Over the last decade, two competing control strategies have emerged for solving complex control tasks with high efficacy. Model-based control algorithms, such as model-predictive control (MPC) and trajectory optimization, peer into the gradients of underlying system dynamics in order to solve control tasks with high sample efficiency. However, like all gradient-based numerical optimization methods, model-based control methods are sensitive to initialization and are prone to becoming trapped in local minima. Deep reinforcement learning (DRL), on the other hand, can somewhat alleviate these issues by exploring the solution space through sampling -at the expense of computational cost. In this paper, we present a hybrid method that combines the best aspects of gradient-based methods and DRL. We base our algorithm on the deep deterministic policy gradients (DDPG) algorithm and propose a simple modification that uses true gradients from a differentiable physical simulator to increase the convergence rate of both the actor and the critic. We demonstrate our algorithm on seven 2D robot control tasks, with the most complex one being a differentiable half cheetah with hard contact constraints. Empirical results show that our method boosts the performance of DDPG without sacrificing its robustness to local minima.

This paper studies optimal control problems where a physical simulator of the system is available, which outputs the gradient of the dynamics. Using the gradients proposed by the model, the authors propose to add two additional terms in the loss function for critic training in DDPG, where these to terms corresponding to the prediction error of $\nabla_{a} Q(s,a)$ and $\nabla_b Q(s,a)$, respectively. However, my main concern is that the form of gradient given in equation (2) might contains an error.
1. Equation (2). Note that in DDPG, the action is given by a deterministic policy. Thus, we have $a_t = \pi(s_t)$ for all $t\geq 0$. For critic estimation, it seems you are basing on the Bellman equation
$ Q(s,a) = r(s,a) + Q(s', \pi(s'))$, where $s'$ is the next state following $(s,a)$. Then, it seems that Equation (2) is obtained by taking gradient with respect to $(s,a)$. However, I cannot understand what $\nabla_{\pi} Q$ stands for. If it is $\nabla_a Q(s_{i+1}, a_{i+1}) \cdot \nabla_s \pi(s_{i+1}) $, then that makes sense.
2. Based on the experiments, it seems that the proposed method does not always outperform MPC or DDPG, even in a small-scale control problem Mountaincar. Moreover, it seems that the performance is similar to that of the DDPG.
3. Here the model-based gradient in equation (2) is defined by only unroll one-step forward by going from $s_i, a_i$ to $s_{i+1}$. It would be interesting to see how the number of unroll steps affect the algorithm, which is a gradient version of TD($\lambda$).
4. Missing reference: Differential Temporal Difference Learning https://arxiv.org/abs/1812.11137


Deep neural networks often have millions of parameters. This can hinder their deployment to low-end devices, not only due to high memory requirements but also because of increased latency at inference. We propose a novel model compression method that generates a sparse trained model without additional overhead: by allowing (i) dynamic allocation of the sparsity pattern and (ii) incorporating feedback signal to reactivate prematurely pruned weights we obtain a performant sparse model in one single training pass (retraining is not needed, but can further improve the performance). We evaluate our method on CIFAR-10 and ImageNet, and show that the obtained sparse models can reach the state-of-the-art performance of dense models. Moreover, their performance surpasses that of models generated by all previously proposed pruning schemes.

This work proposes a simple pruning method that dynamically sparsifies the network during training. This is achieved by performing at fixed intervals magnitude based pruning for either individual weights or entire neurons. While similar methods have been explored before, this work proposes a slight twist; instead of updating the weights of the model by following the gradient of the parameters of the dense model, they update the parameters of the dense model according to the gradients of the sparse model. Essentially, this corresponds to a variant of the straight-through estimator [1], where in the forward pass we evaluate the compressed model, but in the backward pass we update the model as if the compression didn’t take place. The authors argue that this process allows for ``feedback” in the pruning mechanism, as the pruned weights still receive gradient updates hence they can be ``re-activated” at later stages of training. They then provide a convergence analysis about the optimization procedure with such a gradient, and show that for strongly convex functions the method converges in the vicinity of the global optimum, whereas for non-convex functions it converges to the neighbourhood of a stationary point. Finally, the authors perform extensive experimental evaluation and show that their method is better than the baselines that they considered.
This work is in general well written and conveys the main idea in an effective manner.  It is also a timely contribution as sparse models / compression are important topics for the deep learning community. The overall method seems simple to implement, doesn’t introduce too many hyper-parameters and seem to work very well. For this reason I tend towards recommending for acceptance, provided that the authors address /comment on a couple of issues I found in the draft.
More specifically:
- The connection to the error feedback is kind of loose and not well explained. After skimming Karimireddy et al. I noticed that 1. it evaluates the gradient at a point (i.e. the current estimate of the parameters), 2. compresses said gradient, 3. updates the parameters while maintaining the difference of the original w.r.t. the compressed gradient. In this sense, it seems a bit different that DPF, as your notation at the first equation of page 4 implies that you take the gradient of a different point, i.e. w_t + e_t instead of w_t. I believe that expanding a bit more about the connection would help in making the manuscript more clear.
- There seems to be a typo / error on your definition of an m-strongly convex function at the “convergence of Convex functions” paragraph. I believe it should be <\nabla f(v), w-v> <= f(w) - f(v) - 0.5 m ||w - v||^2, instead of <\nabla f(w), w-v> <= f(w) - f(v) - 0.5 m ||w - v||^2.
- The proposed gradient estimator seems to be an instance of the STE [1] estimator, that, as the authors mention, has been using at the Binary Connect algorithm. It would be interesting to see some more discussion about this similarity perhaps also expanding upon recent work that discusses the STE gradient as a form of coarse gradient [2].
- At section 5.2 the authors mention that “dynamic pruning methods, and in particular DPF, work on a different paradigm, and can still heavily benefit from fine-tuning”. This claim seems to contradict the results at Figure 4; there it seems that the masks have “converged” in the later stages of training, hence one could argue that the fine-tuning already happens thus it wouldn’t benefit DPF. I believe it would be interesting if the authors provide a similar plot as the one in Figure 4 but rather for the ResNet-20 network on CIFAR 10 (which seems to benefit heavily from FT). Do the masks still settle at the end of training (as it was the case for WideResNet-28-2) and if they do, why is fine-tuning still increasing the accuracy?
- Minor: Try to use consistent coloring at Figure 6 as while (a), (b) share the same color-coding, (c) is using a different one hence could be confusing.
[1] Estimating or Propagating Gradients Through Stochastic Neurons for Conditional Computation, Yoshua Bengio, Nicholas Léonard, Aaron Courville, 2013
[2] Understanding Straight-Through Estimator in Training Activation Quantized Neural Nets, Penghang Yin, Jiancheng Lyu, Shuai Zhang, Stanley Osher, Yingyong Qi, Jack Xin, 2019


Meta-learning has achieved great success in few-shot learning. However, the existing meta-learning models have been evidenced to overfit on training tasks when using over-parameterized convolutional neural networks. This means that the generalization performance of the meta-learner cannot be improved by merely applying more complex networks. To remedy this deficiency, we propose a sparsity-constrained meta-learning approach to learn from training tasks a subnetwork from which first-order optimization methods can quickly converge towards the optimal network in testing tasks. Our theoretical analysis shows the benefit of sparsity for reducing the generalization gap of the estimated meta-learner. We have implemented our approach on top of Reptile assembled with varying network pruning routines including Dense-Sparse-Dense (DSD) and Iterative Hard Thresholding (IHT). Extensive experimental results on benchmark datasets with different over-parameterized deep networks demonstrate that our method not only effectively alleviates meta-overfitting but also in many cases improves the overall generalization performance when applied to few-shot classification tasks.

============= Post Rebuttal Assessment =============
I appreciate the authors thorough response: I believe the writing has improved considerably and the presentation is more convincing.
All in all, I think it's a good paper but not completely ready for publication based on the following final assessment.
The theoretical contribution of the paper is not entirely relevant to the proposed method as also mentioned by other reviewers. The empirical aspect of the work is incremental; by combining two prior works. In this situation, I would happily suggest acceptance if 1) the experimental setup is very thorough and 2) the results are consistent and conclusive 3) the improvements are significant.
Regarding these, the paper's most interesting result is 5-way 5-shot classification with IHT/DSD + Reptile. I think that makes the paper borderline since the results are not state of the art and the experiments are not thoroughly done, while on the other hand, it does show clear improvement for this case. For such a borderline scenario, and since I have to choose between weak reject and weak accept, I would lean towards weak reject as I believe the experimental setup can be significantly improved by following some of the items below for the next version:
- A thorough ablation study on all the components of IHT and DSD
- A study of the effect of the hyperparameters of IHT/DSD
- Additional datasets/architectures to show consistent improvement for various cases.
- ResNet results are not reliable in the current form. I understand that it would need a sizable computational buget to perform a proper comparison. However, that means either the results should be taken away or done appropriately.
To reiterate, the reason I am asking for the above experiments is that the paper comes with incremental novelty as the main point, in my opinion. Thus it has to be backed up by extensive experiments to be confidently considered for publication.
dget to perform a proper comparison. However, that means either the results should be taken away or done appropriately.
To reiterate, the reason I am asking for the above experiments is that the paper comes with incremental novelty as the main point, in my opinion. Thus it has to be backed up by extensive experiments to be confidently considered for publication.
============= Summary =============

The paper addresses the issue of overfitting the meta-parameters of optimization-based meta learning techniques. It uses an iterative training-pruning-retraining setup to learn the meta-parameters. The pruning step in each iteration is to limit the capacity of the meta-learner and thereby alleviate overfitting. Two pruning methods called DSD and IHT are employed on top of a first-order meta learning technique called Reptile. The combination is tested on 4 few-shot classification scenarios of two datasets; omniglot and miniImageNet. Results suggests improved accuracy on top of the Reptile meta-learning algorithm on miniImageNet.

