The source code of a program not only serves as a formal description of an executable task, but it also serves to communicate developer intent in a humanreadable form. To facilitate this, developers use meaningful identifier names and natural-language documentation. This makes it possible to successfully apply sequence-modeling approaches, shown to be effective in natural-language processing, to source code. A major advancement in natural-language understanding has been the use of pre-trained token embeddings; BERT and other works have further shown that pre-trained contextual embeddings can be extremely powerful and can be finetuned effectively for a variety of downstream supervised tasks. Inspired by these developments, we present the first attempt to replicate this success on source code. We curate a massive corpus of Python programs from GitHub to pre-train a BERT model, which we call Code Understanding BERT (CuBERT). We also pre-train Word2Vec embeddings on the same dataset. We create a benchmark of five classification tasks and compare finetuned CuBERT against sequence models trained with and without the Word2Vec embeddings. Our results show that CuBERT outperforms the baseline methods by a margin of 2.9-22%. We also show its superiority when finetuned with smaller datasets, and over fewer epochs. We further evaluate CuBERT's effectiveness on a joint classification, localization and repair task involving prediction of two pointers.

# Summary
This paper presents a BERT-inspired pretraining/finetuning setup for source code tasks. It collects a corpus of
unlabeled Python files for BERT pretraining, designs or adopts 5 tasks on established smaller-scale Python corpora, and
adjusts the BERT model to tokenize and encode source code snippets appropriately.
# Strengths
* The idea of applying the pretraining/finetuning paradigm to program analysis tasks makes sense, and has been
  informally attempted by multiple groups in the community in 2019. This is the first high-quality submission to a
  top-tier ML conference I've seen on the subject, though.
* The authors exercised commendable care and diligence in preparing the training data, adopting BERT to source code
  inputs, and ensuring correctness of the experimental setup. I appreciated all the provided details on tokenization
  (Section 3.3), deduplication (Sections 3.1-3.2), and task setup (Section 3.5). This should become a technical standard
  in the community.
* The paper is written clearly and concisely, and is generally a pleasure to read.
# Weaknesses
I have a gripe with the authors' choice to ignore program structure (e.g. abstract syntax trees) or features (e.g.
types) in their program representation. Without this extra information (easily available from a compiler/interpreter
API) the pipeline is not substantially different from the original NLP pipeline of BERT et al. The main program-related
representation insight comes in tokenization (Section 3.3) and the definition of "sentences". To repeat, I appreciate
the effort the authors put in making tokenization appropriate for BERT processing of source code, but this is a drop in
the bucket compared to the all the other program-related features the work is leaving off the table. Programs are not
natural language.
The argument that source code analysis would "pass on the burden ... to downstream tasks" (Page 3) is odd. First, most
downstream tasks of interest occur in the settings where this analysis is already available: IDEs, code review
assistants, linters, etc. Second, one often needs program analysis to even define downstream tasks in the first place --
for example, determining whether function arguments are swapped required detecting a function call and boundaries of its
arguments, thus parsing the program!
This work obtains (and nicely analyzes) impressive results obtained by applying CuBERT. However, it does not put the
results in context with prior work based on structured program representations. Without this, it is difficult to say
whether the improvement comes from pretraining or from the language model simply learning a better "parsed"
representation of an input program from all the unlabeled corpus. If it's the latter, one might argue that supplying the
model with structured program features explicitly might eliminate much of the need for the unlabeled corpus.
I personally think that there will still be a gap between pretraining and finetuning even with structured program
features simply due to the sheer volume of available data, which, as the authors showed, is crucial for good
generalization of Transformer. However, this still needs to be shown empirically.
The "Function-Docstring Mismatch" task, as presented, seems too easy. If the distractors (negative examples) are truly
chosen at random, most of them are going to use obviously different vocabulary from the original function signature (as
Figure 4 demonstrates). A well designed task would somehow bias the sampling toward subtle distractors such as `get` vs.
`set` docstrings, but this seems challenging.
This also explains why the task is not influenced as much by reduction of training data (Table 3).
The Next Sentence Prediction pretraining task, as adapted for CuBERT, seems too difficult, in contrast. If the paired
sentences (i.e. code lines) are chosen at random, the model would lack most of the context required to make a decision
about the logical relationship between them, such as which variables are defined and available in context, which
functionality is being implemented, etc. I wonder, can the authors experiment with pretraining CuBERT only with the
Masked Language Model task? Will it worsen the results substantially or at all?
# Questions
Section 3.2: "similar files according to the same similarity metric..."
What are these metrics?
What is the fraction of positive/negative examples in the constructed finetuning datasets?
What is the motivation for making Variable Misuse and Wrong Operator/Operand into a simple classification tasks instead
of the original (more useful) correction task?


In this paper, we formulate hypothesis verification as a reinforcement learning problem. Specifically, we aim to build an agent that, given a hypothesis about the dynamics of the world can take actions to generate observations which can help predict whether the hypothesis is true or false. Our first observation is that agents trained end-to-end with the reward fail to learn to solve this problem. In order to train the agents, we exploit the underlying structure in the majority of hypothesesthey can be formulated as triplets (pre-condition, action sequence, post-condition). Once the agents have been pretrained to verify hypotheses with this structure, they can be fine-tuned to verify more general hypotheses. Our work takes a step towards a "scientist agent" that develops an understanding of the world by generating and testing hypotheses about its environment.

This paper trains agents which are able to verify hypotheses, such as “the blue switch causes the door to open”. It does this by first pretraining the agent to perform interventions in the environment which change the states of the objects of interest, and then finetuning the agent to actually make a decision about whether the given hypothesis is correct. The paper shows that agents trained using this procedure are able to not only verify the types of hypotheses seen during pre-training, but also learn to verify more complex hypotheses. In contrast, an agent which is trained directly on the hypothesis verification task is unable to learn to do it.
Overall, I enjoyed reading this paper and thought that it provided an interesting take on the question of how to train agents that can appropriately gather information about their environments. However, (1) the paper lacks any discussion of related work in terms of causal reasoning and partial observability, and (2) the experiments and analysis seem weak. I thus am giving a score of “weak reject”, though it is possible I could increase my score is some of my concerns can be addressed.
First, I was very surprised to see that the paper included no discussion at all about either causal reasoning or partial observability. The whole notion of verifying hypotheses—particularly those in the triplet form as presented in the paper—is equivalent to the idea of performing inference about the structure of a causal graph with three variables. The choice of which interventions to perform in order to make these inferences is a well-studied problem [1] and has been recently explored in the context of RL as well [2]. The novelty here seems to be in embedding the problem of causal reasoning in harder credit assignment problems (i.e. longer time horizon), though see [3]. Similarly, the setup of the MDP in the paper is actually a POMDP, where the state includes the truth value of the hypothesis but where observations do not include this information. Yet, there is no mention of POMDPs or discussion of the literature on partial observability in the paper.

Second, I felt that the setup was overly complex in places making it difficult to draw conclusions, that there were a lack of comparisons, and that the analysis was not as in depth as it could have been. For example, why is it necessary to represent the hypothesis with natural language? Why not use a symbolic representation? It seems like including the pseudo-natural language adds unnecessary complexity and makes it difficult to distentangle what about the problem is hard (Understanding the hypothesis? Choosing the right interventions? Parsing the observations correctly?). The utility of having it be closer to language is that you might see generalization between related hypotheses, but this isn’t really something that is actually tested for since all hypotheses are trained on either during pretraining or finetuning.

I also feel like the choice of pretraining reward feels somewhat arbitrary, and it would have been nice to see comparisons to other alternatives (and even better, to other forms of intrinsic motivation). For example, here are a few alternate ways of rewarding the agent that seem intuitively like they could also work:
Reward the agent for changing the state of any of the objects in the environment
Reward the agent for changing the state of any object referenced in the hypothesis
Reward the agent for observing a state of the world it has not seen before (i.e. count-based exploration)
In other words, how important is the fact that the reward is given based on the pre and postconditions?
I thought the paper would benefit from more detailed analyses to tease apart the behavior of the agent. For example, I am curious how many errors are a result of errors in the predictor versus poor exploration behavior by the policy. Could you report (1) how frequently the policy’s behavior results in the right observations necessary to make a decision, and (2) results with a policy which uses an oracle predictor (i.e. which will always report the correct answer, if there was enough data in the last N frames to detect that answer)?
On the more practical side, I also thought the quality of the evaluations was not very thorough. For instance, it looks like the pretraining proceeds for 1e8 steps and finetuning for 5e7 steps, based on the plots (these values should be stated more explicitly in the paper). However, this is a bit of an unfair comparison for the “RL Baseline”, as it only is trained for 5e7 steps while the other agents are trained for 1.5e8 steps. I would like to see a comparison where the RL Baseline agent is trained for 1.5e8 steps as well. Similarly, on the bottom of page 6 the paper says “we show the max out of five for each of the methods shown”. However, only reporting the max value is considered bad practice and can result in misleading comparisons (see Joelle Pineau’s talk on “Reproducible, Reusable, and Robust Reinforcement Learning” at NeurIPS 2018). I’d like to see the data in all figures and tables reported with means or medians across seeds, rather than best seeds.
A few minor comments:
- Please state in the main text which RL algorithm you use.
- Can you clarify whether Figure 2 show the proxy rewards or the true rewards?
- For R_pre and R_ppost, what values do you use for C and N?
[1] Pearl, J. (2000). Causality: models, reasoning and inference (Vol. 29). Cambridge: MIT press.
[2] Dasgupta, I., Wang, J., Chiappa, S., Mitrovic, J., Ortega, P., Raposo, D., ... & Kurth-Nelson, Z. (2019). Causal reasoning from meta-reinforcement learning. arXiv preprint arXiv:1901.08162.
[3] Denil, M., Agrawal, P., Kulkarni, T. D., Erez, T., Battaglia, P., & de Freitas, N. (2016). Learning to perform physics experiments via deep reinforcement learning. arXiv preprint arXiv:1611.01843.
--
Update after rebuttal:
Thank you very much for your response. However, I do not feel that all of my concerns have been addressed and thus will keep my score as it is. In particular, I still feel the paper lacks sufficient discussion of the literature on causal reasoning. I also do not think it is sufficient to add an appendix with the results across multiple seeds: these results should be in the main paper. I'm not sure I follow the justification that max seeds make sense because "the reward distribution is quite binary in nature"---the plots shown in Figure 3 and 4, for example, span a range of values from 0 to 1. I find the plots that have both variance and max seed very hard to interpret---in some cases the mean is so much lower than the max seed that the variance region doesn't overlap at all. More broadly, it might be easier to compare using bar plots showing final performance, rather than training curves
I appreciate the additional results, especially with different pretraining schemes---thanks for adding these! I have a bit of hard time interpreting the results though since there are no direct comparisons with the triplet pretraining scheme; it would be helpful if these results could be included in these figures too.


