Neural Architecture Search (NAS) is an exciting new field which promises to be as much as a game-changer as Convolutional Neural Networks were in 2012. Despite many great works leading to substantial improvements on a variety of tasks, comparison between different methods is still very much an open issue. While most algorithms are tested on the same datasets, there is no shared experimental protocol followed by all. As such, and due to the under-use of ablation studies, there is a lack of clarity regarding why certain methods are more effective than others. Our first contribution is a benchmark of 8 NAS methods on 5 datasets. To overcome the hurdle of comparing methods with different search spaces, we propose using a method's relative improvement over the randomly sampled average architecture, which effectively removes advantages arising from expertly engineered search spaces or training protocols. Surprisingly, we find that many NAS techniques struggle to significantly beat the average architecture baseline. We perform further experiments with the commonly used DARTS search space in order to understand the contribution of each component in the NAS pipeline. These experiments highlight that: (i) the use of tricks in the evaluation protocol has a predominant impact on the reported performance of architectures; (ii) the cell-based search space has a very narrow accuracy range, such that the seed has a considerable impact on architecture rankings; (iii) the hand-designed macrostructure (cells) is more important than the searched micro-structure (operations); and (iv) the depth-gap is a real phenomenon, evidenced by the change in rankings between 8 and 20 cell architectures. To conclude, we suggest best practices, that we hope will prove useful for the community and help mitigate current NAS pitfalls, e.g. difficulties in reproducibility and comparison of search methods. We provide the code used for our experiments at link-to-come.

The paper scrutinizes commonly used evaluation strategies for neural architecture search.
The first contribution is to compare architectures found by 5 different search strategies from the literature against randomly sampled architectures from the same underlying search space.
The paper shows that across different image classification datasets, the most neural architecture search methods are not consistently finding solutions that achieve a better performance than random architectures.
The second major contribution of the paper is to show that the state-of-the-art performance achieved by the many neural architecture search methods can be largely attributed to advanced regularization tricks.
In general the paper is well written and easy to follow.
The paper sheds a rather grim light on the current state of neural architecture search, but I think it could raise awareness of common pitfalls and help to make future work more rigorous.
While poorly designed search spaces is maybe a problem that many people in the community are aware of, this is, to the best of my knowledge, the first paper that systematically shows that for several commonly used search spaces there is not much to be optimized.
Besides that, the paper shows that, maybe not surprisingly, the training protocol seems to be more important than the actual architecture search, which I also found rather worrisome.
It would be nice, if Figure 3 could include another bar that shows the performance of a manually designed architecture, for example a residual network, trained with the same regularization techniques.
A caveat of the paper is that mostly local methods with weight-sharing are considered, instead of more global methods, such as evolutionary algorithms or Bayesian optimization, which also showed strong performance on neural architecture search problems in the past.
Furthermore, the paper doesn't mention some recent work in neural architecture search that present more thoroughly designed search spaces, e.g Ying et al.
It would also be helpful if the paper could elaborate, on how better search spaces could be designed.
Nas-bench-101: Towards reproducible neural architecture search
C Ying, A Klein, E Real, E Christiansen, K Murphy, F Hutter
ICML 2019
Minor comments:
- Section 4.1 How are the hyperparameters of drop path probability, cutout length and auxiliary tower weight chosen?
post rebuttal
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I thank the authors for taking the time to answer my questions and performing the additional experiments. The paper highlights two important issues in the current NAS literature: evaluating methods with different search spaces and non-standardised training protocols. I do think that the paper makes an important contribution which hopefully helps future work to over come these flaws.


Recent research efforts enable study for natural language grounded navigation in photo-realistic environments, e.g., following natural language instructions or dialog. However, existing methods tend to overfit training data in seen environments and fail to generalize well in previously unseen environments. In order to close the gap between seen and unseen environments, we aim at learning a generalizable navigation model from two novel perspectives: (1) we introduce a multitask navigation model that can be seamlessly trained on both Vision-Language Navigation (VLN) and Navigation from Dialog History (NDH) tasks, which benefits from richer natural language guidance and effectively transfers knowledge across tasks; (2) we propose to learn environment-agnostic representations for navigation policy that are invariant among environments, thus generalizing better on unseen environments. Extensive experiments show that our environment-agnostic multitask navigation model significantly reduces the performance gap between seen and unseen environments and outperforms the baselines on unseen environments by 16% (relative measure on success rate) on VLN and 120% (goal progress) on NDH, establishing the new state of the art for the NDH task.

This paper addresses some challenges of following natural language instructions for navigating in visual environments. The main challenge in such tasks is the scarcity of available training data, which results in generalization problems where the agent has difficulty navigating in unseen environments. Therefore, the authors propose two key ideas to tackle this issue and incorporate them in the reinforced cross-modal matching (RCM) model (Wang et al, 2019). First, they use a generalized multitask learning model to transfer knowledge across two different tasks: Vision-Language Navigation (VLN) and Navigation from Dialog History (NDH). This results in learning features that explain both tasks simultaneously and hence generalize better. Moreover, by training on both tasks the effective size of training data is increased significantly. Second, they propose an environment-agnostic learning technique in order to learn invariant representations that are still efficient for navigation. This prevents overfitting to specific visual features of the environment and therefore helps improving generalization. The contribution of this paper is combining and incorporating these two key ideas in the RCM framework and verifying it on VLN and NDH tasks. This approach is novel compared to prior results in tackling the VLN task. Their experimental results show that the two proposed techniques improve generalization in a complementary fashion, measured by decreased performance gap between seen and unseen environments.  They demonstrate that their technique outperforms state-of-the-art methods on unseen data on some evaluation metrics.
Even though the two key ideas proposed in the paper has been explored in the literature in other contexts, this paper contributes to natural language guided navigation by incorporating these ideas in a unified framework and demonstrates promising results on two datasets. Therefore, I would recommend accepting this paper if some issues in delivery and clarity are addressed.
In particular, Section 3, where the authors introduce the novelty of the paper in more detail, could be better explained and a cleaner line should be drawn between prior results from other papers and novel results proposed by this paper. In general, the new ideas would require more emphasis, since they are somewhat lost between adaptations from prior work. Most importantly, Eq. (3) is stated without sufficient motivation and would require a more detailed explanation.
In addition to these points, I would like to disclose some recommendations that might improve the paper but are not strictly part of my decision. In some cases the notation is not clear and some variables are not defined or explained. For instance, after Eq. (8) Attention(.) is used without citation or definition, in Eq. (9) Wc and Wu are not defined and some of the notation in Eq. (6)-(7) are not defined. Moreover, reading the decrease in performance gap from the presented table format is inconvenient and a better visual representation might help demonstrating the improvement in generalization better.  Lastly, I noticed that the navigation error for shared decoder is slightly higher than for separate encoders in Table 3, even though it outperforms the separate encoders in every other measures. Is there a particular explanation for this?


We revisit the one-shot Neural Architecture Search (NAS) paradigm and analyze its advantages over existing NAS approaches. Existing one-shot method (Bender et al., 2018), however, is hard to train and not yet effective on large scale datasets like ImageNet. This work propose a Single Path One-Shot model to address the challenge in the training. Our central idea is to construct a simplified supernet, where all architectures are single paths so that weight co-adaption problem is alleviated. Training is performed by uniform path sampling. All architectures (and their weights) are trained fully and equally. Comprehensive experiments verify that our approach is flexible and effective. It is easy to train and fast to search. It effortlessly supports complex search spaces (e.g., building blocks, channel, mixed-precision quantization) and different search constraints (e.g., FLOPs, latency). It is thus convenient to use for various needs. It achieves start-of-the-art performance on the large dataset ImageNet.

This paper presents a new one-shot NAS approach. Parameter updating and structure updating are optimized separately. In the process of parameter optimization, different from the previous methods, the network samples the structure according to the uniform probability distribution. This sampling method can avoid the coupling caused by optimizing the structural parameters at the same time. After training the supernet, the network uses the genetic algorithm to search the structure.
Pros:
+ This paper is well-written and easy to follow.
+ The method proposed in this paper is very efficient in the search stage and saves memory. During the searching stage, the constraints of the model can be restricted by the genetic algorithm.
+ This method could directly search architectures on the large scale dataset.
+ The results are promising. Experiments are performed on various structures and including quantization layers.
Still, I have several minor concerns regarding the algorithm and experiments.
1. Why does the author think that the supernet needs to be trained by single path all the time? In the architecture searching space, under the same computational constraints, some models perform well, and some do not. Why do the good models and the worse models use the same probability to sample? Wouldn't it require much more time to optimize the supernet? In the experiment part, the author compares a related work FBNet, which uses the structure parameter \theta and temperature parameter \tau to control the sampling. When the temperature \tau is high, the distribution of the samples degenerates into the single path sampler, and the accuracy is used to optimize the parameter \theta, which makes \theta tend to select the well-performed models. With the decrease of the temperature \tau, the probability of sampling well-performed architectures is higher than the worse-performed models. Therefore, what is the advantage of the single path sampling method over \tau controlled sampler? It seems that gradually pruning the worse-performed search space would accelerate searching time. More analysis is preferred rather than the superior results from the experiments.
2. Is identity in the search space? For at the last of Page4, the author said 'our choice block does not have an identity branch', and the listed architecture on page 13 has the identity.
3. Is the supernet training for 120 epochs necessary? Is the rank of network structures become steady when training for 120 epochs. Because for the subsequent EA-based network structure search, the loss scale is not important, but the sorting (ranking) is important. (This beyond the scope of this paper, but relates to the NAS area)
4. What is the number of parameters for all the listed models in Tab. 3 & Tab. 4? Listing the parameters makes it easier for the followers.
5. What kind of structure do the mixed-precision networks use? The original resnet module, or the bireal resnet module [r1]?
6. While recalculating the statistics of all the BN,  is backpropagation required or just run the inference without gradient backpropagation.
7. The author uses the approximate complete set of Imagenet to train supernet. If we directly inherit the parameter from the supernet, can we accelerate the training of searched good structure? Will Top-1 acc lower than training from scratch?
[r1] Bi-real net: Enhancing the performance of 1-bit cnns with improved representational capability and advanced training algorithm


