M EASURING THE R ELIABILITY OF R EINFORCEMENT L EARNING A LGORITHMS
Anonymous authors
Paper under double-blind review
A BSTRACT
Lack of reliability is a well-known issue for reinforcement learning (RL) algorithms.
This problem has gained increasing attention in recent years, and efforts to improve it have grown substantially.
To aid RL researchers and production users with the evaluation and improvement of reliability, we propose a set of metrics that quantitatively measure different aspects of reliability.
In this work, we focus on variability and risk, both during training and after learning (on a ﬁxed policy).
We designed these metrics to be general-purpose, and we also designed complementary statistical tests to enable rigorous comparisons on these metrics.
In this paper, we ﬁrst describe the desired properties of the metrics and their design, the aspects of reliability that they measure, and their applicability to different scenarios.
We then describe the statistical tests and make additional practical recommendations for reporting results.
Finally, we apply our metrics to a set of common RL algorithms and environments, compare them, and analyze the results.
I NTRODUCTION
Reinforcement learning (RL) algorithms, especially Deep RL algorithms, tend to be highly variable in performance and considerably sensitive to a range of different factors, including implementation details, hyper-parameters, choice of environments, and even random seeds (Henderson et al., 2017).
This variability hinders reproducible research, and can be costly or even dangerous for real-world applications.
Furthermore, it impedes scientiﬁc progress in the ﬁeld when practitioners cannot reliably evaluate or predict the performance of any particular algorithm, compare different algorithms, or even compare different implementations of the same algorithm.
Recently, Henderson et al.
(2017) has performed a detailed analysis of reliability for several policy gradient algorithms, while Duan et al.
(2016) has benchmarked average performance of different continuous-control algorithms.
In other related work, Colas et al.
(2018) have provided a detailed analysis on power analyses for mean performance in RL, and Colas et al.
(2019) provide a comprehensive primer on statistical testing for mean and median performance in RL.
In this work, we aim to devise a set of metrics that measure reliability of RL algorithms.
Our analysis distinguishes between several typical modes to evaluate RL performance: "evaluation during training", which is computed over the course of training, vs. "evaluation after learning", which is computed after training to evaluate a ﬁxed policy.
These metrics are also designed to measure different aspects of reliability, e.g. reproducibility (variability across training runs and variability across rollouts of a ﬁxed policy) or stability (variability within training runs).
Additionally, the metrics capture multiple aspects of variability – dispersion (the width of a distribution), and risk (the heaviness and extremity of the tails of a distribution).
Standardized measures of reliability can beneﬁt the ﬁeld of RL by allowing RL practitioners to compare algorithms in a rigorous and consistent way.
This in turn allows the ﬁeld to measure progress, and also informs the selection of algorithms for both research and production environments.
By measuring various aspects of reliability, we can also identify particular strengths and weaknesses of algorithms, allowing users to pinpoint speciﬁc areas of improvement.
In this paper, in addition to describing these reliability metrics, we also present practical recommendations for statistical tests to compare metric results and how to report the results more generally.
As examples, we apply these metrics to a set of algorithms and environments (discrete and continuous,
Dispersion (D)
Risk (R)
D U R
I NG
T R A
I N I
NG
Across Time (T) (within training runs)
IQR ∗ within windows, after detrending
Short-term: CVaR † on ﬁrst-order differences
Long-term : CVaR † on
Drawdown
Across Runs (R)
IQR ∗ across training runs, after low-pass ﬁltering.
CVaR † across runs
A F
TE R
LE A
R N I
NG
Across rollouts on a Fixed Policy (F)
IQR ∗ across rollouts for a ﬁxed policy
CVaR † across rollouts for a ﬁxed policy off-policy and on-policy).
We will release the code used in this paper as an open-source Python package to ease the adoption of these metrics and their complementary statistics.
R ELIABILITY M ETRICS
We target three different axes of variability, and two different measures of variability along each axis.
We denote each of these by a letter, and each metric as a combination of an axis + a measure, e.g.
"DR" for "Dispersion Across Runs".
See Table 1 for a summary.
