Posts in category: CMU

Figure 1: Modeled recommendation cycle. We demonstrate how enforcing group-fairness in every recommendation slate separately does not necessarily promote equity in second order variables of interest like network size.

Connection recommendation is at the heart of user experience in many online social networks. Given a prompt such as ‘People you may know’, connection recommender systems suggest a list of users, and the recipient of the recommendation decides which of the users to connect with. In some instances, connection recommendations can account for more than 50% of the social network graph [1]. Depending on the platform, being connected to the right people is tied to important advantages such as job opportunities or increased visibility. While this makes it imperative to treat users fairly, it is far from obvious how fairness can be enforced or what it even means to have a ‘fair’ system in this scenario. In fact, when enforcing fairness in dynamic systems like this, we are often interested in second-order variables while interventions target equity in single steps [2]. In connection recommendation, this generally means enforcing some sort of parity condition in each recommendation slate, e.g. equal exposure of female and male users for every query, while simultaneously hoping that this will promote more equitable network sizes in the long run. In our work, we demonstrate how this approach can fail and common statistical notions of recommendation fairness do not ensure equity of network sizes in the long run. In fact, we see that fairness interventions are not even sufficient to mitigate the amplification of existing biases. We reach these conclusions based on an extensive simulation study supplemented by theoretical limit analyses. In the following, we focus on a discussion of empirical results and refer to the full paper for theoretical derivations.

Recommendation procedure

The assumed recommendation cycle is depicted in Figure 1. We briefly summarize the involved steps and give more detail on the most important components in the following sections. On the left in the flowchart, a user queries a connection recommendation, for example, by loading the ‘People You may Know’ page on the platform’s website. The system then computes relevance scores between the user who is seeking recommendations – which we will refer to as the source user – and other previously unconnected users who will be referred to as the destination users. Based on these relevance scores, we derive a ranking of destination users subject to fairness constraints and display a list of possible connections to the source user. After new connections have been made, the cycle repeats.

Fairness constrained probabilistic ranking framework

For each recommendation query, the system obtains a set of relevance scores and derives a probabilistic ranking. This probabilistic ranking takes the form of a matrix (P_{s,d}^q) where the entry in the (d)th row and (r)th column denotes the probability of displaying member (d) in slot (r) of the recommendation list. The probabilities are selected to maximize the expected utility for the source user which is common practice in the recommendation literature [3].

More formally, we denote the source member as (s) and the destination member as (d). (q) denotes a query for an ordered list of (m) destination members and (u_{s,d}^q) the relevance score of (s) and (d) under query (q). We model a form of position bias by discounting the expected attention a recommended user receives based on how far down the list the recommendation, i.e. we define the exposure of slot (r) as (v(r)=1/log(r+1)). Given these quantities, the optimization problem for query (q) can be written as

$$argmax_{P}u_s^TP^q_sv$$

$$text{s.t.} sum_{i=1}^nP_s^q(d,i)leq 1 text{ for all } din[D_q],$$

$$sum_{i=1}^{D_q}P_s^q(i,r)=1text{ for all }rin[m],$$

$$0leq P_s^q(i,r)leq 1text{ for all }iin[D_q],jin[m].$$

The constraints in this problem ensure that each slot has a recommended user and each user can be recommended at most once in a given list. We explore two types of fairness constraints to add to this problem. First, we consider demographic parity of exposure which is a commonly suggested form of fairness in recommendations. It requires that groups receive expected exposure proportional to their population shares, i.e. for groups (G_0) and (G_1)

$$frac{1}{vert G_0vert}sum_{din G_0}sum_{r=1}^mP_s^q(d,r)v_r=frac{1}{vert G_1vert}sum_{din G_1}sum_{r=1}^mP_s^q(d,r)v_r.$$

Assume a setting in which there is no position bias (v), the population is split into 60% majority group and 40% minority group, and each recommendation list has 10 slots. In this setting, demographic parity of exposure requires (in expectation) that 6 of the recommended members belong to the majority group while 4 belong to the minority group in every recommendation list.

Second, we explore a dynamic parity of utility constraint. As opposed to the first constraint, this fairness measure does not only consider the exposure of groups but also the total utility that can be expected from the exposure, i.e. for two groups (G_0) and (G_1),

$$frac{1}{vert G_0vert}sum_{din G_0}u_{s,d}^qsum_{r=1}^mP_s^q(d,r)v_r=frac{1}{vert G_1vert}sum_{din G_1}u_{s,d}^qsum_{r=1}^mP_s^q(d,r)v_r.$$

On a high level, the constraint requires that the sum of relevance scores across groups is proportional to the population share of groups discounted by the exposure limitations posed by position bias. To understand what this means, let us consider the example setting from before with no position bias, a 60%/40% group split, and recommendation lists with 10 slots. Assume that all destination members of the majority group have a relevance score of 0.12 while all destination members of the minority group have a fixed relevance of 0.08. The probabilistic ranking fulfills dynamic parity of utility if the expected group-split in the recommendation list is 50%/50% because (0.5 * 10 * 0.12 = 0.6) and (0.5 * 10 * 0.08 = 0.4).

How do we model relevance scores?

Relevance scores usually model the probability of connection if recommended, a measure of downstream engagement or some mixture of the two. The exact models employed by social media platforms are usually proprietary, but we opt for a synthetic model in the form of logistic regression in three realistic features [4,5]. Assuming our prediction target is the probability of connection, we first use the source member’s network size. This is based on the assumption that users with larger networks are more likely to be proactive in connection forming as they are generally more active on the platform. Next, we assume that users with more common connections are more likely to connect. The common connections feature is rooted in social network literature where it is commonly referred to as triadic closure [e.g. 6,7]. Lastly, we make the assumption that users with similarities such as demographics, interests, education, workplace, etc. are more likely to connect. This follows the observation that individuals like to be connected to similar individuals commonly referred to as homophily in sociology and other social sciences [e.g. 8].

The main simulation procedure makes use of the relevance scoring model for user pairs as follows. We assume a fixed-size graph of evolving connections with two groups of members. 65% of members belong to an initially more connected majority group. First, we assume a ground truth model for matching scores by imposing ground-truth parameter values in the presented logistic regression function. We use this function to simulate a data set of recommendations and formed connections and use the synthetic data to train a logistic regression matching scores model. 

Simulation procedure

We sample covariate vectors from group-dependent distributions for each member in the graph. These vectors will be used to compute the similarity between members which we set as negative Euclidean distance. The connections in the graph are initialized with a stochastic block model in which user pairs in the majority group are slightly more likely to connect than user pairs in the minority group and user pairs who belong to the same group are slightly more likely to connect than user pairs who belong to opposite groups. This models the initial advantage for majority group members we would expect to see in practice and accounts for homophily preferences. Given the initial specifications, we go through the previously described recommendation cycle for 2,500 timesteps and keep track of key fairness and performance metrics. Following our reasoning from the scoring model, the frequency with which users seek out recommendations is based on exponential waiting times with a mean depending on the current network size of a user. The whole simulation procedure is repeated with each fairness intervention separately and without intervention for comparison. Results are averaged over 10 runs. 

Rich-gets-richer in groups

Figure 2 depicts the performance of all 3 intervention types. With no intervention – which is displayed in red in the graphs – we observe that the gap in average network sizes between groups drastically increases over time. In fact, our results reveal a group-wise rich-get-richer effect in which network sizes tend to a power law distribution with a lower mode in the minority population. Members whose networks are in the tail of the distribution tend to be the members who had large networks, as compared to their peers, to begin with. These observations are in line with previous findings on rich-get-richer phenomena under homophily.

Demographic parity of exposure intervention

We now move to the results for the demographic parity of exposure intervention. First, we can see that the majority group share of exposure in recommendations is down to 66.3% which suggests that the intervention is working. However, as we can see in panels (a) and (b), the gap in average network sizes is still increasing over time. Why is this the case? First, majority group members seek out recommendations more frequently based on their already larger network sizes and activity levels. This leads to more connections formed with majority group members at the source side of the recommendation while our intervention can only target the destination side. Second, majority group members have higher ranking scores and are thus more likely to be invited for connection even if both groups are exposed equally. Consider the following example recommendation:

Here, both female and male users have the same exposure – we will ignore position bias for this example. However, the probability of connection and its proxy – the matching score – are much lower for women than for men essentially leading to fewer new connections for women than for men. While the intervention suggests recommendations are made fairly, this does not align with our intuitive goal of more equitable network sizes.