We consider the problem of fair and robust model training in the presence of data poisoning. Ensuring fairness usually involves a tradeoff against accuracy, so if the data poisoning is mistakenly viewed as additional bias to be fixed, the accuracy will be sacrificed even more. We demonstrate that this phenomenon indeed holds for state-of-the-art model fairness techniques. We then propose FR-GAN, which holistically performs fair and robust model training using generative adversarial networks (GANs). We first use a generator that attempts to classify examples as accurately as possible. In addition, we deploy two discriminators: (1) a fairness discriminator that predicts the sensitive attribute from classification results and (2) a robustness discriminator that distinguishes examples and predictions from a clean validation set. Our framework respects all the prominent fairness measures: disparate impact, equalized odds, and equal opportunity. Also, FR-GAN optimizes fairness without requiring the knowledge of prior statistics of the sensitive attributes. In our experiments, FR-GAN shows almost no decrease in fairness and accuracy in the presence of data poisoning unlike other state-of-the-art fairness methods, which are vulnerable. In addition, FR-GAN can be adjusted using parameters to maintain reasonable accuracy and fairness even if the validation set is too small or unavailable.

This paper proposes to use a GAN style approach for training a classifier that is robust to data poisoning and can achieve a pre-specified notion of group fairness.
The contribution of this paper is incremental in the context of prior Adversarial Debasing (AD) approach using essentially same GAN for group fairness and prior work presenting ideas of utilizing clean validation data to defend against data poisoning. This paper is proposing to add an additional discriminator to the AD approach that distinguishes training data and clean validation data. If the training data is poisoned, such distinguishment may be possible and maximizing loss of this discriminator can help to robustify against poisoned samples.
Experimental results are insufficient to argue improvement over the AD. There are no AD results in the equalized odds Adult experiment in the supplement. I recommend more detailed comparison against the AD method (including results showing confusion matrices). Also note that AD, as presented in the original paper, is optimizing for demographic parity, but can also be adjusted to other group fairness metrics. Finally, in the context of Adult dataset, it is important to also report performance metrics such as balanced TPR since the labels are quite imbalanced.
Are there any real data examples where poisoning does not need to be introduced artificially and the proposed method helps to improve the fairness properties? I think an interesting direction could be to consider data where labels are subjective. For example, a dataset on loan decisions can be naturally "poisoned" with human biases, i.e. information that someone did not receive the loan may be due to an error or bias of a human in charge of the decision making.
Lastly I think that the discussion of the prior related work on fairness is incomplete. This paper exclusively covers group fairness, which indeed has been shown to have some disadvantages. For example, prior work [1] has shown that some group fairness notions can not be satisfied simultaneously in certain cases. In this regard it is also important to report multiple group fairness metrics simultaneously in the experiments. The other fairness definition, that has not been mentioned in this paper, is individual fairness [2]. It has legal and intuitive interpretations. Multiple recent papers have explored the direction of individual fairness [3,4,5,6].
[1] Kleinberg, J., Mullainathan, S., & Raghavan, M. (2016). Inherent trade-offs in the fair determination of risk scores.
[2] Dwork, C., Hardt, M., Pitassi, T., Reingold, O., & Zemel, R. (2012, January). Fairness through awareness.
[3] Garg, S., Perot, V., Limtiaco, N., Taly, A., Chi, E. H., & Beutel, A. (2019, January). Counterfactual fairness in text classification through robustness.
[4] Yurochkin, M., Bower, A., & Sun, Y. (2019). Learning fair predictors with Sensitive Subspace Robustness.
[5] Kearns, M., Roth, A., & Sharifi-Malvajerdi, S. (2019). Average Individual Fairness: Algorithms, Generalization and Experiments.
[6] Jung, C., Kearns, M., Neel, S., Roth, A., Stapleton, L., & Wu, Z. S. (2019). Eliciting and Enforcing Subjective Individual Fairness.


Neural networks for structured data like graphs have been studied extensively in recent years. To date, the bulk of research activity has focused mainly on static graphs. However, most real-world networks are dynamic since their topology tends to change over time. Predicting the evolution of dynamic graphs is a task of high significance in the area of graph mining. Despite its practical importance, the task has not been explored in depth so far, mainly due to its challenging nature. In this paper, we propose a model that predicts the evolution of dynamic graphs. Specifically, we use a graph neural network along with a recurrent architecture to capture the temporal evolution patterns of dynamic graphs. Then, we employ a generative model which predicts the topology of the graph at the next time step and constructs a graph instance that corresponds to that topology. We evaluate the proposed model on several artificial datasets following common network evolving dynamics, as well as on real-world datasets. Results demonstrate the effectiveness of the proposed model.

This paper proposes a framework to model the evolution of dynamic graphs for the task of predicting the topology of next graph given a sequence of graphs. Specifically, the paper uses a combination of recently proposed techniques in graph representation learning (Graph Neural Network) and Graph Generation (GraphRNN [You et. al. 2018]). Given a sequence of graphs as input, a GNN (to obtain low-dimensional representations of the graphs in this sequence) and LSTM (to model the sequence of these representations)  based encoder is used to compute a vector representation of the topology of next graph in the sequence. The learned vector is then used as input to a GraphRNN decoder to generate a graph that would serve as a predicted next graph in the sequence. The proposed approach is validated with experiments on three synthetic datasets and one real-world dataset (Bitcoin is same dataset from two different resources with little difference in characteristics) and compared against random graph models.
This paper should be rejected due to following reasons:
(1) The authors do not justify/discuss the motivation and importance of the task and corresponding applications that would require to predict topology of complete graph in the next step.
(2) The proposed techniques are an adhoc combination of existing techniques with major concerns (details below) but also with little novelty (if any) for achieving this combination.
(3) The empirical efforts are very limited and does not provide enough evidence about the efficacy of the method, miss several details and does not serve as motivation for designing such a method in first place. Please note that negative results on cycle graphs has no role to play in this assessment. In fact,
I appreciate the authors for reporting negative results as it provides a transparent insights into the effectiveness of model in different settings.
Overall, the paper needs lot of work on all aspects - motivation, technique and experiments to make it fit for a conference publication.
Major Concerns:
(a) Motivation: The authors do not discuss or motivate the problem and why it is important to the community. The authors mention that many existing work on dynamic graphs focus on learning representations. This is the case because learned representations can then be used for various downstream applications and even future event predictions. When such methods can be used to do future predictions required for most applications, why does one need to predict the topology of complete next graph? The authors need to provide concrete justification for the problem they address, instances where such a task would be useful and discussion on other techniques that can do similar tasks but lack in aspects that such a method can capture. For instance, as a preliminary step, can the authors explain how solving this problem would be helpful to bitcoin?
(b) Technical: The technical contributions of this paper lack novelty and has several flows:
- Figure 1 seems to show that graph only grows in size. While the authors do provide an experiment with removal process, that experiment does not seem to perform well. So, does the method is only good to support growing graphs?
- Authors mention that the edge and node attributes are considered to be fixed. However, if the number of nodes and edges change, X and L should also change in terms of dimensions and adding values for new nodes/edges. so why should it not be considered time-varying?
- What was the motivation for using GRU for update function in Eq 3? Was simple MLP tried and not useful? Was GRU used to capture some long term dependencies in structure? If so, the authors must explain how it is useful for this task.
- Why Set2Set was used for ReadOut function? This seems to be a particularly adhoc and odd choice. when sum did not work well, jump to Set2Set is not justified. Can the authors provide an explanation for the same?
- The authors claim that the embedding h_G_T incorporates topological information -- I find this claim highly unsubstantiated and needs justification. For instance, can you provide some rigorous analysis to demonstrate that this is the case? At the least, can the authors use this vector and pass it through a graph decoder to recover the original graph?
- What is novel in 3.2.3 as compared to You et. al.? Infact, it is hard to see any novelty in the entire combination. Was it challenging to achieve this combination? If so, what was the challenging part? It is not clear what the authors contributed to address such a challenge. Was the training challenging? If so, please explain. If not, why is this a novel approach?
(c) Empirical: The empirical efforts are inadequate and raises more questions than answers.
- Synthetic datasets are simple and more datasets should be used e.g. You et. al. 2018 to validate the performance. Only one real-world dataset from two different sources is used. It is hard to understand author's motivation in doing so. Why not use various graph datasets available in papers that learn representations (e.g. cited by authors themselves) What is special about bitcoin dataset that makes it suitable for this task?
- Node/edge attributes are chosen in adhoc manner and it is unclear what role they perform. Do they help with prediction? If not, would it be useful to first show experiments without them? Or does this method absolutely need attributes? It is not clear why it is useful to set all attributes for edge as 1.
- How was window size of 10 chosen? Why is the same window size good for all graphs? What impact does window size has on performance?
- What is the motivation for using Graph kernel for similarity? The authors borrow the decoder from You et. al. 2018 which also provides a principled method to compare graphs using MMD based on statistics. Why not employ the same?
- GraphRNN (You et. al.) and other generative models can learn over multiple graphs? Did the authors try to feed the sequence of graphs to such models and then try to generate a new graph to see if they can produce similar results? It is true that those generative models do not specifically model temporal sequence, but such an experiment would help to distinguish the efficacy of the proposed method.
-The technique of using MLP for generating predictions using random graph models seem to be highly unfair for the baselines. Can you elaborate more as it is difficult to understand why one should handicap those models by using learned information instead of data information?
- A rigorous discussion on insights explaining the results is required. The authors show high performance on Bitcoin dataset. However,  it is not clear what part is contributing to the performance. Similarly, authors should dig deep into the failure cases and provide justification of why such a method would fail in particular cases and propose alternatives.
- Why was Graph size used as a statistic to report? Two graphs of same size can be entirely different and I do not see any merit in using such a metric. Again, something like MMD based metric may be useful.
Improvements that would make future revision strong but has not impacted current assessment:
Overall, the presentation of the paper is very unpolished. The authors are missing many important details as described above while spending a lot of time in describing (repeating) known techniques verbatim as original works. This can be removed and condensed into very short preliminary section.
- Notations: The authors must use clear notations. For instance, on Page 2, L is used to  describe edge attributes but then it is replaced by E in Page 3. Also, both X and L are shown to have dimension d. Are edge and node attributes of same dimension? w is used for window-size of sequence used as input and also as neighbor node. When modeling evolution of graphs where a sequence is available over time points 0...T, it is not useful to use T to also represent time step of GNN propagation. Infact, authors should avoid using time steps to signify GNN iterations.
- Empirical details: The details provided for datasets and experimental setup is inadequate. Why are the two Bitcoin datasets different from each other? What does Pos. Edges in Table 1 mean? What does  Mean and 90th percentile in Table 2 signify? Authors only talk about train-test split but then mention
validation set for hyper-param tuning. How was this validation set obtained? Also, what hyper-params were tuned and what was sensitivity of those hyper-params? Authors use GNN and multiple RNN's, what was the model capacity used and how it impacted the performance? Figure 5 (c) what is a circle graph?


