should be true). Thus, it seems that your theorem implies that for $\alpha_T < \frac32 d$, no such translation-invariant kernel $R$ exists. This might be already easy to see from a Fourier definition of nuclear dominance, I'm not sure, but if not it is something that seems of somewhat independent interest.
It is also notable that both your practical results and your theorem are for algorithms essentially without any regularization other than the choice of kernel: the regression setting is exact interpolation, and your soft-margin uses $C = 10^4$ so is "almost" a hard-margin SVM. This is also fine – interpolation methods have seen a lot of interest of late, and certainly can perform well. But it's not the typical setting, and it would be interesting to see if the curves of Figure 1 look different when using e.g. a cross-validated setting for the amount of regularization.
Another complaint: you argue that applying Theorem 1 with this particular notion of effective dimension seems to give good results, but at least as it's stated, Theorem 1 doesn't actually apply with effective dimension, only ambient dimension. Is it possible to prove Theorem 1 with an appropriate version of effective dimension? I didn't carefully check the proof, but from your outlined sketch it seems like it might be only a small change.
Empirically, your investigations are nice, but it would be good to consider some other shift-invariant kernels as well: inverse multiquadric, Matérn, or spline RBF kernels would be prominent options.
Overall: I think this is a worthwhile study with interesting results. The theoretical setting, though, is somewhat limited by its fundamental approach, and the experiments aren't as thorough as they could be. Also, honestly, I'm not sure ICLR is the best venue for it (if I had written this paper around this time, I probably would have submitted it to AISTATS; it's certainly not *off* topic for ICLR, but fairly distant from most work at it).
Some typos:
- Under (2): "man-square error."
- Under (25): "where where."


Neural ordinary differential equations (ODEs) have been attracting increasing attention in various research domains recently. There have been some works studying optimization issues and approximation capabilities of neural ODEs, but their robustness is still yet unclear. In this work, we fill this important gap by exploring robustness properties of neural ODEs both empirically and theoretically. We first present an empirical study on the robustness of the neural ODE-based networks (ODENets) by exposing them to inputs with various types of perturbations and subsequently investigating the changes of the corresponding outputs. In contrast to conventional convolutional neural networks (CNNs), we find that the ODENets are more robust against both random Gaussian perturbations and adversarial attack examples. We then provide an insightful understanding of this phenomenon by exploiting a certain desirable property of the flow of a continuous-time ODE, namely that integral curves are non-intersecting. Our work suggests that, due to their intrinsic robustness, it is promising to use neural ODEs as a basic block for building robust deep network models. To further enhance the robustness of vanilla neural ODEs, we propose the time-invariant steady neural ODE (TisODE), which regularizes the flow on perturbed data via the time-invariant property and the imposition of a steady-state constraint. We show that the TisODE method outperforms vanilla neural ODEs and also can work in conjunction with other state-of-the-art architectural methods to build more robust deep networks.

This paper studied the robustness of neural ODE-based networks (ODENets) to various types of perturbations on the input images. The authors observed that ODENets are more robust to both Gaussian perturbation and adversarial attacks, which the authors explained as non-intersecting of the integral curves for different initial points. Moreover, the authors proposed the time-invariant steady neural ODE (TisODE) to enhance the robustness of ODENets. I list my concerns below:
1. To show the ODENet is more robust, the authors should bound the gap between the integral curves for different inputs. Non-intersecting of the integral curves does not guarantee the robustness.
2. The ODENet architecture showed in Figure~1 can be regarded as an augmented CNN. I think the identity map gives a good trade-off between robustness and generalization. To enhance robustness, one might design an expansion map, but this, in general, hurt the accuracy of the model.
3. Why do not perform experiments on the CIFAR10 benchmark dataset? I think it is very important to add these results.
4. To verify the robustness of ODENets and CNNs, the authors should also perform adversarial training besides training on the original and noisy images with Gaussian perturbation.
5. Theorem~1 is wrong. I suggest the authors check the conditions to make it valid. We can construct an ODE of the form (1) that blows up in finite-time, e.g., dx/dt = x^2.
6. Most importantly, the authors should match the number of function evaluations of neural ODE with the depth of the CNN, in addition to matching the number of parameters. Please perform such a comparison in rebuttal. (THIS IS THE MOST IMPORTANT RESULT I WANT TO SEE IN REBUTTAL)
7. The authors did not compare with existing work that tries to improve the robustness of neural nets from a differential equation viewpoint. The related works should be elaborated.
======================
I would like to point out a few related papers that lift the dimension of ODE to a transport equation and improve the neural nets' robustness from the lens of the transport equation's theory. Also, the author should compare their results with some reported results in 1, 3, 4.
1. Bao Wang, Binjie Yuan, Zuoqiang Shi, Stanley J. Osher. ResNets Ensemble via the Feynman-Kac Formalism to Improve Natural and Robust Accuracies, arXiv:1811.10745, NeurIPS, 2019
2. Bao Wang, Xiyang Luo, Zhen Li, Wei Zhu, Zuoqiang Shi, Stanley J. Osher. Deep Neural Nets with Interpolating Function as Output Activation, NeurIPS, 2018
3. Bao Wang, Alex T. Lin, Zuoqiang Shi, Wei Zhu, Penghang Yin, Andrea L. Bertozzi, Stanley J. Osher. Adversarial Defense via Data Dependent Activation Function and Total Variation Minimization, arXiv:1809.08516, 2018
4. B. Wang, S. Osher. Graph Interpolating Activation Improves Both Natural and Robust Accuracies in Data-Efficient Deep Learning, arXiv:1907.06800
=======================
Please address the previously mentioned concerns in rebuttal.


ABSTRACT Q-learning suffers from overestimation bias, because it approximates the maximum action value using the maximum estimated action value. Algorithms have been proposed to reduce overestimation bias, but we lack an understanding of how bias interacts with performance, and the extent to which existing algorithms mitigate bias. In this paper, we 1) highlight that the effect of overestimation bias on learning efficiency is environment-dependent; 2) propose a generalization of Qlearning, called Maxmin Q-learning, which provides a parameter to flexibly control bias; 3) show theoretically that there exists a parameter choice for Maxmin Q-learning that leads to unbiased estimation with a lower approximation variance than Q-learning; and 4) prove the convergence of our algorithm in the tabular case, as well as convergence of several previous Q-learning variants, using a novel Generalized Q-learning framework. We empirically verify that our algorithm better controls estimation bias in toy environments, and that it achieves superior performance on several benchmark problems.

This paper proposes a new Q learning algorithm framework: maxmin Q-learning, to address the overestimation bias issue of Q learning. The main contributions of this paper are three folds: 1) It provides an inspiring example on overestimation/underestimation of Q learning. 2) Generalize Q learning by a new maxmin Q-learning by maintaining independent Q estimator and interact them in a max-min way for the update. 3) Provide both theoretical and empirical analyses of their algorithm.
I have two main concerns for this paper:
1) When is your algorithm useful? What's your criterion of picking the hyper-parameters (e.g. number of Q functions you want to learn).
2) Comparison to more intriguing way for jointly update of multiple Q functions, like soft Q learning.
For the first concern, the paper has shown an interesting example in Figure 2. However, it seems that we cannot decide whether overestimation or underestimation will help the exploration, since the reward function is often unknown in real world. And in both cases, maxmin Q learning is not the best algorithm than either Q learning and double q learning. On the other hand, if we use a softmax policy for Q function, e.g. $\pi(a|s) \propto \exp(\alpha Q(s,a))$, a drift for Q learning(e.g. Q(s,a) = Q*(s,a) + c) has no effect on our policy. I believe in this case we should more focusing on the inner difference between different value of Q function, rather than comparing our estimate Q function with the true Q*.
For the second concern, we can view the framework of maxmin q learning as a joint update scheme for different Q function. In experimental part, the comparison is not fair since the paper use multiple Q function to compare with single or double Q function. One reasonable baseline is to update N different Q function, and take the minimum of the final Q function as our decision policy, compare with maxmin Q learning with N different Q function. Another baseline the paper should consider is soft Q learning, where it maintain multiple Q function and jointly update Q different function to maximize the entropy while moving towards an improvement Q.
Overall, I believe the idea of the paper is novel and interesting, but further improvements should be added in order to improve the score the paper.


Generative models of natural images have progressed towards high fidelity samples by the strong leveraging of scale. We attempt to carry this success to the field of video modeling by showing that large Generative Adversarial Networks trained on the complex Kinetics-600 dataset are able to produce video samples of substantially higher complexity and fidelity than previous work. Our proposed model, Dual Video Discriminator GAN (DVD-GAN), scales to longer and higher resolution videos by leveraging a computationally efficient decomposition of its discriminator. We evaluate on the related tasks of video synthesis and video prediction, and achieve new state-of-the-art Fréchet Inception Distance for prediction for Kinetics-600, as well as state-of-the-art Inception Score for synthesis on the UCF-101 dataset, alongside establishing a strong baseline for synthesis on Kinetics-600.