============= Strengths and Weaknesses =============
+ overfitting the meta learner due to the small number of samples (shots) per task and the large number of meta-parameters and/or base-learner parameters is an important problem in meta learning which is the focus of this work.
+ the results suggest improvements over the Reptile baseline on miniImageNet.

General concerns:
- abstract: “the existing meta-learning models have been evidenced to overfit on meta-training tasks when using deeper and wider convolutional neural networks.” several methods such as CAVIA and MetaOptNet (among many others) address this issue by limiting the capacity of the learner.
- what is the formal definition of meta-generalization and meta-overfitting? This definition will be helpful for understanding the paper’s arguments, for instance, why “reducing meta-overfitting” and “improving meta-generalization” are two different matters (as suggested in the last part of the abstract).
- Figure 1.b: the green bars (proposed method) don’t seem to improve the generalization (testing accuracy). I can only speculate that the figure is to demonstrate that (in the rightmost plot) the difference between train and test accuracy for green bars is less than it is for the red bars. However, one should note that it seems to be due to the training accuracy being lower, which can be achieved, in the extreme case, by a random classifier (zero gap). So, it’s not necessarily useful when testing accuracy is not improved.
- eq (1) and eq (2): the left-most loss L should be on D^{query}
- page 4: “In view of the “lottery ticket hypothesis” (Frankle & Carbin, 2018), the model in equation 2 can be interpreted as a first-order meta-learner for estimating a subnetwork“ -> eq (2) in the current form still requires a 2nd-order derivative and I cannot see how (Frankle & Carbin, 2018) helps make it first-order optimization.
- the usefulness of the provided theory is in question since the final method does not enforce the sparsity in practice. That is, the output of the final meta-parameters are *dense*.
- page 7 mentions “top k_l entries”: what does “top” mean here? k_l dimensions of \theta with the highest absolute value, maybe?
- why do the two separate steps of only training the pruned subnetwork using Reptile and then retrain the whole network (with the updated subnetwork) again using Reptile? One can instead only train Reptile on the whole \theta^{(i)}_M (with L0 norm constrained using the M projection) in a single Reptile step. Doing the former should be justified over the latter since its twice as expensive. Also it should be shown empirically (as an ablation study) that the former works better.
- reference list: arXiv versions of many papers are cited, it’s good to cite the peer-reviewed version of papers when applicable. For instance, IHT pruning method does not seem to be peer-reviewed which is a caveat for the current work.
- 10 pages seem excessive for the content of the paper. For instance, the experiments section can be shortened extensively and the theories can be put into the appendix.

Experimental concerns:
- Has the standard miniImageNet split been used? This split is especially important to be respected since CAVIA’s accuracy is taken from the original paper.
- The reported number for CAVIA in table 2 is not the best number the original paper achieve. The best number is 51.82 ± 0.65% for one-shot, and 65.85 ± 0.55% for 5-shot.
- There are quite a few new hyperparameters (3 iteration numbers for pretraining, pruning/finetuning, and retraining, and then the sparsity level k_l). It’s important to mention how the hyper-parameters are chosen, especially since they are different for different setups.
- there seems to be no meta validation set for Omniglot.
- For a fair comparison, the network size of the baseline as well as the learning rate should be searched with the same budget as the hyperparameter search done for the proposed method.
- ResNet experiment is especially concerning since 1) there is an even higher-level of hyperparameter tuning for ResNet: first conv layer is not pruned, different pruning rates for different residual blocks are used. 2) the baseline is only tried with one setting for the capacity. It is evident in Table 2 that there is a sweet spot for the capacity of the ConvNet baseline, there is no reason this does not apply to ResNet.
- Ablation study:  “For the purpose of fair comparison, only the retraining phase is removed and other settings are the same as proposed in Section 5.1”: this is not fair. I believe a fair comparison would be to repeat the hyperparameter search for the ablation studies with the same budget as the full version of the proposed method.
- Table 2 only compares with CAVIA while many other meta learning methods could be relevant here such as MetOptNet which also limits the number of base learner’s learnable parameters thereby helping with overfitting. Also, CAVIA has results on ResNet useful for the last experiment.

============= Final Decision =============
While the paper addresses an important problem and reports improvements, there are many concerns with it including the writing, method, and experimental setup.  My “weak reject” rating, however, is mainly based on the experimental concerns especially regarding the hyperparameters and the baselines.

============= Minor Points =============
- code is not provided. I think it’s in general very helpful to release the codes for reproducibility and replicability of the experiments, especially in the case of an incremental study.
- what meta learning task has been used for Figure 1?
- There are different ways of including batchnorm in a meta learning setup. For instance, Reptile used two different strategies. How is batchnorm implemented for this paper’s experiments? Particularly, indicate if you are using transductive or non-transductive version of batchnorm at test time.

The text as well as the math notations require polishing on various occasions including the following (non-exhaustive) list:
- abstract: “sparsity constrained” -> sparsity-constrained
- abstract: “can not only” -> rephrase so that it’s not read as “cannot only”
- abstract and intro: “ease meta-overfitting” can be interpreted as facilitating overfitting -> maybe better to say “alleviate meta-overfitting”
- intro: “memorize the experience from previous meta-tasks for future meta-task learning with very few samples” → memorize the experience from previous tasks for a future task with very few samples
- intro: “As can be observed from Figure 1(a) that” -> It can be observed from Figure 1(a) that
- intro: “sparsity benefits considerably to the” → sparsity benefits considerably the
- intro: “along with two specifications to two widely used networking pruning methods”: rephrase
- related works: “most closely” -> closest
- page 4: “ultra goal -> maybe ultimate goal?
- page 4: \theta is not defined
- page 4: eq (2): i -> m or m -> i
- page 4: the definition of an unordered set (S) coming as a sample of the product of m \Tau spaces is not precise. Better to say each T_i \in \Tau.
- page 4: J_l is not defined,
- sec 3.3: the minimization are done over \theta, it’s better to put that under “min” and the conditions should be clearly indicated by “with or s.t. or similar”
- page 7: zero-one -> binary
- page 7: “ as the restriction of \theta^{(t)} over the mask M^{(t)}” -> rephrase
- page 7: “it deems to reduce” -> rephrase
- page 8: “this is consist” -> consistent

- it’s also good to settle on a single term for each concept to make it an easier read, for instance:
- “meta-training tasks” and “training tasks” have been used interchangeably. I think “training tasks” and “mata training dataset” are better choices since a “meta-training” task can refer to the whole task of meta learning.
- Meta-overfitting and meta-level overfitting
- meta-learner, meta-estimator, model
- meta-level training accuracy, meta-training accuracy
- meta training, meta learning
- base learner, learner, model → I think it’s better to emphasize on learner being “base learner”, avoid model as it is not clear what it refers to.

============= Points of improvements =============
The paper would significantly improve if 1) the text is polished and the equations revised. 2) hyperparameter optimization is done carefully and thoroughly described for both the proposed method as well as the baselines


Increasing model size when pretraining natural language representations often results in improved performance on downstream tasks. However, at some point further model increases become harder due to GPU/TPU memory limitations, longer training times, and unexpected model degradation. To address these problems, we present two parameter-reduction techniques to lower memory consumption and increase the training speed of BERT . Comprehensive empirical evidence shows that our proposed methods lead to models that scale much better compared to the original BERT. We also use a self-supervised loss that focuses on modeling inter-sentence coherence, and show it consistently helps downstream tasks with multi-sentence inputs. As a result, our best model establishes new state-of-the-art results on the GLUE, RACE, and SQuAD benchmarks while having fewer parameters compared to BERT-large.

The authors present ALBERT, a modification of the BERT architecture with substantially fewer parameters. They show that despite being much smaller, the performance is very strong and achieves state of the art on a variety of different tasks. There are several ideas proposed here: embedding factorization, sharing layers, and sentence ordering as a training objective.
1. The point that naively increasing the size of the BERT architecture does not work is a good one, but the authors don't acknowledge that this is tied up in the effect of regularization. Cross layer parameter sharing has a regularization effect that simply scaling up BERT large to x-large or such sizes does not have. This is also an issue with the authors making the statement that they are the first to show that dropout is harmful for Transformers. This is a large generalization that seems to be a special case of not only the regularized architecture they propose but also the large quantity of data that the model still underfits to.
2. The authors propose embedding factorization to reduce the number of parameters in the embedding dimension. This is very intuitive, but the authors do not cite or compare to related approaches. I understand these models are computationally intensive and thus do not expect large quantities of detailed ablations. However, this kind of dimensionality reduction has been explored with other techniques, for example for knowledge distillation, quantization, or even adaptive input/softmax (and with subword as well, not just whole word modeling). These techniques have also been applied to machine translation models, which do not use them to learn rare words. I believe a better discussion of these methods should be added to the paper, as this is not a novel proposition.
3. A large takeaway I have from this paper is that parameter size is not a good metric. While ALBERT is substantially smaller, the authors do not make it clear that this model is very slow at inference time due to the large size. This raises several questions: is it better to have models that are deeper or more wide? Can the authors actually report the latency in a comparative table next to BERT? Can the authors provide a sense of how large this model is in MB - e.g. presumably a goal of less parameters would be to have a model with less memory, but then the decision between memory and latency that different models make should be made more clear.
4. Section 4.8 is not clear. Exactly how much data, in terms of GB of uncompressed text, is used here? Is it the data of XLNet and RoBERTa, so larger than both of those settings individually? Further, the authors train for 1 million steps. This is larger than both XLNet and RoBERTa, is that correct? Or there is some detail about the size of the batch that actually makes it comparable? The many small tables where the changes are not clearly delineated makes it difficult to compare results.