Dynamic parity of utility intervention

Some of the problems with the demographic parity of exposure intervention are addressed by the dynamic parity of utility intervention. We see that the majority group share of destination members of new connections is down to 65.4% as desired. Yet, even with this type of constraint, panels (a) and (b) show that the gap in average network sizes is still increasing over time. Like in the previous case, one of the reasons for this is that majority group members seek out recommendations more frequently. In addition, our analysis reveals that source members from the majority group generally form more connections per recommendation query leading to the increased share in panel (d). To understand why this is the case, consider the following example:

In the first row, a majority group member – here displayed as male – receives recommendations. In the second row, a minority group member – here female – receives recommendations. In both recommendation lists the dynamic parity of utility constraint is fulfilled, but the male source member receives more overall utility from the query because the constraint can only target fairness within a list and not in between different sets of recommendations.

Summary of findings

Let us summarize the key findings. Our study shows that unconstrained connection recommendation leads to a group-wise rich-get-richer effect. Enforcing demographic parity of exposure or dynamic parity of utility between groups, which are commonly suggested remedies against demographic bias in recommender systems, leads to less bias amplification but is not sufficient in order to mitigate an increase in the disparities in network sizes over time. As shown in the full paper, theoretical limit analysis shows that dynamic parity of utility would be the optimal intervention if there was no source-side bias. Yet, this is an unrealistic assumption in practice.

Overall, the common practice of measuring fairness in recommender systems in a one-shot or time-aggregate static manner can lead to an illusion of fairness and deployment of fairness-enhancing algorithms with unforeseen consequences. Connection recommendation operates on a dynamical system that needs to be taken into account to ensure equitable outcomes in the long run.

The full paper is published in the proceedings of the AAAI / ACM conference on Artificial Intelligence, Ethics, and Society (AIES 2022). A preprint is available here.

References

[1] LinkedIn PYMK: https://engineering.linkedin.com/teams/data/artificial-intelligence/people-you-may-know [Online; accessed 7/6/22] [2] Lydia T. Liu, Sarah Dean, Esther Rolf, Max Simchowitz, and Moritz Hardt. Delayed impact of fair machine learning. In Proceedings of the 35th International Conference on Machine Learning (ICLM 2018), 2018.

[3] Deepak K. Agarwal and Bee-Chung Chen. 2016. Statistical Methods for Recommender Systems. Cambridge University Press.

[4] LinkedIn PYMK: https://engineering.linkedin.com/teams/data/artificial-intelligence/people-you-may-know [Online; accessed 7/6/22] [5] Facebook PYMK: https://www.facebook.com/help/336320879782850 [Online; accessed 7/6/22] [6] Kossinets, G., & Watts, D. J. (2006). Empirical Analysis of an Evolving Social Network. In Science (Vol. 311, Issue 5757, pp. 88–90). American Association for the Advancement of Science (AAAS).

[7] David Liben-Nowell and Jon Kleinberg. 2007. The link-prediction problem for social networks. J. Am. Soc. Inf. Sci. Technol. 58, 7 (May 2007), 1019–1031.

[8] McPherson, M., Smith-Lovin, L., & Cook, J. M. (2001). Birds of a Feather: Homophily in Social Networks. In Annual Review of Sociology (Vol. 27, Issue 1, pp. 415–444). Annual Reviews.

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Figure 1. Our implementation of recurrent model-free RL outperforms the on-policy version (PPO/A2C-GRU), and a recent model-based POMDP algorithm (VRM) on most tasks of a POMDP benchmark where VRM was evaluated in their paper.

While algorithms for decision-making typically focus on relatively easy problems where everything is known, most realistic problems involve noise and incomplete information. Complex algorithms have been proposed to tackle these complex problems, but there’s a simple approach that (in theory) works on both the easy and the complex problems. We show how to make this simple approach work in practice.

Why POMDPs?

Decision-making tasks in the real world are messy, with noise, occlusions, and uncertainty that are typically missing from their canonical problem formulation as a Markov decision process (MDP; Bellman, 1957). In contrast, Partially Observable MDPs (POMDPs; Åström, 1965) can capture the uncertainty in the states, rewards, and dynamics. Such uncertainty arises in applications such as robotics, healthcare, NLP and finance.

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Apart from being realistic, POMDPs are a general framework that contains many subareas in RL, including:

• Meta-RL (Schmidhuber, 1987, Thrun and Pratt, 2012, Duan et al., 2016, Wang et al., 2017): assume the hidden states (task variables) of a POMDP do not vary through time. For example, a robot has to discover which goal state it is supposed to reach.
• Robust RL (Bagnell et al., 2001, Rajeswaran et al., 2017, Pinto et al., 2017, Pattanaik et al., 2018): maximizing the worst-case returns over tasks. For example, the motor friction of a robot is unknown, and the goal is to learn a control policy that works for the worst-case choice of motor friction.
• Generalization in RL (Whiteson et al., 2011, Zhang et al., 2018, Packer et al., 2018, Cobbe et al., 2019): maximizing the returns over unseen tasks during testing.
• Temporal credit assignment (Sutton, 1984, Hung et al., 2018, Arjona-Medina et al., 2019, Ren et al., 2021): assume reward function is history-dependent.

What is recurrent model-free RL?

Solving POMDPs is hard because the agent needs to learn two tasks simultaneously: inference and control. Inference aims to infer the posterior over current states conditioned on history. Control aims to perform RL / planning algorithms on the inferred state space. While prior methods typically decouple the two jobs with separate models, deep learning, provides us with a general and simple baseline: combine an off-the-shelf RL algorithm with a recurrent neural network (RNN; e.g., LSTM (Hochreiter & Schmidhuber, 1997) and GRU (Chung et al., 2014)).

By backpropagating the gradients from policy loss, RNNs make it possible to process sequences (histories in POMDPs) and learn implicit inference on the state space for control. We refer to it as recurrent model-free RL. Fig. 2 presents our design, where actor and critic networks each have an RNN as the history encoder.

Recurrent model-free RL has many merits at first glance:

• Conceptually simple. The policy purely learns from rewards, without extra objectives.
• Easy to implement. Practitioners can just change several lines of code from model-free RL.
• Expressive in theory. RNNs have been shown as universal function approximators (Siegelmann & Sontag, 1995, Schäfer & Zimmermann, 2006) and, thus recurrent model-free RL can (approximately) express any memory-based policies.

Due to its simplicity and expressivity, there is rich literature (Schmidhuber, 1991, Bakker, 2001, Wierstra et al., 2007, Heess et al., 2015, Hausknecht & Stone, 2015) on studying different RL algorithms and RNN architectures of recurrent model-free RL. However, prior work has shown that it often fails in practice with poor or unstable performance (Igl et al., 2018, Hung et al., 2018, Packer et al., 2018, Rakelly et al., 2019, Zintgraf et al., 2020, Han et al., 2020, Zhang et al., 2021, Raposo et al., 2021), with only a few exceptions (Yu et al., 2019, Fakoor et al., 2020).

Motivated by the poor performance of this simple baseline, prior work has proposed more sophisticated methods. Some introduce model-based objectives that explicitly learn inference, while others incorporate the assumptions used in the subarea of POMDPs as inductive bias. Both achieve good results on a range of respective tasks, although the model-based methods may have staleness issue in the belief states stored in the replay buffer, and the specialized methods require more assumptions than recurrent model-free RL (e.g., meta-RL methods normally assumes the hidden variable is constant within a single episode).

How to train recurrent model-free RL?

In this work, we found that recurrent model-Free RL is not fatally failed, but just needed to be implemented differently, with differences including:

1. Separating the RNNs in actor and critic networks. Un-sharing the weights can prevent gradient explosion, and can be the difference between the algorithm learning nothing and solving the task almost perfectly.
2. Using an off-policy RL algorithm to improve sample efficiency. Using, say, TD3 instead of PPO greatly improves sample efficiency.
3. Tuning the RNN context length. We found that the RNN architectures (LSTM and GRU) do not matter much, but the RNN context length (the length of the sequence fed into the RL algorithm), is crucial and depends on the task. We suggest choosing a medium length as a start.

Properly tuned, the simple baseline outperforms alternatives on many POMDPs

With these changes, our implementation of recurrent model-free RL is at least on par with (if not much better than) prior methods, on the tasks those prior methods were designed to solve. While prior methods are typically designed to solve special cases of POMDPs, recurrent model-free RL applies to all types of POMDPs.