Summary:
This paper presents a method for training a generative adversarial network on high resolution videos and complex datasets. They propose decomposing the discriminator in Adversarial Networks into a spatial and temporal discriminator similar to previous works, however, the temporal discriminator downsamples the input using average pooling before forwarding it through the network. In experiments, the presented method outperforms previous state-of-the-art methods in the used metrics. In addition, the videos generated from the Kinetic-600 dataset in a non-conditional setting are the most realistic looking up to date.
Pros:
+ Best generated video quality out there (In the Kinetics-600 dataset)
+ Numerically outperforms baselines in all datasets
Weaknesses / comments:
* What is the message of the paper?
- It is not clear to me whether this paper is about a new method or if it’s about an empirical study of the network size for video prediction algorithms. If the paper is about a new method, then the novelty is lacking. Decomposing the discriminator into space and time discriminators was originally proposed by MoCoGAN. Therefore, the only difference I can see is that the input to the time discriminator passes through a downsampling function (average pooling). On the other hand, if the paper is about showing that a bigger video model generates better video, the paper is lacking a more in depth evaluation. It seems that the size (frame resolution and number of frames) is only done on the Kinetics-600 dataset (Table 1). However, it is not clear to me whether there is a conclusion to be made from these results about the model size. The FID seems to favor smaller models and IS favors bigger models? But the last (biggest) model does not increase the IS? I am not sure what to make of these results. In addition, there is no such results on the other datasets (UCF101 and BAIR) or on the frame conditioned experiments for Kinetics-600. Do the authors have any comments or clarifications on this?
* Lacking proof that the network is not just overfitting to each class.
- It seems that the authors train separate models for each video class. The generated videos are the best I have seen in such complicated dataset. The authors claim that the fact that the Kinetics-600 dataset is large automatically removes the concern of overfitting. However, I would like to see  evidence that this is true. Can the authors do something like sample a video and find its nearest neighbor in the training data and compare them to see if the model is simply memorizing the training set? Something like this could serve as evidence that the network is not simply memorizing the training data.
* FVD Evaluation on Robot Push (marginal improvement based on FVD paper)
- In Table 3, the authors present quantitative comparisons for frame-conditioned video prediction with state-of-the-art methods. The authors of the FVD paper state the following:
“In Figure 5 it can be seen that when the difference in FVD is smaller than 50, the agreement with human raters is close to random (but never worse).”
The difference between DVD-GAN and SAVP / Video Transformer is below 50. Does this mean that this result may not significant? It seems that basically the top 3 methods are performing similarly. Can the authors comment on this?
* Comparing 11 frame conditional generation with 16 frame unconditional generation (DVD-GAN)?
- In Table 4, the authors are comparing DVD-GAN-FP, Video Transformer and DVD-GAN. DVD-GAN-FP clearly outperforms Video Transformer. However, the authors make a comment about the DVD-GAN result being much better than the other two and that “the synthesis model’s improved performance on this task seems to indicate that the advantage of being able to select videos to generate is greater than the advantage of having a ground truth distribution of starting frames.”. However, the DVD-GAN model generates 16 frames, and not 11 like the other 2. Is this comparison correct? Also the other 2 methods (DVD-GAN-FP and Video Transformer) are constrained by what they must predict given input frames, does this fact affect the comparison / conclusion by the authors?
* Claim of diversity but no evidence in the video prediction setting (frame conditional generation).
- The authors claim that their method generates diverse videos, however, there is no palpable evidence that this is true. Something like showing examples of different videos generated given the same condition should be good or per-frame evaluations like PSNR and SSIM with error bars of the N number of samples generated given the same condition could also serve as proof that the generation is diverse.
* Video results only provided for Kinetics-600
- It looks like the authors only provide actual video files for the un-conditional generative model for Kinetics-600. Could the authors provide videos of the frame conditioned experiments as well (UCF101, BAIR and Kinetics-600)?
* Argument in paper: “The synthesis model’s improved performance on this task seems to indicate that the advantage of being able to select videos to generate is greater than the advantage of having a ground truth distribution of starting frames”
- I do not fully agree with this argument. Optimally, a frame-conditional model should identify all objects/background observed in the input frame and object/background dynamics if multiple frames are given. Given the optimally identified factors, video generation/prediction should be much better or the same as a purely generative model. The fact that the experiments in this paper show that the conditional model is not as good as the non-conditional model is most likely due to the model and/or objective function and not the generation scenario. Do the authors have any comments on this?
Conclusion:
This paper does indeed present the best video generation up-to-date given the dataset difficulty. However, the paper itself has multiple issues as stated above. Please try to address these in the next revision.


ABSTRACT Q-learning with neural network function approximation (neural Q-learning for short) is among the most prevalent deep reinforcement learning algorithms. Despite its empirical success, the non-asymptotic convergence rate of neural Qlearning remains virtually unknown. In this paper, we present a finite-time analysis of a neural Q-learning algorithm, where the data are generated from a Markov decision process and the action-value function is approximated by a deep ReLU neural network. We prove that neural Q-learning finds the optimal policy with O(1/ √ T ) convergence rate if the neural function approximator is sufficiently overparameterized, where T is the number of iterations. To our best knowledge, our result is the first finite-time analysis of neural Q-learning under non-i.i.d. data assumption.

[Summary]
This paper studies the convergence of Q-Learning when a wide multi-layer network in the Neural Tangent Kernel (NTK) regime is used as the function approximator. Concretely, it shows that Q-learning converges with rate O(1/T) with data sampled from a single trajectory (non-i.i.d.) of an infinite-horizon MDP + a certain (stationary) exploration policy.
[Pros]
The results in this paper improve upon recent work on the same topic. It is able to handle multi-layer neural nets as opposed to two-layer, prove a faster rate O(1/T), and handle non-iid data (as opposed to iid data where (s,a,r,s’) are sampled freshly from the beginning at each step.)
The paper is generally well-written. The results and proof sketches are well presented and easy to follow. The proof seems correct to me from my check, including the indicator issue pointed out in the comments which I think can be easily fixed (by explicitly writing out the indicator and thus the Cauchy-Schwarz will still apply.)
[Cons]
The result in this paper seems more or less like a direct combination of existing techniques, and thus may be limited in bringing in new techniques / messages. Key technical bottlenecks that are assumed out in prior work are still assumed out in this paper with potentially different forms but essentially the same thing.
More concretely, the proof of the main theorem (Thm 5.4) seems to rely critically on Lemmas 6.2 and 6.3, both of which are rather straightforward adaptations of prior work:
Lemma 6.2 (concentration of stochastic gradients on linearized problem): Seems to me like almost the same as [Bhandari et al. 2018], expect that now the network is an affine function---rather than a linear function---of \theta, where the additional constant term f(\theta_0; s, a) depends on (s, a).
Lemma 6.3 (good landscape of linearized problem): Comparing with prior work (Theorem 6.3, Cai et al. 2019), this Lemma works by directly assuming out the property of the arg-max operator in Assumption 5.3, which has a slightly different form from, but is essentially the same thing as (Assumption 6.1, Cai et al. 2019).
To be fair, the paper has to deal with the linearization error of a multi-layer net, which is dealt with in Lemma 6.1 and should be valued. But still I tend to think the above adaptations are rather straightforward and technically not quite novel.
[Potential improvements]
I would like to hear more from the authors about the technical novelty in this paper, specifically how Lemma 6.1 - 6.3 compare with prior work. I would be willing to improve my evaluation if this can be addressed.


This paper presents a new Graph Neural Network (GNN) type using feature-wise linear modulation (FiLM). Many standard GNN variants propagate information along the edges of a graph by computing "messages" based only on the representation of the source of each edge. In GNN-FiLM, the representation of the target node of an edge is additionally used to compute a transformation that can be applied to all incoming messages, allowing feature-wise modulation of the passed information.
Results of experiments comparing different GNN architectures on three tasks from the literature are presented, based on re-implementations of baseline methods. Hyperparameters for all methods were found using extensive search, yielding somewhat surprising results: differences between baseline models are smaller than reported in the literature. Nonetheless, GNN-FiLM outperforms baseline methods on a regression task on molecular graphs and performs competitively on other tasks.