Please see Appendix A for more detailed deﬁnitions of the terms used here.
2. A XES OF VARIABILITY
Our metrics target the following three axes of variability.
The ﬁrst two capture reliability "during training", while the last captures reliability of a ﬁxed policy "after learning".
We follow the terminology used in Machado et al.
During training: Across Time (T)
In the setting of evaluation during training, one desirable property for an RL algorithm is to be stable within each training run.
In general, smooth monotonic improvement is preferable to noisy ﬂuctuations around a positive trend, or unpredictable swings in performance.
This type of stability is important for several reasons.
During learning, especially when deployed for real applications, it can be costly or even dangerous for an algorithm to have unpredictable levels of performance.
Even in cases where bouts of poor performance do not directly cause harm, e.g. if training in simulation, high instability implies that algorithms have to be check-pointed and evaluated more frequently in order to catch the peak performance of the algorithm.
Furthermore, while training, it can be a waste of computational resources to train an unstable algorithm that tends to forget previously learned behaviors.
During training: Across Runs (R) During training, RL algorithms should have easily and consistently reproducible performances across multiple training runs.
Depending on the components that we allow to vary across training runs, this variability can encapsulate the algorithm’s sensitivity to a variety of factors, such as: random seed and initialization of the optimization, random seed and initialization of the environment, implementation details, and hyper-parameter settings.
Depending on the goals of the analysis, these factors can be held constant or allowed to vary, in order to disentangle the contribution of each factor to variability in training performance.
After learning: Across rollouts of a ﬁxed policy (F) When evaluating a ﬁxed policy, a natural concern is the variability in performance across multiple rollouts of that ﬁxed policy.
Each rollout may be speciﬁed e.g. in terms of a number of actions, environment steps, or episodes.
This metric combines stochasticity from the environment with stochasticity from the training procedure (the optimization), and practitioners may sometimes wish to keep one or the other constant if it is important to disentangle the two factors (e.g. holding constant the random seed of the environment while allowing the random seed controlling optimization to vary across rollouts).
2. M EASURES OF VARIABILITY
For each axis of variability, we have two kinds of measures: dispersion and risk.
Dispersion Dispersion is the width of the distribution.
To measure dispersion, we use "robust statistics" such as the Inter-quartile range (IQR)
(i.e. the difference between the 75th and 25th percentiles) and the Median absolute deviation from the median (MAD) , which are more robust statistics and don’t require assuming normality of the distributions.
2 We prefer to use IQR over
MAD, because it is more appropriate for asymmetric distributions (Peter J. Rousseeuw & Christophe
Croux, 1993).
Risk In many cases, we are concerned about the worst-case scenarios.
Therefore, we deﬁne risk as the heaviness and extent of the tails of the distribution.
This is complementary to measures of dispersion like IQR, which cuts off the tails of the distribution.
To measure risk, we use the
Conditional Value at Risk (CVaR) , also known as “expected shortfall".
CVaR measures the expected loss in the worst-case scenarios, deﬁned by some quantile α .
It is computed as the expected value in the left-most tail of a distribution (Acerbi & Tasche, 2002).
Originally developed in ﬁnance, it has also seen recent adoption in Safe RL as an additional component of the objective function, e.g.
Bäuerle & Ott (2011); Chow & Ghavamzadeh (2014); Tamar et al. (2015).
We use CVaR of a random variable X for a given quantile α to be deﬁned as:
[Equation]
where α ∈ (0 , 1) and the V aR α
(Value at Risk) is just the α -quantile of the distribution of X .
2. D ESIDERATA
We require that our metrics and statistical tests fulﬁll the following criteria:
• A minimal number of conﬁguration parameters – to facilitate standardization as well as to minimize “researcher degrees of freedom" (where ﬂexibility may allow users to tune settings to produce more favorable results, leading to an inﬂated rate of false positives) (Simmons et al., 2011).
• Robust statistics, when possible.
Robust statistics are less sensitive to outliers and have more reliable performance for a wider range of distributions.