The uncertainty estimation is critical in real-world decision making applications, especially when distributional shift between the training and test data are prevalent. Many calibration methods in the literature have been proposed to improve the predictive uncertainty of DNNs which are generally not well-calibrated. However, none of them is specifically designed to work properly under domain shift condition. In this paper, we propose Unsupervised Temperature Scaling (UTS) as a robust calibration method to domain shift. It exploits unlabeled test samples instead of the training one to adjust the uncertainty prediction of deep models towards the test distribution. UTS utilizes a novel loss function, weighted NLL, which allows unsupervised calibration. We evaluate UTS on a wide range of model-datasets to show the possibility of calibration without labels and demonstrate the robustness of UTS compared to other methods (e.g., TS, MC-dropout, SVI, ensembles) in shifted domains.

The authors present an algorithm for postprocessing neural networks to ensure calibration under domain shift.
Calibration under domain shift is an interesting challenge that has been receiving increasing attention and tackling this in an unsupervised manner is an interesting approach. However, I have 2 major concerns regarding the approach presented by the authors.
What makes calibration under domain shift useful and appealing is that the model is then robust against any changes in the test distribution that can occur during the life cycle of a model. These often include erroneous/samples (corresponding to truly OOD samples), but also gradual domain shift, where the test distribution continuously moves away from the training distribution (e.g. due to a continuous drift in user behaviour/change in customer base) or unforeseen changes. My first major concern is regarding the requirements for UTS, which render this approach not very useful in many of these practical  applications: UTS first requires knowledge of and access to the test distribution; in addition it assumes that the distribution of the labels remains unaffected under domain shift. These assumptions are violated in the practical applications described above, in particular those where a gradual, continuous domain shift occurs - in this case, access to the test distribution is difficult since it changes continuously. On this note I also would have liked to see some analysis on how performance depends on the number of samples that are available from the test set, since in practice this might be substantially smaller than the full test set used.
Furthermore, I find the assumption that the distribution of labels remains unchanged problematic (q_s(y) = q_t(y) and even q_s(y|x)=q_t(y|x)): once sufficiently out-of-domain, labels become meaningless and predictions for truly OOD samples should have maximum entropy. Even for small domain shifts in practical applications it is not clear why q_s(y|x)=q_t(y|x) should hold and it would have been useful to see a discussion and some robustness analysis on this.
Finally,  the algorithm requires re-calibration whenever the test distribution changes, which in practice is  often not clear (and part of the reason why dealing with predictions under domain shift is so challenging).
In addition to doubts on practical applicability, my second major concern is regarding the depth of the evaluation.
First, while the authors present some comparisons to probabilistic methods, I am missing a crucial comparison to Evidential Deep Learning (Sensoy et al, NeurIPS 2018), which results in far superior performance than deep ensembles, SVI or dropout. Importantly, the comparisons to probabilistic approaches presented by the authors are very limited. The big advantage of those approaches is that, once trained, no further recalibration is necessary and well calibrated predictions can be made for any level of domain shift, whereas UTS requires a recalibration step for very level of domain shift. That is why I think it is crucial to not only show one arbitrarily picked level of domain shift for each dataset/perturbation, but calibration across all levels of domain shift, as for TS and TS-Target; since no recalibration is required for those probabilistic approaches
 this is very straight-forward and would be very informative - especially since e.g Figure 5 shows that UTS has only very minor advantages over TS in many settings.
I appreciate that the authors report some performance in terms of ECE in the supplement, but I think it would be very informative to report performance in terms of ECE for all domain-shift experiments: The Brier score conflates accuracy with calibration (see eg the 2 component decomposition), whereas ECE directly quantifies calibration and is hence easier to interpret and arguably the more meaningful measure when quantifying calibration.
Minor:  I find the manuscript lacks clarity. Aspects such as the definition of calibration as well as implications and interpretation of Proposition 1 should be described in more detail in the manuscript.


Deep Infomax (DIM) is an unsupervised representation learning framework by maximizing the mutual information between the inputs and the outputs of an encoder, while probabilistic constraints are imposed on the outputs. In this paper, we propose Supervised Deep InfoMax (SDIM), which introduces supervised probabilistic constraints to the encoder outputs. The supervised probabilistic constraints are equivalent to a generative classifier on high-level data representations, where class conditional log-likelihoods of samples can be evaluated. Unlike other works building generative classifiers with conditional generative models, SDIMs scale on complex datasets, and can achieve comparable performance with discriminative counterparts. With SDIM, we could perform classification with rejection. Instead of always reporting a class label, SDIM only makes predictions when test samples' largest logits surpass some pre-chosen thresholds, otherwise they will be deemed as out of the data distributions, and be rejected. Our experiments show that SDIM with rejection policy can effectively reject illegal inputs including outof-distribution samples and adversarial examples.

The paper proposes a scalable approach to train generative classifiers using information maximizing representation learning, with the motivation that generative classifiers could be more robust to adversarial attacks than discriminative classifiers. An off-the-shelf mutual information maximizer (MINE, DIM) is used to learn low-dimensional representations of images. Then, class-conditioned generative models of the representations are learned avoiding full generative modeling of the images. An additional loss is used to train the generative classifier which maximizes likelihood margins. Finally, percentile-based thresholds of the class log-probabilities is proposed to be used to reject classification for out-of-manifold inputs.
The paper cites existing literature which indicates that generative classifiers might be more robust to adversarial attacks, and uses recently-proposed representation learning techniques to scale up learning generative generative classifiers. The motivation of the proposed technique is clear, and the problem itself is relevant. Similar prior work use generative modeling at the pixel-level. Generative modeling of representations is novel, afaik.
The technique is evaluated on out-of-distribution sample detection (FashionMnist->MNIST and Cifar10->SVHN) and adversarial attacks. FGSM, PGD, CW-L2 attack, deepfool.
The experiments section is not very clearly written. Some of the evaluation itself is nonstandard in which only the first example of digit 0 of MNIST is used. The paper needs to have a clearer explanation and interpretation of the results. It’s not clear what the logits in table 4 and table 6 are, and what is being shown by the comparison.
Summary: The authors propose a new technique for training generative classifiers with the aim to improve robustness to adversarial attacks and confidence on out-of-distribution samples. The method is well-motivated and explained, but the experiment section is not very clearly written and I’m not confident whether the technique represents an advancement in the state-of-the-art or not.
Misc comments:
“By adopting a generative approach p(x, y) = p(y)p(x|y), we assume that the data follows the manifold assumption: the (high-dimensional) data lies on low-dimensional manifolds corresponding to their class labels.”
This sentence seems to be making a stronger claim than is needed, which is possibly incorrect. Assuming a generative approach doesn’t require assuming the manifold assumption.
Nit: “possible MI low-bounds”
Nit: “state-of-the-arts”
Typo: “The original image is the fist sample of class 0”


This paper presents a new methodology for modeling the local semantic distribution of responses to a given query in the human-conversation corpus, and on this basis, explores a specified adversarial learning mechanism for training Neural Response Generation (NRG) models to build conversational agents. The proposed mechanism aims to address the training instability problem and improve the quality of generated results of Generative Adversarial Nets (GAN) in their utilizations in the response generation scenario. Our investigation begins with the thorough discussions upon the objective function brought by general GAN architectures to NRG models, and the training instability problem is proved to be ascribed to the special local distributions of conversational corpora. Consequently, an energy function is employed to estimate the status of a local area restricted by the query and its responses in the semantic space, and the mathematical approximation of this energy-based distribution is finally found. Building on this foundation, a local distribution oriented objective is proposed and combined with the original objective, working as a hybrid loss for the adversarial training of response generation models, named as LocalGAN. Our experimental results demonstrate that the reasonable local distribution modeling of the query-response corpus is of great importance to adversarial NRG, and our proposed LocalGAN is promising for improving both the training stability and the quality of generated results.