The paper proposes a new Graph Neural Network (GNN) architecture that uses Feature-wise Linear Modulation (FiLM) to condition the source-to-target node message-passing based on the target node representation. In this way, GNN-FiLM aims to allow a GNN's message propagation to "focus on feature that are especially relevant for the update of the target node." The authors clearly describe prior GNN architectures, showing that the do not incorporate such forms of message propagation. The authors then describe several intuitive ways of adding such a form of message propagation, before describing why those approaches do not work in practice. Finally, the authors introduce GNN-FiLM, which is computationally reasonable and works well in practice, as evaluated according to several GNN benchmarks. The GNN-FiLM model is also quite simple and elegant, which makes me think it is likely to work on more tasks than the authors experiment on.
The paper is clear and easy to follow. The authors' description of other GNNs architectures is clear, and their own approach seems well motivated and clearly described in relation to previous GNNs.
The authors have released the code for method, where they have also reimplemented several popular GNN methods. The open-source codebase also seems to be valuable contribution for future research and reproducibility in work on GNNs.
The empirical evaluation seems thorough. GNN-FiLM works well on 3 graph tasks (PPI, QM9, VarMisuse) with different properties. To compare models, the authors conduct a search of hyperparameter ranges for each model. The authors even improve several of the baseline methods, generalizing some approaches to include different edge types and to add self-loops, as well as using better networks (adding dropout and increasing hidden dimensions). The paper even finds that one existing/obvious GNN architecture (GNN-MLP) is underrated. The paper reads like an honest analysis of existing methods, even though it also introduces its own, new method that works better.
Questions:
* Do you have any intuition about why the Eqn. 5 model is less stable than GNN-FiLM?
* On GNN-FiLM's training stability and regularization: I am interested in the negative result described in the following sentence: "Preliminary experiments on the citation network data showed results that were at best comparable to the baseline methods, but changes of a random seed led to substantial fluctuations (mirroring the problems with evaluation on these tasks reported by Shchur et al. (2018))" Do the authors have any intuition about why the results are highly dependent on the random seed? The results on other tasks seems to not have much variance. It could be interesting to try various techniques to stabilize learning on that task. A simple approach like gradient clipping might work, or there are perhaps other techniques. For example, in "TADAM: Task dependent adaptive metric for improved few-shot learning", the authors find it important to regularize FiLM parameters \gamma and \beta towards 1 and 0, respectively, which may make learning more stable here. In general, previous work seems to find it important to regularize the parameters that predict FiLM parameters, which may also fix GNN-FiLM's overfitting on VarMisuse. Exploring such approaches could make it easier for future work to use FiLM with GNNs.
* On potential related work: GNN-FiLM is a "self-conditioned" model which learns to apply feature-wise transformations based on the activations at the current layer. If I am not mistaken, the self-conditioning aspect of GNN-FiLM makes it related to the self-conditioned models described in "Feature-wise Transformations" ([Feature-wise transformations](https://distill.pub/2018/feature-wise-transformations/)) - for example, see the "Image Recognition" section (Squeeze-and-Excitation Networks and Highway Networks) and the "Natural Language Processing" section (LSTMs, gated linear units, and gated-attention reader). Do the authors see a connection with such models? If so, it would be interesting to hear these works discussed (in the rebuttal and paper) and the exact connection described.


An important research direction in machine learning has centered around developing meta-learning algorithms to tackle few-shot learning. An especially successful algorithm has been Model Agnostic Meta-Learning (MAML), a method that consists of two optimization loops, with the outer loop finding a meta-initialization, from which the inner loop can efficiently learn new tasks. Despite MAML's popularity, a fundamental open question remains -is the effectiveness of MAML due to the meta-initialization being primed for rapid learning (large, efficient changes in the representations) or due to feature reuse, with the meta initialization already containing high quality features? We investigate this question, via ablation studies and analysis of the latent representations, finding that feature reuse is the dominant factor. This leads to the ANIL (Almost No Inner Loop) algorithm, a simplification of MAML where we remove the inner loop for all but the (task-specific) head of the underlying neural network. ANIL matches MAML's performance on benchmark few-shot image classification and RL and offers computational improvements over MAML. We further study the precise contributions of the head and body of the network, showing that performance on the test tasks is entirely determined by the quality of the learned features, and we can remove even the head of the network (the NIL algorithm). We conclude with a discussion of the rapid learning vs feature reuse question for meta-learning algorithms more broadly.

This paper is exploring the importance of the inner loop in MAML. It shows that using the inner loop only for the classifier head (ANIL) results are comparable to MAML. It also shows that using no inner loop at all (NIL) is okay for test time but not for training time.
It is indeed interesting to understand the effect of the inner loop. But, as the authors noted (“Our work is complementary to methods extending MAML, and our simplification and insights could be applied to such extensions also”), for it to be useful I’d like to see whether these insights can be extended to SOTA models. MAML is less than 50% accuracy on 1-shot mini-imagenet while current SOTS models achieve 60-65%.
The NIL experiment that shows low performance when no inner loop is used in training time doesn’t make sense. This is basically the same as the nearest-neighbour family of methods, e.g. ProtoNet (Snell et al., 2017), which have been shown to perform similarly to (or even better than) MAML.
After rebuttal:
I do think it's important to also have that kind of analysis works. My main concern is with how ANIL and NIL are introduced as new algorithms and not just an ablation of the MAML method. Presented as new algorithms I tend to compare them against the leaderboard where they are very far from the top. I am keeping my previous rating.


Sequence-to-sequence models such as transformers, which are now being used in a wide variety of NLP tasks, typically need to have very high capacity in order to perform well. Unfortunately, in production, memory size and inference speed are all strictly constrained. To address this problem, Knowledge Distillation (KD), a technique to train small models to mimic larger pre-trained models, has drawn lots of attention. The KD approach basically attempts to maximize recall, i.e., ranking Top-k" tokens in teacher models as higher as possible, however, whereas precision is more important for sequence generation because of exposure bias. Motivated by this, we develop Knowledge Acquisition (KA) where student models receive log q(y t |y <t , x) as rewards when producing the next token y t given previous tokens y <t and the source sentence x. We demonstrate the effectiveness of our approach on WMT'17 De-En and IWSLT'15 Th-En translation tasks, with experimental results showing that our approach gains +0.7-1.1 BLEU score compared to token-level knowledge distillation.

[Overview]
In this paper, the authors proposed a new method called knowledge acquisition (KA) for distilling the learned knowledge from the teacher model to the student model. Unlike the conventional KL-divergence based knowledge distillation method, the authors take the reverse version which learns the student to increase the precision. The paper gave a thorgough analysis on the proposed KA strategy and compared with other strategies like KL and JS divergence. On the sequence generation task (translation), the authors showed that the proposed KA strategy achieved better performance compared with KD based methods when distilling the knowledge from a teacher model to a student model.
[Pros]
1. The authors proposed a new strategy to perform the knowledge distillation from a teacher model to student model for sequence generator. To improve the precision of the student model, the authors proposed to invert the formula of KL divergence, i.e., the position of prediction probability from teacher and student models.
2. The authors presented a thorough analysis on the proposed KA strategy and compared it with KL strategy in terms of the precision and recall for the student models. I think it is very readable and understandable. This analysis align with those put on generative adversarial network.
3. The authors performed the experiments on the translation tasks showing that the proposed KA strategy outperforms both KL and JS strategy in terms of the generation performance. Also, the authors ablated the number of top reference tokens from the teacher model and showed that using a reasonable number of top tokens is important to help alleviate the noised in the teacher model.
[Cons]
The main concern about the proposed method is whether it can be used as a generic strategy for transferring the knowledge from the teacher model to student model.
1. First, I have a doubt on the stability of the proposed strategy. In my opinion, the improvements on the sequence generation tasks are mainly due to the tuned hyper parameters for the training, especially the lambda in Eq(12), which is tuned at the validation set. It controls how much to modulate the prediction distribution of student model toward that of teacher model. However, a less tuned lambda would cause either over curve fitting or under curve fitting. As a result, the authors should: 1) first show how the performance would be affected by varying the lambda in the formula; 2) from the reading, I did not see whether the lambda was tuned as well for KD or (KD + KA) / 2. If not, then for fair comparison, the authors should tune the lambda for the KD and (KD + KA) / 2 strategy as well. At some point, I would think the combination of KD and KA would be better than either of them.
2. Second, some experimental results are somewhat counter-intuitive to me. These are two folds: a) In Figure 4(b), we can see that the KA strategy has learned to generate more new tokens compared with KD. This is a bit strange to me because, KA will focus on the precision instead of recall. To me, pushing the precision will high likely sacrifice the recall and thus the number of novel tokens generated by the model. b) similarly, in Figure 5, it is shown that KA has generally higher entropy than KD. This is also a bit counter intuitive. In Eq(6), it is obvious that the proposed strategy has a entropy term which will be reduced when we want to reduce the KL divergence during the training time. From Figure 5, KA and KD start from the same point (I guess it is because the same pre-trained student model) is used. However, for KA, the entropy start to increase and then converge to a stable number which is consistently higher than KD strategy.
3. Third, Figure 4(a) also indicates some thing. When only the top few tokens are used to transfer the knowledge from teacher model to student model, KA focus on the precision of a small subspace, which tends to have few modes. However, when the number of tokens is increased, the mode number would also increase drastically. i guess that’s why the both strategies finally become very close to each other, and the minor gap between them is probably due to the benefit from hyper-parameter fine-tuning.
Besides the above comments. there are some minor points which are missed in the paper:
1. As pointed above, it is not clear whether the same tuning is also applied to KD and (KD + KA) / 2. the authors should mention this in the experiment section.
2. It is also not clear how many tokens is used for reporting the numbers in Table 2. Is it the whole vocabulary side? If this is the case, the gap between KA and KD on validation set are pretty close while more significant on test set.
3. In Eq (11), should there be a minus sign before the expectation?
4. Also, is there any more comment on why it is hard to train the student model joint from scratch? what will happen in this case?
[Summary]
In this paper, the authors proposed a new strategy called Knowledge Acquisition which is used for distilling the knowledge learned from  teacher model to the student model. Different from KD strategy, it inverted the position of probability distributions for teacher and student models. By this way, the KA strategy learns a student model which can achieves higher precision. The proposed strategy is evaluated on sequence generation, particularly translation task.  However, as pointed above, in my opinion, there are some counter-intutive observations in the experimental results. It would be good if the authors can address these concerns in the rebuttal.