Robust statistics are especially important when applied to training performance, which tends to be highly non-Gaussian, making metrics such as variance and standard deviation inappropriate.
For example, training performance can often be bi-modal, with a concentration of points near the starting level and another concentration at the level of asymptotic performance.
• Invariance to sampling frequency – results should not be biased by the frequency at which an algorithm was evaluated during training.
See Section 2.5 for further discussion.
• Enable meaningful statistical comparisons on the metrics, while making minimal assumptions about the distribution of the results.
We thus designed statistical procedures that are non-parametric (Section 4).
Median Performance
Dispersion across Time
Long-term Risk across Time Short-term Risk across Time
Dispersion across Runs
OpenAI Gym -- During Training
Risk across Runs n o r m a l
i
z
e d m e a n r a n k n o r m a l i
z
e d m e a n r a n k
Median Performance Dispersion of Fixed Policy
Risk of Fixed Policy
[Figure]
2. M ETRIC D EFINITIONS
Dispersion across Time (DT): IQR across Time To measure dispersion across time (DT), we want to isolate higher-frequency variability, rather than capturing longer-term trends.
We do not want our metrics to be inﬂuenced by positive trends of improvement during training, which are in fact desirable sources of variation in the training performance.
Therefore, we apply detrending before computing dispersion metrics: Inter-quartile range (IQR) within a sliding window along the training curve (after detrending).
For detrending, we used differencing (i.e. y t (cid:48) =
y t − y t − 1 ).
Short-term Risk across Time (SRT): CVaR on Differences For this measure, we wish to measure the most extreme short-term drop over time.
To do this, we apply CVaR to the changes in performance
[Figure]
n o r m a l
i z e d m e a n r a n k n o r m a l i z e d m e a n r a n k
[Figure]
Runs
Atari -- After Learning
Median Performance Dispersion of Fixed Policy
Risk of Fixed Policy n o r m a l
i
z
e d m e a n r a n k from one evaluation point to the next.
I.e., in Eq. 1, X represents the differences from one evaluation time-point to the next.
We ﬁrst compute the time-point to time-point differences on each training run.
These differences are normalized by the distance between time-points, to ensure invariance to evaluation frequency (see Section 2.5).
Then, we obtain the distribution of these differences, and ﬁnd the α -quantile.
Finally, we compute the expected value of the distribution below the α -quantile.
This gives us the worst-case expected drop in performance during training, from one point of evaluation to the next.
Long-term Risk across Time (LRT): CVaR on Drawdown For this measure, we would also like to be able to capture whether an algorithm has the potential to lose a lot of performance relative to its peak, even if on a longer timescale, e.g. over an accumulation of small drops.
For this measure, we apply CVaR to the Drawdown .
The Drawdown at time T is the drop in performance relative to the highest peak so far, and is another measure borrowed from economics (Chekhlov et al., 2005).
I.e. Drawdown T =
R T − max t< = T R t .
Like the SRT metric, the LRT can capture unusually large short-term drops in performance, but can also capture unusually large drops that occur over longer timescales.
Dispersion across Runs (DR): IQR across Runs Unlike the rest of the metrics described here, the dispersion across training runs has previously been used to characterize performance (e.g. Duan et al.
; Islam et al.
; Bellemare et al.
; Fortunato et al.
Nagarajan et al.
This is usually measured by taking the variance or standard deviation across training runs at a set of evaluation points.
We build on the existing practice by recommending ﬁrst performing low-pass ﬁltering of the training data, to ﬁlter out high-frequency variability within runs (this is instead measured using Dispersion across Time, DT).
We also replace variance or standard deviation with robust statistics like IQR.
Risk across Runs (RR): CVaR across Runs In order to measure Risk across Runs (RR), we apply
CVaR to the ﬁnal performance of all the runs.
This gives a measure of the expected performance of the worst runs.
Dispersion across Fixed-Policy Rollouts (DF): IQR across Rollouts When evaluating a ﬁxed policy, we are interested in variability in performance when the same policy is rolled out multiple times.
To compute this metric, we simply compute the IQR on the performance of the rollouts.