POST-REBUTTAL FEEDBACK
I share the same concerns as that of reviewer 2 in the response to the rebuttal. Hence, my score remains unchanged.
SUMMARY OF REVIEW
This paper motivates the need to "contextualize" responses based on the query to bring about stable training in NRG and consequently proposes localGAN to realize this. On the overall, I like the motivation and the proposed approach of this paper. The experimental results also look convincing.
On the flip side, the technical formulation and theoretical results are not presented rigorously and important technical details are missing, as discussed below. As a result, clarifications from the authors are needed to ensure the correctness of their formulation. The authors also need to improve the presentation and proof of the theoretical results; the correctness has to be checked again. In my opinion, these theoretical results do not improve my current assessment of the paper and can be removed to cut down to 8 pages. If the authors like to keep them, they need to revise them based on my concerns above.
It would be good to show some sample queries and corresponding "meaningful" responses produced by their proposed LocalGAN that are not considered safe responses which are produced by the other tested methods.
DETAILED COMMENTS
For Lemmas 1 and 2 and Theorem 1, the authors need to present them rigorously by specifying the exact math expressions since they have not defined what it means by sufficient, approximates, small enough, and estimate properly. This will also eliminate any discrepancy in their interpretations. For example, the authors have used Taylor series expansion to approximate the expectation of F(q,r) in equation 19 (instead of bounding it). Hence, one can claim that Lemma 2 does not hold and hence Theorem 1 does not hold as well.
In Section 4.3, the described mechanism is confusing to me:
(a) Are the authors saying that it is performed sequentially from foundation to phase-1, followed by phase-2? Or are the authors saying that these three phases are expected behaviors occurring during the optimization in equation 17?
(b) For the foundation phase, is the DBM pre-trained, that is, prior to optimization in equation 17?
(c) Are there multiple response clusters, that is, one for each q? If so, the second RELU term in the minimizing criterion in equation 17 does not seem to properly reflect this.
(d) How are the response cluster centers r_c exactly determined? The authors vaguely say that they are modeled from training data. Is it one center per response cluster? Are the cluster centers also optimized in equation 17, besides the generator's weights? Can the authors provide the argument under the min operator in equation 17? It is confusing to leave out r_c from the subscript of alpha.
I would have preferred that the authors specify the expression of the evaluation metrics to be self-contained.
In Fig. 2, how exactly do the authors measure stability? If the entropy rapidly increases like that of LocalGAN and Adver-REGS, are they considered stable?
Minor issues
Page 1: Despite of?
Page 3: inequation?
Page 3: Equation 4 and 5?
Equation 6: The first summation should just be over q, unless there are multiple sets of R_q per q.
tilde{R}_q is not used in equation 6.
Page 4: a limited samples?
Page 5: defined in 3.2?
Page 5: To be consistent, mathbb should be applied to E.
Page 9: valid this aspect?
Page 9: from the the?


Statistical models are inherently uncertain. Quantifying or at least upperbounding their uncertainties is vital for safety-critical systems. While standard neural networks do not report this information, several approaches exist to integrate uncertainty estimates into them. Assessing the quality of these uncertainty estimates is not straightforward, as no direct ground truth labels are available. Instead, implicit statistical assessments are required. For regression, we propose to evaluate uncertainty realism-a strict quality criterion-with a Mahalanobis distance-based statistical test. An empirical evaluation reveals the need for uncertainty measures that are appropriate to upper-bound heavy-tailed empirical errors. Alongside, we transfer the variational U-Net classification architecture to standard supervised imageto-image tasks. It provides two uncertainty mechanisms and significantly improves uncertainty realism compared to a plain encoder-decoder model.

This paper considers the important open question of how to ensure that uncertainty estimates of neural network predictions actually reflect real world error distributions. The paper introduces an uncertainty quality metric along with a statistical test based off this metric that enables a binary decision of whether to accept a model’s uncertainties as realistic. The paper also introduces a new model for supervised image-to-image tasks that combines two existing uncertainty mechanisms, and achieves reasonable uncertainty estimates, in particular, demonstrating robustness to out-of-sample data.
I am tending to reject, because although each of the two distinct contributions are good starts on interesting approaches, neither provides a convincing solutions for the main question, and the two contributions are quite distinct, so that the paper lacks a consistent thread.
First, the Mahalanobis-based uncertainty evaluation makes sense, but it is not clear what it adds beyond the standard average negative log-likelihood (NLL) metric. Mahalanobis distance increases monotonically with negative log-likelihood, so is there any reason to expect it is a better way to compare models based on their uncertainty? Is there some experiment that could show that the new metric is better than NLL at evaluating uncertainty realism?
The statistical test could potentially be a nice real world tool for deciding whether to trust neural network uncertainties. However, the paper only applies the test in one case, where the MC dropout model is shown to have unrealistic uncertainties. To show that this test is useful, there should also be experiments where uncertainty estimates are shown to be realistic. Is there some alternative to MC dropout for regression or some improvements to the algorithm that could yield realistic uncertainties under this statistical test? E.g., would the U-Net-based model in the paper pass the test if it were adapted to regression problems?
Second, the new U-Net-based classification model looks like a reasonable approach, but it is disjoint from the new statistical test, and it is not clear that the method yields improvements to uncertainty realism, since there are no comparisons to external results. Since only a new architecture is used, it is not clear that the deficiencies in uncertainty realism are not architecture-specific. Is it that there are no existing architectures that can be applied to this problem? Also, is there some more realistic setting where the CVAE approach would improve in-sample scores, i.e., where out-of-sample data is not generated synthetically? Can the statistical test be adapted to the classification setting? Similar, to the case of regression, the uncertainty realism metrics used for classification are tightly coupled with the prediction accuracy; is there a way to decouple these, would one want to? The conclusion that CVAE is better than MC for this problem is solid, but is there a more general conclusion to be drawn? E.g., could a CVAE model yield realistic estimates in the regression setting?


Generative replay (GR) is a method to alleviate catastrophic forgetting in continual learning (CL) by generating previous task data and learning them together with the data from new tasks. In this paper, we propose discriminative variational autoencoder (DiVA) to address the GR-based CL problem. DiVA has class-wise discriminative latent embeddings by maximizing the mutual information between classes and latent variables of VAE. Thus, DiVA is directly applicable to classification and class-conditional generation, which are efficient and effective properties in the GR-based CL scenario. Furthermore, we use a novel trick based on domain translation to cover natural images which are challenging to GR-based methods. As a result, DiVA achieved competitive or higher accuracy compared to state-of-the-art algorithms in Permuted MNIST, Split MNIST, and Split CIFAR10 settings.

-- This paper seeks to combine several ideas together to propose an approach for image classification based continual learning tasks. In this effort, the paper combines previously published approaches from generative modeling with VAEs, mutual information regularization and domain adaptation.
I am a making a recommendation for reject for this paper with the main reason being that I believe the primary derivations for their method appear flawed.
--In the main section describing the approach (Section 4), the authors start with a claim that Equation 1 and 2 are equal; I don’t believe 1 and 2 are equal.
--In Section 4.1, it appears that they are instead making a claim about Equation 2 being a bound for equation 1; but even this derivation appears to have a problem. The following is the concern:
--In the second line of Equation 5, the KL term appears to be measuring a distance between distributions on two different variables; z|c and c|z. If one were to interpret the second one as the unnormalized distribution on z defined via the likelihood for c given z; even this has an issue because then the expression for KL where we plug the unnormalized density in place of the normalized need not be positive which is something they need to derive their bound.
--Another issue is that the regularization lambda should apply to both the terms in the bound but in Equation (7) only appears selectively for one of the two terms.
It is also not clear how the loss function proposed differs from that of the CDVAE, etc.  If the novelty is in applying to continual learning and new datasets, it is not clear that this is sufficient.
Additional feedback for authors (not part of the main decision reasoning):
- What is dt in Algorithm 1 description?
Figure 1:
-typo “implmented”
-What’s the 3d plot supposed to represent?
Doesn't the classification loss have a dependency on the input condition?
--What does a "heavy classifier" imply concretely?
--“Redundant weights” seems like not a very strong constraint especially for a small cardinality label space (like 10, in the case of this paper).
--The notation for the proposed parameters theta, theta’, phi, phi’ are not consistent with the notation in the intro section, where phi was used for the encoder and theta for the decoder. In later sections they use theta and theta’ for encoder/decoder resp.
-- “When the encoder and decoder networks are sufficiently complex, it is enough to implement each the prior and classification network as one fully-connected layer” → what do the authors mean “when … networks are sufficiently complex” or do they actually mean when the “when the problem is simple enough”?


Continual learning aims to learn new tasks without forgetting previously learned ones. This is especially challenging when one cannot access data from previous tasks and when the model has a fixed capacity. Current regularization-based continual learning algorithms need an external representation and extra computation to measure the parameters' importance. In contrast, we propose Uncertaintyguided Continual Bayesian Neural Networks (UCB), where the learning rate adapts according to the uncertainty defined in the probability distribution of the weights in networks. Uncertainty is a natural way to identify what to remember and what to change as we continually learn, and thus mitigate catastrophic forgetting. We also show a variant of our model, which uses uncertainty for weight pruning and retains task performance after pruning by saving binary masks per tasks. We evaluate our UCB approach extensively on diverse object classification datasets with short and long sequences of tasks and report superior or on-par performance compared to existing approaches. Additionally, we show that our model does not necessarily need task information at test time, i.e. it does not presume knowledge of which task a sample belongs to.

** post rebuttal start **
After reading reviews and authors' response, I decided not to change my score.
I am happy with the author's response addressing my concerns (mainly about the fairness on the size of the model), so I recommend its acceptance. I believe it is a good addition to the community of continual learning.
** post rebuttal end **
- Summary:
This paper proposes to use a way to improve continual learning performance by taking "Bayes-by-backprop" method. They claim that the uncertainty can naturally be measured by estimating (log of) the standard deviation, and it is indeed useful to judge the importance of each learnable parameter. Experimental results on several benchmarks show that their method outperforms few state-of-the-art methods.
- Decision and supporting arguments:
Weak accept.
1. The proposed method is simple but effective. However, It is still questionable whether \sigma is the best measure of the weight importance. An ablation study with different choices of the importance measure (maybe \mu can also be incorporated as well as \sigma?) would be good to see.
2. Survey and comparison with memory-based methods are limited. Though memory-based methods require some memory to keep the experience, the proposed method also requires additional memory for \sigma; it essentially doubles the model capacity, assuming that \sigma is solely for measuring the weight importance. In particular, when it comes to large-scale models, memory for storing some important experiences would be small compared to the memory to store the model.
Here are some papers about recently proposed memory-based methods, which are not cited:
Castro et al. End-to-End Incremental Learning. In ECCV, 2018.
Wu et al. Large Scale Incremental Learning. In CVPR, 2019.
Lee et al. Overcoming Catastrophic Forgetting with Unlabeled Data in the Wild. In ICCV, 2019.
3. Comparison should include the model capacity as in Table 1(b). Again, compared to the conventional non-Bayesian model, half of the model capacity is used for computing \sigma (uncertainty), I wonder it causes a performance drop when the model capacity is the same over all compared methods. If they used the same model architecture and just doubled the number of learnable parameters for \sigma, then it is obviously unfair.
- Comments:
1. Pruning is not beneficial in terms of the performance. I hope to see some quantitative benefits obtained by introducing pruning. In Table 1(b), why doesn't pruning reduce the number of parameters?