Knowledge-grounded dialogue is a task of generating an informative response based on both discourse context and external knowledge. As we focus on better modeling the knowledge selection in the multi-turn knowledge-grounded dialogue, we propose a sequential latent variable model as the first approach to this matter. The model named sequential knowledge transformer (SKT) can keep track of the prior and posterior distribution over knowledge; as a result, it can not only reduce the ambiguity caused from the diversity in knowledge selection of conversation but also better leverage the response information for proper choice of knowledge. Our experimental results show that the proposed model improves the knowledge selection accuracy and subsequently the performance of utterance generation. We achieve the new state-of-the-art performance on Wizard of Wikipedia (Dinan et al., 2019) as one of the most large-scale and challenging benchmarks. We further validate the effectiveness of our model over existing conversation methods in another knowledge-based dialogue Holl-E dataset (Moghe  et al., 2018).

Post author response edit: The authors did a good job of addressing many of the concerns of reviewers. I believe with these new results (esp to reviewer 4), they will have a stronger version for the camera ready. I'm bumping up my recommendation for this reason.
The authors propose a novel architecture for selecting knowledge in knowledge-grounded multi-turn dialogue. Their knowledge selection module uses a sequential latent variable scheme, and is claimed to be able to both handle diversity of knowledge selection in conversation as well as leverage the information from the response. The proposed model yields state of the art on two relevant benchmark datasets in terms of perplexity and F1, and scores higher in human evaluations as well.
The paper is relatively well-written, and the authors offer extensive insight into their approach, providing relevant equations and diagrams where necessary. The approach is well-motivated, and the experiments indicate that the model indeed helps on all evaluation fronts. A variety of baselines are considered and are shown to be inferior, in nearly every metric. I did not spend a lot of effort to try to understand their factorization, but the intuition makes sense, and their use of gumbel softmax provides a clear avenue to fix some of the hard-backprop issues apparent in the original Dinan et al. paper. I also appreciate the addition of the knowledge loss to the PostKS baseline: it’s a good effort to make the baseline as good as possible.
A few things bother me with the paper. The primary one is it concerns me a bit that the BERT pretraining does not improve significantly over the E2E transformer memnet (with just bert vocabulary). Unless I’m missing something, that model contained NO pretraining, so I would expect massive improvements. A sanity check there would be checking ppl with gold knowledge: if that doesn’t significantly improve, then I suspect the authors have something really weird about the pretraining or fine tuning. However, It also appears to me that replacing the GRU with a transformer in PostKS might be unfair: Transformers are way more data hungry than RNNs, and so both variants should be tried (though I would be okay with the loser being relegated to a footnote or appendix).
The human evaluations are not as convincing as the authors propose them to be, especially the difference in the “Test Seen” case. It is unclear to me why the authors believe that their “model’s merit would be more salient” in a multi-turn setting, and I think such an experiment would be good to show - or, at the very least, an indication that such an experiment was tried but results were not considered due to reasons X,Y, Z, etc. Overall, the rough improvement that is being provided in the first-stage of the two stage setting seems rather minor (23% -> 26% accuracy; 2.21 -> 2.35 human eval), and that the task remains extremely difficult
Questions
* I know the Dinan et al. models, at human evaluation time, hardcoded to not pick the same knowledge twice. Do you have a similar restriction? If not, maybe you can at least say that you manage to get rid of the need for that!
* As mentioned earlier, I would be curious to see multi-turn human evaluations. I understand this is expensive and a large ask.
* How are the examples in figure 3 chosen? Are they generally indicative of what is seen throughout the human evaluation?
* It would be useful to see a qualitative example of the model’s knowledge selection process when comparing to other models, rather than just the utterance generation (which is not the novel contribution of the paper).
Nits
* Small grammatical errors dealing with subject-verb agreement (plurals mostly).
* Using “-” instead of n/a in tables would make it mildly easier to see digest and see where metrics don’t make sense.


Current artificial neural networks (ANNs) can perform and excel at a variety of tasks ranging from image classification to spam detection through training on large datasets of labeled data. While the trained network usually performs well on similar testing data, certain inputs that differ even slightly from the training data may trigger unpredictable behavior. Due to this limitation, it is possible to generate inputs with very small designed perturbations that can result in misclassification. These adversarial attacks present a security risk to deployed ANNs and indicate a divergence between how ANNs and humans perform classification. Humans are robust at behaving in the presence of noise and are capable of correctly classifying objects that are occluded, blurred, or otherwise distorted. It has been hypothesized that sleep promotes generalization and improves robustness against noise in animals and humans. In this work, we utilize a biologically inspired sleep phase in ANNs and demonstrate the benefit of sleep on defending against adversarial attacks as well as increasing ANN classification robustness. We compare the sleep algorithm's performance on various robustness tasks with two previously proposed adversarial defenses, defensive distillation and fine-tuning. We report an increase in robustness after sleep to adversarial attacks as well as to general image distortions for three datasets: MNIST, CUB200, and a toy dataset. Overall, these results demonstrate the potential for biologically inspired solutions to solve existing problems in ANNs and guide the development of more robust, human-like ANNs.

Disclosure on reviewer's experience: I am not an expert on adversarial attack methods or defenses, but I am well read in the general literature on robustness and uncertainty in deep neural networks.
The authors present a biologically inspired sleep algorithm for artificial neural networks (ANNs) that aims to improve their generalization and robustness in the face of noisy or malicious inputs. They hypothesize that "sleep" could aid in generalization by decorrelating noisy hidden states and reducing the overall impact of imperceptible perturbations of the input space. The proposed sleep algorithm broadly involves 1) converting the trained ANN to a "spike" neural network (SNN), 2) converting the input signal (pixels) to a Poisson distributed "spike train" where brighter pixels have higher firing rates than darker pixels, 3) propagating the neuronal spikes through the SNN, updating weights based on a simplified version of spike-timing-dependent plasticity (STDP), and 4) converting the network back to an ANN after the sleep phase has finished. They present a detailed comparative study spanning three datasets, four types of adversarial attacks and distortions, and two other baseline defense mechanisms, in which they demonstrate significant improvements (in some cases) of the sleep algorithm over the baselines.
The core concept behind the authors' work is novel and interesting, and the experimental design is thorough and well controlled. Although the results are (I would argue) somewhat mixed, they are nonetheless positive enough to encourage more work in applying "sleep" and other relevant ideas from neuroscience to the problem of robustness in deep neural networks. I have some questions and concerns which I will detail per-section below, but overall, I believe that this paper is a valuable contribution to the literature and should be accepted once the authors have made a few necessary revisions.
Section 1: Introduction
"We report positive results for four types of adversarial attacks tested on three different datasets (MNIST, CUB200, and a toy dataset) ..."
It's debatable whether or not the results from the CUB-200 dataset are positive. The sleep algorithm fails to outperform the baselines for each attack type (except for an almost negligible advantage in accuracy on JSMA) and barely even outperforms the control network in most cases (2/4 attacks it actually underperforms the control). I think the authors should consider rephrasing this statement to better reflect the actual results.
Section 2: Adversarial Attacks and Distortions
FGSM: The notation used here is somewhat inconsistent with the source paper. Goodfellow et al use epsilon to denote what I think the authors call eta, and call the second term, epsilon*sign(grad(J)), eta. Furthermore, the authors state that "this represents the direction to change each pixel in the original input in order to decrease the loss function." But this doesn't make sense. An adversary should want to *increase* the loss function enough to cause a misclassification. Goodfellow et al use this expression to formulate a L1-like regularization term and describe the training procedure "minimizing the worst case error when the data is perturbed by an adversary", which seems more sensible. This section should be rewritten to be more consistent with the source.
Section 3: Adversarial defenses
Regarding distillation: "We use T=50 to compare with the sleep algorithm"
The authors should elaborate a bit more on the reasoning for this choice. It seems very arbitrary.
Sectioin 4: Sleep algorithm
1. Algorithm 1: Why is line 9 inside of the for loop? It doesn't seem to be at all dependent on t. One would expect the input to only need to be converted once. Additionally, in lines 11-13, the l's in W(l,l-1) and similar should be unbolded. It's confusing that the format changes (unless I am missing something and it's actually a different variable).
2. Spike trains should be more rigorously defined, preferably with formalized notation. It's a bit unclear exactly what they are from the current text. Are they just parameters for a Poisson? Or outputs from a poison over T time steps? Or something else?
3. "weights are scaled by a parameter to induce high firing rates in later layers"
It would be good to include more details on this parameter, how the values are chosen, and the intuition behind this idea. I assume it's because of higher level feature representations in later layers of deep neural networks.
Section 5: Results
1. It's confusing that sometimes accuracy refers to classification accuracy and sometimes adversarial attack accuracy. I would recommend assigning a different name to the latter, or making sure that a qualifier precedes every reference to "accuracy" in this section.
2. In the second section of the results table (which is missing a label), why is the JSMA value for Defensive Distillation bolded? The distance measures for both the control network and for fine-tuning are higher. It seems like fine-tuning should be the one bolded.
3. Figure 1: caption is incorrect; it states "adversarial attack accuracy" and it should be "classification accuracy", otherwise the plots make no sense.
4. "we observe that in the Patches and CUB-200 dataset, sleep has beneficial results in moving the accuracy function above the other defense methods"
It should be noted that this is only true for eta < 0.1. After that, sleep and the control both converge to 50% accuracy. Also this sentence should be reworded to be less visual and more quantitative (e.g. sleep tends to have higher median accuracy scores than the other methods for eta < 0.1).
5. "We observe that performance continued to drop after a sufficiently large amount of noise was added"
More than that, the other methods converged to a small band of accuracy values; sleep continued to deteriorate. This is a significant difference. It would be a good idea to re-run this experiment with a binary classification problem (e.g. only two digits of MNIST) and see if this phenomenon still occurs. Then, the noisy sleep classifier predictions could simply be inverted to get improved accuracy scores.
6. In the analysis of JSMA, as noted before,, it's rather dubious to claim that sleep had any kind of significant effect on the attack success rate (or distance) for CUB-200. I would rewrite this section to better represent the results.
7. Figure 2 formatting: Legend is overflowing out of the first figure. Additionally, the legend colors should be made to match across all three figures, and the legend should either appear in all three (if necessary for some reason) or only in one.
8. Figure 2: The caption is incomplete and possibly incorrect. It's not clear why the first and last figures differ from each other, and the caption does not indicate this. The caption also only mentions two datasets, even though it says "for the following three datasets".
Appendix:
General formatting needs improvement. A lot of figures are off-centered, text misaligned, missing axis labels, etc.