Risk across Fixed-Policy Rollouts (RF): CVaR across Rollouts This metric is similar to DF, except that we apply CVaR on the rollout performances.
2. I NVARIANCE TO FREQUENCY OF EVALUATION
Different experiments and different tasks may produce evaluations at different frequencies during training.
Therefore, the reliability metrics should be unbiased by the choice of evaluation frequency.
As long as there are no cyclical patterns in performance, the frequency of evaluation will not bias any of the metrics except Long-Term Risk across Time (LRT).
For all other metrics, changes in the frequency of evaluation will simply lead to more or less noisy estimates of these metrics.
For LRT, comparisons should only be made if the frequency of evaluation is held constant across experiments.
R ECOMMENDATIONS FOR REPORTING METRICS AND PARAMETERS
Whether evaluating an algorithm for practical use or for research, we recommend evaluating all of the reliability metrics described above.
Each metric measures a different aspect of reliability, and can help pinpoint speciﬁc strengths and weaknesses of the algorithm.
Evaluating the metrics is easy with the open-source Python package that will be released soon.
Reporting parameters.
Even given our purposeful efforts to minimize the number of parameters in the reliability metrics, a few remain to be speciﬁed by the user that can affect the results, namely: window size (for Dispersion across Time), frequency threshold for low-pass and high-pass ﬁltering (Dispersion across Time, Dispersion across Runs), evaluation frequency (only for Long-term Risk across Time), and length of training runs.
Therefore, when reporting these metrics, these parameters need to be clearly speciﬁed, and must also be held constant across experiments for meaningful comparisons.
The same is true for any other parameters that affect evaluation, e.g., the number of roll-outs per evaluation, the parameters of the environment, whether on-line or off-line evaluation is used, and the random seeds chosen.
Collapsing across evaluation points.
Some of the in-training reliability metrics (Dispersion across
Runs, Risk across Runs, and Dispersion across Time) need to be evaluated at multiple evaluation points along the training runs.
Since it is useful to obtain a small number of values to summarize each metric, we recommend dividing the training run into "time frames" (e.g. beginning, middle, and end), and collapsing across all evaluation points within each time frame.
Normalization by performance.
Different algorithms can have vastly different ranges of performance even on the same task, and variability in performance tends to scale with actual performance.
Thus, we normalize our metrics in post-processing by a measure of the range of performance for each algorithm.
For "during training" reliability, we recommend normalizing by the median range of performance, which we deﬁne as the p P 9 5 − p t =0 , where p P 9 5 is the 95th percentile and p t =0 is the starting performance.
For "after learning" reliability, the range of performance may not be available, in which case we use the median performance directly.
Ranking the algorithms.
Because different environments have different ranges and distributions of reward, we must be careful when aggregating across environments or comparing between environments.
Thus, if the analysis involves more than one environment, the per-environment median results for the algorithms is ﬁrst converted to ranks, by ranking all algorithms within each task.
To summarize the performance of a single algorithm across multiple tasks, we compute the mean ranking across tasks.
Per-environment analysis.
The same algorithm can have different patterns of reliability for different environments.
Therefore, we recommend inspecting reliability metrics on a per-environment basis, as well as aggregating across environments as described above.
C ONFIDENCE I NTERVALS AND S TATISTICAL S IGNIFICANCE T ESTS FOR C OMPARISON 4. C ONFIDENCE INTERVALS
We assume that the metric values have been converted to mean rankings, as explained in section 3.
To obtain conﬁdence intervals on the mean rankings for each algorithm, we apply bootstrap sampling on the runs, by resampling runs with replacement (Efron & Tibshirani, 1986).
For metrics that are evaluated per-run (e.g. Dispersion across Time), we can resample the metric values directly, and then recompute the mean rankings on each resampling to obtain a distribution over the rankings; this allow us to compute conﬁdence intervals.
For metrics that are evaluated across-runs, we need to resample the runs themselves, then evaluate the metrics on each resampling, before recomputing the mean rankings to obtain a distribution on the mean rankings.