This paper is concerned with solving combinatorial optimization problems, in particular, the capacitated vehicle routing problems (CVRP). Classical Operations Research (OR) algorithms such as LKH3 (Helsgaun, 2017) are extremely inefficient (e.g., 13 hours on CVRP of only size 100) and difficult to scale to larger-size problems. Machine learning based approaches have recently shown to be promising, partly because of their efficiency (once trained, they can perform solving within minutes or even seconds). However, there is still a considerable gap between the quality of a machine learned solution and what OR methods can offer (e.g., on CVRP-100, the best result of learned solutions is between 16.10-16.80, significantly worse than LKH3's 15.65). In this paper, we present the first learning based approach for CVRP that is efficient in solving speed and at the same time outperforms OR methods. Starting with a random initial solution, our algorithm learns to iteratively refines the solution with an improvement operator, selected by a reinforcement learning based controller. The improvement operator is selected from a pool of powerful operators that are customized for routing problems. By combining the strengths of the two worlds, our approach achieves the new stateof-the-art results on CVRP, e.g., an average cost of 15.57 on CVRP-100.

EDIT: I have read the responses and increased my rating to Weak Accept.
The paper proposes an algorithm for the Capacitated Vehicle Routing problem that starts with a random solution and then iteratively improves it by using a learned policy to select an improvement operator to apply to the current solution. Once the solution stops improving for a number of steps, a perturbation is applied to the solution, and the iterations continue by applying improvement operators selected by the learned policy. The problem is posed as a sequential decision problem, and the policy is learned using reinforcement learning. Results on synthetic instances of size 20, 50, and 100 show that the approach is able to achieve better objective value than relevant baselines and faster running time than the LKH algorithm.
Pros:
- Better objective value than baselines and running time than LKH is an impressive result.
- Paper is clearly written and easy to follow. CVRP and other background information is sufficient to fully understand the paper.
Cons:
- The proposed approach has the benefit of using a handcrafted pool of improvement operators that other learning-based approaches don’t have. This makes the comparison to previous learning approaches unfair, and the observed improvements may simply be due to the extra information that the approach gets in the form of the operator pool.
- The evaluation should be expanded to larger instances and existing benchmarks such as CVRPLib (which contains larger instances as well) to understand scalability and generalization to different instance distributions. For example, would the same improvement operator pool suffice for a completely different distribution of instances?
Additional comments:
- Typically when using RL for learning a local search policy, the reward is defined as the change in objective after applying a local move such that the sum of rewards and the initial objective value gives the actual objective value and the policy will be learning to optimize the objective function. In this paper the reward definitions RF1 and RF2 don’t have this property, which suggests that the policy is not being trained to directly optimize the CVRP objective function. Is there an explanation for why it still works?
- It would be useful to explore how well the self-attention network architecture scales to larger problems (e.g., > 1000 customers), and whether using a graph neural network instead results in better or worse results.
- Typo: “significantly worse then”
- Typo: “their would be no discounting”


We propose a fully convolutional network architecture that is able to estimate a full surface of pass probabilities from single-location labels derived from high frequency spatio-temporal data of professional soccer matches. The network is able to perform remarkably well from low-level inputs by learning a feature hierarchy that produces predictions at different sampling levels that are merged together to preserve both coarse and fine detail. Our approach presents an extreme case of weakly supervised learning where there is just a single pixel correspondence between ground-truth outcomes and the predicted probability map. By providing not just an accurate evaluation of observed events but also a visual interpretation of the results of other potential actions, our approach opens the door for spatiotemporal decision-making analysis, an as-yet little-explored area in sports. Our proposed deep learning architecture can be easily adapted to solve many other related problems in sports analytics; we demonstrate this by extending the network to learn to estimate pass-selection likelihood.

The aim of the system presented in this paper is to produce a 2D map of probabilities showing the chance of successful completion of a soccer pass to all locations on the field, given coordinate locations of players and the ball sampled over time.  A network based on a fully-convolutional style semantic segmentation network is applied to a 2D, 8-channel game state representation, with final sigmoid layer to predict a pass success indicator at each location.  The system is trained using manually annotated pass success and destinations, which corresponds to a label on the destination point; locations other than the labeled point are not trained (treated as incomplete/"don't-care" training targets).  Evaluation is performed using both log loss and probability calibration measure, to measure effectiveness of predictions as well as how well they calibrate to correspond to probabilities in the sense defined by the measurement.
This is a fun application and it appears the system is effective at a basic level.  However, I think both the theory/explanation and experiments leave a fair bit of uncertainty as to what the probabilities mean and how to interpret them, including conflation of success probability and the model's certainty in its estimate.
In particular, it is unknown to what degree the values output by the model can be interpreted as a predictive probability of pass completion for anywhere on the field.  If one location says 0.8 and the other 0.5, does this mean that if the player were to actually pass to the 0.5 location, the chance of success is actually lower?  Or does it mean that the model is less confident or that this location was under-trained for this state?  The ECE measurement in conjunction with loss error doesn't quite address this:  although a good verification of calibration in its own sense, ECE simply confirms that for cases where the model predicts 0.5, there is success 0.5 of the time for locations that *exist in the test set*, which is sampled according to player action.  To verify the probability maps at all locations, one would need to be able to measure *any* point in the field, not just those already selected by the players' actions.  I think discussion and attempt to measure this is fairly important, as one of the intended applications in the motivation is analyzing what might have happened had a player selected a different destination point.
Unfortunately, knowing the true outcomes at arbitrary locations the players didn't pass to is impossible, so addressing this issue is not straightforward, and unclear to me how it might be done.  A possible suggestion, is to use the destination selection predictions that the paper also mentions can be found using softmax instead of sigmoid.  Although this does not entirely eliminate the issue (these predictions themselves may conflate model confidence with actual selection probability), these maps would likely provide a good indication of player selections.  Thus they might be used to sample or reweight the test set, so that unlikely destination points are sampled more, to try to get a more uniform sample.
Even with this issue, though, I feel that this is an interesting application and system that seems reasonable in its current state, if with important caveats.  Thus, I'd lean towards accepting.  However, I'd encourage the authors to discuss these differences and issues of output interpretation, and to try addressing if possible.
Additional questions and comments:
* The train/val/test split appears to be uniform random by pass event.  It would be interesting to hold out all events for one or more teams, or holding out full games, to measure generalizability to these cases.
* Are the destinations for unsuccessful passes the intercepted location, or an estimated intended location?  Does this difference affect the completion prediction at the intended location (beyond the interception location)?