We investigate multi-task learning approaches which use a shared feature representation for all tasks. To better understand the transfer of task information, we study an architecture with a shared module for all tasks and a separate output module for each task. We study the theory of this setting on linear and ReLU-activated models. Our key observation is that whether or not tasks' data are well-aligned can significantly affect the performance of multi-task learning. We show that misalignment between task data can cause negative transfer (or hurt performance) and provide sufficient conditions for positive transfer. Inspired by the theoretical insights, we show that aligning tasks' embedding layers leads to performance gains for multi-task training and transfer learning on the GLUE benchmark and sentiment analysis tasks; for example, we obtain a 2.35% GLUE score average improvement on 5 GLUE tasks over BERT LARGE using our alignment method. We also design an SVD-based task reweighting scheme and show that it improves the robustness of multi-task training on a multi-label image dataset.

This paper analyzed the principles for a successful transfer in the hard-parameter sharing multitask learning model. They analyzed three key factors of multi-task learning on linear model and relu linear model: model capacity (output dimension after common transformation), task covariance (similarity between tasks) and optimization strategy (influence of re-weighting algorithm), with theoretical guarantees. Finally they evaluated their assumptions on the state-of-the-art multi-task framework (e.g GLUE,CheXNet), showing the benefits of the proposed algorithm.
Main comments:
This paper is highly interesting and strong. The author systematically analyzed the factors to ensure a good multi-task learning. The discovering is coherent with with previous works, and it also brings new theoretical insights (e.g. sufficient conditions to induce a positive transfer in Theorem 2). The proof is non-trivial and seems technically sound.
Moreover, they validated their theoretical assumptions on the large scale and diverse datasets (e.g NLP tasks, medical tasks) with state-of-the-art baselines, which verified the correctness of the theory and indicated strong practical implications.
Minor comments:
The main message of the paper is clear but some parts still confuse me:
1. I suggest the author to merge the Figure 3 and Data generation (Page 4) part for a better presentation. e,g which “diff.covariance” is task 3 or 4 ?  And why we use different rotation matrix Q_i ?
2. In algorithm 1 (Page 5) , I suggest the author use a formal equation (like algorithm 2) instead of descriptive words.
     -- Step 2, I have trouble in understading this step.
     -- Step 3, how to jointly minimize R_1,\dots, R_k, A_1, \dots, A_k ? we use loss (3)  or other losses ?
     -- I suggest that the author release the code for a better understanding.
3. For theorem 2, can we find some “optimal” c to optimize the right part ? Since 6c + \frac{1}{1-3c}\frac{\epsilon}{\X_2\theta_2} might be further optimized
4. In section 3.3. (Figure 6)  of the real neural network, the model capacity is the dimension of Z or simply the dimension before last fc-layer ?
5. Some parts in the appendix can be better illustrated:
    (a) I am not clear how proposition 4 can derive proposition 1.
    (b) Page 15, proving fact 8: last line \frac{1}{k^4}sin(a^{prime},b^{prime}) should be \frac{1}{k^4}sin^{2}(a^{prime},b^{prime}).
Overall I think it is a good work with interesting discoverings for the multi-task learning. I think it will potentially inspire the community to have more thoughts about the transfer learning.


When humans observe a physical system, they can easily locate objects, understand their interactions, and anticipate future behavior, even in settings with complicated and previously unseen interactions. For computers, however, learning such models from videos in an unsupervised fashion is an unsolved research problem. In this paper, we present STOVE, a novel state-space model for videos, which explicitly reasons about objects and their positions, velocities, and interactions. It is constructed by combining an image model and a dynamics model in compositional manner and improves on previous work by reusing the dynamics model for inference, accelerating and regularizing training. STOVE predicts videos with convincing physical behavior over hundreds of timesteps, outperforms previous unsupervised models, and even approaches the performance of supervised baselines. We further demonstrate the strength of our model as a simulator for sample efficient model-based control in a task with heavily interacting objects.

This paper introduces a structured deep generative model for video frame prediction, with an object recognition model based on the Attend, Infer, Repeat (AIR) model by Eslami et al. (2016) and a graph neural network as a latent dynamics model. The model is evaluated on two synthetic physics simulation datasets (N-body gravitational systems and bouncing billiard balls) for next frame prediction and on a control task in the billiard domain. The model can produce accurate predictions for several time steps into the future and beats a variational RNN and SQAIR (sequential AIR variant) baseline, and is more sample-efficient than a model-free PPO agent in the control task.
Overall, the paper is well-structured, nicely written and addresses an interesting and challenging problem. The experiments use simple domains/problems, but give good insights into how the model performs.
Related work is covered to a satisfactory degree, but a discussion of some of the following closely related papers could improve the paper:
* Chang et al., A Compositional Object-Based Approach To Learning Physical Dynamics, ICLR 2017
* Greff et al., Neural Expectation Maximization, NeurIPS 2017
* Kipf et al., Neural Relational Inference for Interacting Systems, ICML 2018
* Greff et al., Multi-object representation learning with iterative variational inference, ICML 2019
* Sun et al., Actor-centric relation network, ECCV 2018
* Sun et al., Relational Action Forecasting, CVPR 2019
* Wang et al., NerveNet: Learning structured policy with graph neural networks, ICLR 2018
* Xu et al., Unsupervised discovery of parts, structure and dynamics, ICLR 2019
* Erhardt et al., Unsupervised intuitive physics from visual observations, ACCV 2018
In terms of clarity, the paper could be improved by making the used model architecture more explicit, e.g., by adding a model figure, and by providing an introduction to the SuPAIR model (Stelzner et al., 2019) — the authors assume that the reader is more or less familiar with this particular model. It is further unclear how exactly the input data is provided to the model; Figure 2 makes it seem that inputs are colored frames, section 3.1 mentions that inputs are grayscale videos (do all objects have the same appearance or different shades of gray?), which is in conflict with the statement on page 5 that the model is provided with mean values of input color channels. Please clarify.
In terms of novelty, the proposed modification of SQAIR (separating object detection and latent dynamics prediction) is novel and likely leads to a speed-up in training and evaluation. Using a Graph Neural Network for modeling latent physics is reasonable and has been shown to work on related problems before (see referenced work above and related work mentioned in the paper). Similarly, using such a model for planning/control is interesting and adds to the value of the paper, but has in related settings been explored before (e.g. Wang et al. (ICLR 2018) and Sanchez-Gonzalez (ICML 2018)).
Experimentally, it would be good to provide ablation studies (e.g. a different object detection module like AIR instead of SuPAIR, not splitting the latent variables into position, velocity, size etc.) and run-time comparisons (wall-clock time), as one of the main contributions of the paper is that the proposed model is claimed to be faster than SQAIR. The overall model predictions are (to my surprise) somewhat inaccurate, when looking at e.g. the billiard ball example in Figure 2. In Steenkiste et al. (ICLR 2018), roll-outs appear to be more accurate. Maybe a quantitative experimental comparison could help?
Why does the proposed model perform worse than a model-free PPO baseline when trained to convergence on the control task? What is missing to close this gap?
Do all objects have the same appearance (color/greyscale values) or are they unique in appearance? In the second case, a simpler encoder architecture could be used such as in Jaques et al. (2019) or Xu et al. (ICLR 2019).
Overall, I think that this paper addresses an important issue and is potentially of high interest to the community. Nonetheless I think that this paper needs a bit more work and at this point I recommend a weak reject.
Other comments:
* This sentence is unclear to me: “An additional benefit of this approach is that the information learned by the dynamics model is reused for inference — […]”
* What are the failure modes of the model? Where does it break down?
* How does the model deal with partial occlusion?
---------------------
UPDATE (after reading the author response and the revised manuscript): My questions and comments are addressed and the additional ablation studies and experimental results on energy conservation are convincing and insightful. I think the revised version of the paper meets the bar for acceptance at ICLR.