Our first comparison looks at meta-RL tasks, which are usually approached by methods that decouple the task inference and reward maximization steps (Rakelly et al., 2019, Zintgraf et al., 2020). When comparing these prototypical methods (on-policy variBAD (Zintgraf et al., 2020) and off-policy variBAD (Dorfman et al., 2020)), we find that our recurrent model-free approach can often perform at least on par with them. These results (Fig. 3, 4) suggest that disentangling inference and control may be not that necessary in many tasks.

Next, we move on to the robust RL setting, which is mostly solved by algorithms that explicitly maximize the worst returns (Rajeswaran et al., 2017, Mankowitz et al., 2020). By comparing one recent robust RL algorithm (Jiang et al., 2021), we find that our recurrent model-free approach performs better in all the tasks. The results (Fig. 5) indicate that with the power of implicit task inference with RNNs, we can improve both average and worst returns.

Then we explore the generalization in RL, where people have different kinds of specialized methods, including policy regularization (Farebrother et al., 2018) and data augmentation (Lee et al., 2020). Here we choose a popular benchmark SunBlaze (Packer et al., 2018) which provides a specialized baseline EPOpt-PPO-FF (Rajeswaran et al., 2017). The results (Fig. 6) show that despite not explicitly enhancing generalization, our recurrent model-free approach can perform better in extrapolation than the baseline. This suggests that the task inference learned by RNN is generalizable.

Finally, we study the temporal credit assignment domain where the methods for solving it usually involve reward decomposition/redistribution (Liu et al., 2019, Hung et al., 2018). Here, we choose a recent specialized method IMPALA+SR (Raposo et al., 2021), and evaluate our method on their benchmark with pixel-based discrete control and sparse rewards. Despite being unaware of the reward structure and not performing credit assignment explicitly, our recurrent model-free approach can perform better. The results (Fig. 7) indicate that recurrent policies can effectively cope with sparse rewards, perhaps better than previously expected.

Conclusion

In a sense, our finding can be interpreted as echoing the motivation for deep learning: we can achieve better results by reducing a method to a single differentiable architecture, optimized end-to-end with a single loss. This is exciting because RL systems often involve many interconnected parts (e.g., feature extracting, model learning, value estimation) trained with different objectives, but perhaps they might be replaced by end-to-end approaches if equipped with sufficiently expressive architectures.

We have open-sourced the code on GitHub to support reproducibility and to help future work develop better POMDP algorithms. Please see our project site for the paper and our ICML 2022 presentation.

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Over the past decade, machine learning (ML) has grown rapidly in both popularity and complexity. Driven by advances in deep neural networks, ML is now being applied far beyond its traditional domains like computer vision and text processing, with applications in areas as diverse as solving partial differential equations (PDEs), tracking credit card fraud, and predicting medical conditions from gene sequences. However, progress in such areas has often required expert-driven development of complex neural network architectures, expensive hyperparameter tuning, or both. Given that such resource intensive iteration is expensive and inaccessible to most practitioners, AutoML has emerged with an overarching goal of enabling any team of ML developers to deploy ML on arbitrary new tasks. Here we ask about the current status of AutoML, namely: can available AutoML tools quickly and painlessly attain near-expert performance on diverse learning tasks?

This blog post is dedicated to two recent but related efforts that measure the field’s current effectiveness at achieving this goal: NAS-Bench-360 and the AutoML Decathlon. The first is a benchmark suite focusing on the burgeoning field of neural architecture search (NAS), which seeks to automate the development of neural network models. With evaluations on ten diverse tasks—including a precomputed tabular benchmark on three of them—NAS-Bench-360 is the first NAS testbed that goes beyond traditional AI domains such as vision, text, and audio signals. Specifically, the 10 tasks vary in their domain (including image, finance time series, audio, and natural sciences), problem type (including regression, single-label, and multi-label classification), and scale (ranging from several thousands to hundreds of thousands of observations).

The second is a NeurIPS 2022 competition (which we are soft-launching today!) that builds on our NAS-Bench-360 work yet has a broader vision of understanding what is truly the best approach for a practitioner to take when faced with a modern ML problem.  During the public development phase of the competition we will release a set of diverse tasks that will be representative of (but distinct from) the final set of test tasks on which evaluation will be performed. Unlike most past competitions in the AutoML community, competitors in the AutoML Decathlon are free (and in fact encouraged) to consider a wide range of approaches from traditional hyperparameter optimization and ensembling methods to modern techniques such as NAS and large-scale transfer learning.

You can learn more about getting involved with either of these efforts at the bottom of this post.

NAS-Bench-360: A NAS Benchmark for diverse tasks

NAS-Bench-360 is a benchmark suite consisting of ten ML tasks that we developed jointly with Renbo Tu, Nick Roberts, Junhong Shen, and Fred Sala. These tasks represent a diverse set of signals, including various kinds of imaging sources, simulation data, genomic data, and more. At the same time, we constrain all tasks to be amenable to modern NAS search spaces, i.e. we do not include tabular or graph-based data, thus allowing for the application of most NAS methods. Our evaluation on NAS-Bench-360 is thus a robustness test that checks whether the massive amount of largely computer vision-driven progress in the field of NAS is actually indicative of wider success of AutoML across a variety of applications, data types, and tasks. More importantly, the benchmark will serve as a useful tool to develop and evaluate new, better methods for NAS.

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So can AutoML tools—specifically NAS methods—quickly and painlessly attain near-expert performance on NAS-Bench-360? In positive news, searching over a large search space such as DARTS using a state-of-the-art algorithm such as GAEA does yield models that outperform available expert architectures on half of the tasks, in addition to consistently beating perennial Kaggle favorite XGBoost and a recent attempt at a general-purpose architecture, Perceiver IO. On the other hand it fails catastrophically on several tasks, doing little better than a simple baseline, namely a tuned Wide ResNet (Figure 1, left panel). Indeed, despite being developed on CIFAR-10 it does surprisingly poorly on 2D classification tasks from the medical and audio domains. Furthermore, in a resource-constrained setting where AutoML methods are not given much more time than running a single architecture, the leading NAS method DenseNAS does worse than an untuned Wide ResNet (Figure 1, right panel).

Our evaluation of modern NAS methods on NAS-Bench-360 demonstrates the need for such a benchmark and a lack of robustness in the field. NAS-Bench-360 is also useful for understanding past and future search spaces and algorithms, specifically whether current beliefs about NAS extend to diverse tasks. For example, Figure 2 shows that high-performing architectures transfer well between vision tasks—a quality used extensively in NAS research—but not between diverse tasks. Other examples of scientific uses of NAS-Bench-360—such as one investigating a recent paper on operation redundancy—are provided in our paper and in a recent ICLR 2022 blog post on zero-cost proxies. We also expect NAS-Bench-360 to be used for the development of new NAS methods; to further this, for two of the datasets we provide precomputed models for all architectures in the NAS-Bench-201 search space; together with existing CIFAR-100 precompute results this means three NAS-Bench-360 datasets have precomputed tabular benchmarks to accelerate search algorithm development. 

The AutoML Decathlon: A competition focused on diverse tasks and methods

Our goal in releasing NAS-Bench-360 is to spur the development of NAS methods that work well on diverse tasks. However, given the mixed performance of NAS on this benchmark, there remains a question of whether automatic architecture design should even be the focus of AutoML research more broadly. Building on our efforts from NAS-Bench-360, a group of researchers at CMU, Hewlett Packard Enterprise (HPE), Wisconsin-Madison, and Morgan Stanley are organizing the AutoML Decathlon competition at NeurIPS 2022 precisely to ask the following broader question: what automated technique(s) are best for diverse tasks?

This competition is designed to address two gaps between research and practice:

1. Lack of task diversity. The field of NAS is no exception here, as the vast majority of recent AutoML benchmarking and competition efforts have focused on computer vision or other well studied tasks in speech and language processing. Evaluating AutoML methods on such well-studied tasks does not give a good indication of their utility on more far-afield applications.
2. Siloed methodological development. Many developments in AutoML narrowly focus on particular techniques rather than the downstream benefits to the end user. A practitioner with a specific ML task ultimately cares about the quality of the resulting model (in terms of accuracy and other non-accuracy metrics), as opposed to the underlying technical details of the procedure yielding this model, e.g., whether the model is the result of a weight-sharing NAS method, a fine-tuned large model,  a more classical non-deep learning AutoML technique, or some other automated procedure.