Linear Programs (LPs) are a fundamental class of optimization problems with a wide variety of applications. Fast algorithms for solving LPs are the workhorse of many combinatorial optimization algorithms, especially those involving integer programming. One popular method to solve LPs is the simplex method which, at each iteration, traverses the surface of the polyhedron of feasible solutions. At each vertex of the polyhedron, one of several heuristics chooses the next neighboring vertex, and these vary in accuracy and computational cost. We use deep valuebased reinforcement learning to learn a pivoting strategy that at each iteration chooses between two of the most popular pivot rules -Dantzig and steepest edge. Because the latter is typically more accurate and computationally costly than the former, we assign a higher wall time-based cost to steepest edge iterations than Dantzig iterations. We optimize this weighted cost on a neural net architecture designed for the simplex algorithm. We obtain between 20% to 50% reduction in the gap between weighted iterations of the individual pivoting rules, and the best possible omniscient policies for LP relaxations of randomly generated instances of five-city Traveling Salesman Problem. Our results indicate that learning within combinatorial optimization algorithms is possible and that there is much room for improvement in learning more sophisticated pivoting strategies, especially for larger LP instances.

The authors present a learned method for speeding up optimization of LP, with an application to the TSP problem. In particular, they discuss choosing a pivoting strategy in the simplex algorithm that is set up as a 2-class classification problem, taking the simplex tableau and outputting one of two classes (Dantzig or steepest edge). They consider both the supervised learning approach where they first compute the optimal policy Q*, as well as the RL approach.
The paper presents a quite interesting approach to solving the TSP, using NNs on top of the tableaus. I enjoyed the presented ideas, however the authors could have done a great job of clearly presenting their work. Notation is not the best, and the experiments are quite limited, indicating limited practical value of the current approach. Detailed comments follow:
- Especially given that the authors have 2 more pages for writing, it would be beneficial to add more visualization and intuitive explanations of the presented ideas.
- The notation should be improved, especially given that there isn't that much notation anyway. E.g., eq (1e) and the following one are not quite clear, what is M? Is it a scalar, or a set? Reading closely it becomes clear it is a set, but the authors use upper-case letter both for scalars and sets, leading to confusion. This is very easy to fix, and would help readers quite a lot.
- The first paragraph in Section 4 is literally a copy-paste of the last paragraph in Section 3.
- Accompanying Section 4 discussion, would be good to add a figure showing an example tableau. Actually, tableau is not even mentioned here and is the main input to the network, it is only mentioned later.
- Using just 5 cities does seem small, indicating limited practical value of the method. Please comment on the actual full size of the exact graph of the relaxation, and why is it infeasible to store. Currently the explanation is hand-wavy.
- "The state space is the set of possible simplex tableau", so you enumerate all the possible tableaus of extreme points prior to training? It seems yes, but would be good to explain that explicitly.
- In "Reward function" section, "as the objective value ...", please add a reference to eq (1a) here. It helps readers follow the text by referencing already introduced parts.
- Where did the equations for rewards come from? They are just given, without much explanation or intuitive discussion.
- Above Section 5.1, "where s_{t-1} -> s_t", where is this notation even used?
- Typo: "value of at"
- Is it "tableau" or "tableaux"? Choose one.
- Section 5.1, are both outputs updated at each iteration? It says that a random action is taken, but is that after Q-values for both actions are checked? It seems yes, but it is not clear.
- In general, a number of small details are missing, and the authors should make sure to not skip them. This introduces confusion to the text which should clearly be avoided.
- "Epsilon is decayed appropriately." How?
- Please define an epoch. In particular, what constitutes a 0.5 epoch, and how does the update actually work here? So you store examples into batches, keep them on the side, and once half an epoch passes only then use them to update the model? It seems yes, but again would be good to be more gentle in explanations.
- Maybe add an algorithm illustrating the methods? In addition to visualization mentioned above.
- Figures are not really super visible. Also, figures should have captions, so text go below the figure.
- Figure 2 is referenced in Section 6.2, where it should be Figure 3.
- "weighted" vs. "unweighted" iteration should be defined earlier. It is nowhere introduced, and while it may be clear what it means, it is not clearly defined and it should be.
- "Adams optimizer"? Do you mean Adam?
- Experiments are somewhat weak, and seem to indicate that the method does not have much practical value. Is the method useful beyond 5-city size?
===== AFTER THE REBUTTAL ======
Thank you for your rebuttal, and especially for the extra experiments! It definitely adds a lot of value to this effort.
The writing could still be improved, as a number of details are missing as explained in the review and to some extent acknowledged by the authors. I liked the idea quite a lot and would not mind seeing it in the conference, but given the number of issues raised by myself and others it seems that the best route forward is rewriting the paper given the inputs by the reviewers and submitting to a future venue.
I will remain at a "borderline" evaluation, and if the other reviewers change their recommendations to (weak) accept I would not mind accepting the paper (assuming all the changes and promised fixes are implemented).


Recent work suggests goal-driven training of neural networks can be used to model neural activity in the brain. While response properties of neurons in artificial neural networks bear similarities to those in the brain, the network architectures are often constrained to be different. Here we ask if a neural network can recover both neural representations and, if the architecture is unconstrained and optimized, the anatomical properties of neural circuits. We demonstrate this in a system where the connectivity and the functional organization have been characterized, namely, the head direction circuits of the rodent and fruit fly. We trained recurrent neural networks (RNNs) to estimate head direction through integration of angular velocity. We found that the two distinct classes of neurons observed in the head direction system, the Ring neurons and the Shifter neurons, emerged naturally in artificial neural networks as a result of training. Furthermore, connectivity analysis and in-silico neurophysiology revealed structural and mechanistic similarities between artificial networks and the head direction system. Overall, our results show that optimization of RNNs in a goal-driven task can recapitulate the structure and function of biological circuits, suggesting that artificial neural networks can be used to study the brain at the level of both neural activity and anatomical organization.

## Overview
This paper studies whether a recurrent neural network trained to solve a particular task (integration of angular velocity to generate head direction). Given trained recurrent networks that solve the task, the paper analyzes these using a number of different methods (visualizing tuning curves, perturbation experiments, and varying input statistics). Overall, I think this is a nice paper that shows the power of using artificial networks as a model system to answer neuroscientifically motivated questions. In particular, I found the perturbation analyses particularly illuminating. These kinds of experiments are only possible in these artificial networks, and can highlight/guide future biological experiments.
## Major comments
- "Units with minimal tuning to both variables are discarded from further analysis"  -- how many units end up being discarded? The reason I ask is because the number of discarded neurons affects this statement: "Therefore, units in the trained RNN could be mapped on to the biological head direction system both in terms of general functional architecture and detailed tuning properties.". If a large number of neurons are discarded, then the statement should be amended to say that "a fraction of units in the trained RNN" can be mapped onto the HD system. However, my understanding is that many biological neurons have tuning properties that are hard to classify, perhaps the discarded neurons could map on to these previously uncharacterized neurons?
- The paper demonstrates a number of qualitiative similarities between artificial and biological networks (e.g. both contain neurons tuned for HD or AV). It would be even more compelling if, wherever possible, these comparisons were made to be quantitative.
- "We conjecture that Ring units in the trained RNN serve to maintain a stable activity bump in the absence of inputs". I think a cool direct test of this idea would be to use the techniques in Barak & Sussillo 2013 (find fixed points of the recurrent network dynamics, and analyze the linearized system at those fixed points) to identify the ring attractor structure. In particular, numerical auto-differentiation can be used to automatically identify these points (c.f. the methods in https://arxiv.org/abs/1907.08549). Using these tools, can one find the ring attractor hidden in these networks?
## Minor comments/questions
- The layout in Fig 2a (and Fig 5c, 5f, and 5i) is a little misleading. If I understand correctly, the axes labels apply to each individual panel (which shows tuning for a particular neuron). However, since the labels extend across many panels, it looks as if the panels themselves are organized according to angular velocity and head direction, which doesn't make sense.
- Missing citation towards the end of pg. 3
- Consider setting the panels in Fig 5a-h to have the same axes limits, for easier comparison.


We propose Dynamically Pruned Message Passing Networks (DPMPN) for largescale knowledge graph reasoning. In contrast to existing models, embeddingbased or path-based, we learn an input-dependent subgraph to explicitly model reasoning process. Subgraphs are dynamically constructed and expanded by applying graphical attention mechanism conditioned on input queries. In this way, we not only construct graph-structured explanations but also enable message passing designed in Graph Neural Networks (GNNs) to scale with graph sizes. We take the inspiration from the consciousness prior proposed by Bengio (2017) and develop a two-GNN framework to encode input-agnostic full structure representation and learn input-dependent local one coordinated by an attention module. Experiments show the reasoning capability of our model to provide clear graphical explanations as well as predict results accurately, outperforming most stateof-the-art methods in knowledge base completion tasks.

The paper presents a graph neural network model inspired by the consciousness prior of Bengio (2017) and implements it by means of two GNN models: the inattentive and the attentive GNN, respectively IGNN and AGNN.
Introduction outlines clearly what is the goal and why this is in principle an interesting avenue to investigate, however I found it could be more precise. In particular message passing techniques can be implemented very efficiently and are highly scalable. Section on Cognitive intuition of the consciousness prior doesn’t tell much beyond the re-stating of what it is, I am more interested in what it brings to the table and on what is the intuition behind its application to this domain.
One thing I would argue agains is that the input-dependent local subgraph requires access to the global graph, therefore going back to a conventional GNN. The argument is that the message passing can be constrained to reduce the computational burden. However, this can also be done by means of anchor graphs or other data structures, dynamic pooling and so fort. How do the authors compare to such choices?
Overall I like the “global conditioning“ by means of sampling to have better local representations at each node, an idea that while it can be cast as consciousness prior it is also related to neural processes and architectures alike.
The implementation section could be made a bit clearer. Currently, for instance, there are references to prediction tasks while I think it would be nicer to have it fully self contained. Also, the aggregation strategy seems to be that of Kipf et al., is it a constraint of the model or other strategies could be used as well?
The experiment section is clearly explained and results are interesting, showing the potential of the proposed approach. Also the thorough analysis of the model is very well done.
I wonder what is the performance when using no sampling at all, shouldn’t this be the reference?
The convergence analysis states that the model converges very fast, does it also translate to better results in case of small amount of training data?