Hypernetworks are meta neural networks that generate weights for a main neural network in an end-to-end differentiable manner. Despite extensive applications ranging from multi-task learning to Bayesian deep learning, the problem of optimizing hypernetworks has not been studied to date. We observe that classical weight initialization methods like Glorot & Bengio (2010) and He et al. (2015), when applied directly on a hypernet, fail to produce weights for the mainnet in the correct scale. We develop principled techniques for weight initialization in hypernets, and show that they lead to more stable mainnet weights, lower training loss, and faster convergence.

Review of “Principled Weight Initialization for Hypernetworks”
There has been a lot of existing work on neural network initialization, and much of this work has made large impact in making deep learning models easier to train in practice. There has also been a line of work on indirect encoding of neural works (i.e. HyperNEAT work of Stanley, and more recent Hypernetworks proposed by Ha et al) which showed promising results of training very large networks (in the case of Stanley), or have network weights that can adapt to the training data (in the case of Hypernetworks), and these approaches have been shown to be useful in applications such as meta-learning or few-shot learning (i.e. [1]). However, as far as I know, there hasn't been any work that looks at a principled way of initializing the weights of a weight-generating network, which this work tries to explore.
Making the observation (and claim) that traditional init methods don't init hypernetworks properly, they propose a few techniques to initialize hypernetworks ("Hyperfan"-family), which are justified in a similar way as original classical init techniques (i.e. preserving variance like in Xavier init), and they demonstrate that their method works well for feed forward networks on MNIST, CIFAR-10 tasks compared to traditional classical init methods, as well for a continual learning task.
I liked the paper as they identified a problem that hasn't been studied, and proposed a reasonable method to solve it. Their method may be able to make Hypernetworks accessible to many more researchers and practitioners, the way classifical init techniques have made neural net training more accessible.
There are a few things that could improve the paper (and get an improvement score from me). The authors don't have to do all of these, but just a few suggestions:
1) The experiments, to my understanding, are all feed forward networks. How about RNNs or LSTMs?
2) Are there any (interesting) tasks that use Hypernetworks that are not trainable with existing methods, but made trainable using this proposed scheme?
3) Would this method also work with HyperNEAT [2] or Compressed Network Search [3]? (probably should cite that line of work too). In [3], a research group at IDSIA used DCT compression to compress millions of weights into a few dozen parameters, so would be interesting if the approach will work on similar "learn-from-pixels" RL experiments.
I'm assigning a score of 6 (it's currently like a "really good" workshop paper, but a normal conf paper IMO), but I like this paper and would like to see the authors make an attempt to improve it, so I can improve the score to see it get accepted with a higher certainty.
Good luck!
[1] i.e. https://www.ncbi.nlm.nih.gov/pmc/articles/PMC6519722/ https://arxiv.org/pdf/1710.03641.pdf https://arxiv.org/pdf/1703.03400.pdf
[2] http://eplex.cs.ucf.edu/hyperNEATpage/
[3] http://people.idsia.ch/~juergen/compressednetworksearch.html
*** Revised Score ***
Nov20: Upon reading the other reviews, and looking at the changes to the paper with the extra citations, I'm improving the score to 8. (For the record, if this was a 1-10 scale, I would have liked my score to be a 7).


Given a video and a sentence, the goal of weakly-supervised video moment retrieval is to locate the video segment which is described by the sentence without having access to temporal annotations during training. Instead, a model must learn how to identify the correct segment (i.e. moment) when only being provided with video-sentence pairs. Thus, an inherent challenge is automatically inferring the latent correspondence between visual and language representations. To facilitate this alignment, we propose our Weakly-supervised Moment Alignment Network (wMAN) which exploits a multi-level co-attention mechanism to learn richer multimodal representations. The aforementioned mechanism is comprised of a Frame-By-Word interaction module as well as a novel Word-Conditioned Visual Graph (WCVG). Our approach also incorporates a novel application of positional encodings, commonly used in Transformers, to learn visual-semantic representations that contain contextual information of their relative positions in the temporal sequence through iterative message-passing. Comprehensive experiments on the DiDeMo and Charades-STA datasets demonstrate the effectiveness of our learned representations: our combined wMAN model not only outperforms the state-of-the-art weakly-supervised method by a significant margin but also obtains an improvement of 10% for the Recall@1 accuracy metric over stronglysupervised state-of-the-art methods on the DiDeMo dataset.

Summary:
This paper proposes a method for aligning an input text with the frames in a video that correspond to what the text describes in a weakly supervised way. The authors propose a combination of a “Frame-By-Word” (FBW) representation and a Word-Conditioned Visual Graph (WCVG). The proposed method outperforms the weakly supervised baseline presented in the paper in experiments by a large margin. In addition, it quantitatively performs close to previous strongly supervised methods.
Pros:
+ New Word-Conditioned Visual Graph representation
+ Outperforms weakly supervised baseline
+ Ablation study of the moving parts
+ Interesting use of positional embeddings for multi-modal learning
Weaknesses / comments:
- What is the processing speed of the method compared to the baseline?
The proposed method makes multiple comparisons while computing the attention weights over all words and frames. Does this cause the method to be slower than the baseline? If so, how much slower is it?
Answers to these questions can help readers to keep in mind the trade-off of the proposed method for achieving the accuracy presented in the paper.
- Number of parameters comparison with baseline:
Did the authors make sure to have similar number of model parameters for the baselines and the proposed method? Maybe I missed it, but I couldn’t see a mention of this anywhere. It would be useful to state this so that readers are sure that it’s not the number of parameters that is helping the method.
- Assumption that sentences are only associated with its ground truth video:
The authors mention that they have the same assumption as Mithun et al., 2019. Can this assumption be detrimental if the dataset does not follow it? Say there are sentences in the dataset that could describe segments in multiple videos. Could this assumption lead to suboptimal representation learning / relationship learning for words / video frames?
- Determining the size of the sliding window:
From reading the paper, it looks like the sliding window used for computing the word / frame relationships has to be manually defined. This seems a bit suboptimal for the generalizability of this method. Do the authors have any comments on this?
- Can this model be supervised? If so, how does it compare to the supervised baselines?
The authors point out that their weakly supervised method performs close to the strongly supervised previously proposed. This is a nice finding, however, have the authors try to answer the question of what would happen if the proposed model is supervised? Will the proposed model outperform the strongly supervised baselines? Or at least perform the same?
Conclusion:
In conclusion, the proposed method makes sense and it has been shown to empirically outperforms a previous weakly supervised baseline. The authors also provide an ablation study of the moving parts to show that the entire pipeline is important to achieve the highest performance in the hardest setting. It would be nice if the authors successfully answer / address the questions / concerns mentioned above in the rebuttal.


This paper addresses the problem of training a classifier on a dataset with missing features and its application to a complete or incomplete test dataset. A supervised learning method is developed to train a general classifier, such as a logistic regression or a deep neural network, using only a limited number of observed entries (features), assuming sparse representations of data vectors on an unknown dictionary. The pattern of missing entries is independent of the sample and can be random or structured. The proposed method simultaneously learns the classifier, the dictionary and the corresponding sparse representations of each input data sample. A theoretical analysis is also provided comparing this method with the standard imputation approach, which consists on performing data completion followed by training the classifier based on their reconstructions. The limitations of this last "sequential" approach are identified, and a description of how the proposed new "simultaneous" method can overcome the problem of indiscernible observations is provided. Additionally, it is shown that, if it is possible to train a classifier on incomplete observations so that its reconstructions are well separated by a hyperplane, then the same classifier also correctly separates the original (unobserved) data samples. Extensive simulation results are presented on synthetic and well-known reference datasets that demonstrate the effectiveness of the proposed method compared to traditional data imputation methods.