Deep ensembles have been empirically shown to be a promising approach for improving accuracy, uncertainty and out-of-distribution robustness of deep learning models. While deep ensembles were theoretically motivated by the bootstrap, non-bootstrap ensembles trained with just random initialization also perform well in practice, which suggests that there could be other explanations for why deep ensembles work well. Bayesian neural networks, which learn distributions over the parameters of the network, are theoretically well-motivated by Bayesian principles, but do not perform as well as deep ensembles in practice, particularly under dataset shift. One possible explanation for this gap between theory and practice is that popular scalable approximate Bayesian methods tend to focus on a single mode, whereas deep ensembles tend to explore diverse modes in function space. We investigate this hypothesis by building on recent work on understanding the loss landscape of neural networks and adding our own exploration to measure the similarity of functions in the space of predictions. Our results show that random initializations explore entirely different modes, while functions along an optimization trajectory or sampled from the subspace thereof cluster within a single mode predictions-wise, while often deviating significantly in the weight space. We demonstrate that while low-loss connectors between modes exist, they are not connected in the space of predictions. Developing the concept of the diversityaccuracy plane, we show that the decorrelation power of random initializations is unmatched by popular subspace sampling methods.

This paper analyzes ensembling methods in deep learning from the perspective of the loss landscapes. The authors empirically show that popular methods for learning Bayesian neural networks produce samples with limited diversity in the function space compared to modes of the loss found using different random initializations. The paper also considers the low-loss paths connecting independent local optima in the weight-space. The analysis shows that while the values of the loss and accuracy are nearly constant along the paths, the models corresponding to different points on a path define different functions with diverse predictions. The paper also demonstrates the complementary benefits of using subspace sampling/weight averaging in combination with deep ensembles and shows that relative benefits of deep ensembles are higher.
The paper is well-written. The experiments are described well and the results are presented clearly in highly-detailed and visually-appealing figures. There are occasional statements which are not formulated rigorously enough (see comments below).
The paper presents a thorough experimental study of different ensemble types, their performance, and function space diversity of individual members of an ensemble. In my view, the strongest contribution of the paper is the analysis of the diversity of the predictions for different sampling procedures in comparison to deep ensembles. However, the novelty and the significance of the other contributions are limited (see comments below). Therefore, I consider the paper to be below the acceptance threshold.
Comments and questions to authors:
1) The practical aspects of different ensembling techniques are not discussed in the paper. While it is known that deep ensembles generally demonstrate stronger performance [1], there is a trade-off between the ensemble performance and training time/memory consumption. The considered alternative ensembling procedures can be favorable in specialized settings (e.g. limited training time and/or memory).
2) It remains unclear to me what new insights does the analysis of the low-loss connectors provide? It is expected (and in fact can be shown analytically) that if the two modes define different functions then intermediate points on a continuous path define functions which are different from those defined by the end-points of the path. This result was also analyzed before from the perspective of the performance of ensembles formed by the intermediate points on the connecting paths (see Fig. 2 right in [2]).
Moreover, I would encourage authors to reformulate the statements on the connectivity in the function space such as:
-- “We demonstrate that while low-loss connectors between modes exist, they are not connected in the space of predictions.”  (Abstract)
-- “the connectivity in the loss landscape does not imply connectivity in the space of functions” (Discussion)
In my opinion, these claims are somewhat misleading. What does it mean that the modes are disconnected in the function space? Neural networks define continuous functions (w.r.t to both the inputs and the weights), and a connector is continuous path in the weight space which continuously connects the modes in the function space (i.e. a path defines a homotopy between two functions). It is true that two modes correspond to two different functions. However, it is unclear in which sense these functions can be considered to be disconnected.
[1] Balaji Lakshminarayanan, Alexander Pritzel, and Charles Blundell. Simple and scalable predictive uncertainty estimation using deep ensembles. In NeurIPS, 2017.
[2] Timur Garipov, Pavel Izmailov, Dmitrii Podoprikhin, Dmitry P Vetrov, and Andrew G Wilson. Loss surfaces, mode connectivity, and fast ensembling of DNNs. In NeurIPS, 2018.


We consider the problem of learning high-level controls over the global structure of sequence generation, particularly in the context of symbolic music generation with complex language models. In this work, we present the Transformer autoencoder, which aggregates encodings of the input data across time to obtain a global representation of style from a given performance. We show it is possible to combine this global embedding with other temporally distributed embeddings, enabling improved control over the separate aspects of performance style and and melody. Empirically, we demonstrate the effectiveness of our method on a variety of music generation tasks on the MAESTRO dataset and an internal dataset with 10,000+ hours of piano performances, where we achieve improvements in terms of log-likelihood and mean listening scores as compared to relevant baselines.

This paper presents a technique for encoding the high level “style” of pieces of symbolic music. The music is represented as a variant of the MIDI format. The main strategy is to condition a Music Transformer architecture on this global “style embedding”.  Additionally, the Music Transformer model is also conditioned on a combination of both “style” and “melody” embeddings to try and generate music “similar” to the conditioning melody but in the style of the performance embedding.
Overall, I think the paper presents an interesting application and parts of it are well written, however I have concerns with the technical presentation in parts of the paper and some of the methodology. Firstly, I think the algorithmic novelty in the paper is fairly limited. The performance conditioning vector is generated by an additional encoding transformer, compared to the Music Transformer paper (Huang et. al. 2019b). However, the limited algorithmic novelty is not the main concern. The authors also mention an internal dataset of music audio and transcriptions, which can be a major contribution to the music information retrieval (MIR) community. However it is not clear if this dataset will be publicly released or is only for internal experiments.
In terms of technical presentation, I think the authors should clarify how the model is trained. It took me a couple of passes and reading the Music Transformer paper to realise that in the melody and performance conditioning case, the aim is to generate the full score (melody and accompaniment) while conditioning on the performance style and melody (which is represented using a different vocabulary). This point can be easily clarified in Figure 1, by adding the input to the encoder as input to the decoder for computing the loss. Although I understand the need for anonymity and constraints while referring to unreleased datasets, it would still be useful for the reader/reviewer to have some details of how the melody was extracted and represented. “An internal procedure” is quite mysterious.
Measuring music similarity is a difficult problem and the topic has been the subject of at least 2 decades of research. I find the description of the “performance feature” to be lacking in necessary background and detail. Firstly, I am not sure what the final dimensionality of the feature vector is. Is it real valued? The authors mention (Yang and Lerch, 2018) but use a totally different set of attributes compared to that paper. I also don’t see the connection between this proposed feature vector and using the IMQ kernel for measuring similarity. This connection is not motivated adequately and after reading (Jitkrittum et. al. 2019) its not obvious to me why this is the most appropriate metric. Finally, it would be useful if the authors comment on existing methods for measuring music similarity in symbolic music and how their proposed feature fits into existing work. A lot of work has been published on this topic, most recently in the context of Query-by-Humming [1].
Minor Comments
1. “...which typically incorporate global conditioning as part pf the training procedure” Could you elaborate on this point? Is the global conditioning the samples from the noise distribution?
2. Figure 1 should be clarified or another figure should be added to show how the melody conditioning works. Maybe a comment on the melody vocabulary or a reference would also be useful.
3. The MAESTRO dataset is described in terms of the number of performances while the internal dataset is described in terms of the number of hours of audio. Its not possible for the reader to get a sense of the relative sizes of the 2 datasets and how the results should be interpreted.
4. There should be more background and description in Section 4. Where does the performance feature come from? Why use this feature compared to existing techniques for measuring similarity between symbolic music pieces? Is it computational efficiency? Why not compare the conditioning melody with the generated performance similar to query-by-humming? Where does the IMQ kernel come from? What is the size of the feature vector?
5. In section 5.2, a conditioning sample, a generated sequence and an unconditional sample are used to compute the similarity measure. Which terms do these correspond to in the MMD-like term (x,y,y’)?
6. I like the experiments performed in Section 5.3 with the linear combination of 2 performance embeddings.
[1] A Survey of Query-By-Humming Similarity Methods: http://vlm1.uta.edu/~athitsos/publications/kotsifakos_petra2012.pdf


Discrete choice models with unobserved heterogeneity are commonly used Econometric models for dynamic Economic behavior which have been adopted in practice to predict behavior of individuals and firms from schooling and job choices to strategic decisions in market competition. These models feature optimizing agents who choose among a finite set of options in a sequence of periods and receive choice-specific payoffs that depend on both variables that are observed by the agent and recorded in the data and variables that are only observed by the agent but not recorded in the data. Existing work in Econometrics assumes that optimizing agents are fully rational and requires finding a functional fixed point to find the optimal policy. We show that in an important class of discrete choice models the value function is globally concave in the policy. That means that simple algorithms that do not require fixed point computation, such as the policy gradient algorithm, globally converge to the optimal policy. This finding can both be used to relax behavioral assumption regarding the optimizing agents and to facilitate Econometric analysis of dynamic behavior. In particular, we demonstrate significant computational advantages in using a simple implementation policy gradient algorithm over existing "nested fixed point" algorithms used in Econometrics.