Weakly supervised localization (WSL) aims at training a model to find the positions of objects by providing it with only abstract labels. For most of the existing WSL methods, the labels are the class of the main object in an image. In this paper, we generalize WSL to counting machines that apply convolutional neural networks (CNN) and density maps for counting. We show that given only ground-truth count numbers, the density map as a hidden layer can be trained for localizing objects and detecting features. Convolution and pooling are the two major building blocks of CNNs. This paper discusses their impacts on an end-toend WSL network. The learned features in a density map present in the form of dots. In order to make these features interpretable for human beings, this paper proposes a Gini impurity penalty to regularize the density map. Furthermore, it will be shown that this regularization is similar to the variational term of the β-variational autoencoder. The details of this algorithm are demonstrated through a simple bubble counting task. Finally, the proposed methods are applied to the widely used crowd counting dataset the Mall to learn discriminative features of human figures.

This paper presents a method to train a network for counting/localizing objects in a weakly supervised framework.
The network is optimized based on weak supervision about target object counts; training images have only the ground truth of the total number of object counts without their positions in images.
Through analyzing the feature maps of the network trained on toy bubble images, the authors propose two regularization techniques for rotation robustness and sparseness of the map in order to improve  performance of object localization in the feature map.
The experimental results on object counting tasks using the Mall dataset show that the proposed method produces favorable performance.
This paper is leaning toward rejection due to the following two reasons.
(1) The presented techniques are limited to the specific task of object counting.
(2) They are derived in an ad-hoc way based on less theoretical background and thus lack novelty.
The detailed comments are as follows.
* The technique to embed rotation invariance by Eq.(4) is presented in an ad-hoc way. This seems to be limited to the tasks on toy data such as bubble images shown in the paper. In the real-world tasks/images to count the more complicated objects, the spatial correlation among object parts is an important clue to provide discriminative features for detecting objects such as torso below the head in human figures. Such spatial dependency could be missed by imposing the rotation invariance on the network.
* The regularization by Gini impurity is a well-known technique to induce sparsity, lacking novelty. There is a large body of researches for enhancing sparsity, and thus to validate the regularization, the authors should compare the Gini impurity with the other sparsity-inducing regularization such as entropy. For example, it could be possible to argue the regularizations in terms of their derivatives (gradients) to be used for back-propagation. This paper lacks detailed analysis and discussion about the regularization in this counting framework.
* It is unclear how the perspective from the (beta-)VAE contributes to the analysis of the proposed method. There seems to be less connection between Eq.(8) and the object counting task/framework. The authors just show the similarity between the presented method and VAE in terms of formulation. Since the proposed method belongs to just a simple optimization with sparsity-inducing regularization, the reviewer cannot find any convincing reason to discuss the connection to VAE.
* The method is not fully validated in the experiments. The authors provide only one experimental result on the Mall dataset which is insufficient to validate the effectiveness of the proposed method. Considering that the method is limited to the specific task of object counting, it is necessary to qualitatively and thoroughly evaluate the performance on various datasets that exhibit various environmental conditions regarding such as lighting and occlusion.
Minor comments:
- Show the index for summation in Eqs.(1,4,6,7,8).
- It is confusing to show q_\Theta(D|I) in Eq.(3), even though the authors aim to discuss the connection to VAE. Show the mathematical definition of q_\Theta(D|I) before that.


Proteins are ubiquitous molecules whose function in biological processes is determined by their 3D structure. Experimental identification of a protein's structure can be time-consuming, prohibitively expensive, and not always possible. Alternatively, protein folding can be modeled using computational methods, which however are not guaranteed to always produce optimal results. GRAPHQA is a graph-based method to estimate the quality of protein models, that possesses favorable properties such as representation learning, explicit modeling of both sequential and 3D structure, geometric invariance and computational efficiency. In this work, we demonstrate significant improvements over the state-ofthe-art for both hand-engineered and representation-learning approaches, as well as carefully evaluating the individual contributions of GRAPHQA components.

The paper proposes use of graph convolutional networks (GCN) for quality assessments (QA) of protein structure predictions. In particular, protein structure prediction is a very active area of research witnessing steady progress during the previous decade or so. To estimate the quality of the prediction, many experimentally resolved structures are needed. However, experimental structure determination is expensive and many protein families are notoriously hard to experiment with. Thus, current estimates of the quality of the protein structure prediction models are incomplete and biased. As a result, there is an interest in guessing quality of protein structure predictions on protein families that are not characterized experimentally. Previous papers already proposed several neural network architectures for the QA task. This paper shows that GCN applied on a graph of a predicted protein structure achieves higher accuracy than the previously proposed neural networks
Strengths:
+ The proposed GCN outperforms other neural network baselines.
+ The protein representation is reasonable.
+ The paper is reasonably well written with a nice overview of the related work.
+ Ablation studies are well done, in clean graphs. This can be useful for other authors who work with GCNs.
Weaknesses:
- Methodological novelty is low -- this is a straightforward application of GCN
- The objective of QA is a bit suspect for the sole reason that the training and testing is performed using experimentally resolved protein structures. This data set is biased and there are no guarantees that the reported accuracy will hold over a vast range of protein families that are not structurally characterized.
- Separation encoding is done as a one-hot vector. This could probably be passed as a scalar value. Would be nice to have comparison between 1-hot vs scalar in the experimental results
- Formulas in section 2.3 are cryptic for audience unfamiliar with GCN and it is not specific to this application.
- Figure 3b) shows that there is a cluster of predicting 0 where the ground truth is bigger than 0.6.
Overall, this is a borderline paper. There is little methodological novelty and the QA application is a bit of a niche problem in bioinformatics. However, the results show a decent improvement over the state of the art in this particular application, so this paper might be of importance for a limited audience interested in this problem. Giving this work a benefit of the doubt the entered rating is a weak accept.


We tackle the problem of modeling sequential visual phenomena. Given examples of a phenomena that can be divided into discrete time steps, we aim to take an input from any such time and realize this input at all other time steps in the sequence. Furthermore, we aim to do this without ground-truth aligned sequences -avoiding the difficulties needed for gathering aligned data. This generalizes the unpaired image-to-image problem from generating pairs to generating sequences. We extend cycle consistency to loop consistency and alleviate difficulties associated with learning in the resulting long chains of computation. We show competitive results compared to existing image-to-image techniques when modeling several different data sets including the Earth's seasons and aging of human faces.

This paper introduces the LoopGan, which aims to enforce consistency in a sequential set of images but without aligned pairs.  The prototypical example used in the paper is a network to transform seasonal images, where Summer -> Fall -> Winter -> Spring -> Summer -> etc.
I suggest rejecting the paper.
While the idea has some merit, it is an interesting premise to train a recurrent generator to create images in multiple domains, I feel as though the experiments are quite lacking.  The primary evidence the method works is Figure 3, for which we see only 4 examples of the method on two tasks.  Looking at the results they don't look all that great and the proposed method is hard to identify as the best.
The idea doesn't strike me as particular innovative, feeling like a natural extension of the prior work listed.
Table 1 shows the results of a user study with 20 users.  With only 20 users rating 4 examples of each method we get very little power to resolve the best method, and the papers proposed method is selected in aggregate only 26% of the time out of 6 methods, this is hardly a clear winner.
Figure 4 showing the imputed ages for the generated images doesn't seem that strong of evidence the proposed method is that much better either.  The histograms are difficult to compare by eye, perhaps the paper should report computed estimates of the kl divergence between the two?
The ablation studies of section 6 are out of place.  The paper does not compare against the incremental removal of its' proposed loss, it simply reports results of alternative architectures.


Generative Adversarial Networks (GANs) have shown impressive results in modeling distributions over complicated manifolds such as those of natural images. However, GANs often suffer from mode collapse, which means they are prone to characterize only a single or a few modes of the data distribution. In order to address this problem, we propose a novel framework called LDMGAN. We first introduce Latent Distribution Matching (LDM) constraint which regularizes the generator by aligning distribution of generated samples with that of real samples in latent space. To make use of such latent space, we propose a regularized AutoEncoder (AE) that maps the data distribution to prior distribution in encoded space. Extensive experiments on synthetic data and real world datasets show that our proposed framework significantly improves GAN's stability and diversity.