1. Summary
The authors propose a scheme for simultaneous dictionary learning and classification based on sparse representation of the data within the learned dictionary. Their goal is achieved via optimization of a three-part training cost function that explicitly models the accuracy and sparsity of the sparse model, simultaneously with usual classification error minimization. An alternating optimization algorithm is used, alternating between sparse representations and other parameters.
The problem they want to address with this scheme is training over incomplete/partial feature vectors. A clean theoretical statement is provided that provides conditions under which a classifier trained via partial feature vectors would do no better in terms of accuracy, had it been trained on complete feature vectors. The authors claim this condition can be checked after training, although this ability is not validated/illustrated numerically.
2. Decision and Arguments
Weak Accept
a) Very nice mathematical result and justification. The proof is clear. However, why wasn’t the result used in the numerical section? You claim that the condition (4) can be evaluated to test optimality: how do your trained dictionaries compare to say another dictionary learning scheme? After all, this doesn’t seem to inform your actual learning scheme and is not used to evaluate your results. It would be nice to see a numerical validation/illustration of this result. Also is \delta_K really that easy to compute?
b) The numerical results are good—but lack error bars and comparators. I don’t understand why you considered so many comparators on synthetic data and none on more ‘realistic’ benchmark data.
c) Also I don't feel very satisfied doing image examples, it would be more interesting to work on difficult (eg medical) classification problems with large feature vectors
4. Additional Feedback
a) Very well and clearly written with intuitive examples and clean math. My only suggestion is to clarify in the abstract that there are missing *features*-- when I first read "incomplete data" I think of entire data samples that are missing from the training set. That makes no sense, but it became clear when I got to section 2.
b) Please use markers and dashes etc. with *every* line in your plots. It is hard (or impossible for many) to compare as is with such tiny thin lines.
5. Questions
a) Could you comment on statistical significance of your results? For synthetic data it should be easy to perform the experiments on a number of mask realizations and include error bars.
b) Why no comparators on benchmark datasets?
c) The proof of Thm 3.2 is nice—but how reasonable is the assumption that you have two dictionaries each with the exact same RIP constant \delta_K? Can that property be enforced (even approximately) during training? Or is it trivial that, given one such dictionary, there exists a second one?
d) See 2.a


We propose a potential flow generator with L 2 optimal transport regularity, which can be easily integrated into a wide range of generative models including different versions of GANs and normalizing flow models. With only a slight augmentation to the original generator loss functions, our generator not only tries to transport the input distribution to the target one, but also aims to find the one with minimum L 2 transport cost. We show the effectiveness of our method in several 2D problems, and illustrate the concept of "proximity" due to the L 2 optimal transport regularity. Subsequently, we demonstrate the effectiveness of the potential flow generator in image translation tasks with unpaired training data from the MNIST dataset and the CelebA dataset with a comparison against vanilla WGAN-GP and CycleGAN.

The paper proposes a ‘potential flow generator’ that can be seen as a regularizer for traditional GAN losses. It is based on the idea that samples flowing from one distribution to another should follow a minimum travel cost path. This regularization is expressed as an optimal transport problem with a squared Euclidean cost. Authors rely on the dynamic formulation of OT proposed by Benamou and Brenier, 2000. They propose to learn a time-dependent potential field which gradient defines the velocity fields used to drive samples from a source distribution toward a target one. Experiments on a simple 1D case (where the optimal transport map is known), and on images with an MNIST / CelebA qualitative example.
The use of this dynamic formulation is well known in the OT community. See as a good examples:
Trigila, G., & Tabak, E. G. (2016). Data‐driven optimal transport. Communications on Pure and Applied Mathematics, 69(4), 613-648.
and more generally Chapter 7 of the ‘Computational Optimal Transport’ book by Peyré and Cuturi.
The novelty arises from the use of neural networks to represent the potentials. However, the claim that the obtained map is the optimal transport map seems wrong to me, because:
The class of potential functions over which the optimization is performed is not the whole class of functions, leading to approximations;
The optimality conditions (a.k.a continuity or preservation of mass equations) are only enforced on sampled trajectories, not on the entire space.
While this claim should definitely be lowered, it is nonetheless still acceptable provided that the proposed model is performing good. On this part, the paper strength could be improved provided that comparisons with existing methods computing a Monge map could be given. Notably, a comparison with the approach from Seguy et al. 2018 is missing. On a same level, a qualitative comparison with cycleGAN  in Figure 4 is missing.
There are some unclear elements in the paper. The final, total, optimization problem is never clearly expressed. I believe a general algorithm presentation could help in understanding the general picture of the method. Notably, for instance, It is still not clear if the generator G is disconnected from the potential definition (following Eq. 10 I assume not). How are the trajectories sampled ? Is the discriminator trained on the same sampled trajectories or different ones ?  In the potential generator, it seems that the time is considered the same way as the feature space. Can you comment on this point ? Is it possible to evaluate the flow of different time stamps that the ones used for training ?
As a summary,
Pros:
An interesting way to represent time-dependent potentials with a network for regularizing generative models
Cons:
Not much theoretical novelties in the paper, nor a good analysis on the source of errors of the model (e.g. impact of discretization on the problem)
There are some unclear aspects in the paper (see comments)
The potential benefits of the approach over the state-of-the-art should be more clearly discussed.
Minor comment:
 P3. Uniqueness of Monge problem for the squared Euclidean cost should be attributed to Brenier 91 and his polar factorization theorem. McCann generalized it to Riemannian manifold.


Deep generative models such as Variational AutoEncoder (VAE) and Generative Adversarial Network (GAN) play an increasingly important role in machine learning and computer vision. However, there are two fundamental issues hindering their real-world applications: the difficulty of conducting variational inference in VAE and the functional absence of encoding real-world samples in GAN. In this paper, we propose a novel algorithm named Latently Invertible Autoencoder (LIA) to address the above two issues in one framework. An invertible network and its inverse mapping are symmetrically embedded in the latent space of VAE. Thus the partial encoder first transforms the input into feature vectors and then the distribution of these feature vectors is reshaped to fit a prior by the invertible network. The decoder proceeds in the reverse order of the encoder's composite mappings. A two-stage stochasticity-free training scheme is designed to train LIA via adversarial learning, in the sense that the decoder of LIA is first trained as a standard GAN with the invertible network and then the partial encoder is learned from an autoencoder by detaching the invertible network from LIA. Experiments conducted on the FFHQ face dataset and three LSUN datasets validate the effectiveness of LIA for inference and generation 1 .