This paper deals with a certain class of models, known as discrete choice models. These models are popular in econometrics, and aim at modelling the complex behavioural patterns of individuals or firms. Entities in these models are typically modelled as rational agents, that behave optimally for reaching their goal of maximizing a certain objective function such as maximizing expected cumulative discounted payoff over a fixed period.
This class of models, modelled as a MDP with choice-specific heterogeneity, is challenging as not all the payoffs received by the agents is externally observable. One solution in this case is finding a balance condition and a functional fixed point to find the optimal policy (closely related to value function iteration), and this is apparently the key idea behind ‘nested fixed point’ methods used in Econometrics.
The paper proposes an alternative. First it identifies a subclass of discrete choice models (essentially MDP with stochastic rewards) where the value function is globally concave in the policy. The consequence of this observation is that a direct method, such as the policy gradient that circumvents explicitly estimating the value function, can (at least in principle) converge to the optimal policy without calculating a fixed point. The authors illustrate computational advantages of this direct approach. Moreover, the generality of the policy gradient method enables the relaxation of extra assumptions regarding the behaviour of agents while facilitating a wider applicability/econometric analysis.
The key contribution claimed by the paper is the observation that in the class of dynamic discrete choice models with unobserved heterogeneity, the value function is globally concave in the policy. This enables using computationally efficient policy gradient algorithms with convergence guarantees for this class of problems. The authors also claim that the simplicity of policy gradient makes it also a viable model for understanding economic behaviour in econometric analysis, and more broadly for social sciences.
The paper deals with Discrete choice models with unobserved heterogeneity as a special class of MDP’s and is relevant to ICLR. However, the writing style is quite technical and terse -- while I could appreciate the rigour, the authors develop the basic material until page 5 -- Notation is also somewhat non-standard at places (alternating using delta or sigma for a policy and pi for thresholds of an exponential softmax distribution) and makes it harder to see the additional structure from generic MDPs more familiar in RL. I suspect that a reader more familiar with the relevant econometric, marketing and finance literature could follow the model description more easily.
There are a number of assumptions in the paper, especially 2.4 and 2.5 that relate to the monotonicity and ordering of the states. These assumptions seem to be important in subsequent developments for showing the concavity but they seem to be coming from out of the blue. Unfortunately the authors do not provide any intuition/discussion -- an example problem with these properties would make these assumptions more concrete. I was hoping to find such an example in the empirical application however this section does not make the necessary connections with the theoretical development. There are not even references to basic claims
done in the abstract, for example, I am not able to find an illustration of ‘significant computational advantages in using a simple implementation policy gradient algorithm over existing “nested fixed point” algorithms used in Econometrics’. The lack of any conclusions makes it also hard for me to appreciate the contributions.
Minor:
Abstract:
.. Existing work in Econometrics assumes that optimizing agents are fully rational and requires finding a functional fixed point to find the optimal policy. …
Ambiguous sentence: Existing work in Econometrics [...] requires finding a functional fixed point to find the optimal policy.
Theorem 3.1 and elsewhere  Freéchet =>  Fréchet


Adversarial attacks were shown to be very effective in degrading the performance of neural networks. By slightly modifying the input, an almost identical input is misclassified by the network. To address this problem, we adopt the universal learning framework. In particular, we follow the recently suggested Predictive Normalized Maximum Likelihood (pNML) scheme for universal learning, whose goal is to optimally compete with a reference learner that knows the true label of the test sample but is restricted to use a learner from a given hypothesis class. In our case, the reference learner is using his knowledge on the true test label to perform minor refinements to the adversarial input. This reference learner achieves perfect results on any adversarial input. The proposed strategy is designed to be as close as possible to the reference learner in the worst-case scenario. Specifically, the defense essentially refines the test data according to the different hypotheses, where each hypothesis assumes a different label for the sample. Then by comparing the resulting hypotheses probabilities, we predict the label and detect whether the sample is adversarial or natural. Combining our method with adversarial training we create a robust scheme which can handle adversarial input along with detection of the attack. The resulting scheme is demonstrated empirically.

Summary:
This paper focuses on the area of adversarial defense -- both to improve robustness and to detect adversarially perturbed images. They approach the problem from the universal prediction / universal learning framework.
Modivation:
I had a hard time understanding the motivation of this work -- specifically the connection to the universal learning framework which to be fair I am unfamiliar with. In the absence of the universal learning framework formalism the method proposed here is quite simple and in my opinion clever -- create a new prediction based on performing an adversarial attack to each target class. What value does universal learning bring to this?
Second, I do not follow the intuition for the chosen hypothesis class -- why work off of refined images in the first place? Is there some reason to believe this will improve robustness?
Finally, the view that adversarial defense and attack are important topics to explore is under some debate. I am not considering this as part of my review but I would encourage the authors to look at [1].
Writing:
The writing was clear and typo free.
Experiments:
Overall the experiments seemed inconclusive.
Section 5 shows robustness against the unmodified / unrefined model (the attacks are done on the base model not the refined model). Given that these attacks are performed against the unmodified model then evaluated on the modified model the results seem a bit unfair / harder to interpret. The authors note this, and in Section 6 explore the "Adaptive Adversary" setting.
The results presented are performed on Mnist and Cifar10. Overall the results were not convincing to me. Table 1 shows mixed performance -- a drop in natural accuracy in all cases, decreases in FGSM. The main increase in performance is in the PGD. This was noted, but understanding in more depth why this method helps here will hopefully lead to improved performance in FGSM as well.
Figure 2a shows very weak correlations. Figure 2b seems promising but also not necessarily a surprise given that the adversarial examples are generated against the base model and not the refined model.
For section 6, one risk is that the BPDA attack doesn't successfully work. Having some more proof that the attacks presented here are strong would greatly improve the work.
Larger scale experiments would of course be nice and strengthen the paper but more importantly it would be great to see some form of toy example or demonstration of the principle improving robustness as well over just results. Something to probe the mechanism of action for example.
Finally, having some comparisons to other defense strategies would improve this paper.
Rating:
Given the gap between the universal learning framework and the method proposed, as well as the inconclusive experiments at this point I would not recommend the paper for acceptance.
[1] https://arxiv.org/abs/1807.06732


Humans are able to both learn quickly and rapidly adapt their knowledge. One major component is the ability to incrementally combine many simple concepts to accelerates the learning process. We show that energy based models are a promising class of models towards exhibiting these properties by directly combining probability distributions. This allows us to combine an arbitrary number of different distributions in a globally coherent manner. We show this compositionality property allows us to define three basic operators, logical conjunction, disjunction, and negation, on different concepts to generate plausible naturalistic images. Furthermore, by applying these abilities, we show that we are able to extrapolate concept combinations, continually combine previously learned concepts, and infer concept properties in a compositional manner.

Update: In light of the quality of the author response, I decide to raise my score to 6: Weak Accept. I encourage the authors to keep improving their writing of section 3.4. The description of the dataset is much clearer than the previous version, but I still think it is worthwhile to use more space for a better description.
There are some other issues with this paper that I recommend the authors to address in the revisions.
- Currently all quantitative experiments are based on conjunctions. It would be nice to have quantitative results for disjunctions and negations as well to make the authors' argument more convincing.
- I would suggest removing the result of PixelCNN in the paper. Of course sampling with Langevin dynamics for PixelCNN is hard. I think a more straightforward way is to do Langevin dynamics for each conditional distribution. The current result of PixelCNN is not done in this way and can be misleading for future work.
That being said, I think the idea proposed by this paper is of novel interest, and even though the execution is not ideal, I feel the novelty itself should warrant an acceptance at ICLR.
============ Original Review ===============
This paper proposes several rules to compose different energy-based models for compositional image generation. The authors propose empirical rules for conjunction, disjunction, and negation, which in combination can be used to derive arbitrary logic expressions. The authors demonstrate that using these composition rules, energy-based models can be used for compositional image generation, continual learning, and compositional concept inference.
I agree with the authors that the composition of energy-based models is a very desirable property and a very important direction to explore, and I believe that the work of this paper can have great potential in the future. However, I feel that the current paper is not very mature, and many questions are left unanswered. Here are some detailed comments:
- What's the justification for the formula of concept disjunction? For disjunction, it makes sense to me to form a mixture of distribution where each mixture has the same weight, ie, \sum_i p(x | c_i). However, \sum_i p(x | c_i) is not proportional to \sum e^{-E(x | c_i)} because of the unknown partition functions. Therefore, when the partition functions of two energy-based models differ by a lot, the disjunction will not be a mixture with equal weights for each component. Instead, it will collapse to a single distribution where all weights are put on the component with the smallest partition function. This does not match the intuition of "disjunction".
- One way of solving the disjunction problem might be abandoning the Langevin dynamics sampling procedure (7). Sampling from a mixture of distribution is doable for arbitrary generative models as long as it is possible to sample from each component of the mixture. Why not just apply Langevin dynamics to each energy-based model in the disjunction and return the samples from each model with the same probability? This procedure cannot be trivially composed with other rules such as conjunction and negation, but it suffices to produce all results in this paper and should be more theoretically sound.
- In Table 1, it seems that energy-based models are more robust in concept inference compared to a ResNet. Why is this the case? I would envisage that the energy-based model is also a ResNet and should have the same inductive bias? Is this a property of generative classifiers? Since the results in Table 1 do not involve composition of energies it is desirable to compare the results with other generative models as well, such as conditional PixelCNN.
- Since more steps of negative sampling can give better samples and generalize better, why not use 400 steps in all experiments throughout the paper?
- In the original OpenAI paper for energy-based models [1], the authors tune the coefficients of the gradient and noise terms in Langevin dynamics for better performance. This is equivalent to doing the ordinary Langevin dynamics for a different energy function re-scaled by some temperature parameter. Did you tune the scales of Langevin dynamics as well? If so, since the energies are scaled by some temperature, the original composition rules will be problematic. Did you take account of this temperature scaling in doing the experiments?
- There is no detailed description of model architecture or hyperparameter in the paper. The author provide no detailed information on how the model was trained, for example, the various hyperparameters in Langevin dynamics and replay buffer. No code is available. There is even no appendix. The paper is very hard to reproduce, which hurts the reliability of the experimental results.
- Writing can be improved.  The description of the dataset in section 3.4 is barely readable. The second paragraph in section 3.4 needs to be paraphrased or significantly expanded. At least there should be some more detailed description of the settings in the appendix.
- At the end of the day, why energy-based models? I can imagine that an autoregressive model can be perfectly used for all tasks described in this paper. It does not even have the problem I mentioned in disjunction, since all densities are normalized. No Langevin dynamics sampling is needed. Since autoregressive models decompose the density using the chain rule, all compositions of the densities can also nicely decompose, and sequential sampling still works.
References:
[1] Du, Yilun, and Igor Mordatch. "Implicit generation and generalization in energy-based models." arXiv preprint arXiv:1903.08689 (2019).