4. S IGNIFICANCE T ESTS FOR C OMPARING ALGORITHMS
Commonly, we would like to compare algorithms evaluated on a ﬁxed set of environments.
To determine whether any two algorithms have statistically signiﬁcant differences in their metric rankings, we perform an exact permutation test on each pair of algorithms.
Such tests allow us to compute a p-value for the null hypothesis (probability that the methods are in fact indistinguishable on the reliability metric).
We designed our permutation tests based on the null hypothesis that runs are exchangeable across the two algorithms being compared.
In brief, let A and B be sets of performance measurements for algorithms a and b .
Let Metric ( X ) be a reliability metric, e.g. the inter-quartile range across runs, computed on a set of measurements X .
MetricRanking ( X ) is the mean ranking across tasks on X , compared to the other algorithms being considered.
We compute test statistic
[Equation]
Next we compute the distribution for s MetricRanking under the null hypothesis that the methods are equivalent, i.e. that performance measurements should have the same distribution for a and b .
We do this by computing random partitions A (cid:48) , B (cid:48) of { A ∪ B } , and computing the test statistic s MetricRanking ( A (cid:48) , B (cid:48) ) on each partition.
This yields a distribution for s MetricRanking (for sufﬁciently many samples), and the p-value can be computed from the percentile value of s MetricRanking ( A, B ) in this distribution.
As with the conﬁdence intervals, a different procedure is required for per-run vs across-run metrics.
Please see Appendix C for diagrams illustrating the permutation test procedures.
When performing pairwise comparisons between algorithms, it is critical to include corrections for multiple comparisons.
This is because the probability of incorrect inferences increases with a greater number of simultaneous comparisons.
We recommend using the Benjamini-Yekutieli method, which controls the false discovery rate (FDR), i.e., the proportion of rejected null hypotheses that are false.
4. R EPORTING ON STATISTICAL TESTS
It is important to report the details of any statistical tests performed, e.g. which test was used, the signiﬁcance threshold, and the type of multiple-comparisons correction used.
A NALYSIS OF R ELIABILITY FOR C OMMON A LGORITHMS AND E NVIRONMENTS
In this section, we provide examples of applying the reliability metrics to a number of RL algorithms and environments, following the recommendations described above.
5. C ONTINUOUS CONTROL ALGORITHMS ON O PEN AI G YM
We applied the reliability metrics to algorithms tested on seven continuous control environments from the Open-AI Gym (Greg Brockman et al., 2016) run on the MuJoCo physics simulator (Todorov et al., 2012).
We tested REINFORCE (Sutton et al., 2000), DDPG (Lillicrap et al., 2015), PPO (Schulman et al., 2017), TD3 (Fujimoto et al., 2018), and SAC (Haarnoja et al., 2018) on the following Gym environments: Ant-v2, HalfCheetah-v2, Humanoid-v2, Reacher-v2, Swimmer-v2, and Walker2d-v2.
We used the implementations of DDPG, TD3, and SAC from the TF-Agents library (Guadarrama et al., 2018).
Each algorithm was run on each environment for 30 independent training runs.
We used a black-box optimizer (Golovin et al., 2017) to tune selected hyperparameters on a per-task basis, optimizing for ﬁnal performance.
The remaining hyperparameters were deﬁned as stated in the corresponding original papers.
See Appendix E for details of the hyperparameter search space and the ﬁnal set of hyperparameters.
During training, we evaluated the policies at a frequency oftraining steps.
Each algorithm was run for a total of two million environment steps.
For the “online” evaluations we used the generated training curves, averaging returns over recent training episodes collected using the exploration policy as it evolves.
The raw training curves are shown in Appendix
D. For evaluations after learning on a ﬁxed policy, we took the last checkpoint from each training run as the ﬁxed policy for evaluation.
Each of these policies was then evaluated for 30 roll-outs, where each roll-out was deﬁned as 1000 environment steps.
5. D ISCRETE CONTROL : DQN VARIANTS ON A TARI
We also applied the reliability metrics to the training data released as part of the Dopamine package (Castro et al., 2018).