It is argued in this paper that GANs often suffer from mode collapse, which means they are prone to characterize only a single or a few modes of the data distribution. In order to address this problem, the paper proposed a framework called LDMGAN which constrains the generator to align distribution of generated samples with that of real samples in latent space by introducing a regularized AutoEncoder that maps the data distribution to prior distribution in encoded space.
The major difference of this paper from many traditional GANs is to constrain the distributions of generated data same as distributions of true data in latent space instead of constrain the ability of discriminator. The authors detailed their motivation, the algorithm, and also reported a series of evaluation results on several datasets.
Generally, this paper was well written. However, this paper has the following major concerns:
	（1） Though somewhat new, the novelty of this paper may be incremental to me. It looks like a combination of VEEGAN and AAE.  Though the authors mentioned that VEEGAN autoencoded the noise vectors rather than data items, and AAE exploited the adversarial learning in the encoded space rather than using an explicit divergence,   it appears not significant to me between the proposed model and these two models. At least the authors did not  address sufficiently how significant the proposed method would be.
	 （2） The paper tested the proposed algorithm with a 2D Synthetic dataset. However, I found a lot of discrepancies in the results presented in Table 1 with other published works. The authors show 1 of mode captured on 2D Grid and 2D Ring using the VEEGAN method. However, the VEEGAN paper shows they get 24.6 and 8 on 2D Ring and 2D Grid respectively. Such discrepancies were also observed in Figure 3. These discrepancies must be explained.
	（3） In Figure 4, the authors showed the distribution of MODE scores for GAN and LDMGAN. From the figure, it seemed that LDMGAN improved the sample quality and diversity compared to GANs, but it is still prone to characterizing only a single or a few modes of the data distribution. In another word,  this may alleviate the problem but may not fully solve the problem.  Another minor point, the coordinate and legend are too small in this figure. It would be better if they become bigger.
	（4） The results of Table 4 is not convincing because the comparative methods are truly out-of-date. It would be more convincing if more latest methods can be compared with LDMGAN method. Those results reported are far lower than the state-of-the-art performance in these datasets.
         (5) There is a mistake in the second term of equation 11, it should be ⋯〖-D〗_KL (p^* (y)||p(y))  )


Graph Neural Networks (GNNs) are deep models that operate on data with arbitrary topology represented as graphs. We introduce an efficient memory layer for GNNs that can jointly learn node representations and coarsen the graph. We also introduce two new networks based on this layer: Memory-Based Graph Neural Network (MemGNN) and Graph Memory Network (GMN) that can learn hierarchical graph representations. The experimental results shows that the proposed models achieve state-of-the-art results in eight out of nine graph classification and regression benchmarks. We also show that the learned representations could correspond to chemical features in the molecule data.

The paper proposes to use memory network (self-attention) to summarize information from graphs. The proposed approach "soft clusters" the node embeddings into coarser representation and eventually fed to a final MLP for classification. The empirical results on some standard datasets show promising gains of the algorithm.
The proposed approach stacks a few layers of self-attention on top of either some features of the nodes (including projected edge connections, parametrized by W_0) or the node embeddings of some form of graph neural network. And this stacking seems to be simple combination of existing approaches, without fully integrating them. In fact, the training process is also separated: "task-specific loss are back-propagated batch-wise while the gradients of the unsupervised loss are applied
epoch-wise". It makes me wonder whether we can just separate it into two stages, i.e., first learn a node embedding using graph neural network, then learn this self attention transformation. Due to the above issues, I feel the novelty of the approach is limited and incremental.
Another issue with the paper is that the notations seem to be messed up and some concepts are not explained clearly. For example, the C_{i,j} soft assignment matrix is normalized row-wise, then Eqn (3) seems very suspicious, because it averages the queries using weights along the other direction, thus not normalized. Also, the dimension of the MLP weights do not align well with inputs, for instance in Eqn (4), it should be written as V^(l) W.
There are more questions that are not clearly specified in the current manuscript. For example, where does the keys K come from? From the text description, it seems to be cluster results, and do you do the clustering on every gradient update? Or are they learned from scratch? The distribution P defined in Eqn (11) also seems to be difficult to optimize since it depends on C_{i,j} and is connected to different entries. Is simple SGD sufficient to optimize over P? Moreover, in the experiment section, it is unknown how many layers of self-attention is applied and what are the important parameters. For better comparison, the experiment section should include some estimate of parameter size as well.
The experiment results seem interesting since the approach indeed achieves good performance across many datasets. Also the visualized keys are interesting as well because it captures some meaningful patterns from the data.
There is some related work that you should cite:
Hanjun Dai, Bo Dai and Le Song. Discriminateive Embeddings of Latent Variable Models for Structured Data. International Conference on Machine Learning (ICML) 2016.
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Based on the authors' reply and other reviews, I have changed my rating to "Weak accept".
The authors' reply has clarified the important detail of how the key matrix is learned and now it is clear that the algorithm is not just two-stage separate learning. In light of this clarification, I think the proposed algorithm is novel enough and the jointly training mechanism is also beneficial for the state-of-the-arts results reported in the experiments.


We present a proof of convergence for ReLU networks trained with weight normalization. In the analysis, we consider over-parameterized 2-layer ReLU networks initialized at random and trained with batch gradient descent and a fixed step size. The proof builds on recent theoretical works that bound the trajectory of parameters from their initialization and monitor the network predictions via the evolution of a "neural tangent kernel" (Jacot et al. 2018). We discover that training with weight normalization decomposes such a kernel via the so called "length-direction decoupling". This in turn leads to two convergence regimes and can rigorously explain the utility of WeightNorm. From the modified convergence we make a few curious observations including a natural form of "lazy training" where the direction of each weight vector remains stationary.

*Summary of the contributions:*
This paper deals with convergence, of the hidden layer of a 2-layers Relu Network trained with Weight Normalization which consists in decoupling the direction and the magnitude for the pre-activation layers. The authors show, under mild assumption, the linear convergence (with high probability) of the training loss in the over-parameterized setting.
Conceptually the result says that using random feature selection (the last layer is fixed, initialized with Rademacher random variables), with a large enough network, the hidden weights do not need to move much from their initialization to get arbitrarily small training loss.
Thus, the analysis of the whole dynamics is reduced to a perturbation analysis of the dynamics around the initialization. (I would like to emphasize that even though the final argument ends up to be a ‘simple’ strong convexity convergence proof, I acknowledge that the proof of such result is far from being straightforward.)
The contributions of this paper are the following: in the setting introduced in [15] (the ref numbers correspond to the ones in the paper) the authors prove the linear convergence of the training loss for a large enough output layer of a 2-layer Relu network with Weight Normalization. Regarding to [15] the difference is that the authors study Weight Normalization. They are able to get better bounds on the over parametrization, and provide an analysis that highlights two training regimes: a fast one (V-dominated) and a stable one (G-dominated) that could explain the benefit of weight normalization.
*Decision:*
I am leaning for a weak reject for the following reasons:
1. The main issue to me is that this work builds up on the work by [15] without addressing the issues risen by [12]. One important takeaway from [12] that the ‘lazy training’ regime studied might not be a desired behavior and might not happen in practice. Thus, I think that extending the work form [15] to WeightNormalization would be interesting if the phenomenons described by the theory are backed-up by some practical evidence.
For instance : “we believe that G-dominated convergence actually is common but that it emerges at later stages in training, after the weights have adopted their directions in the V-dominated regime and improves stability.“ is something that the authors could check in practice.
2. I found the discussion regarding the phase transition a bit unclear. The magnitude of the weights v_k is treated as it was alpha the coefficient used to parametrized their initialization. Then since the phase transition depends on the magnitude of \alpha, it is argued that the model naturally transitions as \|v_k\| increases (which is the case because of the discrete gradient updates).
However, to me to make that phase transition argument you would need to show that the scaling of the matrices at time actually depends on the norm of the current iterate v_k(t)
3. Finally, regarding the proof of Theorem 4.1 and 4.2, I found it way more clear in [12]. There is a key subtle bootstrap argument that is not explicitly stated in the proof of Theorem B.1 and B.2: The condition R’ < R  (stated in Lemma 3.4 in [12]) is the key argument that leads to a sufficient bound on the overparametrization.
I put some remark regarding the clarity of the proof in the minor comment section. I think it would improve the quality of the work but did not have a major impact on my grade.
4. The presentation is slightly misleading. The fact that the last layer is not optimized is slightly mentioned once and the author make it appear just like is was done without any loss of generality  “We consider the case where the ck’s are fixed. This does not alter the capacity of the network since the gks are trainable (ck and gk are interchangeable analytically).”. Moreover, the omission that Theorem 4.1 and 4.2 are only true with high probability makes even that fact even more unclear. I think that this aspect (last layer is fixed) should be clearly emphasized in the revision.
*Questions:*
“we believe that G-dominated convergence is common”, can you provides evidence that G-dominated and V-dominated  stages occurs the way you describe it in the discussion ?
Same for the claim “The direction of the weights changes rapidly at the earlier stages of training when α is small, and G-dominated convergence ensues as α grows, leading to improved stability.” Particularly the link between your theory, the norm of v_k and alpha. (c.f point 2. of the decision section)
I think that it is important to emphasize that in your work c_k are randomly sampled and then fixed (it is much more clear in [15], but I do not think that the reader should know the related work to realize that). You seem to argue that it is without loss of generality when you say “We consider the case where the ck’s are fixed. This does not alter the capacity of the network since the gks are trainable (ck and gk are interchangeable analytically).”
but this statement seems wrong since there is a relu activation between c_k and g_k (thus you cannot interchange negative c_k with negative g_k). Can you comment this ?
Can you clarify the bootstrap argument mentioned in section 3. of the decision section ?  More precisely, can you justify the sentence “this contradicts one of Lemmas B.7, B.8 at time T_0.” in the proof of Theorem B.1 ?
*Minor comments: (do not need to be addressed in the rebuttal)*
- In the proof of Theorems B.1 and B.2 the statement “clearly T_0>0” should justified. This statement is true but a continuity argument that should be stated. However, the dependence in t could be easily avoided using the proof technique from [12] (Lemma 3.2) where the result is actually stated for any weight close enough to the initialization.
- The title of [12] has changed and one author is now missing. (since you cite the NeurIPS version you should then cite the right title with all the authors)
- I would not say that  “smaller alpha leads to faster convergence” since the optimal step size depend on \alpha.
=== After rebuttal ===
I would like to thank the author for their detailed answer.
I still think that experimental evidence that the phenomenon described by the theory actually happens in practice should be provided. I maintain my score.