Learning to align multiple datasets is an important problem with many applications, and it is especially useful when we need to integrate multiple experiments or correct for confounding. Optimal transport (OT) is a principled approach to align datasets, but a key challenge in applying OT is that we need to specify a transport cost function that accurately captures how the two datasets are related. Reliable cost functions are typically not available and practitioners often resort to using hand-crafted or Euclidean cost even if it may not be appropriate. In this work, we investigate how to learn the cost function using a small amount of side information which is often available. The side information we consider captures subset correspondence-i.e. certain subsets of points in the two data sets are known to be related. For example, we may have some images labeled as cars in both datasets; or we may have a common annotated cell type in single-cell data from two batches. We develop an end-to-end optimizer (OT-SI) that differentiates through the Sinkhorn algorithm and effectively learns the suitable cost function from side information. On systematic experiments in images, marriage-matching and single-cell RNA-seq, our method substantially outperform state-of-the-art benchmarks.

The authors consider the alignment problem for multiple datasets with side information via entropic optimal transport (Sinkhorn). The authors formulate it as a transport cost learning in optimal transport framework with constraints giving by side information. Empirically, the authors illustrated the effectiveness of the proposed approach over state-of-the-art on several applications (e.g. single-cell RNA-seq, marriage-matching, MNIST with its perturbed one.
The paper show good results of the proposed method for dataset alignment on several applications. However, the motivation of the dataset alignment seems quite weak (e.g. it is unclear the advantage for jointly analysis when one merge datasets by alignment). The side information is not clearly easy to obtain in practice, since it simply enforces the constraints on the transportation polytope (i.e. how one knows that which subset of a given class C_A on dataset A is matched with a certain subset of another class C_B on dataset B, it seems easy to obtain the side information about matching over the whole class C_A with C_B, and it seems nontrivial to obtain the subset matching). Additionally, some important information about the proposed method is not in the main text but in the appendix which makes the paper hard to read without checking appendix constantly (especially the main proposed method). Overall, I lean on the negative side.
Below are some of my concerns:
1) As stated above, I am curious how one can obtain the side information about the subset matching? For example, in Figure 1, it seems trivial to have a side information about the whole class matching and quite nontrivial to obtain a matching for subsets of any given class.
2) The side information enforces the constraints on the feasible set of the transportation polytope. It seems to me that one can solve the variant of optimal transport (or Sinkhorn) with those extra constraints directly, it is unclear to me how this kind of side information can navigate the transport cost learning. Moreover, given a new pairs of input, the proposed method needs to optimize the transport cost again which make the benefits to learn to transport cost quite limited. Overall, a trivial baseline for the proposed method is to solve directly optimal transport with those extra constrains (from side information) directly (maybe with the Euclidean cost metric), but not the optimal transport without extra constraints as in the current setting.
3) The authors may need to consider to reorganize the presentation. Much important information of the proposed method is not in the main text, but in the appendix which make the paper hard to follow without checking the appendix constantly. The derivation of gradient in line 6 of Algorithm 1 is not trivial. It is better if the authors give more detail information and discussion. I am quite confused about the idea to back propagate the "gradient" through Sinkhorn-Knopp iterations?
4) It seems that the complexity of gradient update of Algorithm 1 is quite high. The authors should give a comparison about time consumption in the experiments (besides the accuracy matching)
5) It seems that there is nothing in the code sharing folder?


Deep neural networks are highly effective tools for human and animal pose estimation. However, robustness to out-of-domain data remains a challenge. Here, we probe the transfer and generalization ability for pose estimation with two architecture classes (MobileNetV2s and ResNets) pretrained on ImageNet. We generated a novel dataset of 30 horses that allowed for both within-domain and outof-domain (unseen horse) testing. We find that pretraining on ImageNet strongly improves out-of-domain performance. Moreover, we show that for both pretrained and networks trained from scratch, better ImageNet-performing architectures perform better for pose estimation, with a substantial improvement on out-of-domain data when pretrained. Collectively, our results demonstrate that transfer learning is particularly beneficial for out-of-domain robustness.

= Summary
This paper analyzes the effect of ImageNet pretraining on out-of-domain visual recognition. Specifically, in this paper, the recognition problem is narrowed to pose estimation on a horse profile image dataset where the out-of-domain indicates horse IDs unseen during training. The paper presents a new horse pose estimation dataset and extensive experimental analysis to demonstrate the benefit of ImageNet pretraining.
= Decision
I would recommend to reject this submission mainly due to the shortcomings of the proposed dataset, which make the analysis and conclusion of the paper unconvincing.
First, the dataset is very limited in terms of diversity. It only contains 8K horse profiles images, each of which contains only a single horse, and only 30 horses of the same species appear in the images. Furthermore, since the dataset are sampled from video sequences, images of the same horse ID could be too similar in terms of appearance. Thus, all the images in the dataset seems within a single and very specific domain, "profiles of a small number of Thoroughbred horses", and not appropriate to evaluate "out-of-domain" robustness of pose estimation networks in consequence.
Second, the dataset split strategy is weird. Images of 10 horse IDs are considered as the "within domain" dataset while the others as "out-of-domain" dataset, and a subset of the within domain dataset is used for training or finetuning the pose estimation networks. This means that the networks could seriously overfitted to the small image set of 10 horse IDs. Thus, it is obvious that the networks will work very well with and without ImageNet pretraining on the within domain test set in which exactly the same 10 horses appear, and that they will not work well on the "out-of-domain" dataset due to the overfitting issue.
Also, focusing only on the "horse" class looks not proper. Note that ImageNet already contains many horse images, and ImageNet pretrained networks would have a capability to extract horse-related features. Thus, the advantage of ImageNet pretraining on the horse pose estimation task is not surprising but a result that many in this field can easily expect. If this is not a big issue, I rather would like to recommend to exploit existing human pose datasets (e.g., MPII) since they are larger enough in size, and guarantee a larger variety of poses and person appearances than the proposed horse dataset.
= Other comments
The manuscript is overall written clearly, but it is hard to understand the curves in the figures: colors are not clearly distinguishable (e.g., red vs. magenta), the roles of "MobileNets" and "ResNets" placed on top of upper horizontal bars are not unknown too (if they indicate that the top-2 accuracy scores are given by Resnets variants, why are the curves of MobileNets and ResNets connected?)


Even as pre-trained language encoders such as BERT are shared across many tasks, the output layers of question answering, text classification, and regression models are significantly different. Span decoders are frequently used for question answering, fixed-class, classification layers for text classification, and similarityscoring layers for regression tasks, We show that this distinction is not necessary and that all three can be unified as span extraction. A unified, span-extraction approach leads to superior or comparable performance in supplementary supervised pre-trained, low-data, and multi-task learning experiments on several question answering, text classification, and regression benchmarks.