By designing our competition in a practitioner-centric fashion and accounting for the two aforementioned gaps, our competition aims to spur innovation in AutoML with results that are directly transferable to ML practitioners. We envision that the results of our competition will provide novel empirical insights into several open practical and scientific questions, including:

• Given the growing methodological diversity of (Auto)ML approaches, what methods should I consider as a practitioner in 2022?  
• How do leading NAS methods compare to the increasingly popular pre-training/fine-tuning paradigm?
• How do either of these more modern approaches compare to classical AutoML approaches or to standard baselines such as XGBoost or a tuned ResNet?
• Should I consider using any AutoML procedure given that I’m working on a specific scientific, technological, or industrial problem that seemingly differs drastically from well-studied tasks in computer vision and NLP?  
• Given a reasonable computational budget, can any AutoML approach (whether classical or more modern) consistently outperform bespoke models that were hand-crafted by either domain experts and/or ML experts?

We note that while AutoML is not a new research area, we view our competition as being particularly timely given (1) rapid growth of ML task diversity, (2) progress in ML model development, and (3) acceleration in the scale of both datasets and available compute resources. Indeed, recent progress along these three dimensions has led us to make remarkably different design choices from those of past competitions like the AutoDL competition, which was launched just three years ago. For instance, we work with bigger datasets, allow larger computational budgets, consider an expanding set of applications, and perform more robust evaluations based on performance profiles. Relatedly, while over the past three years we’ve witnessed significant progress in NAS and the emergence of the pretrain/fine-tuning paradigm in various settings, neither of these types of approaches featured prominently in the AutoDL competition (or other past competitions). In contrast, we hypothesize that these approaches will be more prominently featured in the AutoML Decathlon.

The AutoML Decathlon is built around a set of 20 datasets that we have curated which represent a broad spectrum of practical applications in scientific, technological, and industrial domains. As explained in Figure 3, ten of the tasks will be used for development and an additional ten tasks will be used for final evaluation and revealed only after the competition. We will provide computational resources to participants as needed, with funding provided by Morgan Stanley. The results of our performance-profile based evaluation will determine monetary prizes, including a $15K first prize, with sponsorship provided by HPE.

Getting Involved: Using NAS-Bench-360 and competing in the AutoML Decathlon

Our goal with both NAS-Bench360 and the AutoML Decathlon is to encourage community participation in evaluating what AutoML is already good at, what areas need improving, and what directions seem most promising for future work. We hope that these rigorous benchmarking activities will help the field more rapidly move towards a truly democratized ML toolkit that can be used by researchers and practitioners alike.

To learn more, check out the following links:

• NAS-Bench360: You can download the ten datasets on the website, and learn more about the benchmark and our various insights from our paper.
• AutoML Decathlon: The competition officially starts next week and runs through mid October, but we are soft-launching today to spread the word. You can learn more about the details at the competition website and the associated CodaLab website. 

Also, stay tuned for a follow up blog post where our collaborator Junhong Shen describes our recent algorithmic NAS work targeting diverse tasks.

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Reinforcement learning (RL) has achieved astonishing successes in domains where the environment is easy to simulate. For example, in games like Go or those in the Atari library, agents can play millions of games in the course of days to explore the environment and find superhuman policies [1]. However, transfer of these advances to broader real-world applications is challenging because the cost of exploration in many important domains is high. For example, while RL-based solutions for controlling plasmas in the nuclear fusion power generation are promising, there is only one operating tokamak in the United States and its resources are in excessive demand. Even the most data-efficient RL algorithms typically take thousands of samples to solve even moderately complex problems [2, 3], which is infeasible in plasma control and many other applications.

In contrast to conventional machine learning settings where the data is given to the decision maker, an RL agent can choose data to learn from. A natural idea for reducing data requirements is to choose data wisely such that a smaller amount of data is sufficient to perform well on a task. In this post, we describe a practical implementation of this idea. Specifically, we offer an answer to the following question: “If we were to collect one additional datapoint from anywhere in the state-action space to best improve our solution to the task, which one would it be?”. This question is related to a more fundamental idea in the design of intelligent agents with limited resources: such agents should be able to understand what information about the world is the most useful to help them accomplish their task. We see this work as a small step towards this bigger goal.

In our recent ICLR paper, “An Experimental Design Perspective on Model-Based Reinforcement Learning“, we derive an acquisition function that guides an agent in choosing data for the most successful learning. In doing this, we draw a connection between model-based reinforcement learning and Bayesian optimal experimental design (BOED) and evaluate data prospectively in the context of the task reward function and the current uncertainty about the dynamics. Our approach can be efficiently implemented under a conventional assumption of a Gaussian Process (GP) prior on the dynamics function. Typically in BOED, acquisition functions are used to sequentially design experiments that are maximally informative about some quantity of interest by repeatedly choosing the maximizer, running the experiment, and recomputing the acquisition function with the new data. Generalizing this procedure, we propose a simple algorithm that is able to solve a wide variety of control tasks, often using orders of magnitude less data than competitor methods to reach similar asymptotic performance.

Preliminaries

In this work, we consider a RL agent that operates in an environment with unknown dynamics. This is a general RL model for decision-making problems in which the agent starts without any knowledge on how their actions impact the world. The agent then can query different state-action pairs to explore the environment and find a behavior policy that results in the best reward. For example, in the plasma control task, the states are various physical configurations of the plasma and possible actions include injecting power and changing the current. The agent does not have prior knowledge on how its actions impact the conditions of the plasma. Thus, it needs to quickly explore the space to ensure efficient and safe operation of the physical system—a requirement captured in the corresponding reward function.

Given that each observation of a state-action pair is costly, an agent needs to query as few state-action pairs as possible and in this work we develop an algorithm that informs the agent about which queries to make.

We operate under a setting we call transition query reinforcement learning (TQRL). In this setting, an agent can can sequentially query the dynamics at arbitrary states and actions to learn a good policy, essentially teleporting between states as it wishes. Traditionally, in the rollout setting, agents must simply choose actions and execute entire episodes to collect data. TQRL therefore is a slightly more informative form of access to the real environment.

Main Idea

Inspired by BOED and Bayesian algorithm execution (BAX) [11], we use ideas from information theory to motivate our method to effectively choose data points. Our goal is to sequentially choose queries ((s, a)) such that our agent quickly finds a good policy. We observe that to perform the task successfully, we do not need to approximate the optimal policy (pi^*) everywhere in the state space. Indeed, there could be regions of the state space that are unlikely to be visited by the optimal policy. Thus, we only need to approximate the optimal policy in the regions of the state space that are visited by the optimal policy.

Therefore, we choose to learn about (tau^*)—the optimal trajectory governed by the optimal policy (pi^*). This objective only requires data about the areas we believe (pi^*) will visit as it solves the task, so intuitively we should not “waste” samples on irrelevant regions in the state-action space. In plasma control, this idea might look like designing experiments in certain areas of the state and action space that will teach us the most about controlling plasma in the target regimes we need to maintain fusion.

We thus define our acquisition function to be the expected information gain about (tau^*) from sampling a point (T(s, a)) given a dataset (D): $$EIG_{tau^*}(s, a) = Hbb[tau^* mid D] – Ebb_{s’sim T(s, a)}left[Hbb[tau^*mid Dcup {(s, a, s’)}]right].$$ Intuitively, this quantity measures how much the additional data is expected to reduce the uncertainty (here given by Shannon entropy, denoted (Hbb)) about the optimal trajectory.

At a high level, following methods related to the InfoBAX algorithm [11], we can approximate this acquisition function by a three-step procedure:

• First, we sample many possible dynamics functions from our posterior (e.g., functions that describe plasma evolution).
• Second, we find optimal trajectories on each of the sampled dynamics functions without taking new data from the environment, as we can simulate controls on these dynamics.
• Third, we compute predictive entropies of our model at ((s, a)) and of our model with additional data taken from each optimal trajectory. We can then subtract the trajectory-conditioned entropy from the original entropy.

This final step allows us to estimate the mutual information between (T(s, amid D)) and (tau^*), which is precisely the quantity we want. We give a more precise description of this below.

Inspired by the main ideas of BOED and active learning, we give a simple greedy procedure which we call BARL (Bayesian Active Reinforcement Learning) for using our acquisition function to acquire data given some initial dataset:

1. Compute (EIG_{tau^*}(s, a)) given the dataset for a large random set of state-action pairs. Samples of (tau^*) can be reused between these points.
2. Sample (s’ sim T(s, a)) for the (s, a) that was found to maximize the acquisition function and add (s, a, s’) to the dataset.
3. Repeat steps 1-2 until the query budget is exhausted. The evaluation policy is simply MPC on the GP posterior mean.