Batch size selection affects the generalization ability of gradient descent, and small batch size is usually preferred. Conventionally, weight regularization is performed for every mini-batch without considering when would be the right time to regularize weights during optimization steps. For model compression, which regularizes weights to follow compressed forms, compression-aware training also performs weight compression for every mini-batch to compute the impact of compression on the loss function. In this paper, we propose a new hyper-parameter called "Non-Regularization period" or NR period during which weights are not regularized (or compressed). We first investigate the influence of NR period on regularization using weight decay and weight random noise insertion. Throughout various experiments, we show that stronger weight regularization demands longer NR period (regardless of batch size) to best utilize regularization effects. From our empirical evidence, we argue that weight regularization for every mini-batch allows small weight decay/noise only and limited regularization effects such that there is a need to search for right NR period and weight regularization strength to enhance model accuracy. Consequently, NR period becomes especially crucial for model compression where strong weight regularization is necessary to increase compression ratio. Using various models, we show that simple weight regularization to comply with compression formats along with long NR period is enough to achieve high compression ratio and model accuracy.

This work investigates compression-aware training and introduces a new hyper-parameter called "Non-regularization period". Basically, the paper proposes to apply weight regularization and compression less frequently so that they can use stronger regularization/compression, hence achieving high compression ratio and model accuracy.
Overall, the idea of asynchronous regularization and compression is interesting and worth further investigation. However, I vote for a reject for now because
(1) The paper is hard to follow and the writing can be significantly improved especially for the abstract and introduction. I felt rather confused when I first read the abstract and introduction. The authors frequently use the word "weight update", however it is unclear whether it refers to gradient update or the update caused by regularization/compression. Besides, the title is also a little confusing. There's little discussion about the choice of batch size and I don't really understand how weight regularization is decoupled from batch size after reading the paper. I suggest the authors to think more about the title.
(2) The reason why such a training scheme improves model compression is unclear and needs further investigations. In the paper, the authors first interpret model compression as a way of inducing weight decay (and random weight noise). Particularly, the model accuracy is roughly constant over different value of NR period (as shown in Figure 3 and Figure 4) when weight decay is used. However, the results of model compression are quite different (according to Figure 5). The best performance is only achieved with very large NR period in the case of SVD and pruning. I think the authors should give some explanations for that difference. Also, I notice that quantization behaves more similarly to weight decay and it requires further discussion.
To sum up, I like the idea of asynchronous regularization/compression, but I'm not quite satisfied with current version of paper. I encourage the authors to improve their writing and add more discussions (see my point (2)) to the paper. I'm willing to increase my score if the authors can address my concerns.


The universal approximation theorem, in one of its most general versions, says that if we consider only continuous activation functions σ, then a standard feedforward neural network with one hidden layer is able to approximate any continuous multivariate function f to any given approximation threshold ε, if and only if σ is non-polynomial. In this paper, we give a direct algebraic proof of the theorem. Furthermore we shall explicitly quantify the number of hidden units required for approximation. Specifically, if X ⊆ R n is compact, then a neural network with n input units, m output units, and a single hidden layer with n+d d
hidden units (independent of m and ε), can uniformly approximate any polynomial function f : X → R m whose total degree is at most d for each of its m coordinate functions. In the general case that f is any continuous function, we show there exists some N ∈ O(ε −n ) (independent of m), such that N hidden units would suffice to approximate f . We also show that this uniform approximation property (UAP) still holds even under seemingly strong conditions imposed on the weights. We highlight several consequences: (i) For any δ > 0, the UAP still holds if we restrict all non-bias weights w in the last layer to satisfy |w| < δ. (ii) There exists some λ > 0 (depending only on f and σ), such that the UAP still holds if we restrict all non-bias weights w in the first layer to satisfy |w| > λ. (iii) If the non-bias weights in the first layer are fixed and randomly chosen from a suitable range, then the UAP holds with probability 1.

UPDATE TO MY EARLIER REVIEW
============================
Since this paper presets new findings that will be of significant interest to much of ICLR's audience, and the paper is is well-written, I am changing my rating to "Accept". Since Reviewer #1 did not submit a review and Reviewer #2 indicated that (s)he does not feel well-qualified to review this paper (it is very much on the theoretical side after all), it would be great to get one further review from an area chair or otherwise qualified person.
MY EARLIER REVIEW
=================
This this exciting submission presents a new proof of Leshno's version of the universal approximation property (UAP) for neural networks  -- one of the foundational pillars of our understanding of neural networks. The new proof provides new insights into the universal approximation property. I consider these the main contribution of the paper. Specifically, the authors
- provide an upper bound on the required width for the neural network
- show that the approximation property still holds even if strong further requirements are imposed on the weights of the first or last layer.
I rate this submission a weak accept. It’s a very good paper. The work makes useful contributions that should and will be of interest to many in the field. The paper is generally well-written.
Some remarks:
- Being somewhat long, the “Proof of Theorem 3.1” would be a much better read if the authors prefixed it  with an outline of the strategy that the proof takes.
- The authors point out that the lack of dependence of Theorem 3.1 on epsilon is surprising, and cite Lin’s work from 2017 who previously found such an independence. Lin’s derivation of the epsilon-independent UAP is much more intuitive than that of this submission, in which the epsilon independence really pops out somewhat magically and for me only made sense when I read the paper again. I would encourage the authors to add to Lin’s paper’s citation sentence that this paper motivates the epsilon independence well. Alternatively, the authors could add a few sentences to their paper to provide intuition on how the epsilon-independence comes about in their line of argument.


We introduce a new pre-trainable generic representation for visual-linguistic tasks, called Visual-Linguistic BERT (VL-BERT for short). VL-BERT adopts the simple yet powerful Transformer model as the backbone, and extends it to take both visual and linguistic embedded features as input. In it, each element of the input is either of a word from the input sentence, or a region-of-interest (RoI) from the input image. It is designed to fit for most of the visual-linguistic downstream tasks. To better exploit the generic representation, we pre-train VL-BERT on the massive-scale Conceptual Captions dataset, together with text-only corpus. Extensive empirical analysis demonstrates that the pre-training procedure can better align the visual-linguistic clues and benefit the downstream tasks, such as visual commonsense reasoning, visual question answering and referring expression comprehension. It is worth noting that VL-BERT achieved the first place of single model on the leaderboard of the VCR benchmark.

### Summary:
This paper propose a new model for learning generic feature representations for visual-linguistic tasks by pretraining on large-scale vision and language datasets like Conceptual Captions and language-only datasets like BookCorpus and English Wikipedia. They demonstrate that the pre-training procedure can help improve performance on down-streaming tasks like visual question answering, visual commonsense reasoning.
Overall I liked the design choices made in the presentation. Although the paper doesn't provide insights around what the representations have learned and how they differ from representations learned / used by existing methods, they have provided substantial evidence to suggest that pre-training helps in a lot of downstream tasks.
Although it's hard to evaluate the paper without putting it in context with other concurrent works that have come out recently, I tried my best to evaluate the merits of the paper in isolation.
### Strengths:
- The paper explores an interesting direction of learning generic feature representations for visual-linguistic tasks for down-streaming tasks. Traditionally, people learn feature representations from scratch for each downstream task which might not always be possible if the training data is limited.
- The paper does a decent job mentioning all the concurrent work in the space of learning multi-modal representations that have come out very recently. They distinguish the proposed method from existing work and also compare the performance of the proposed approach with concurrent work on downstream tasks showing performance on-par or better than existing methods.
- I liked some of the design choices made in the paper. (1)  Instead of training a separate  transformer network for each type of input segments (question, ans, caption, image, etc). This makes the model easily extensible to other tasks as long as the correct segment embeddings are used to identify different input sources. (2) They also use a separate embedding for visual features instead of a common embedding  for both language tokens and visual tokens.
- Unlike the pre-training task in concurrent work, the model was pre-trained not just on multi-modal datasets like conceptual captions but also on text-only corpus like BookCorpus and English Wikipedia. The authors claim that this leads them to learn better representations for longer sentences which they found useful for VCR task.
### Weaknesses:
- The authors claim that attention mechanism in cross-modal transformer by concurrent approaches is restrictive but doesn't give substantial evidence that this is true. What are the limitations for cross-modal attention mechanisms compared to a single transformer model as described in this paper.
- On the contrary, by having a cross modal architecture, they can pre-train each modality separately on unaligned data. For instance, the text only transformer can be trained using large text corpora similar to BERT while the image only transformer can be trained on big datasets like OpenImages, ImageNet etc
- While the paper gives a lot of empirical evidence that pre-training helps, it would have been interesting to develop an understanding of what the model is actually learning and how are these representations better than learning representations from scratch for each task. For instance maybe the authors can visualize attention similar to [1].
### Other questions:
- When training on text-only datasets, what is the input on Visual Feature Embedding since there are no associated images. The authors mention that for non-visual elements, the features are extracted on the whole image. It's still unclear what the associated visual features are for text-only datasets.
- One of the pre-training tasks is masked ROI classification but it assigns a hard label to each ROI feature. It might be interesting to instead try learn the entire probability distribution (the output of a pre-trained classifier) by either minimizing the KL-divergence or by using softmax with soft-targets.
- While the model was learnt on text-only data, as mentioned in the above section, will the model help from image-only datasets such as large-scale classification datasets?
- While the models are tested on vision-and-language datasets, will these generic representations also be useful for unimodal tasks?