This paper asks whether it works to remove task-specific heads and treat classification and regression problems as span extraction, by formatting problems in such a way that a single span extraction model can be used.  This is a reasonable question to ask, and the authors performed a very large number of experiments attempting to answer this question.  The authors claim that using span extractive models instead of task-specific heads yields improved performance over separate heads.
My main concern with this work is actually with something that would otherwise be a strength - the very large number of experiments.  Looking at the results tables, I come to a different conclusion from the authors: there does not appear to be a significant difference between using a single head or using multiple heads (this is still an interesting conclusion).  The numbers presented all appear to be within the bounds of random fluctuations, which are not controlled for at all with standard statistical testing methodologies.  And with the very large number of experiments, there are bound to be some that stand out.  This is especially true given the methodology used for small datasets - even if it was used by prior work, it is still not statistically sound to take the max of 20 samples from a training distribution and report the difference without any other statistical testing.
As an example, look at table 3b.  This is claimed as a big win for SpExBERT when comparing the MNLI fine-tuned version.  But if you look at the other rows in the table, SpExBERT is worse than BERT by a *larger margin* than it is better in the MNLI case (contradicting the claimed result from table 2).  And this general trend is seen across the tables - the differences are small and inconsistent, making it look very much like we are just seeing random fluctuations.  This must be controlled for statistically in order to make any valid conclusions.  The one possible exception here seems to be SST.  Those results on the dev set do indeed seem to be more consistent, which is interesting, and hints at the utility of using "positive" and "negative" as natural language descriptions, as the authors claim.  It's not very convincing, however, as the test set difference is very small, and SpExBERT had more opportunities to find a good dev set number, as it had more experiments.
My second major concern is with the experimental set up.  The authors want to claim that using a unified span extraction format yields superior performance to having separate heads.  But there are baselines missing to really demonstrate this claim.  The multiple head setup isn't really evaluated as a baseline in most of the experiments (e.g., using SQuAD / other QA datasets as an intermediate task in table 2, using BERT for any of the QA datasets in table 3).  So, even if the above issue of statistical testing were solved, it would still be very hard to evaluate the claim, as the proper comparisons are not present in the majority of cases.
My main conclusion from reading this paper is that it does not appear to matter what head you use for these particular datasets.  This is an interesting result, though it is not the one that is claimed in the paper.  I think it would be very challenging to extend this approach to a broader set of tasks, however, as the authors suggest towards the end of the paper.  How do the authors propose handling cases where it is not feasible to put all possible outputs in the context?  This includes any generative task (including generative QA) and any kind of structured output (like parsing, tagging, etc.), or a regression task that does not lend itself well to bucketing.
Minor issues:
I would be careful about claiming that you've successfully captured regression in a span extraction format.  You have one regression task, and it's one where the original labels were already bucketed, so the bucketing makes sense.  I am very skeptical that this would actually work for more general regression.
Re the paragraph titled "SpEx-BERT improves on STILTs": Note that SpExBERT requires additional data preprocessing and hand-written templates when switching between tasks, which is not necessary in the method of Phang et al.  There are always tradeoffs.  Neither using separate heads nor doing your additional processing are very hard, so I wouldn't make as big a deal out of this as you do.  If you want to talk about one of the methods using more "human inductive bias", or whatever, the hand-written templates in yours might actually be _more_ "incidental supervision" than a very small difference in model architecture.  But again, the difference here is very small, not worth noting in the paper.


The problem of adversarial examples has shown that modern Neural Network (NN) models could be rather fragile. Among the most promising techniques to solve the problem, one is to require the model to be -adversarially robust (AR); that is, to require the model not to change predicted labels when any given input examples are perturbed within a certain range. However, it is observed that such methods would lead to standard performance degradation, i.e., the degradation on natural examples. In this work, we study the degradation through the regularization perspective. We identify quantities from generalization analysis of NNs; with the identified quantities we empirically find that AR is achieved by regularizing/biasing NNs towards less confident solutions by making the changes in the feature space (induced by changes in the instance space) of most layers smoother uniformly in all directions; so to a certain extent, it prevents sudden change in prediction w.r.t. perturbations. However, the end result of such smoothing concentrates samples around decision boundaries, resulting in less confident solutions, and leads to worse standard performance. Our studies suggest that one might consider ways that build AR into NNs in a gentler way to avoid the problematic regularization.

===== Summary =====
The paper presents new theory to develop understanding about why adversarially robust neural networks show lower test performance compared to their standard counterparts despite being more robust to perturbations in the data. The main hypothesis is that the degradation in performance in adversarially robust networks is due to many samples being concentrated around the decision boundary, which makes the network less confident about its decisions. The paper studies this hypothesis by deriving a bound on the generalization error based on the margin between the samples in the training set and the decision boundary. The paper then presents empirical demonstrations that aim to illustrate the theoretical findings.
Contributions:
1. Derive a generalization bound on the performance of adversarially robust networks  that depends on the margin between training examples and the decision boundary.
2. Provide empirical evaluations that aim to illustrate the theoretical results.
===== Review =====
The problem that the paper addresses is very significant to the robust optimization field and the study of adversarial robustness in neural networks. Thus, I believe that the results could represent a significant contribution. However, due to the way that the information is presented, it is difficult to validate the correctness of the theory and the insights from the paper. Consequently, I consider that the paper should be rejected.
===== Detailed Comments =====
- First, and foremost, the paper should be proof-read for English grammar and writing style. In its current form, it is difficult to follow the main argument of many of the paragraphs. This is exceedingly important because the main subject of the paper is already difficult to digest as is.
- In the related work section, a lot of previous work is referenced without any context about what the contribution of each of those papers is. Each of these papers should be mentioned along with their corresponding contributions. Otherwise, it is difficult to frame the paper within the context of the current literature. Moreover, not providing context makes it difficult to determine which parts of the paper are original and which are the result from previous work.
- The first item in Section 1.1 is difficult to follow because there are many gaps in logic that are left to the reader to fill in. It is reasonable to expect the reader to fill in some of the details, but since the sole purpose of this section is to build intuition about what is about to be presented in the paper, then each step in the explanation should follow as seamlessly as possible.
- The motivation for studying the margins between the training set and the decision boundary is not clear until Section 5.2.1 where it is mentioned that this is a widely used tool in learning theory. This should be presented earlier since not every reader will be completely familiar with learning theory. Moreover, it would also be useful to provide some intuition about how margins relate to the confidence of a classifier.
- After presenting the main result of the paper — Theorem 4.1 — very little intuition is provided about each of the terms in the bounds. It would greatly increase the clarity of the result if each term was explained intuitively, so that the readers can gain the main insight of the paper before reading the proofs. This would also help motivate better the empirical evaluations in the following section.
- The plots in FIgure 3 and Figure 4 are very difficult to understand and unintuitive. For Figure 3, the main reason the plots are difficult to read is because different colors are used for different networks. For Figure 4, it is difficult to understand what is happening because the tallest curves are plotted on top of the shortest ones. Hence, the information from the other curves is mostly lost. This seems like a very minor comment, but this graphs are not very complicated, so they should be easy to understand; yet it takes several minutes to take in what is happening in the graph.
- For the proof of Lemma 4.1it is not clear how to get from Equation (7) to the main result of the lemma even after referencing Theorem 3 of Sokolic et. al. (2017) and Jia et. al. (2019). This could also be my lack of expertise on the topic; however, since the proof is already in the appendix, the proof should not be sparse in the amount of detail that it provides.
===== References =====
Jure Sokolic, Raja Giryes, Guillermo Sapiro, and Miguel R. D. Rodrigues. Robust Large Margin Deep Neural Networks. IEEE Transactions on Signal Processing, 65(16):4265–4280, aug 2017. ISSN 1053-587X. doi: 10.1109/TSP.2017.2708039.
Kui Jia, Shuai Li, Yuxin Wen, Tongliang Liu, and Dacheng Tao. Orthogonal Deep Neural Networks. Technical report, 2019. URL http://arxiv.org/abs/1905.05929.


We introduce switched linear projections for expressing the activity of a neuron in a ReLU-based deep neural network in terms of a single linear projection in the input space. The method works by isolating the active subnetwork, a series of linear transformations, that completely determine the entire computation of the deep network for a given input instance. We also propose that for interpretability it is instructive and meaningful to focus on the patterns that deactive the neurons in the network, which are ignored by the exisiting methods that implicitly track only the active aspect of the network's computation. We introduce a novel interpretability method for the inactive state sensitivity (Insens). Comparison against existing methods shows that Insens is robust (in the presence of noise), complete (in terms of patterns that affect the computation) and a very effective interpretability method for deep neural networks.

The work basically introduced a new way of looking at interpretability; instead of focusing on the source of activations in the network for a given input image, focus on the source of stability (non-active) neurons (in a ReLU network). The work starts by proving (although it is trivial) that in a ReLU (more generally any piece-wise linear) network, for a given input image, there is a locally linear relationship between a given neuron's activation and the image: v= w^T x + b. As the authors correctly mention, focusing on 'w' as the sensitivity analysis is basically the vanilla gradient method. The contribution, however, is focusing on the projection of bias and the introduced notion of 'centre'. With this provided notion, one can focus on the deactivated neurons in the network and how each input pixel is responsible for it. In other words, unlike previous work that focuses on the activation map, the authors correctly refer to the deactivated neurons as another source of the network's prediction.
I'm have reasons for both accepting and rejecting this work.  The work provides a new perspective and asks a very interesting question. The introduced method, although quite simple and trivial, is useful and the authors do a very good job of making valid and reasonable claims about their work's contribution and how it connects to the existing literature. The main drawback of the paper, however, is whether the contributions are enough for this venue. The paper does not convince me that the introduced method would result in better interpretability of deep networks compared to what is already there. Another minor (or for some people in the field major) issue is the experimental setup.  All of the experiments are focused on subjective examples and no objective measure of the introduced method is provided (and the field has many of those objective measures). Providing a few examples of the method in comparison with other methods is not sufficient. Anyhow, the experiment where they prove the usefulness of the method by adding background noise is interesting. I would personally suggest the authors to expand this experiment to testing the method's sanity using the sanity measures provided in previous work: https://arxiv.org/abs/1810.03292 The claims made about the results on smallNORB can be controversial as the authors interpret their method's flipping of importance to be the reality of what's happening in the network and the other method's focus on the edges as false; this is not clear to be true. My score would be subject to change if better experimental results are provided (and the other way round).
A few suggestions and questions:
* One very important issue with the method is that it considers all of the inactive neurons. We know that a substantial percentage of inactive neurons are just dead neurons the stability of which does not matter. How would the method address the issue?
* There definitely needs to be an objective measure of the introduced method's performance compared to previous work.
* The work seems very related to DeepLIFT while there is no mentioning of it.
* I'm not a fan, but adding results on a SOTA ImageNET paper always helps with making the experiments section crisper.
* The authors claim that even small perturbations will change the activation pattern. This is not a small claim and is definitely in need of more evidence.