Does BARL reduce the data requirements of RL?

We evaluate BARL on the TQRL setting in 5 environments which span a variety of reward function types, dimensionalities, and amounts of required data. In this evaluation, we estimate the minimum amount of data an algorithm needs to learn a controller. The evaluation environments include the standard underactuated pendulum swing-up task, a cartpole swing-up task, the standard 2-DOF reacher task, a navigation problem where the agent must find a path across pools of lava, and a simulated nuclear fusion control problem where the agent is tasked with modulating the power injected into the plasma to achieve a target pressure.

To assess the performance of BARL in solving MDPs quickly, we assembled a group of reinforcement learning algorithms that represent the state of the art in solving continuous MDPs. We compare against model-based algorithms PILCO [7], PETS [2], model-predictive control with a GP (MPC), and uncertainty sampling with a GP ((EIG_T)), as well as model-free algorithms SAC [3], TD3 [8], and PPO [9]. Besides the uncertainty sampling (which operates in the TQRL setting and is directly comparable to BARL), these methods rely on the rollout setting for RL and are somewhat disadvantaged relative to BARL.

BARL clearly outperforms each of the comparison methods in nearly every problem in data efficiency. We see that simpler methods like (EIG_T) and MPC perform well on lower-dimensional problems like Lava Path, Pendulum, and Beta Tracking, but struggle with the higher-dimensional Reacher Problem. Model-free methods like SAC, TD3, and PPO are notably sample-hungry.

After further investigation, we also find that models that used data chosen by BARL are more accurate on the datapoints required to solve the problem and less accurate on a randomly chosen test set of points than models using data chosen via (EIG_T). This implies that BARL is choosing the ‘right data’. Since the same model is used in both of these methods, there will inevitably be areas of the input space where each of the methods performs better than the other. BARL performs better on the areas that are needed to solve the problem.

Conclusion

We believe (EIG_{tau^*}) is an important first step towards agents that think proactively about the data that they will acquire in the future. Though we are encouraged by the strong performance we have seen so far, there is substantial future work to be done. In particular, we are currently working to extend BARL to the rollout setting by planning actions that will lead to maximum information in the future. We also aim to solve problems of scaling these ideas to the high-dimensional state and action spaces that are necessary for many real-world problems.

References

[1] Mastering the game of Go with deep neural networks and tree search, Silver et al, Nature 2016

[2] Deep Reinforcement Learning in a Handful of Trials using Probabilistic Dynamics Models, Chua et al, Neurips 2018

[3] Soft Actor-Critic: Off-Policy Maximum Entropy Deep Reinforcement Learning with a Stochastic Actor, Haarnoja et al, ICML 2018

[4] Cross-Entropy Randomized Motion Planning, Kobilarov et al, RSS 2008

[5] Sample-efficient Cross-Entropy Method for Real-time Planning, Pinneri et al, CoRL 2020

[6] Efficiently Sampling Functions from Gaussian Process Posteriors, Wilson et al, ICML 2020

[7] PILCO: A Model-Based and Data-Efficient Approach to Policy Search, Deisenroth & Rasmussen, ICML 2011

[8] Addressing Function Approximation Error in Actor-Critic Methods, Fujimoto et al, ICML 2018

[9] Proximal Policy Optimization Algorithms, Schulman et al, 2017

[10] Universal Kernels, Micchelli et al, JMLR 2006

[11] Bayesian Algorithm Execution: Estimating Computable Properties of Black-box Functions Using Mutual Information, Neiswanger et al, ICML 2021

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There is increasing interest in computer science and elsewhere to understand and improve peer review (see here for an overview). With this motivation, we conducted two experiments regarding peer review which we summarize in this blog post.

Pros and Cons of Posting Preprints Online

Motivation.  Authors posting preprints online before review in double-blind peer-review is a widely debated issue of policy as well as authors’ personal choice. This choice is especially challenging for authors who perceive that they may be at a disadvantage in the review process if their identity is revealed. By posting their preprints online they stand to gain publicity but may lose benefits of double-blind review. We substantiate this debate quantitatively by addressing two research questions. 

Research questions. We study the following research questions:

• (Q1) What fraction of reviewers deliberately search for their assigned paper on the Internet? 
• (Q2) For preprints posted online, what is the relation between the papers’ visibility and the ranking of the authors’ affiliations?

Methods. We conduct survey-based experiments in the ICML 2021 and EC 2021 conferences. 

• (Q1) We conduct an anonymized survey, where we ask each reviewer whether they deliberately searched online for any of their assigned papers.
• (Q2) We consider the papers submitted to ICML or EC which were also available online before review. We survey relevant reviewers to assess the visibility of these papers: we ask them whether they have seen these papers online outside of the reviewing context. Finally, we compute a correlation between papers’ visibility and associated authors’ affiliations’ ranking.

Key findings. We report two main insights:

• (Q1) More than a third of the respondents self-report searching online for their assigned paper in both ICML and EC.
• (Q2) We find a weak positive correlation: preprints from better-ranked affiliations enjoy a higher visibility. In ICML, the correlation coefficient is 0.06 and is statistically significant; in EC, the correlation coefficient is 0.05 and is not statistically significant. In particular, papers associated with the top-10-ranked affiliations had a visibility of about 11% in ICML and 22% in EC, whereas the remaining papers had a visibility of 7% and 18% respectively.

Implications. Conference organizers looking to design blinding policies and authors looking to post preprints online can use our findings to gauge the tradeoffs involved.

Details. https://arxiv.org/pdf/2203.17259.pdf

Citation Bias

Motivation.  Many anecdotes suggest that including citations to the works of potential reviewers is a good (albeit unethical) way to increase the acceptance chances of a manuscript. 

Research question. Does the citation of a reviewer’s work in a submission cause the reviewer to be positively biased towards the submission, that is, cause a shift in reviewer’s evaluation that goes beyond the genuine change in the submission’s scientific merit?

Methods. We pair cited and uncited reviewers for each submitted paper and then carefully analyze the differences in their scores. Our analysis accounts for the many confounding factors that may exist. By pairing reviewers, we alleviate the confounding factor of “paper quality” as both cited and uncited reviewers review the same paper. We also control for confounders related to reviewer identities by accommodating various associated aspects such as the reviewers’ expertise and preferences in reviewing papers. Finally, we analyze reviews of uncited reviewers to exclude cases in which a reviewer genuinely decreases their evaluation of a paper because it fails to cite their own relevant past work. 

Key findings. Our findings suggest that citation bias exists, and papers enjoy higher scores from a cited reviewer. Due to this bias, the expected increase in a cited reviewer’s score is 0.16 (on a 6 point scale) in ICML and 0.23 (on a 5 point scale) in EC. For reference, a one-point increase of a score by a single reviewer improves the position of a submission by 11% on average.

Implications. We detect and quantify the strength of citation bias in peer review, informing stakeholders of the presence of the bias. Our work also raises an important open problem of mitigating citation bias.

Details. https://arxiv.org/pdf/2203.17239.pdf

Acknowledgements

The post is based on joint works with Ivan Stelmakh, Ryan Liu,  Xinwei Shen, Marina Meila, Shuchi Chawla, Federico Echenique, and Nihar B. Shah.

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Imagine training a deep network twice with two different random seeds on the same data, and then measuring the rate at which they disagree on unlabeled test points. Naively, they can disagree with one another with probability anywhere between zero and twice the error rate. But surprisingly, in practice, we observe that the disagreement and test error of deep neural network are remarkably close to each other. The variable (y) refers to the average generalization error of the two models and the variable (x) refers to the disagreement of the two models.

Estimating the generalization error of a model — how well the model performs on unseen data — is a fundamental component in any machine learning system. Generalization performance is traditionally estimated in a supervised manner, by dividing the labeled data into a training set and test set. However, high-quality labels are usually costly and, ideally, we would like to use all of them to train the model. On the other hand, in many real-world settings, a large amount of unlabeled data is readily available. How can we tap into the rich information in these unlabeled data and leverage them to assess a model’s performance without labels?

In this work (full paper), we demonstrate that a simple procedure can accurately estimate the generalization error with only unlabeled data. This result reveals a surprising fact about how neural networks make mistakes and their connection to calibration through an identity we call Generalization Disagreement Equality (GDE).

A surprising observation

Stochastic gradient descent (SGD) is perhaps the most popular optimization algorithm for deep neural networks. Due to the non-convex nature of the deep neural network’s optimization landscape, different runs of SGD will find different solutions. As a result, if the solutions are not perfect, they will disagree with each other on some of the unseen data. This disagreement can be harnessed to estimate generalization error without labels:

1. Given a model, run SGD with the same hyperparameters but different random seeds on the training data to get two different solutions.
2. Measure how often the networks’ predictions disagree on a new unlabeled test dataset.