To facilitate a wide-spread acceptance of AI systems guiding decision making in real-world applications, trustworthiness of deployed models is key. That is, it is crucial for predictive models to be uncertainty-aware and yield well-calibrated (and thus trustworthy) predictions for both in-domain samples as well as under domain shift. Recent efforts to account for predictive uncertainty include post-processing steps for trained neural networks, Bayesian neural networks as well as alternative non-Bayesian approaches such as ensemble approaches and evidential deep learning. Here, we propose an efficient yet general modelling approach for obtaining well-calibrated, trustworthy probabilities for samples obtained after a domain shift. We introduce a new training strategy combining an entropy-encouraging loss term with an adversarial calibration loss term and demonstrate that this results in well-calibrated and technically trustworthy predictions for a wide range of perturbations. We comprehensively evaluate previously proposed approaches on different data modalities, a large range of data sets including sequence data, network architectures and perturbation strategies and observe that our modelling approach substantially outperforms existing state-of-the-art approaches, yielding well-calibrated predictions under domain drift.

The paper presents a method for calibrating neural networks on in- and out-of-distribution data using two additional loss terms: entropy-encouraging loss term which maximizes softmax probabilities for wrong classes and adversarial calibration loss term which pushes confidences to match accuracy on adversarial examples. The idea of using adversarial calibration training is interesting and promising, however, the clarity of the paper needs significant improvement and there are several issues which need to be addressed; for this reason, I recommend a weak reject for the current version.
1. One of the contributions listed in the paper is that authors “illustrate the limitations of entropy as measure for trustworthy predictions and introduce a new metric to quantify technical trustworthiness based on the concept of calibration”; the section 2.1 discusses this in detail. The proposed metric is expected calibration error (ECE) averaged over different levels of noise perturbations applied to data during test time. This metric assumes that for a given dataset we know in advance what kind of noise perturbations can be implied to cause out-of-domain/domain-shift scenarios during test time. This assumption most likely doesn’t hold in real-world applications since domain shifts may be of various kinds. Moreover, calibration may not make sense at all for out-of-domain data if test inputs don’t belong to any of the train classes (as opposed to entropy of predictive distribution which still can be computed and is expected to be higher for such inputs). The metric is also dependent on the considered noise level range; the plot of ECE vs noise level can be illustrative and informative while the averaged value of ECE over all noise levels can be misleading (at least, we may want to have some discount factor to account for the fact that with noise level 0 we strongly care about calibration, while for very high noise levels calibration doesn’t give us much information since the useful patterns in data may be corrupted and it may be impossible even for humans to classify such objects, e.g. on Figure 1-top-left for noise level 100, the digit 6 is corrupted so much that we wouldn’t care about calibration for such inputs but just want to maximize the entropy).
The paper also claims “Recent efforts in terms of evaluating predictive uncertainty have focused on entropy as measure for uncertainty-awareness for predictions under domain shift.” In previous work addressing uncertainty in domain shift [1], not only entropy but other various metrics are considered for out-of-domain detection (Brier score, thresholded confidences, etc), these metrics don’t depend on particular perturbations and are very informative.
The introduced metric, ECE for different noise labels, makes sense only in the toy scenarios where we can control the noise level, however, it would still be better to either look at the plots or to use some discounted averaged ECE over different noise levels, but not equal average. So the significance of this contribution (introduction of new metric) is limited.
2. The clarity of the paper could be significantly improved.
(a) Figure 1: the top left plot suggests that for high noise level “wrong predictions are often made with high confidence” (so the entropy of this distribution is low) while the top right plot shows that on average predictive entropy gradually grows and is high for high noise levels, so the top right plot is probably not a representative example and it might be misleading to claim this is an “often” case.
(b) Could you please clarify what you mean by “after removing non-misleading evidence” in section 2.2.1? In the next sentence, the remaining probability is probably distribution uniformly across C-1, not C, classes. The predictive entropy loss term essentially maximizes the probabilities of wrong classes with a lower coefficient. How would you support the claim that the loss surface is unchanged?
The loss term is “parameter-free” but still we need to tune a coefficient lambda_S for it.
(c) The adversarial loss equation in section 2.2.2 is written as L2-norm of a scalar value, why is L2-norm needed? The acc(B_m) is not differentiable so it is probably just considered as constant in the paper? Please comment on that.
(d) Section 3.2 and Figure 4. On Figure 4 Middle and Right plots have different colors than those listed on legend, please, fix this. On the middle plot, both FALCON and EDL have high ECE for noise levels <50 which indicates that they are both highly underconfident for in-distribution data and low noise levels, while other methods have close to 0 ECE on low noise levels. The authors only comment on EDL underconfidence: “it is worth noting that EDL has a substantially higher ECE for in-domain predictions, reflecting under-confident predictions on the test set”, and not on FALCON underconfidence. However, using the proposed score, ECE averaged over all noise levels (Table 2), it may look like the method is doing a good job, while underconfidence problem is revealed when looking at Figure 4. This is also an illustration of the concern about the proposed metric I raised in point 1.
3.  It would help to have an ablation study in the main text of the paper showing the significance of each loss term: in the appendix Figure S1, it is shown that adding adversarial loss to standard and entropy loss helps. Is the entropy loss needed at all? How does performance change if we only have standard and adversarial loss? How sensitive is performance to the choice of lambda_avd and lambda_s?
[1] Ovadia, Yaniv, et al. "Can You Trust Your Model's Uncertainty? Evaluating Predictive Uncertainty Under Dataset Shift." arXiv preprint arXiv:1906.02530 (2019).


The increasing need for compact and low-power computing solutions for machine learning applications has triggered significant interest in energy-efficient neuromorphic systems. However, most of these architectures rely on spiking neural networks, which typically perform poorly compared to their non-spiking counterparts in terms of accuracy. In this paper, we propose a new adaptive spiking neuron model that can be abstracted as a low-pass filter. This abstraction enables faster and better training of spiking networks using back-propagation, without simulating spikes. We show that this model dramatically improves the inference performance of a recurrent neural network and validate it with three complex spatio-temporal learning tasks: the temporal addition task, the temporal copying task, and a spoken-phrase recognition task. We estimate at least 500× higher energy-efficiency using our models on compatible neuromorphic chips in comparison to Cortex-M4, a popular embedded microprocessor.

The paper promises efficient training of spiking neuron models using back-propagation. The authors say that this is important because spiking networks offer significant energy savings, yet they typically perform poorly compared to prevalent artificial neural networks (ANNs). They aim to support this with several synthetic and one real-world task.
I selected to reject the paper based on the support for the main claim of the paper being weak and inadequately demonstrated. No comparisons are to baselines are presented in the text. Reproducibility is hampered by a great deal of the experimental details missing.
On the experimental results:
* In section 4.1, some justification is needed for why these experiments are relevant.
* In sections 4.4 and 4.5, experiments are discussed, but results are not presented.
* If space is a limitation, I would strongly prefer a table of actual results for sections 4.4 and 4.5 rather than Figure 2.
* Since the encoding of the task in the spiking and non-spiking cases is so drastically different, making that crystal clear would be great.
Other comments:
* The goal of energy savings is very appealing, so it would help to give *some* quantitative measure of savings promised.
* Similarly, the claim about the poor performance of spiking neurons would benefit from some quantitative measures.
* A figure showing the operation of the novel SigmaDelta neuron, compared to the standard aI&F neuron, would be welcome.
Overall I think the paper would benefit from focussing much more on the results, making the claims as quantitatively apparent as possible.


Generating point clouds, e.g., molecular structures, in arbitrary rotations, translations, and enumerations remains a challenging task. Meanwhile, neural networks utilizing symmetry invariant layers have been shown to be able to optimize their training objective in a data-efficient way. In this spirit, we present an architecture which allows to produce valid Euclidean distance matrices, which by construction are already invariant under rotation and translation of the described object. Motivated by the goal to generate molecular structures in Cartesian space, we use this architecture to construct a Wasserstein GAN utilizing a permutation invariant critic network. This makes it possible to generate molecular structures in a one-shot fashion by producing Euclidean distance matrices which have a threedimensional embedding.