The over-parameterized models attract much attention in the era of data science and deep learning. It is empirically observed that although these models, e.g. deep neural networks, over-fit the training data, they can still achieve small testing error, and sometimes even outperform traditional algorithms which are designed to avoid over-fitting. The major goal of this work is to sharply quantify the benefit of data interpolation in the context of nearest neighbors (NN) algorithm. Specifically, we consider a class of interpolated weighting schemes and then carefully characterize their asymptotic performances. Our analysis reveals a U-shaped performance curve with respect to the level of data interpolation, and proves that a mild degree of data interpolation strictly improves the prediction accuracy and statistical stability over those of the (un-interpolated) optimal kNN algorithm. This theoretically justifies (predicts) the existence of the second U-shaped curve in the recently discovered double descent phenomenon. Note that our goal in this study is not to promote the use of interpolated-NN method, but to obtain theoretical insights on data interpolation inspired by the aforementioned phenomenon.

This paper is about interpolation schemes in the particular case of the
Nearest Neighbor algorithm. The authors investigate the benet, mainly
theoretical, of the proposed interpolation. They study minimax rates of
the proposed interpolated-NN for both classication and regression. The
statistical stability of the Interpolated-NN is adressed.
The paper is easy to understand and correctly written. Nevertheless,
It is a particular case of ( \Overtting or perfect tting? Risk bounds for
classication and regression rules that interpolate", Belkin, M., Hsu, D.,
and Mitra, P. (2018a)) with an explicit interpolation schemes given by the
euclidien distance power gamma. It appears as an application of the above
paper which brings only few theoretical advantages and not enough to justify,
although intuitive, the choice of these weights. Only few discussions and
no comparison to others bounds (as those in the above paper) of the main
theorem are given. The paper is too much incremental from the papers of
Belkin et al. (2018) and Xing et al. (2018) and the benets of the proposed
interpolation are limited. Furthermore, the empirical performance of the
interpolate-NN is clearly not convincing and show no signicant practical
advantages of the proposed method. As the goal of the paper is clearly
theoretical, the 'real data analysis' part is not necessary in my opinion.


The problem of verifying whether a textual hypothesis holds based on the given evidence, also known as fact verification, plays an important role in the study of natural language understanding and semantic representation. However, existing studies are mainly restricted to dealing with unstructured evidence (e.g., natural language sentences and documents, news, etc), while verification under structured evidence, such as tables, graphs, and databases, remains under-explored. This paper specifically aims to study the fact verification given semi-structured data as evidence. To this end, we construct a large-scale dataset called TabFact with 16k Wikipedia tables as the evidence for 118k human-annotated natural language statements, which are labeled as either ENTAILED or REFUTED. TabFact is challenging since it involves both soft linguistic reasoning and hard symbolic reasoning. To address these reasoning challenges, we design two different models: Table-BERT and Latent Program Algorithm (LPA). Table-BERT leverages the state-of-the-art pre-trained language model to encode the linearized tables and statements into continuous vectors for verification. LPA parses statements into programs and executes them against the tables to obtain the returned binary value for verification. Both methods achieve similar accuracy but still lag far behind human performance. We also perform a comprehensive analysis to demonstrate great future opportunities.

This work proposes the problem of fact verification with semi-structured data source such as tables. Specifically, the authors created a new dataset TabFact and evaluated two baseline models with different variations. They applied two criteria and different rewards for workers to collect two subsets of different levels (“simple” and “complex”). They also applied a negative rewriting strategy to avoid exploitable cues or patterns in the annotations. They evaluated two baselines models: (1) latent program algorithm (LPA), which makes use of simple string match entity linking and systematic search and trains a neural network discriminator, and (2) Table-BERT, which linearize the table into a sequence through concatenation or template, and treat it as a classfication problem. Both showed reasonable accuracy (~68%), but still below human performance (92.1%) on a held out test set.
I would like to see the paper accepted because:
(1) it proposes an interesting task (table fact verification) with a clean dataset, and the experiments evaluated the ability of the current neural network models, such as BERT, or hybrid models, such as the LPA baseline, to perform (symbolic) reasoning;
(2) special care is done to ensure the dataset doesn't contain simple cues or patterns, which is a common pitfall in dataset collection, and the dataset is also validated through two reasonable baseline models.
Some weakness and concerns are:
(1) some error analysis of the baseline models are missing. For example, what types questions are hard/simple for table-BERT and what are hard/simple for LPA, and some comparison between them. This helps point out where the difficulty come from, for example, whether the difficulty is language understanding or symbolic reasoning.
(2) "To focus on statement verification against the table, we do not feed the caption to the model and simply mask the phrases in the statements which links to the caption with placeholders."
I am not sure this is the right thing to do since even the human annotators requires the caption to understand the context, why not also feed the caption into the model?
(3) Although the Figure 2 showed that the higher order operations are indeed used in a majority of questions, which measures the breadth of the reasoning, it is unclear about the depths of the required reasoning, i.e., how many operations / steps are required to achieve the correct answer. It would help if the average number of steps / operations required for answering the questions are shown.
If the above concerns are addressed, I will be willing to raise my score.
Minor comments:
The paper, especially the Appendix, requires some proof reading, for example, I believe the caption for Figure 5 in Appendix A is misplaced.
"... they are explicitly banned bring ..." -> "banned from bringing"
“As illustrated in Figure 6, the title only acts as a placeholder in the statements to make it sound more natural.” -> From the example, it seems the name of the player is kept unchanged in the sentence, which is different from a placeholder.
Suggestions:
I understand this might require some works, but it would be really helpful to add more comments and maybe examples for the functions shown in Figure 5 (you might need to split the table into two pages or have another table for examples), so that it can be used by works that follows the LPA approach.
“During the annotation, the workers are explicitly guided to modify the words, phrases or sentence structures but retain the sentence style/length to prevent from artificial cues”
Avoiding simple cues or patterns are important, so it will be good if more details can be shared (for example, the instructions/guidelines you showed to the workers).
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Post rebuttal update:
Thanks for the update to the paper. I think this work provides a good dataset and some reasonable baselines, thus should be accepted.
However, I am still a bit concerned about the categorization of questions and the analysis on reasoning depth, because they are all based on the programs generated by LPA, while systematic search's recall is just 77% and the programs potentially contains a lot of spurious ones. So the categorization of the questions in Figure 11 and the number of reasoning steps in Figure 12 has to be taken with a grain of salt. It is worth annotating a few hundred, say 100-300 questions, manually with the ground truth programs for question distribution analysis or reasoning depth analysis, and confirm the numbers estimated using programs from LPA. Those manually annotated examples would also be a great addition to the dataset to aid the researchers for better analysis. A good example is the WikiTableQuestions dataset https://github.com/ppasupat/WikiTableQuestions/releases, which contains 300 manually annotated examples (annotated-all.examples), and they are used to analyze the distribution of the questions in the paper.


Generative Adversarial Networks (GANs) are known to be difficult to train, despite considerable research effort. Several regularization techniques for stabilizing training have been proposed, but they introduce non-trivial computational overheads and interact poorly with existing techniques like spectral normalization. In this work, we propose a simple, effective training stabilizer based on the notion of consistency regularization-a popular technique in the semi-supervised learning literature. In particular, we augment data passing into the GAN discriminator and penalize the sensitivity of the discriminator to these augmentations. We conduct a series of experiments to demonstrate that consistency regularization works effectively with spectral normalization and various GAN architectures, loss functions and optimizer settings. Our method achieves the best FID scores for unconditional image generation compared to other regularization methods on CIFAR-10 and CelebA. Moreover, Our consistency regularized GAN (CR-GAN) improves stateof-the-art FID scores for conditional generation from 14.73 to 11.48 on CIFAR-10 and from 8.73 to 6.66 on ImageNet-2012.