We present a novel network pruning algorithm called Dynamic Sparse Training that can jointly find the optimal network parameters and sparse network structure in a unified optimization process with trainable pruning thresholds. These thresholds can have fine-grained layer-wise adjustments dynamically via backpropagation. We demonstrate that our dynamic sparse training algorithm can easily train very sparse neural network models with little performance loss using the same training epochs as dense models. Dynamic Sparse Training achieves prior art performance compared with other sparse training algorithms on various network architectures. Additionally, we have several surprising observations that provide strong evidence to the effectiveness and efficiency of our algorithm. These observations reveal the underlying problems of traditional three-stage pruning algorithms and present the potential guidance provided by our algorithm to the design of more compact network architectures.

## Update after the rebuttal
I appreciate the author's clarification in the rebuttal and the additional result on ImageNet, which addressed some of my concerns.
# Summary
This paper proposes a trainable mask layer in neural networks for compressing neural networks end-to-end. The main idea is to apply a differentiable mask to individual weights such that the mask itself is also trained through backpropagation. They also propose to add a regularization term that encourages weights are masked out as much as possible. The result on MNIST and CIFAR show that their method can achieve the highest (weight) compression rate and the lowest accuracy reduction compared to baselines.
# Originality
- The idea of applying trainable mask to weights and regularizing toward masking out is quite interesting and new to my knowledge.
# Quality
- The performance seems to be good, though it would be more convincing if the paper showed results on larger datasets like ImageNet.
- The analysis is interesting, but I am not fully convinced by the "strong evidence to the efficiency and effectiveness of our algorithm". For example, the final layer's remaining ratio is constantly 1 in Figure 3, while it starts from nearly 0 in Figure 4. The paper also argues that the final layer was not that important in Figure 4 because the lower layers have not learned useful features. This seems not only contradictory to the result of Figure 3 but also inconsistent of the accuracy being quickly increasing up to near 90% while the remaining ratio is nearly 0 in Figure 4.
- If the motivation of the sparse training is to reduce memory consumption AND computation, showing some results on the reduction of the computation cost after sparse training would important to complete the story.
# Clarity
- The description of the main idea is not clear.
- What are "structure gradient" and "performance gradient"? They are not mathematically defined in the paper.
- I do not understand how the proposed method can "recover" from pruned connection, although it seems to be indeed happening in the experiment. The paper claims that the use of long-tailed higher-order estimator H(x) makes it possible to recover. However, H(x) still seems to have flat lines where the derivative is 0. Is H(x) in Equation 3 and Figure 2d are showing "derivative" or step function itself? In any cases, I do not see how the gradient flows once a weight is masked out.
# Significance
- This paper proposes an interesting idea (trainable mask), though I did not fully get how the mask is defined/trained and has a potential to recover after pruning. The analysis of the compression rate throughout training is interesting but does not seem to be fully convincing. It would be stronger if the paper 1) included more results on bigger datasets like ImageNet, 2) described the main idea more clearly, and 3) provided more convincing evidence why the proposed method is effective.


Deep reinforcement learning (RL) algorithms can use high-capacity deep networks to learn directly from image observations. However, these kinds of observation spaces present a number of challenges in practice, since the policy must now solve two problems: a representation learning problem, and a task learning problem. In this paper, we aim to explicitly learn representations that can accelerate reinforcement learning from images. We propose the stochastic latent actor-critic (SLAC) algorithm: a sample-efficient and high-performing RL algorithm for learning policies for complex continuous control tasks directly from high-dimensional image inputs. SLAC learns a compact latent representation space using a stochastic sequential latent variable model, and then learns a critic model within this latent space. By learning a critic within a compact state space, SLAC can learn much more efficiently than standard RL methods. The proposed model improves performance substantially over alternative representations as well, such as variational autoencoders. In fact, our experimental evaluation demonstrates that the sample efficiency of our resulting method is comparable to that of model-based RL methods that directly use a similar type of model for control. Furthermore, our method outperforms both model-free and model-based alternatives in terms of final performance and sample efficiency, on a range of difficult image-based control tasks. Our code and videos of our results are available at our website.

This paper proposes an actor-critic method that tries to aid learning good policies via learning a good representation of the state space (via a latent variable model). In actor-critic methods, the critic is learnt to evaluate policies in the latent space, which further helps with efficient policy optimization. The proposed method is evaluated on image-based control tasks, with baseline evaluations against both model-based and model-free methods in terms of sample efficiency.
- The key argument is that learning policies in the latent space is more efficient, as it is possible to learn good representations in the latent space. There are quite a few recent works (e.g DeepMDP, Gelada et al., 2019;  Dadashi et al., 2019) that talks about representation learning in RL, and yet the paper makes no relations or references to previous works. I find it surprising that none of the past related works are mentioned in the paper.
- I find the arguments on solving a POMDP instead of a MDP a bit vague in this context. I understand that the goal is to solve image based control tasks - for which learning good representations via a latent variable model might be useful, but it does not explicitly require references to a POMDP? In most ALE tasks, we have pixel based observations too, which makes the ALE environments a POMDP in some sense, but we use approximations to it to make it equivalent to a MDP with sufficient history. The arguments on POMDP seems rather an additional mention, with no necessary significance to it?
- The paper mentions solving RL in the learned latent space, which is empirically proposed to be a good approach without theoretical justifications. There are several recent works that tries to understand the representation learning in RL problem from a theoretical perspective too - it would be useful to see where this approach stands in light of those theoretical results? Otherwise, the contribution seems rather limited : solving RL in latent space is useful, but there are no justifications to it? Why should this approach even be adapted or what is the significance of it?
- The proposed actor-critic method in the latent space is built on top of Soft Actor-Critic (SAC). I understand this is a design/implementation approach building from previous works - but it would have been useful to add more context as to what it means to learn a critic in the latent space. If the critic evaluates a policy in the latent space - then is this a good policy evaluation for actor-critic itself? Why or why not? I do not understand why the critic evaluation in the latent space is even a good approach?
- My first impression was that the paper proposes a separate auxilliary objective for learning good representations based on which actor-critic algorithms can be made more efficient. However, this does not seem to be the case directly? Following on previous point - I find the argument of solving a critic in the latent space rather vague.
- The sequential latent variable model proposed is based on existing literature. This can be any latent variable model (e.g VAEs), but I understand, as mentioned in the paper, the design choice of using sequential models to capture the temporal aspect.
- The proposed algorithm is in fact a combination of SAC and sequential latent variable models, both of which are well-known in the literature. The SLAC algorithm combines these to solve image-based control tasks. As per equation 10, which is the regular policy optimization objective with max entropy - the only difference is that the critic is evaluated in the latent space. This appears to me as more of an engineeering choice, and experimentally one that perhaps give good results - but the lack of justifications of why equation 10 is even the right objective to solve makes the paper rather less appealing.
- I think overall the contribution of the paper is rather limited. It is more of an experimental design and engineering approach that combines previous known techniques. The paper mentions learning good representations for RL, without any references or justifications - and it appears that overall there are bold claims made in the paper but it lacks significant scientific contribution.
- Experimental evaluations are made on image based control tasks. Experimental results are compared to few baselines - but it is not clear whether these are even the right baselines. For example, it would have been good to include analysis of the proposed model with different latent variable models (including VAE) to perhaps justify the choice of the latent variable model. Results in figure 5 appear a bit concerning to me - these are mostly the standard Mujoco tasks from the OpenAI suite. Are these all image based benchmarks too, or the standard baselines? It is not clear from the text. Assuming they are standard baselines, the comparisons made are rather unfair (for example : SAC and MDP performs much better on tasks like HalfCheetah-v2). Why are the baselines performing so poorly in the results?
- Overall, I think the paper needs more work in terms of writing and justifying the choice of the approach. There are significant references missing in the paper. Most importantly, there are quite a few claims made in the paper which are not properly justified, that makes the overall contribution and novelty of the paper rather limited. I would tend for a rejection of this paper, as it requires more work - both in terms of theoretical justifications (including references) and experimetnal ablation studies and more simpler benchmarks explaining the choice of the approach.