We find that the disagreement rate is approximately equal to the average test error over the two models. Our observation builds on the phenomenon reported by Nakkiran and Bansal (2020) [1]: given two networks of the same architecture trained to zero training error on two independently drawn datasets of the same size, the disagreement rate of the pair on the test dataset is nearly equal to the average test error. Our observation generalizes prior work by showing that the same phenomenon holds for small changes in hyperparameters and, more importantly, the same dataset, which makes the procedure relevant for practical applications.

This procedure estimates the test error with unlabeled data, but the mechanisms behind it are not immediately obvious. Let (h(x)) be the prediction of classifier (h(x)) and (y) be the true label. By the triangle inequality, the disagreement rate can be anywhere between 0 and 2 times the test error: ( 0 leq mathbb{E}[h(x) ne h’(x)] leq mathbb{E}[h(x) ne y] + mathbb{E}[h’(x) ne y]). Given that the models observe the same data, we may expect the models to extract similar knowledge from the data and consequently make similar errors, which would make the disagreement rate lower than the test error. Yet, we find that in practice, the disagreement rate approximates the test error without any proportionality constant. Why is this the case?

The final parameters found by SGD depend on many sources of randomness: 1) random initialization, 2) random ordering of a fixed training dataset, and/or 3) random sampling of training data. To understand this phenomenon, we analyze what kind of randomness is responsible for this peculiar property. It is possible to have other sources of randomness, such as dropout, which are not studied in this work.

We study the phenomenon by observing how the behavior of disagreement changes when the different sources of randomness are isolated. For example, when examining the effect of different initialization,s we fix the dataset and the order in which the dataset is presented to the model and only change the random initialization. We observe that across different types of randomness, disagreement remains consistently close to the test error. This approach is particularly useful because we can use the same training data to train the two copies of the model. In addition, we empirically observe the phenomenon across a wide range of model architectures (ResNet, VGG, and fully-connected networks) and several popular image recognition benchmarks (MNIST, SVHN, Cifar10, and Cifar100).

Furthermore, estimating generalization error is especially important when the test distribution is different from the training distribution. On that note, we see some promising observations in the PACS data [2]. This dataset consists of 4 different environments (Photo, Art, Cartoon, Sketch) of different objects. For each environment, we trained two ResNet18 models on that environment with different initialization and order of the data and measured their disagreement rate on the remaining environments. We observe that similar phenomena hold across many (but not all) pairs of environments,  suggesting that the technique might be adaptable for estimating generalization error under distribution shift.

Generalization-Disagreement Equality

We will now theoretically investigate the sufficient condition under which the disagreement rate equals generalization error.

In the deep learning literature, it is well-known that ensembles of SGD-trained deep networks are well-calibrated over the training distribution [3]. An ensemble is well-calibrated if the confidence ( tilde{h}_k(x) = mathbb{E}_{h_k sim H_A}[h(x)] ) it outputs for class ( k ) matches the expected accuracy i.e. ( P(y mid tilde{h}_k(x) = p) = p). There exist various formalisms for calibration. In this paper, we show that if an ensemble satisfies class-wise calibration for a distribution D (a more general form of calibration is discussed in the paper), then (mathbb{E}_{h, h’}[mathbb{E}_D[h(x) neq h'(x)]] = mathbb{E}_h[mathbb{E}_D[h(x) neq y]]) with strict equality. We refer to this equality as the Generalization Disagreement Equality (GDE).

Proof Sketch

The proof sketch we show here focuses on a special case, where class-wise calibration holds. Consider binary classification. Say that we have a distribution over the hypotheses ( H_A) given SGD algorithm (A) and we sample two hypotheses (h, h’) from this distribution. Now given some test data (D), we partition it by the confidence output by the ensemble i.e. (D_q = P(X | tilde{h}_0(x) = q)). For any fixed (x) in the support of (D_q), the disagreement rate in expectation over (h, h’) is

$$ E_{h,h’}[h(x) ne h'(x)] \ = P(tilde{h}(x) = 1)P(tilde{h}(x) = 0) + P(tilde{h}(x) = 0)P(tilde{h}(x) = 1) \ = q(1-q) + (1-q)q = 2q(1-q).$$

Additionally, note that for any (x in D), the expected error equals (tilde{h}_{1 – y}(x)). Since the ensemble is also class-wise calibrated, for any (x in D_q) the expected error over (h in H_A) is

$$E_h[h(x) ne y] \= tilde{h}_0(x)P(y = 1 | tilde{h}(x) = 1) + tilde{h}_1(x)P(y = 0 | tilde{h}(x) = 0) \ = q(1-q) + (1-q)q = 2q(1-q)$$

We proved that for each calibration level set, GDE holds. Since the disagreement rate 2q(1-q) equals the expected error 2q(1-q), we conclude that the expected error equals the disagreement rate. Since the disagreement rate 2q(1-q) equals the expected error 2q(1-q), we conclude that the expected error equals the disagreement rate. So in expectation over D, GDE holds.

---

Note the theorem only shows that the test error and expected disagreement are equal in expectation over all the models learned by SGD, but does not necessarily explain why the equality seems to hold for as few as a single pair of training runs. It captures the observation’s essence, but explaining why a single pair of models is sufficient is still an open problem. Intuitively, this can be true if the distribution of disagreement has an unusually small variance. In our experiments, we do observe very small variance for disagreement, but a rigorous theoretical discussion of why the variance is small remains unsettled.

Further, in practice, no models are perfectly calibrated, but we could still characterize how the deviation from calibration affects the GDE. We show that calibration error upper bounds the absolute difference between the expected disagreement and the expected calibration error. This inequality generalizes the GDE and implies that as long as the ensemble is reasonably calibrated, we can expect a good estimation of generalization error from disagreement. Finally, we empirically validate that this assumption often holds in practice by training 100 copies of the same model to produce an ensemble that is faithful to the true ensemble and measure their calibration error. The results show that these ensembles are indeed well-calibrated.

Conclusion

We have presented a method for estimating the generalization error of black-box deep neural networks with only unlabeled data, as well as some theoretical motivation for why the method works. Specifically, we showed that if the ensembles of the models trained by SGD are well-calibrated, the expected disagreement is equal to the expected test error. However, in practice, merely a single pair of models is sufficient for accurately estimating the generalization error. In the broader picture, this result marks a departure from the more traditional approaches of studying generalization and points to the tantalizing possibility of leveraging unlabeled data to estimate the generalization error. We are excited about the results we presented in the paper, but we are even more excited about the questions that we did not answer in the paper. We hope this work will encourage future work to investigate more unconventional ways of understanding generalization in deep learning.

Reference

[1] Nakkiran and Bansal. Distributional Generalization: A New Kind of Generalization. 2020.
[2] Li et al. Deeper, Broader and Artier Domain Generalization. IEEE Intl. Conf. on Computer Vision (ICCV), 2017.
[3] Lakshminarayanan et al. Simple and Scalable Predictive Uncertainty Estimation using Deep Ensembles. Conference on Neural Information Processing Systems (NeurIPS), 2017.

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Figure 1: Training instability is one of the biggest challenges in training GANs. Despite the existence of successful heuristics like Spectral Normalization (SN) for improving stability, it is poorly-understood why they work. In our research, we theoretically explain why SN stabilizes GAN training. Using these insights, we further propose a better normalization technique for improving GANs’ stability called Bidirectional Scaled Spectral Normalization.

Generative adversarial networks (GANs) are a class of popular generative models enabling many cutting-edge applications such as photorealistic image synthesis. Despite their tremendous success, GANs are notoriously unstable to train—small hyper-parameter changes and even randomness in optimization can cause training to fail altogether, which leads to poor generated samples. One empirical heuristic that is widely used to stabilize GAN training is spectral normalization (SN) (Figure 2). Although it is very widely adopted, little is understood about why it works, and therefore there is little analytical basis for using it, configuring it, and more importantly, improving it.

In this post, we discuss our recent work at NeurIPS 2021. We prove that spectral normalization controls two well-known failure modes of training stability: exploding and vanishing gradients. More interestingly, we uncover a surprising connection between spectral normalization and neural network initialization techniques, which not only help explain how spectral normalization stabilizes GANs, but also motivate us to design Bidirectional Scaled Spectral Normalization (BSSN), a simple change to spectral normalization that yields better stability than SN (Figure 3). 