This paper proposes to use Consistency Regularization for training GANs, a technique known to work well in unsupervised learning. The technique consists in applying a transformation to real images and enforcing that the features of the discriminator between the transformed inputs and the original inputs are similar. The author show that using this technique enables them to improve the performance of a standard GAN significantly on CIFAR10. They also carry an ablation study studying the influence of the different part of the proposed technique.
Overall I'm in favor of accepting this paper. The paper is well written, with convincing experiments and an interesting ablation study. However I have several minor issues that I think could greatly improve the paper if addressed.
Minor comments:
- I think an idea which is somewhat related but hasn't been mentioned in the paper, is the idea of adding noise to the input when training GANs [1]. I think this is worth mentioning in the related work.
- Related to the previous point, why penalizing features and not directly output ? What about also trying to classify the transformed images as real ? Also you say that penalizing the last layer, I think including the influence of m (eq 2) in the ablation study would be interesting.
- The authors provide some measure of standard deviation on some experiments but not on all of them. It would be nice to systematically report the standard deviation for every experiments.
- In figure 1 the author make the hypothesis that the discriminator will output very different score to images semantically close together. Did the author verify this hypothesis experimentally ?
- Also why penalizing only the samples from the real distribution and not from the generator ? have you tried both ?
- When the test accuracy of the discriminator is low, it could also be that the discriminator is under-fitting, it would be nice to also report the train accuracy for the discriminator.
- I think the conclusion about the effect of consistency regularization vs data augmentation is a bit vague since consistency regularization has no sense without data-augmentation.
- It's quite interesting but also disappointing that combining transformations doesn't give that much of an improvement. Do the author have any intuition why this is the case ? and why learning them one after the other would work ?
References:
[1] Arjovsky and Bottou. "Towards Principled Methods for Training Generative Adversarial Networks." (ICLR 2017)


Presence of bias and confounding effects is inarguably one of the most critical challenges in machine learning applications that has alluded to pivotal debates in the recent years. Such challenges range from spurious associations of confounding variables in medical studies to the bias of race in gender or face recognition systems. One solution is to enhance datasets and organize them such that they do not reflect biases, which is a cumbersome and intensive task. The alternative is to make use of available data and build models considering these biases. Traditional statistical methods apply straightforward techniques such as residualization or stratification to precomputed features to account for confounding variables. However, these techniques are generally not suitable for end-to-end deep learning methods. In this paper, we propose a method based on the adversarial training strategy to learn discriminative features unbiased and invariant to the confounder(s). This is enabled by incorporating a new adversarial loss function that encourages a vanished correlation between the bias and learned features. We apply our method to synthetic data, medical images, and a gender classification (Gender Shades Pilot Parliaments Benchmark) dataset. Our results show that the learned features by our method not only result in superior prediction performance but also are uncorrelated with the bias or confounder variables. The code is available at http://blinded_for_review/.

The authors propose a method based on GAN  to classify data while automatically removing confounding effects during training, in order to obtain a classifier whose features are not biased by any confounding effect. The proposed idea is based on the extension of classical classification architectures to account for bias prediction. In practice, the parameters of the feature extraction component are updated to solve both bias prediction and the desired classification problem in adversarial fashion. Pearson’s correlation was chosen as a metric for bias.
The paper is interesting and addresses an important problem for the application of machine learning methods in several real context. The feeling is however that the paper should have better explored the implication of the proposed model of bias, and better investigated the relationship with simpler approaches relying on similar hypothesis.
Here are my main comments for this work:
- Why Pearson’s correlation should be a reliable metric to quantify bias? This metric is insensitive to affine scaling of the data, which is a quite common form of bias (for example in medical images).
- The authors should have investigated the relationship between the proposed method and bias removal through canonical correlation analysis (CCA), and perhaps its non-linear variants. At the end this is what their network is doing, although in an end-to-end fashion. Using the CCA projections in the latent space for classification would be the closest approach to the state of the art for bias removal in statistical analysis (residual analysis).
- The experimental setting illustrated in 4.1 is not clear. In which sense \sigma_A is a common factor for the two groups? Why the theoretical maximum classification accuracy is 90%? Figure 2 is not clear either and doesn’t help understanding the structure of the generated data (e.g. axis labels missing, colorbars units not specified).
- It is not clear why authors quantify the correlation in the latent space with tSNE projections. tSNE is highly sensitive to the choice of parameters and it would be important to ensure that it was a “fair competition” between all the methods, when showing the results of the dimensionality reduction. This is another modelling step relying on specific assumptions which decreases interpretability of the findings. The authors also proposed to assess the decorrelation of the estimated features throughout the different methods by measuring the squared distance correlation. Naturally, their method is the one which exhibits the best performances using this metric. However, this way of assessing the decorrelation of the features with the biases is unfair to the other methods, as in their case they specifically built their model to avoid statistical correlation between features and biases.
- Experiment 4.2 has some controversial aspects, as the bias correction is performed on the control population only, while the model is trained on the entire population. I understand the fact that confounding can be estimated only on healthy conditions, however in this case the network is going to be biased by the control group by construction. The effect of such a choice in the end-to-end optimisation scheme is really not clear.
- We also observe that the results of the baseline CNN are very close to the BR-Net. The main difference lies in the fact that the CNN tends to have an unbalanced classification between true negatives and true positives. However, what would happen if we corrected for age before applying the CNN ?
- In the case where the performances of the CNN would be improved, this last question would raise another one. Indeed, if I already know the confounding effects I want to correct for, why wouldn’t I correct them beforehand in order to avoid to train a complex GAN, which leads to more instability during training. This aspect points to the limit of having an online bias-correction (at least for the medical data case).


Training an agent to solve control tasks directly from high-dimensional images with model-free reinforcement learning (RL) has proven difficult. The agent needs to learn a latent representation together with a control policy to perform the task. Fitting a high-capacity encoder using a scarce reward signal is not only sample inefficient, but also prone to suboptimal convergence. Two ways to improve sample efficiency are to extract relevant features for the task and use off-policy algorithms. We dissect various approaches of learning good latent features, and conclude that the image reconstruction loss is the essential ingredient that enables efficient and stable representation learning in image-based RL. Following these findings, we devise an off-policy actor-critic algorithm with an auxiliary decoder that trains end-to-end and matches state-of-the-art performance across both model-free and model-based algorithms on many challenging control tasks. We release our code to encourage future research on image-based RL 1 .

The paper aims to tackle the problem of improving sample efficiency of model-free, off-policy reinforcement learning in an image-based environment. They do so by taking SAC and adding a deterministic autoencoder, trained end-to-end with the actor and critic, with the actor and critic trained on top of the learned latent space z. They call this SAC-AE. Experiments in the DeepMind control suite demonstrate that the result models train much faster than SAC directly on the pixels, in some cases reaching close to the performance of SAC on raw state. Ablation studies demonstrate their approach is most stable with deterministic autoencoders proposed by (Ghosh et al, 2019), rather than the beta-VAE autoencoder proposed in (Nair et al, 2018), end-to-end learning of the autoencoder gives improved performance, and the encoder transfers to some similar tasks.
I thought the paper was written well, and its experiments were done quite carefully, but it was lacking on the novelty front. At a high level, the paper has many similarities with the UNREAL paper (Jaderberg et al, 2017), which is acknowledged in the related work. This paper says it differs from UNREAL because they use an off-policy algorithm, and that UNREAL's auxiliary tasks are based off real-world inductive priors.
I don't see the off-policy distinction as very relevant, because in the end, both UNREAL and SAC-AE are actor-critic algorithms (using A3C and SAC respectively). The way that SAC is used in the paper always collects data in a near on-policy manner, and UNREAL includes experience replay from a replay buffer, which introduces some off-policy nature to UNREAL as well. Therefore this doesn't feel like a strong argument.
Furthermore, although some of the auxiliary tasks in UNREAL are based off human intuition for what makes sense in those environments, they also include task-agnostic auxiliary tasks: reward prediction and pixel-level control. These do not depend on real-world inductive priors, and are shown to improve performance.
Overall, this doesn't feel like a strong enough contribution for ICLR.
More specific comments:
* Section 6.1 examines the representation power of the encoder by reconstructing proprioceptive state from the encoder. I am not sure the comparison between SAC+AE and SAC is particularly meaningful here. The predictors are learned on top of the encoder output, and in SAC+AE we would expect task information to be encoded in the learned z. But in baseline SAC, there is no reason to expect this to be true - task information is more likely to be distributed across the entire network architecture. The case for SAC+AE seems much stronger from the reward curves, rather than these plots.
* The paper argues that their approach is stable and sample-efficient, but when looking at the reward curves, it looked about as stable as SAC. Figure 3 (where they do not train the VAE end-to-end in the red curve) has a similar story. This makes me believe that any claims of added stability are more thanks to SAC, rather than proposed methods.
Edit: I would like to clarify that the rating system only provides a 3 for Weak Reject and 6 for Weak Accept. On a 1-10 scale I would rate this as a 5, I feel it is closer to Weak Accept than Weak Reject.
Edit 2: I've read the other author's comments. I'm not particularly convinced by the case for novelty, but I didn't realize that UNREAL's replay buffer was only 2k transitions instead of 1 million transitions. On reflection, I believe the main contribution here is showing that deterministic autoencoders are more reliable than stochastic ones for the RL setting, and this isn't the biggest contribution, but it's enough to make me update to weak accept.