This paper addresses the important problem of molecular structures generation, and more generally of efficient point-cloud distributions learning in d-dimensional space.
The paper is written clearly, the pseudo-code is presented in a clear way, striking a good balance between explicit-ness and concision.
After my first reading I was disappointed in the experiments, because I read the paper quite quickly at first.  After a second more careful read I understood most of it and was much more enthusiastic. Disclaimer: I am inexperienced in this particular field (GANs and GANs for molecular generation) so I lack literature knowledge, and I may be over-evaluating the quality of performances (compared to recent results).
But currently I believe that the authors are a bit too humble about their results (a rather uncommon phenomenon). There is a part of the method that I would like to have clarified (about bond/atom types), but other than this clarification, I strongly recommend the paper to be accepted.
The paper deals with a couple of distinct, related problems.  One is that of sampling valid (Euclidean) distances matrices (EDM). This is done with algorithm 1.
The paper uses these EDM to train a generator G directly in EDM-space, against a Critic network C (the architecture of which is taken from existing literature).
Some of the output configurations have to be discarded due to incorrect bond types assignment (this is the part that is still obscure to me).
The remaining outputs are chemically sensible in terms of bond types/valence/local chemistry/etc, but also, and quite impressively, have reasonable ground state energies !  In this sense, the paper produces samples that may deserve to be added into the QM9 data set (After some data augmentation using DFT or other physics-validated methods of course).
I have mainly two requests:
1. The bond type or atom assignment is not clearly explained. I ask further detailed questions below, but overall I think you should attempt to make a pedagogical explanation of how the atom types are assigned/learned, and how some of them are later discarded.
'The  generator produces an additional type vector in a multi-task fashion which is checked against a  constant type reference with a cross-entropy loss.'
Could you explain this better ? At least in the appendix. Otherwise this very dense sentence remains mysterious. Eq.11 is currently the single occurrence of the H, t, and tref terms.
About the validity test using Open Babel. Again, what happens with bond types is not very clear. Are they set in stone at generation time, and then most of these affected types are 'wrong' and are discarded by Open Babel ?
Why don't you include this validation at training time (if it's very complicated to do, explain why) ?
In any case, please clarify this paragraph, as for now it is cryptic.
2. Part of the paper goal is to achieve learning of point clouds distributions and not about chemistry.  However, discovery of new structures (and their conformations) is in itself a big topic.  I think it would be good to mention a couple of follow ups to your work in the conclusion. For instance, it would seem rather natural to me to include some equivalent of OpenBAbel and Energy-estimates within the learning loop, so that the generator directly generates valid (open-babel wise) and reasonable (energy level-wise) structures.
Besides the conclusion, you should stress out better the significance of your results with a couple of comments here and there. (I have more precise suggestions below).
Some other comments to improve the paper (in clarity or other):
In algorithm 1, you should precise that G() is your NN-based generator network. At this point of the paper G and z and N_z have never been mentioned. This is a problem when reading the paper for the first time.
Line 5, you could explicitly precise, 'with (5)'.  Also I am puzzled by the use of the softplus here, but later in page 5 you say g() is softplus for the first three eigenvalues, and set to 0 for all others. Why not already anticipate and say this in section 2 ?
Line 8, I would have written 'eigenvalues .... of D'  (what is the role of Eq. 1 here?)
At some point (i.e. around end of section 2), a comment would be welcomed, about whether you may sample the space of EDMs uniformly at random using algorithm 1 (I think you do not, and it is ok, but the question naturally arises and it's not addressed).
´´which transforms a prior distribution into a target distribution´´
you could specify that this prior is the Gaussian N(0,1)^Nz in this case, to better connect with algorithm 1.
About equation 6: it would be nice to have some intuitive explanation of what the output values of C(x) mean. They are scalars that represent the opinion of C on the molecule x, so they are the probability that the observed molecule is 'a true molecule x' ?  You should recall that for the inexperienced reader.
Still about Eq.6 : could you quickly provide the motivation for demanding C to be L-Lipschit with  $L \leq 1$ ?
The drift term Eq.9 seems to be some sort of regularization, maybe it could be mentioned once in the text for completeness?
Using Mopac Stewart and figure 4: you could insist more on this result. Up to that point I was very dubious about the usefulness of the whole work, because I would have expected many generated samples to be highly unrealistic, i.e. having huge energies, and so being extremely unstable. Instead here you show it is not the case, and even all your energies lie within the range of observed energies !  This is a very strong result, that is not obvious to expect, and is highly valuable (even after keeping only 7.5% of structures, this is still a strong result.)
I think this test and the corresponding result should be emphasized more.
You observe new topological types and complain there are not many. I think ~20 new topologies is not a small number (for so few atoms), and you may be rather proud of it.  What is too bad is that you do not have a tool for differentiating between the very similar conformations (that correspond to thermal fluctuations around a given structure) and the conformations that encode a new structure (which does not necessarily means new topology).
If you had this tool, you could enrich figure 3 with a curve showing the new structures (not counting conformational variants).
refs 2017a and 2017b are the same.


Unsupervised knowledge transfer has a great potential to improve the generalizability of deep models to novel domains. Yet the current literature assumes that the label distribution is domain-invariant and only aligns the feature distributions or vice versa. In this paper, we explore the task of Generalized Domain Adaptation: How to transfer knowledge across different domains in the presence of both shift in the feature and label distribution? We propose a feature and label distribution CO-ALignment (COAL) model to tackle this problem. Our model leverages prototype-based conditional alignment and label distribution estimation to alleviate the negative effect of the the types of domain shift respectively. We demonstrate experimentally that when both types of shift exist in the data, COAL leads to state-of-the-art performance on several cross-domain benchmarks.

This paper proposes domain adverarial approaches modified to address covariate shift
even in the case of shifting label distributions. The paper is interesting and the authors
are looking at an important problem, but the paper suffers several major misconceptions
and the exposition is full of errors.
The paper proposes a method called “self training” to “estimate and align” the  target label distribution
and a “prototype-based method” for conditional alignment.
The paper purports to introduce a new problem: “generalized domain adaptation”
but actually this is just covariate shift.
They confuse the term “label shift” and the colloquial “shifting label distribution”.
Moreover when they describe the method formally they fail
to even state the covariate shift assumption (that p(y|x) = q(y|x) ).
Absent this statement, the problem is unfdamentally underspecified.
They have stated only that p(y) \neq q(y) and that p(x|y) \neq q(x|y).
Thus the claimed contribution is to solve an impossible (more accurately, underspecified problem).
The proposed method leverages a “similarity classifier”
The thing that the authors call a similarity-based classifier
isn’t well explained. It looks like an ad-hoc variation on a standard
softmax prediction layer.
Here, not that similarity means similarity between x and the label weights w,
not similarity between examples and each other.
Moreover this classifier is trained as a classifier using a
standard cross-entropy objective on the target domain.
The paper lacks any formal justification for what this is offering
that we do not get from a standard classifier.
The next component of the model is "Prototype-based Conditional Alignment by Minimax Entropy”
and it is also confusingly explained.
The paper attempts to make some reference to the theory of Shai Ben David
which has been badly misapplied in the deep domain papers
(see discussion by Johannson et al 2019 and Wu et al 2019).
Strangely, the authors misattribute the theory to Zhao 2019.
There are some nice ideas in the paper and the experimental results
(flaws in domain adaptation benchmarks notwithstanding)
appear to be promising.
However the paper is written too confusingly, is outright wrong in many places
and runs the risk of badly misleading readers over even the most basic of definitions.
I encourage the authors to give the paper a gut rewrite
and do not believe that it can be published while resembling its current form.
“only aligns the covariate shift”
>>> 	Be more formal, not clear what it means to “align the shift”
	Moreover, note that owing to lack of shared support , it’s not clear
	what precisely the current methods (domain-adversarial) do
	or according to what principles they work.
“the covariate shift needs to be minimized”
>>> 	This is not a coherent way of describing the problem.
	The covariate shift is a property of the data.
	You cannot “minimize the shift”
“label shift (p(y) ̸= q(y))”
>>> 	Actually this is a “shfit in label distribution”.
	Note that you can have a shift in label distribution
	even under the covariate shift assumption.
	Label shift is the reverse assumption that p(x|y) = q(x|y).
“minimizing the label shift”
>>>	Again, this doesn’t make sense. The practitioner doesn’t get to choose the data
	that they will face at test time. The “shift” refers to the data.
"Specifically, we assume p(x|y) ̸= q(x|y) and p(y) ̸= q(y)”
>>>	The problem described in this paper is called Generalized Domain Adaptation”
	but actually it is just “covariate shift” this is not a new problem.
	The use of new terminology for old problems and misapplication of old terminology,
	e.g. “label shift” make this paper a potential danger to readers
	who then will be confused in their subsequent interactions with
	the wider literature on distribution shift.
“These methods have achieved state-of-the- art performance on several domain adaptation benchmarks“
>>>	It’s worth pointing out that benchmark SOTA is a dubious way to assess performance out of sample.
	The point is that in supervised learning you get to know that your target is the same as your source,
	so it’s ok to have a whole community smash the validation set and then see if we push the leaderboard on test data
	With domain adaption, the relevant sample size is the number of shifts, no the number of images.
	Having the community pound on 2-3 shifts tells us virtually nothing.
"our approach diminishes covariate and label shift”
>>>	Again this is not the accurate way to describe what you do.
	You attempt to salvage classifier performance under these shifts,
	you cannot “diminish the shift”.
“Recently, Azizzadenesheli et al. (2019b) propose a regularized algorithm to correct shifts in the label distribution by estimating the importance weights using labeled source data and unlabeled target data. Lipton et al. (2018b) introduce a test distribution estimator to detect and correct for label shift.”
>>>	This is not exactly the right characterization of the related work.
	The method proposed by Lipton 2018 is precisely what
	Azzizadeneshelli 2019 build upon (by adding a regularizer)
“Conventional domain adaptation approaches … only align marginal feature distribution”
>>>	Again, the authors speak about “aligning the marginal feature distribution”,
	but this is confusing, Representations are aligned, not features.

“This motivates us to align the conditional feature distribution, i.e. p(x|y) and q(x|y)”
>>>	Again these are not things that can be “aligned”. They are properties of the data.
	The entire paper needs to be re-written to be semantically coherent.


Although ADAM is a very popular algorithm for optimizing the weights of neural networks, it has been recently shown that it can diverge even in simple convex optimization examples. Several variants of ADAM have been proposed to circumvent this convergence issue. In this work, we study the ADAM algorithm for smooth nonconvex optimization under a boundedness assumption on the adaptive learning rate. The bound on the adaptive step size depends on the Lipschitz constant of the gradient of the objective function and provides safe theoretical adaptive step sizes. Under this boundedness assumption, we show a novel first order convergence rate result in both deterministic and stochastic contexts. Furthermore, we establish convergence rates of the function value sequence using the Kurdyka-Łojasiewicz property.