Exploding and vanishing gradients cause training instability

Exploding and vanishing gradients describe a problem in which gradients either grow or shrink rapidly during training. It is known in the community that these phenomena are closely related to the instability of GANs. Figure 4 shows an illustrating example: when exploding and vanishing gradients happen, the sample quality measured by inception score (higher is better) deteriorates rapidly.

In the next section, we will show how spectral normalization alleviates exploding and vanishing gradients, which may explain its success.

How spectral normalization mitigates exploding gradients

The fact that spectral normalization prevents gradient explosion is not too surprising. Intuitively, it achieves this by limiting the ability of weight tensors to amplify inputs in any direction. More precisely, when the spectral norm of weights = 1 (as ensured by spectral normalization), and the activation functions are 1-Lipschitz (e.g., (Leaky)ReLU), we show that

$$ | text{gradient} |_{text{Frobenius}} leq sqrt{text{number of layers}} cdot | text{input} |.$$

(Please refer to the paper for more general results.) In other words, the gradient norm of spectrally normalized GANs cannot exceed a strict bound. This explains why spectral normalization can mitigate exploding gradients. 

Note that this good property is not unique to spectral normalization—our analysis can also be used to show the same result for other normalization and regularization techniques that control the spectral norm of weights, such as weight normalization and orthogonal regularization. The more surprising and important fact is that spectral normalization can also control vanishing gradients at the same time, as discussed below.

How spectral normalization mitigates vanishing gradients

To understand why spectral normalization prevents gradient vanishing, let’s take a brief detour to the world of neural network initialization. In 1996, LeCun, Bottou, Orr, and Müller introduced a new initialization technique (commonly called LeCun initialization) that aimed to prevent vanishing gradients. It achieved this by carefully setting the variance of the weight initialization distribution as $$text{Var}(W)=left(text{fan-in of the layer}right)^{-1},$$ where fan-in of the layer means the number of input connections from the previous layer (e.g., in fully-connected networks, fan-in of the layer is the number of neurons in the previous layer). LeCun et al. showed that

• If the weight variance is larger than ( left(text{fan-in of the layer}right)^{-1} ), the internal outputs of the neural networks could be saturated by bounded activation or loss functions (e.g., sigmoid), which causes vanishing gradients.
• If the weight variance is too small, gradients will also vanish because gradient norms are bounded by the scale of the weights.

We show theoretically that spectral normalization controls the variance of weights in a way similar to LeCun initialization. More specifically, for a weight matrix (Win mathbb{R}^{mtimes n}) with i.i.d. entries from a zero-mean Gaussian distribution (common for weight initialization), we show that

$$ text{Var}left( text{spectrally-normalized } W right) ~~~text{ is on the order of }~~~left( maxleft{ m,n right} right)^{-1} $$

(Please refer to the paper for more general results.) This result has separate implications on the fully-connected layers and convolutional layers:

• For fully-connected layers with a fixed width across hidden layers, (maxleft{m,nright} =m =n =text{fan-in of the layer} ). Therefore, spectrally-normalized weights have exactly the desired variances as LeCun initialization!
• For convolutional layers, the weight (i.e., convolution kernel) is actually a 4-dimensional tensor: ( W in mathbb{R}^{c_{out} c_{in} k_w k_h} ), where (c_{out},c_{in},k_w,k_h) denote the number of output channels, the number of input channels, kernel width, and kernel hight respectively. The popular implementation of spectral normalization normalizes the weights by ( frac{W}{sigmaleft( W_{c_{out} times left(c_{in} k_w k_hright)} right)} ) where (sigmaleft( W_{c_{out} times left(c_{in} k_w k_hright)} right)) is the spectral norm on the reshaped weight, i.e., ( m= c_{out}, n=c_{in} k_w k_h). In hidden layers, usually (maxleft{m,nright} =maxleft{c_{out}, c_{in} k_w k_hright} =c_{in} k_w k_h=text{fan-in of the layer} ). Therefore, spectrally-normalized convolutional layers also maintain the same desired variances as LeCun initialization!

Whereas LeCun initialization only controls the gradient vanishing problem at the beginning of training, we observe empirically that spectral normalization preserves this nice property throughout training (Figure 5). These results may help explain why spectral normalization controls vanishing gradients during GAN training.

How to improve spectral normalization

The next question we ask is: can we use the above theoretical insights to improve spectral normalization? Many advanced initialization techniques have been proposed in recent years to improve LeCun initialization, including Xavier initialization and Kaiming initialization. They derived better parameter variances by incorporating more realistic assumptions into the analysis. We propose Bidirectional Scaled Spectral Normalization (BSSN) so that the parameter variances parallel the ones in these newer initialization techniques:

• Xavier initialization. The idea of Xavier initialization is to set the variance of parameter initialization distribution to be (text{Var}(W)=left(frac{text{fan-in of the layer} + text{fan-out of the layer}}{2}right)^{-1},) which they show to not only control the variances of outputs (as in LeCun initialization), but also the variances of backpropagated gradients, giving better gradient values. We propose Bidirectional Spectral Normalization that normalizes convolutional kernels by (frac{W}{left( sigmaleft(W_{c_{out} times left(c_{in} k_w k_hright)}right) +sigmaleft(W_{c_{in} times left(c_{out} k_w k_hright)}right) right)/2}~~~~~~~). We show that by doing this, the parameter variances mimic the ones in Xavier initialization.
• Kaiming initialization. The analysis in LeCun and Xaiver initialization did not cover activation functions like (Leaky)ReLU which decrease the scales of the network outputs. To cancel out the effect of (Leaky)ReLU, Kaiming initialization scales up the variances in LeCun or Xavier initilization by a constant. Motivated from it, we propose to scale the above normalization formula with a tunable constant (c): (ccdotfrac{W}{left( sigmaleft(W_{c_{out} times left(c_{in} k_w k_hright)}right) +sigmaleft(W_{c_{in} times left(c_{out} k_w k_hright)}right) right)/2}~~~~~~~).

BSSN can be easily plugged into GAN training with minimal code changes and little computational overhead. We compare spectral normalization and BSSN on several image datasets, using standard metrics for image quality like inception score (higher is better) and FID (lower is better). We show that simply replacing spectral normalization with BSSN not only makes GAN training more stable (Figure 6), but also improves sample quality (Table 1). Generated samples from BSSN are in Figure 7.

Links

This post only covers a portion of our theoretical and empirical results. Please refer to our NeurIPS 2021 paper and code if you are interested in learning more.

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Figure 1. Overview of LOOP: Model-free Reinforcement Learning learns a policy by training a value function. In this setting, the performance of the policy is dependent on the accuracy of the learned value function. We propose LOOP, an efficient framework to learn with a policy that finds the best action sequence using imaginary rollouts with a learned model. This allows LOOP to potentially reduce dependence on value function errors. LOOP achieves strong performance across a range of tasks and problem settings.

Model-Free Off-Policy Reinforcement Learning

Reinforcement learning (RL) enables artificial agents to learn different tasks by interacting with the environment. Within RL, off-policy methods have brought about numerous successes recently for efficiently learning behaviors in applications such as robotics due to their ability to leverage previously collected data efficiently and incorporate data from a variety of sources.

How does off-policy reinforcement learning work? A model-free off-policy reinforcement learning algorithm typically consists of a parameterized actor and a value function (see Figure 2). The actor interacts with the environment collecting the transitions in the replay buffer. The value function is trained using the transitions from the replay buffer to predict the cumulative return of the actor, and the actor is updated by maximizing the action-values at the states visited in the replay buffer. This framework suffers from the following issues:

1. The performance of the actor is highly dependent on the accuracy of the learned value function. Learning an accurate value function is challenging in deep reinforcement learning with issues pointed out by previous works such as divergence, instability, rank loss, delusional bias and overestimation. 
2. Traditionally in model-free RL methods, the parametrized actor is a neural network which is uninterpretable and inflexible in dealing with constraints during deployment. On the other hand, risk-sensitive domains such as healthcare or autonomous driving require us to reason about why the policy chose a particular action or incorporate safety constraints.

So, how should the actor choose actions if the value function is inaccurate? In this work, we suggest using a policy that looks ahead in the future using a learned model to find the best action sequence. This lookahead policy is more interpretable than the parametric actor and also allows us to incorporate constraints. Then we present a computationally efficient framework of learning with the lookahead policy that we call LOOP. We also show how LOOP can also be applied to the offline RL and safe RL along with the online RL setting.