How do humans acquire a meaningful understanding of the world with little to no supervision or semantic labels provided by the environment? Here we investigate embodiment and a closed loop between action and perception as one key component in this process. We take a close look at the representations learned by a deep reinforcement learning agent that is trained with visual and vector observations collected in a 3D environment with sparse rewards. We show that this agent learns semantically meaningful and stable representations of its environment without receiving any semantic labels. Our results show that the agent learns to represent the action relevant information extracted from pixel input in a wide variety of sparse activation patterns. The quality of the representations learned shows the strength of embodied learning and its advantages over fully supervised approaches with regards to robustness and generalizability.

Paper summary:
This is an empirical study of the representations learned by a reinforcement learning agent. An agent is trained, using a standard RL algorithm, to solve puzzles by navigating through a 3D visual environment (Unity obstacle tower challenge). The analyses in the paper show that the visual representations of the trained agents are sparse and cluster according to the actions performed by the agent. The goal of the paper is to show that these features are due to the embodied nature of the agent. Specifically, the paper states that “the quality of the representations learned shows the strength of embodied learning and its advantages over fully supervised approaches with regards to robustness and generalizability”.
Decision:
I suggest to reject this paper. While the topic is interesting and the paper is clearly written, there is a lack of control/comparison experiments, such that the paper’s conclusions are not backed up by the analyses. However, with more experiments, I think this line of research has large potential.
Further justification for the decision:
My main criticism is that the paper claims to show that embodiment is important for representation learning, but never actually compares representations learned by an embodied agent to representations learned in some other way.
Comparing to a random network is a sanity check, but not sufficient to support the paper’s claims.
One way to experimentally dissociate embodiment/agency from supervised learning would be to train two separate models, one that is “embodied”/active, and another that gets the same sensory input, but without embodiment (“passive”). The passive network could be trained using the sensory inputs recorded while training the active network. The passive network could be trained to predict the value and/or the actions of the active network. Thus, the passive network would be trained in a supervised way, whereas the active network would be trained by RL (i.e. in an embodied way).
The representations of the two networks could then be compared using the analyses used in the paper. This setup would experimentally isolate the effect of embodiment. Without such comparisons, it is unclear whether representations learned in a supervised way would be any different from those learned by RL.
In addition to the descriptive analyses presented in the paper, a transfer learning approach could test whether there is actually a functional difference between the “embodied” and the supervised representations: Take the representations of the “active agent” and the “passive agent” and freeze the weights. Then re-initialize and re-train only the dense layer before the action probabilities on the RL task, leaving everything else frozen. Does the model from the “active agent” do better on the RL task? This would suggest that the embodied agent learned better representations.
Minor comment: The website contains a link to a YouTube profile that is not completely anonymous (it contains the first name and a profile photo). While I did not identify the authors when visiting the paper website, I recommend removing links to personal YouTube profiles and create submission-specific anonymous accounts.


We present a technique to improve the generalization of deep representations learned on small labeled datasets by introducing self-supervised tasks as auxiliary loss functions. Although recent research has shown benefits of self-supervised learning (SSL) on large unlabeled datasets, its utility on small datasets is unknown. We find that SSL reduces the relative error rate of few-shot meta-learners by 4%-27%, even when the datasets are small and only utilizing images within the datasets. The improvements are greater when the training set is smaller or the task is more challenging. Though the benefits of SSL may increase with larger training sets, we observe that SSL can have a negative impact on performance when there is a domain shift between distribution of images used for meta-learning and SSL. Based on this analysis we present a technique that automatically select images for SSL from a large, generic pool of unlabeled images for a given dataset using a domain classifier that provides further improvements. We present results using several meta-learners and self-supervised tasks across datasets with varying degrees of domain shifts and label sizes to characterize the effectiveness of SSL for few-shot learning.

Summary:
There are three main contributions of the paper:
i) The authors present an empirical study of different self-supervised learning (SSL) methods in the context of self-supervised learning.
ii) They point out how SSL helps more when the dataset is harder.
iii) They point out how domain matters while using SSL for training and present a method to choose samples from an unlabeled dataset.
Strengths:
1) They confirm the results of [7] and provide additional evidence of the benefit of the self-supervised learning in the few-shot setting.  They also showcase an interesting new result that self-supervised learning helps more in case of harder problems.
2) The authors have a done a commendable job of coming up with a meaningful set of experiments by varying base-models, self-supervised methods, datasets, and few-shot learning methods in Section 4.1. This is quite a comprehensive study.
3)  The paper is well-written and well-motivated.
Weaknesses:
1) The main weakness of the paper is Section 4.2's experimental setup.
i) The definition of domain distance in not quite meaningful. Since the chosen datasets have very different classes (airplanes vs dogs etc), the average embeddings for different datasets/classes will be far from each other.  In Figure 4d, it is misleading to show a trendline that includes the same domain as that will always be 0. If that datapoint is removed the trend line is mostly flat. The authors want to present a quantifiable way to show how domain distribution affect performance on self-supervised learning methods. But this definition of domain distance is more meaningful in the domain adaptation setting (like Amazon-Office dataset used for domain adaptation (https://people.eecs.berkeley.edu/~jhoffman/domainadapt/)) as in that case the requirement is to get the embeddings close to each other for the same class but from different domains.
ii) The authors go on to create an "unlabeled pool" by combining images from many domains. Then they train a domain classifier by labeling in-domain images as positive and  labeling the images in pool as negative. Considering all images in the pool as negative is not correct as there can be images of same class in unlabeled pool.
iii) Then they choose the samples which the classifier predicts comes from the same domain. This probably succeeds as it is done on top of ResNet-101 features (that has seen all of ImageNet). This technique probably works possibly due to the ResNet being pre-trained with so many labeled classes. One baseline might have just been to choose the k-nearest neighbors (from unlabled pool)  to the average embedding of all the images of the chosen dataset. Since, it is quite easy for classifiers to detect from which dataset an image came from [6] it might be easy to choose an image from similar domain by using nearest neighbor in the embedding space.
I am not sure how well their heuristic will work for an unlabeled pool that the classifier has never seen. Additionally, a portion of the dataset has been created by combining existing datasets. Since statistics of different datasets vary a lot artificially, the creation of an unlabeled pool by combining different datasets might work in the favor of the proposed heuristic of looking at "domain distance" to choose the samples.
2) Effect of domain shift in SSL (Figure 4b) is studying an extreme case where the domain shift results in almost no common classes in the SSL training phase. It would make more sense to include datasets where at least some of the classes are shared so that self-supervised learning methods get to see some relevant classes. In practice, a self-supervised learning method would be applied on a large unlabeled pool of images. Hopefully with increasing diversity and number of images, there might be some images on which ding SSL helps the downstream few-shot task. Hence comparison with such a dataset like ImageNet/iNatrualist is important here.
Decision:
The paper presents an well thought-out empirical study on self-supervised learning for few-shot learning. But there are  major concerns with the empirical setup and methods presented in the section where they propose a method to choose samples for SSL from an unlabeled pool of images.
Minor Comments:
1)  “In contrast, we humans can quickly learn new concepts from limited training data” - Remove we.
2) “Despite recent advances, these techniques have only been applied to a few domains (e.g., entry-level classes on internet imagery), and under the assumption that large amounts of unlabeled images are available.” This is not true. Self-supervised learning methods have been used for continuous control in reinforcement learning[1, 2], cross-modal learning[3], navigation [5], action recognition[4] etc. Later on in related work the authors list many papers that use self-supervised learning in different contexts. This line should be modified to reflect how common self-supervised learning methods are in other fields as well and with less data.
3) “making the rotation task too hard or too trivial to benefit main task” - add respectively.
4) "With random sampling, the extra unlabeled data often hurts the performance, while those sampled using the “domain weighs” improves performance on most datasets." replace weighs with weights
5) [8] points out how self-supervised learning on a large dataset but with a domain shift (YFCC100M) is not as effective for pre-training as it is doing self-supervised learning on the downstream task's dataset (ImageNet). While it is a different setting it is inline with one of the main conclusions of the paper.
References:
[1] “PVEs: Position-Velocity Encoders for Unsupervised Learning of Structured State Representations” Rico Jonschkowski, Roland Hafner, Jonathan Scholz, and Martin Riedmiller.
[2] “Learning Actionable Representations from Visual Observations” Debidatta Dwibedi, Jonathan Tompson, Corey Lynch, Pierre Sermanet
[3] “Look, Listen and Learn” Relja Arandjelović, Andrew Zisserman
[4] “Self-supervised Spatiotemporal Learning via Video Clip Order Prediction” Dejing Xu, Jun Xiao, Zhou Zhao, Jian Shao, Di Xie, Yueting Zhuang.
[5] “Scaling and Benchmarking Self-Supervised Visual Representation Learning” Priya Goyal, Dhruv Mahajan, Abhinav Gupta, Ishan Misra
[6] "Unbiased Look at Dataset Bias" Antonio Torralba and Alexei A. Efros.
[7] "Boosting ´few-shot visual learning with self-supervision." Spyros Gidaris, Andrei Bursuc, Nikos Komodakis, Patrick Perez, and Matthieu Cord.
[8] "Deep clustering for unsupervised learning of visual features" Mathilde Caron, Piotr Bojanowski, Armand Joulin, and Matthijs Douze