LIA: Latently Invertible Autoencoder Review
This paper proposes a novel generative autoencoder, and a two-stage scheme for training it. A typical VAE is trained with a variational approximation: during training latents are sampled from mu(x) + sigma(x) * N(0,1), mu and sigma are regularized with KL div to match an isotropic normal, and the model minimizes a reconstruction loss. A LIA is instead first trained as a standard GAN, where an invertible model, Phi, (e.g. a normalizing flow) is hooked up to the Generator/Decoder, such that the output is G(Phi^{-1}(z)) with z~p(z), a simple distribution. In the second stage, the Generator/Decoder and Discriminator are frozen, and an Encoder is trained to minimize a reconstruction loss (in this paper, a pre-trained VGG network is used as a feature extractor to produce a perceptual loss) and maximize the “real” output of the frozen Discriminator on reconstructed samples.
The key advantage of this method is that during the second stage no stochasticity is injected into the network and Phi is not involved.This means that the encoder does not need to be regularized to produce a specific parametric form of its output (no KL(p || q))), instead implicitly learning to match the latent distribution expected by the generator through the reconstruction losses. Additionally, because the latent space is not e.g. an isotropic Gaussian, it can be more expressive and flexible, only being constrained to an invertible transformation of the distribution p(z) chosen during the first training stage.
The training procedure is evaluated using a StyleGAN architecture on several high-res, single-class datasets (faces and LSUN Cats/Cars/Bedrooms). The quality of the resulting reconstructions is compared against several methods which are also capable of inference (like ALI and post-training an encoder on a standard StyleGAN), and samples and interpolations are presented. There is also an experiment that compares gradients in the encoder when training using LIA against training using a more typical VAE setup.
My take: The key idea behind this paper is quite promising, and I believe this paper has tremendous potential. I agree with the authors that the usefulness of implicit generative models is limited by their typical lack of an encoder network, and that existing approaches have several design drawbacks, and incorporating invertible networks and advances in flow-based modeling looks like a fruitful avenue of research.
However, I have a litany of concerns with the paper itself, concerning its high similarity with a paper published in May, its motivation, its presentation, its empirical evaluation, and the analysis presented within. While my concerns and suggestions are extensive, this paper is perhaps unusual in that all of the issues I have are quite fixable; the core idea is good, but its realization and presentation in the paper need a substantial amount of revision. I am currently giving this paper a weak reject as I do not believe it is ready for publication, but I believe that with an overhaul this paper could be a more clear accept.
Update, post rebuttal:
Thanks to the authors for their response. While I appreciate their insistence that my issues with the paper likely stem from my simply not understanding it (or the underlying topics), I hope they can appreciate that such an appeal is unlikely to allay said concerns. Pointwise:
1. While there is of course a difference between the LIA setup and the GLF setup, regardless of the two-stage training or the inclusion of an adversarial or perceptual loss or any other bells and whistles that get attached, the fact remains that the resulting architecture for both LIA and GLF is an autoencoder with an invertible model in the middle. Arguing that the LIA setup is somehow fundamentally different is akin to arguing that a VAE-GAN is an utterly different model from a VAE with a VGG perceptual loss. Yes, they're optimizing slightly different things (distribution-wise differences vs sample-wise differences) , they have different characteristics, etc., but at the end of the day they're still autoencoders with extra bits on the end. The same general principle holds here. As I stated in my original review, I consider the differences relatively minor and maintain my stance that comparison is warranted.
1(a). While the authors may have completed the work over a year ago, the fact that the other work was made public multiple months before this work means that it does, in fact, count as prior work. There is plenty of precedent at ICLR for work which appeared on arXiv well before submission date to be considered as prior work. I understand that this can be frustrating if the authors have previously submitted to other conferences and wished to wait until acceptance before making the work public, but that is a personal choice that does not change the nature of the situation.
2. If interfacing with image manipulation techniques is the motivation for improving reconstructions, this motivation should be clearly stated in the paper. After rebuttal there is still no mention of this motivation, which suggests to me that the authors expect all readers to consider "reconstruction" (which I again posit is not really a task) to matter intrinsically.
3. I once again appreciate that the authors hold that this reviewer is incorrect about basic facts. The forward KL placed on the latent space of a VAE only encourages it to resemble a particular distribution (typically isotropic gaussian) but the information content passed through the bottleneck can indeed grow with the size of the latent space, as one can see experimentally by ablating the latent dimensionality. This general principle should also be reinforced when one considers that flow models with exact inference (i.e. perfect reconstructions) require dz==dx.
4. This reviewer maintains that sampling a random input from a distribution during training involves stochasticity.
5. This still does not address my concern that reconstruction is not a particularly relevant task.
7-9: Thank you for modifying the caption in this figure, though I still hold that the y-axis should be correctly labeled. This still does not address my concern that this experiment does not actually show what the authors claim it does--the magnitude of the gradient noise is not by any measure a viable indication that the inclusion of phi is doing anything meaningful in place of a standard MLP  as the comparison is instead made to an entirely different training setup.
I maintain my stance of rejection.
Original review:
First off, a paper published in May on arXiv titled “Generative Latent Flow” (GLF) proposes an idea which is in essence identical to the one proposed in this paper. In GLF, a VAE is trained, but rather than using the reparameterization trick, a true normalizing flow is trained to model the distribution of the output of the encoder (i.e. with NLL using the change of variables formula common to flow-based models), such that the training of the actual autoencoder is truly deterministic (in the sense that at no point is an epsilon~p(z) sampled like in a normal VAE. The core difference between LIA and GLF is that GLF learns to model the distribution of the encoder outputs to enable sampling, while LIA incorporates an invertible model into a generator which explicitly through sampling, and then fits an encoder post-hoc. There are other differences in implementation and the choice of datasets, but those are (IMO) minor details relative to the core similarity. Given that GLF was published 4 months before the ICLR2020 deadline, this paper absolutely must be cited, compared against, and discussed. I am somewhat inclined to argue that given the similarity, LIA is merely incremental relative to GLF, but for now I think it is sufficient to point out the existence and similarity.
Second, the stated motivation in this paper is, I think, misguided. The authors argue for the need of an inference network, but they explicitly make clear that their goal is to train this network to enable reconstruction of an x given a z, rather than e.g. to learn a “good representation” (bearing in mind that what constitutes a good representation is strongly subject to debate). The authors do not provide any motivation for why reconstruction matters. At no point is an application or downstream task presented or mentioned in which good reconstructions are relevant. One might argue that choosing reconstruction quality is as arbitrary as pursuing improved sample quality (as is in vogue in GAN papers)  but there is substantial evidence that improved sample quality correlates with improved representation learning (mode dropping in GANs notwithstanding); the case is more complex for high-quality reconstructions.
Reconstruction could perhaps be motivated from the point of view of compression, but this paper makes no attempt to examine compression: rate-distortion tradeoffs are not considered, nor are any empirical metrics of compression ratio or likelihood such as bits/dim presented. Given that one can produce a model which achieves arbitrarily high-quality reconstructions by simply increasing the dimensionality of the bottleneck, I do not find reconstruction to be a compelling problem.
One might also argue that improved reconstruction capacity is indicative of better ability to fit the distribution (i.e. less mode dropping), but in the LIA setup the generator is trained as a standard StyleGAN with the only modification being the replacement of the MLP with Phi, so there’s no reason to believe that the implicit model defined by G has been meaningfully affected by the inclusion of the post-hoc trained encoder.
If the authors wish to pursue “reconstruction” as the primary motivation for learning an encoder, I would suggest they spend more time discussing compression and the latent bottleneck, as well as performing more detailed empirical evaluations (explained below). Basically, *why* does reconstruction matter? Alternatively, the authors could demonstrate the usefulness of their learned encoders for downstream tasks to indicate that the representations they learn are of high quality and useful.
Third, the presentation of this paper needs a lot of work. There are typos and confusing statements throughout, as well as several instances of overstatement.
The key insight of this paper appears to be that “having an invertible network at the input to the generator makes it more amenable to post-hoc learning an encoder.” If I understand correctly, the only difference between this method and Encoded StyleGAN is that this paper uses an invertible model in place of the StyleGAN MLP. If this is the case, then the paper needs to (a) make clear the minimality of this difference and (b) devote substantial exposition to exploring the difference and why this is important (see my comments in the experimental section).
Phrases like “the two-stage training successfully handles the existing issues of generative models” suggests that this method has solved all of the problems in generative modeling, which the authors have by no means demonstrated to be the case.
Calling the two stage training “Stochasticity free” is incorrect—if you’re training the model as a GAN, then (1) you’ll be sampling z’s in the first place so it already has a latent distribution defined and (2) the end result of training will be much more variable than, say, training with a likelihood metric. There is a *ton* of stochasticity in the first stage of training!
The paper states several times that the “critical limitation” of adversarial models is their lack of an encoder. While implicit generative models do not generally require an encoder, there are plenty of methods (BiGAN by Donahue and ALI by DuMoulin, along with all the VAE-GAN hybrids) that jointly learn encoders, and much work on training an encoder post-hoc. These methods are acknowledged in the related work, but I think they should be taken into consideration when describing this “critical limitation.” While not having an encoder does indeed hinder or prevent the use of an implicit model for inference, I think stability, mode dropping, and mode collapse are more prominent issues with GANs. I think the authors might do better to say something to indicate that the challenge is to train a model which both has sharp, high-quality samples (as with GANs) which is still capable of inference or explicit likelihood evaluation (VAEs, etc).
In general, I found the description of the model itself to be confusing, and needed several thorough read-throughs just to understand what was going on: what was being frozen when, the fact that the model is just a GAN with a post-hoc trained encoder--I felt that there was a lot of obfuscatory language obscuring the actual simplicity of the method (which might arguably be its strength).
While I would generally like the paper’s exposition to be improved, I understand that saying “write it better” is unhelpful so please see my individual notes at the end of this review for additional specific points.
Fourth, I found the empirical evaluations to be somewhat weak. To be clear, the results appear to be very good-the model retains the sample quality of  StyleGAN (at least as far as can be seen from the presented samples) while achieving noticeably higher-quality reconstructions on all the tested datasets. However, the metrics used for evaluation are limited—while at least MSE is presented, I would again stress that reconstruction is an odd metric to use when other factors like compression rates are not considered. While it is interesting to note that in this exact setup (mostly dim_z=512) LIA outperforms the baselines wrt the chosen metrics, a more thorough evaluation would, for instance, sweep the choice of dim_z, and ideally present NLL results (which I think are possible to evaluate given that LIA has a flow model even if it’s not trained using NLL, but I’m not 100% sure on this front and am open to counterarguments on this front).
What’s more, the datasets chosen are all single-class datasets with a massive amount of data—as far as generative modeling is concerned, these are very datasets with a minimal amount of variation. This is critical because the LIA method relies on pre-training a GAN, meaning that it does nothing to deal with problems like mode dropping and mode collapse. While we may not see much mode dropping on these very easy datasets (where there are, essentially, very few modes), this is still a substantial problem in the general case, as can be seen by results on e.g. ImageNet. If your GAN collapses or drops modes then post-training the encoder is not likely to be able to recover them. This is also arguably a weakness of this paper relative to GLF which incorporates the encoder into the training loop of the decoder and is likely to be better at covering modes.
Accordingly, I have substantial concerns that this method will not work well on datasets outside of these highly-constrained, nearly-unimodal, single-object, very-high-data datasets. While I would of course prefer to see results on something massively multimodal like ImageNet (training on a 100-class subset @ 64x64 resolution would be about 100,000 images and should be even less hardware intensive than the already performed experiments) I am aware of how cliché it is for reviewers to ask for imagenet results. Auxiliary experiments on CIFAR-100 or something with more than one class would go a long way towards allaying my concerns on this front.
Next, no error bars are presented; this is simply inexcusable. Given that no hardware requirements are presented it is difficult to judge if expecting multiple runs is unreasonable but unless each run requires weeks of the authors’ full hardware capacity, there is no reason for the authors not to include error bars or expected variances on the numbers for as many of their experiments as possible.
Further, I found the experiment in 5.3 to be confusing and the results irrelevant to the argument made by the authors. First of all, what does it mean that the “gradients” are plotted in the figures relating to this experiment? Are these gradient norms for a layer in the network, and if so, what type? Is the loss in Figure 5c the training loss or the test loss? I also disagree that the VAE “gradients” are “more unstable” than the LIA “gradients,” they are simply noisier. I do not see why the increased gradient noise relative to LIA is indicative of the superiority of the method, but is instead entirely expected given that noise is explicitly injected into a standard VAE—I would argue that the change in gradient noise is simply the result of removing the stochasticity, but it says nothing as to whether or not the LIA method is better than the VAE method. Again, I agree that using an invertible network in some capacity is preferable to using the reparameterization trick, but I found this specific experiment to be distracting.
I think the paper would do better to explore the importance of the invertible network relative to the exact same procedure but with the invertible network replaced with an arbitrary MLP of similar capacity. This appears to be what the encoded styleGAN model is, but I think it would do more to elucidate the key insights of this paper if the analysis was to focus more on this front. Why is it helpful to have an invertible phi in place of the StyleGAN MLP? What happens as the capacity of this portion of the model is increased or decreased? What is the form of the distribution output by Phi (maybe just some histogram visualizations along different dims?), and how does it compare to that of the typical MLP? What is the form of the distribution output by the encoder, and how does it differ from (a) the analytical latent distribution in the case of encoded styleGAN and (b) the empirical latent distribution of LIA? There’s quite a bit to explore there but this paper doesn’t dig very deep on this topic.
I recognize that the amount of suggestions and changes I have listed are exceptionally large (more than I’ve personally ever written before, for sure), and I want to make it clear that I don’t expect the authors to address them all in the limited timespan of the rebuttal period. While this unfortunately may mean that there is simply not enough time for my concerns to be addressed, if this is the case then I hope these suggestions prove useful for publication in the next conference cycle, where this paper could be very strong. As it is, given the extent of my concerns, this paper is currently sitting at about a 4/10 in my mind.
Minor notes:
“In the parlance of probability,” page 2. I liked this alliteration a lot. This paragraph as a whole was quite clear and well written.
“But it requires the dimension dx of the data space to be identical to the dimension dz of the latent space” Minor nitpick, but I would swap “dx of the data” with “dz of the latent space” in this sentence, to make it clear that the model’s latent dimensionality is constrained by the dimensionality of the data. As written it makes it sound like it’s the other way around.
“The prior distribution can be exactly fitted from an unfolded feature space.” While flows have exact inference, saying that you can exactly fit the distribution of the encoder is arguably inaccurate unless you can show perfect generalization. Specifically, if you attain 0 training loss for the flow, do you also have 0 test loss (i.e. the NLL of the flow on  the encoder’s output for test samples is also minimized).
Furthermore, the phrasing “unfolded feature space” (used elsewhere in the paper) is confusing and not in common usage—does this mean the output of the encoder, or some sort of Taylor expansion? It’s not immediately clear, and I would recommend the authors find a different way to express what they mean.
“Therefore the training is deterministic” Training is not deterministic if the first stage of training involves training a GAN. You are still sampling from a preselected prior in this stage.
“As shown in Figure 1f, we symmetrically embed an invertible neural network in the latent space of VAE, following the diagram of mapping process as…” This sentence is confusing. The term “embed” has a specific meaning in the literature: you might use word embeddings, or embed a sample in a space, but to “embed a [model] in a latent space” doesn’t make sense to me. I think the authors would do well to use more standard terminology, and to reconsider their description of the model to be more concise and clear.
“Our primal goal is to faithfully reconstruct real images from the latent code.” Primal should be primary. I would also like to see this motivated better—why do you care to exactly reconstruct real images? Is there a downstream task where this is relevant or an intrinsic reason why we should care about being able to attain exact reconstructions?
“indispensable discriminator.” Indispensible means “something you can’t get rid of,” whereas it would appear the discriminator is not used after  training (and is frozen after the first stage)—do the authors perhaps mean “dispensable” or “disposable”?
“The interesting phenomenon is that the StyleGAN with encoder only does not succeed in recovering the target faces using the same training strategy as LIA, even though it is capable of generating photo-realistic faces in high quality due to the StyleGAN generator” This sentence is confusingly written and poorly supported. While I do agree that the LIA reconstructions are superior to the encoded styleGAN reconstructions, exactly what do the authors mean that LIA “recovers” the target faces while StyleGAN does not? The LIA reconstructions are not identity preserving—while most of the semantic features are the same, and the model does do a good job of picking up on unusual details such as hats, the facial identities are definitely not preserved (i.e. for every face in row 1 and row 2, I would say that the two faces belong to different people with similar features, but they are still definitely different people) .
“This indicates that the invertible network plays the crucial role to make the LIA work” This statement is unsupported. There are a number of differences in training setup, and the authors, in this reviewer’s opinion, have not presented evidence to indicate that the use of the flow model is specifically responsible for this. Specifically, what would happen if during the decoder training stage, the invertible network was not employed? While I do believe that the inclusion of the invertible network is important, the authors should go to greater lengths to elucidate exactly what it does (see my comments above in the experimental section re. the shape of the distribution and how the encoder ends up matched to the decoder depending on what the actual latent distribution is from the POV of the generator).
“To further evaluate LIA on the data with large variations” The choice of three single-category, single-subject datasets for evaluation is strictly at odds with this statement. These are highly constrained, clean datasets with tremendous amounts of data per class, which are substantially less difficult to model than e.g. ImageNet
“They will be made them available for evaluation.” -> “These subsets will be made available for evaluation”
“The experimental results on FFHQ and LSUN databases verify that the symmetric design of the invertible network and the two-stage training successfully handles the existing issues of generative models.” This statement is far too strong—saying a method “successfully handles the existing issues of generative models” suggests that this method is the end-all be-all and has solved the problem of generative modeling entirely. I would suggest the authors dial back the strength of this claim.
“Table 2: FID accuracy of generative results.” What is FID accuracy? Do the authors just mean FID?
Specify hardware used and training times, at least in the appendix.