H-step Lookahead Policy

In order to increase the performance, safety, and interpretability of reinforcement learning, we use online planning (“H-step lookahead”) with a terminal value function. In H-step lookahead, we use a learned dynamics model to roll out action sequences for H-horizon into the future and get the cumulative reward. To reason about the future reward beyond H steps, we attach a value function at the end of the rollout. The objective is to select the action sequence that will lead to rollout with the best cumulative return.

Stated formally, H-step lookahead objective aims to find an action sequence ((a_{0:H-1})) that maximizes the following objective:

$$max_{a_{0:H-1}} left[mathbb{E}_{hat{M}}[sum_{t=0}^{H-1}gamma^tr(s_t,a_t)+gamma^Hhat{V}(s_H)]right]$$

where (hat{M}) is the learned dynamics model, (hat{V}) is the learned terminal value function, (r) is the reward function and (gamma) is the discount factor.

H-step lookahead provides several benefits: 1. H-step lookahead reduces dependency on value function errors by using the model rollouts which allows it to trade-off value errors with model-errors. 2. H-step lookahead offers a degree of interpretability that is missing in fully parametric methods and 3. H-step lookahead allows the user to incorporate constraints (even non-stationary) and behavior priors during deployment. 

We can also provide theoretical guarantees that demonstrate using an H-step lookahead instead of a parametric actor (1-step greedy actor) can reduce dependency on value errors by a large margin while introducing a dependence on model errors. Despite the additional model errors, we argue that the H-step lookahead is useful as value errors can stem from several reasons as discussed in the previous section. In the low data regime, value errors can also stem from compounding sampling errors whereas the model can be expected to have smaller errors as it is trained with denser supervision using supervised learning. We hypothesize that these numerous sources of errors in value learning make the tradeoff of value-errors with model-errors beneficial and see empirical evidence for the same in our experiments.

LOOP: Learning Off-Policy with Online Planning

As described above, the H-step lookahead policy uses a terminal value function at the end of the H steps.  How do we learn the value function for this H-step lookahead policy?  The difficulty is that, in learning a value function, we need to evaluate the H-step lookahead policy from different states.  However, evaluating the H-step lookahead policy is somewhat slow (Lowrey et al.), since the lookahead policy requires simulating the dynamics for H-steps, which makes such an approach computationally expensive.

Instead, we propose to learn a parameterized actor to more efficiently learn the terminal value function; to learn the value function, we can evaluate the actor (which is fast) instead of evaluating the H-step lookahead policy (which is slow).  We call this approach LOOP: Learning off-policy with online planning.  However, the problem with this approach is that there might be a difference between the H-step lookahead policy and the parametric actor (see Figure 3).  The difference between these policies can cause unstable learning, which we refer to as “actor divergence.” 

Our solution to actor divergence is to constrain the H-step lookahead policy based on the KL-divergence to a prior, where the prior is based on the parametric actor.  This constrained optimization helps ensure that the H-step lookahead policy remains similar to the parametric actor, leading to significantly more stable training. Specifically, we propose actor regularized control (ARC), which uses the following objective 

$$p^tau_{opt}=text{argmax}_{p^tau} mathbb{E}_{p^tau} left[mathbb{E}_{hat{M}}[R_{H,hat{V}}(s_t,tau)]right]~,~textrm{s.t}~~D_{KL}(p^tau||p^tau_{prior})le epsilon$$

The inner expectation estimates the return of the H-step lookahead (R_{H,hat{V}}) under model uncertainty while the outer expectation is under a distribution of action sequences.

In the above objective, we aim to find a distribution (p^tau=p^tau_{opt}) over the action sequence (tau) that maximizes the H-step lookahead return (R_{H,hat{V}}(s_t,tau)) while ensuring that the distribution of the action sequence is close to some predefined prior  (p^tau_{prior}). In ARC we set this prior to be equal to the parametrized actor and this ensures that H-step lookahead is close to the parametrized actor while still improving the cumulative return. This constrained optimization has a closed-form solution given by ( p^tau_{opt} propto p^tau_{prior} e^{frac{1}{eta}mathbb{E}_{hat{M}}[R_{H,hat{V}}(s_t,tau)]} ). Since the closed-form solution is unnormalized, we approximate it by a gaussian and improve the estimate of its mean and variance by iterative self-normalized importance sampling.

LOOP for Offline and Safe RL

In the previous section, we have seen that ARC optimizes for the expected return in the online RL setting.  LOOP can be extended to work in two other domains: 1. Offline RL: Learning from a fixed dataset of collected experience 2. Safe RL: Learning to maximize rewards which ensures that the constraint violations are below some threshold. 

For offline RL, ARC optimizes for the following underestimate of H-step lookahead return similar to previous offline RL methods ([1,2]).

$$text{mean}_{[K]}[R_{H,hat{V}}(s_t,tau)] – beta_{pess}text{std}_{[K]}[R_{H,hat{V}}(s_t,tau)]$$

where ([K]) denote model ensembles for uncertainty estimation and (beta_{pess}) is an hyperparameter.

In this setting, the off-policy algorithm is also replaced by an offline RL algorithm (see Figure 5).

For safe RL, ARC optimizes for a constrained H-step lookahead objective which ensures that the cumulative constraint cost in the planning horizon are less than the predefined threshold (see Figure 6).

$$text{argmax}_{a_t} mathbb{E}_{hat{M}}[R_{H,hat{V}}(s_t,tau)]~~text{s.t}~max_{[K]}sum_{t=t}^{t+H-1}gamma^t c(s_t,a_t)le d_0$$

where (c) is the cost function.

Experiments: Online, Offline, and Safe RL

Online RL: We use SAC as the off-policy algorithm in LOOP and test it on a set of MuJoCo locomotion and manipulation tasks. LOOP is compared against a variety of baselines covering model-free (SAC), model-based (PETS-restricted), and hybrid model-free+model-based (MBPO, LOOP-SARSA, SAC-VE) methods. LOOP-SARSA is a variant of LOOP that evaluates the replay buffer policy in its critic.

LOOP-SAC significantly improves performance over SAC, the underlying off-policy algorithm used to learn the terminal value function. The increase in efficiency over the SAC  empirically confirms that model-error tradeoff with value-error is indeed beneficial. LOOP-SAC is also competitive to MBPO in locomotion tasks, outperforming it significantly in manipulation tasks.

Offline RL: We combine LOOP with two offline RL methods Critic Regularized Regression (CRR) and Policy in latent action space (PLAS) and test it on D4RL datasets. LOOP improves over CRR and PLAS with an average improvement of 15.91% and 29.49% respectively on the D4RL locomotion datasets. This empirically demonstrates that H-step lookahead improves performance over a pre-trained value function (obtained from offline RL) by reducing dependence on value errors.

Safe RL: For testing the safety performance of LOOP we experiment on the OpenAI safety gym environments. In the two environments, CarGoal and PointGoal, the agent needs to navigate to a goal while avoiding obstacles. 

SafeLOOP (Figure above) is the modification of LOOP with constrained H-step lookahead that incorporates constraints. safeLOOP can learn orders of magnitude faster while still being safer than safeRL baselines.

Next Steps

A benefit of using H-step lookahead for deployment is its ability to incorporate non-stationary exploration priors, as this framework disentangles the exploitation policy (parametrized actor) and the exploration policy (H-step lookahead) to a certain degree. Exploring how more principled exploration techniques can enable data collection that leads to better policy improvement is an interesting future direction.    

Learning with H-step lookahead efficiently is challenging and unscalable. In our work, we demonstrated one particular way to learn efficiently with H-step lookahead but our approach introduced the issue of actor divergence. Some open questions are 1. What are other ways to learn efficiently with an H-step lookahead policy that does not suffer from actor divergence? 2. How can the actor divergence be reduced without restricting the H-step lookahead policy to be near the parametrized policy (eg. Offline RL)?

Further reading

If you’re interested in more details, please check out the links to the full paper, the project website, talk, and more!

Citation

This blog post is based on the following paper (BibTeX) :

Harshit Sikchi, Wenxuan Zhou, and David Held.
Learning Off-Policy with Online Planning.
In Conference of Robot Learning, November 2021.

Acknowledgments

Thanks to Wenxuan Zhou, Ben Eysenbach, Paul Liang, and David Held for feedback on this post! This material is based upon work supported by the United States Air Force and DARPA under Contract No. FA8750-18-C-0092, LG Electronics and the National Science Foundation under Grant No. IIS-1849154.

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