In this work, the authors consider a variation of ADAM with a boundedness assumption on the step size and focus on unconstrained, smooth, non-convex minimization setting.
The authors provide non-asymptotic convergence rates for deterministic and stochastic settings, with respect to the gradient norm. Moreover, they also prove convergence in function value for a class of functions that satisfy Kurdyka-Lojasiewicz (KL) property. To the best of my knowledge, this is the first work that utilizes KL property and respective analysis for ADAM-like methods. I have to note that I disagree with your statement of being “adaptive”.
I summarize my comments step by step below:
I find the presentation and organization of the paper clear and structured. Related work is sufficient, the authors cite relevant papers with respect to convergence in deterministic and stochastic setting and present detailed comparison between their framework. Similarly, the momentum idea is motivated through Polyak’s Heavy ball. The known rates for KL functions are provided in conjunction with momentum-based methods.
Zaheer et al. (2018) assume \beta_1 = 0, meaning their proof works for RMSProp. However for this paper, given that Theorems 4.2 and 4.3 are provided for Algorithm (2), then the algorithm in question is not exactly the same as ADAM either, in my opinion. The bias correction steps are missing. The authors should clarify this point in the paper.
Definition of adaptivity is a little vague for me. There exist different notions of adaptivity (adaptation to global/local smoothness without knowing L, adaptation to non-smooth & smooth problems simultaneously etc.) The authors define adaptivity as “computing step size using gradient history”. However, their upper bound for the step size requires knowledge of L. Also, they assume a uniform lower bound for step size. These make their framework rather non-adaptive in my opinion.
Follow up comment: How would one apply this method to neural networks, or any class of problems where Lipschitz constant is virtually unknown?
Convergence rate in deterministic oracle setting, provided in Theorem 4.2, is plausible. The proof is nice and easy to read. Compared to De et al., the authors show faster rates with respect to number of iterations. But the rate depends on upper/lower bounds of the step size.
Convergence rates in the stochastic setting suggest the quantity does not go to zero, but converges to some noise dominated region (equivalently to some neighborhood) of stationary points. Zaheer et al. has a similar rate characterization for RMSProp, but this paper considers first order moment accumulation on top Zaheer et al. I am not sure about the impact of this results compared to existing ones for ADAM variants. Similar to deterministic case, the analysis is nice and clean. The rate has no dependence on dimension, but so does the analysis of De et al. (2018) and Zaheer et al. (2018). It is not new, but it is a desirable property of the analysis.
I have doubts about “not having bounded gradient assumption”. There exists a uniform lower bound for a_n, which implies the sum of square of each coordinate of gradients are bounded, which implies the infinity norm of gradients is bounded. I believe there is an implicit assumption of bounded gradients. It also makes me question if somehow the dimension dependence is hidden under this step size lower bound. I would expect the authors to address the concerns about bounded gradient and dimension dependence.
Convergence characterization for KL functions with (sort of) adaptive step size is new also to the best of my knowledge. The convergence analysis is based on PALM (Bolte et al. (2014)) and Bolte et al. (2018) and these previous results are adapted to ADAM. My concern about this direction is whether neural networks belong to this class of functions. If not, how useful it is to use ADAM for this class of functions?
Overall, authors approach ADAM-like methods from a generalized scheme based on Heavy Ball, and provide analysis for smooth, non-convex functions with deterministic/stochastic gradients. Having dimension-independent rates is a positive trait of the analysis, but I would like to see a clarification regarding my previous point. In the stochastic setting, dimension-free rate for ADAM (which has very similar characterization to RMSProp in Zaheer et al.) seems to be an important results of this paper. I think the KL function analysis is a new result for “adaptive”, evolving step sizes, as well. However, I do not agree with the claim that the authors do not make bounded gradient assumption. In a way, the uniform lower bound on the step size implies it. Knowledge of Lipschitz constant (through step size upper bound) is a restriction for “highly non-convex” neural network optimization problems. Considering that ADAM is a classical optimizer for neural networks, I also doubt KL property holds for complex networks. Also, I am not convinced that the algorithm is truly adaptive (upper bounding step size with a function of Lipschitz constant.)
I am inclined to give a weak reject to this paper because I am not convinced that the results presented in the paper are compatible with the application. I would also like to see the justification/clarification of the authors for my previous concerns before making the final decision.


The ability to detect objects regardless of image corruptions or weather conditions is crucial for real-world applications of deep learning like autonomous driving. We here provide an easy-to-use benchmark to assess how object detection models perform when image quality degrades. The three resulting benchmark datasets, termed PASCAL-C, COCO-C and Cityscapes-C, contain a large variety of image corruptions. We show that a range of standard object detection models suffer a severe performance loss on corrupted images (down to 30-60% of the original performance). Furthermore, we provide evidence that increased performance on those benchmarks translates into increased robustness towards real-world "natural" distortions such as real-world fog, rain and snow. Using our benchmark we show that corruption robustness scales with performance on clean data and that a simple data augmentation trick-stylizing the training images-leads to a substantial increase in robustness for both synthetic and natural corruptions on all dataset. We envision our comprehensive benchmark to track future progress towards building robust object detection models. Benchmark, code and data are available at https: //....

Summary:
- key problem or question: assessing / improving the robustness of object detectors to image corruptions (simulated fog, frost, snow, dragonfire...);
- contributions: 1) a benchmark (obtained by adding image-level corruptions to PASCAL, COCO, and Cityscapes) and an experimental protocol to measure detection robustness , 2) extensive experiments quantifying the severe lack of robustness of multiple state-of-the-art models, 3) experiments showing that data augmentation via style transfer (Geirhos et al, ICLR'19) improves robustness at little cost (at most -2% performance degradation on clean COCO images).
Recommendation: Weak Reject
Key reason: unclear novelty w.r.t. Geirhos et al ICLR 2019, especially due to the lack of specificity to object detection (which is the main goal of the paper).
- Although the paper from Geirhos et al. study a specific question (texture bias in CNNs), they propose a similar experimental protocol for assessing robustness, where the only differences are i) they use different corruptions (cf. Fig.6 in their paper, vs. Figs. 5, 7, 8, 9 here), ii) they do not have Cityscapes results (but they have PASCAL and COCO results).
- Furthermore, Geirhos et al 2019 also study the benefits of style-transfer-based data augmentation (this submission uses their technique), they report similar results and conclusions to this submission, including for object detection on PASCAL and COCO (cf. Table 2 in Geirhos et al 2019).
- What is, in the authors' opinion, the main differentiator of this submission? Does the difference in corruptions and evaluated models combined with the addition of Cityscapes yield new insights compared to Geirhos et al 2019?
- Beyond this similarity, what is specific to object detection vs. image classification in this submission? Besides the summary evaluation metrics, the corruptions and stylization are global (image-level) and not object-specific. Is the observed lack of robustness due to localization errors, mis-classifications, or other types of detection mistakes (cf. Hoiem et al ECCV'12)? What are the conclusions about detection robustness that differ from the image classification ones? What would be local corruptions that specifically degrade object detection performance (as studied for instance in the adversarial attack community, including physical attacks like Eykholt et al 2018)?
Additional feedback / questions:
- The results in section 3.4 / Fig.6 seem counterintuitive: more corruption should yield more degradation (as evidenced in Fig. 5 w.r.t. corruption severity). Is RMSE the right metric? Maybe SSIM would be better (more related to perceptual quality)?
- The aforementioned remark also raises the point that corruption difficulty night not be related to its intensity / noise level, but more with the (hard to quantify) domain gap w.r.t. clean data. For instance, if some images contain natural fog, fog corruption robustness should be naturally higher, whereas robust to never seen unrealistic dragonfire is expected to be naturally low. Can this relation between corruption and domain gap be somehow assessed? For instance using perceptual distance (using features from intermediate layers) to nearest clean neighbors? Or maybe by correlating with a subjective measure of realism of the corruption assessed globally per corruption type via a human study?
- Are corruption degradations dataset-specific? Fig. 7,8,9 seem to show different behaviors.
- How does the proposed benchmark compare to the Robust Vision Challenge (http://www.robustvision.net) proposed at CVPR 2018? How does robustness to corruptions and robustness across datasets correlate? Are they both similar "out of domain" robustness measures? How does this "out of domain" issue relate to adversarial examples (besides being "less extreme")?
- Could Fig. 5 include error bars / variance across corruption types?
- rPC is a good metric to compare models but I am not sure it is great to compare robustification methods, because when improving "clean" performance you mechanically decrease rPC, hence why combined is worse than stylized (e.g., in Table 2). What would be a better metric?
- Why does the stylized approach on COCO yields worse mPC (cf. Table 2 and 4), whereas it is expected to improve robustness under corruption (and does on other datasets), esp. since it sacrifices performance on the clean images by a lot?
- What is the impact of the choice of style images on robustness induced by stylization? Is diversity the most important factor (this can be tested by reducing the number of styles available)? If not, what is and how can it be measured?
- Do certain corruption (at certain severity levels) result in unrecoverable objects? For instance, dragonfire might completely occlude certain objects on the side, which might be a problem (e.g., there are frequent parked cars on the side in Cityscapes). What is the upper bound after corruption and how can it be measured?
- What is the human robustness for the new corruptions not present in Geirhos et al 2019? (Also relates to the aforementioned upper bound.)
- The paper is well written and I enjoyed the multiple pop culture references to Game of Thrones.