Mode connectivity provides novel geometric insights on analyzing loss landscapes and enables building high-accuracy pathways between well-trained neural networks. In this work, we propose to employ mode connectivity in loss landscapes to study the adversarial robustness of deep neural networks, and provide novel methods for improving this robustness. Our experiments cover various types of adversarial attacks applied to different network architectures and datasets. When network models are tampered with backdoor or error-injection attacks, our results demonstrate that the path connection learned using limited amount of bonafide data can effectively mitigate adversarial effects while maintaining the original accuracy on clean data. Therefore, mode connectivity provides users with the power to repair backdoored or error-injected models. We also use mode connectivity to investigate the loss landscapes of regular and robust models against evasion attacks. Experiments show that there exists a barrier in adversarial robustness loss on the path connecting regular and adversarially-trained models. A high correlation is observed between the adversarial robustness loss and the largest eigenvalue of the input Hessian matrix, for which theoretical justifications are provided. Our results suggest that mode connectivity offers a holistic tool and practical means for evaluating and improving adversarial robustness.

This paper proposes an adversarial defense method based on mode connectivity. The goal of the method is to repair tampered networks using a limited number of clean data examples. The authors consider two types of adversarial attacks: backdoor attacks and error-injection attacks. The proposed method takes two potentially tampered networks, then constructs a low-loss path connecting the weight vectors of the given models in the space of network parameters (the path is constructed using the small set of clean data examples), finally an intermediate point on the path is used as a weight vector corresponding to the “repaired” model. The authors analyze the properties of the paths and show that intermediate points on the mode-connecting paths deliver both high clean-data accuracy and low attack success rate. In the experiments the proposed method shows better results compared to baseline defense techniques including fine-tuning, training from scratch, and pruning followed by fine-tuning. The paper also analyzes evasion adversarial attacks from the perspective of mode-connectivity and observes the existence of barriers in the landscape of robustness loss on the paths connecting regular and adversarially-trained models.
I would like to note that the text of the paper is well-structured and clear. Another strength of paper is that the authors consider multiple supporting experimental settings and extensions of the proposed method. The considered cases include adaptive attacks (the settings in which the attacker is aware about the employed defense method).
Although there are many strong sides of this paper, I have identified several serious flaws in the justification of the approach and the results. Thus, I consider the paper to be marginally below the acceptance threshold. I am willing to increase the score if the authors address my concerns expressed below.
1) What is the conceptual difference between using mode-connectivity and fine-tuning?  Both methods try to find a point in the weight space which (1) is close to the initial point and (2) delivers low loss on the bonafide data. What feature of the proposed method can explain its success? The “technical explanations” for the effectiveness of the proposed path connection method only show that the random sampling procedure fails to find models with high-clean-accuracy and low-attack-accuracy. However, this doesn’t necessarily mean that fine-tuning (which performs directed search) cannot find models which perform similarly to the models found by the proposed method (potentially the hyperparameters of the fine-tuning procedure can be tuned better). Given the aforementioned similarity of the proposed approach and fine-tuning, the explanation (either theoretical or empirical) for the effectiveness of the proposed method has to be provided in order to motivate the methodological proposal of the paper.
2) Please report the error bars of the accuracy computed over multiple runs of the experiments (according to Appendix E multiple runs were performed, but only the mean values of the accuracy are reported). Including the error bars would help to quantify the statistical significance of the results.
3) What strategy was used to choose the parameter t? The parameter has different values depending on the model/dataset. How should this value be chosen in general?
4) In the formulation of Proposition 1 it is first stated (assumption (c)) that the directions of the gradient w.r.t. x and the vector v are aligned (the normalized dot product of the vectors is >= c), however then the proposition requires that the vectors must be similar. Why assumption (c) has to be included in this formulation, if the proposition also requires a stronger condition? Either the assumptions or the claim of the proposition has to be formulated clearly. For example, it can be explicitly stated that the proportionality holds approximately (up to terms which go to 0 as c goes to 1). I also recommend to include a term which accounts for the tail of the Taylor expansion in equation A4 instead of using the “approximately equals” sign. Moreover, I recommend to include the discussion of the effect of this tail term on the proof and the statement of the preposition.
Additional minor comments, which do not affect the assessment:
In Section 3.1, paragraph 3 the description of Figure 1 reads as follows: “our path connection is trained using different portion of test data”. Another sentence below in the paragraph: “For example, path connection using merely 1000/2500 CIFAR-10 samples from the test set only reduces the test accuracy of VGG16 models by at most 10%/5%”. Which part of the dataset was used for finding the path connections? How the “test data”, which is claimed to be used for finding paths, is different from the test set used to evaluate the accuracy of the models?