The data comprise the training runs of four RL algorithms, each applied to
Atari games.
The RL algorithms are: DQN (Mnih et al., 2015), Implicit Quantile (IQN) (Dabney et al., 2018), C51 (Bellemare et al., 2017), and a variant of Rainbow implementing the three most important components (Hessel & Modayil, 2018).
The algorithms were trained on each game fortraining runs.
Hyper-parameters follow the original papers, but were modiﬁed as necessary to follow
Rainbow (Hessel & Modayil, 2018), to ensure apples-to-apples comparison.
See Appendix E for the hyperparameters.
During training, the algorithms were evaluated in an “online” fashion every 1 million frames, averaging across the training episodes as recommended for evaluations on the ALE (Machado et al., 2018).
Each training run consisted of approximately 200 million Atari frames (rounding to the nearest episode boundary every 1 million frames).
For evaluations after learning on a ﬁxed policy (“after learning”), we took the last checkpoint from each training run as the ﬁxed policies for evaluation.
We then evaluated each of these policies for 125,000 environment steps.
5. P ARAMETERS FOR RELIABILITY METRICS , CONFIDENCE INTERVALS , AND STATISTICAL TESTS
For the MuJoCo environments, we applied a sliding window of 100000 training steps for Dispersion across Time.
For the Atari experiments, we used a sliding window size of 25 on top of the evaluations for the Dispersion across Time.
For metrics with multiple evaluation points, we divided each training run into 3 time frames and averaged the metric rankings within each time frame.
Because the results were extremely similar for all three time frames, we here report just the ﬁnal time frames.
Statistical tests for comparing algorithms were performed according to the recommendations in section 4.
We used pairwise permutation tests using 10,000 permutations per test, with a signiﬁcance threshold of 0.05 and Benjamini-Yekutieli multiple-comparisons correction.
5. M EDIAN PERFORMANCE
The median performance of an algorithm is not a reliability metric, but it is interesting to see side-byside with the reliability metrics.
For analyzing median performance for the DQN variants, we used the normalization scheme of (Mnih et al., 2015), where an algorithm’s performance is normalized against a lower baseline (e.g. the performance of a random policy) and an upper baseline (e.g. the performance of a human): P [Equation]
=
[Equation]
Median performance was not normalized for the continuous control algorithms.
5. R ESULTS
The reliability metric rankings are shown in Fig.
1 for the MuJoCo results.
We see that, according to
Median Performance during training, SAC and TD3 have the best performance and perform similarly well, while REINFORCE performs the worst.
However, SAC outperforms TD3 on all reliability metrics during training.
Furthermore, both SAC and TD3 perform relatively poorly on all reliability metrics after learning, despite performing best on median performance.
The reliability metric rankings are shown in Fig.
2 for the Atari results.
Here we see a similar result that, even though Rainbow performs signiﬁcantly better than IQN in Median Performance, IQN performs numerically or signiﬁcantly better than Rainbow on many of the reliability metrics.
The differing patterns in these metrics demonstrates that reliability is a separate dimension that needs to be inspected separately from mean or median performance – two algorithms may have similar median performance but may nonetheless signiﬁcantly different reliability, as with SAC and TD3 above.
Additionally, these results demonstrate that reliability along one axis does not necessarily correlate with reliability on other axes, demonstrating the value of evaluating these different dimensions so that algorithms can be compared and selected based on the requirements of the problem at hand.
To see metric results evaluated on a per-environment basis, please refer to Appendix F. Rank order of algorithms was often relatively consistent across the different environments evaluated. However, different environments did display different patterns across algorithms. For example, even though SAC showed the same or better Dispersion across Runs for most of the MuJoCo environments evaluated, it did show slightly worse Dispersion across Runs for the HalfCheetah environment (Fig 7a).
This kind of result emphasizes the importance of inspecting reliability (and other performance metrics) on a per-environment basis, and also of evaluating reliability and performance on the environment of interest, if possible.
C ONCLUSION
We have presented a number of metrics, designed to measure different aspects of reliability of RL algorithms.
We motivated the design goals and choices made in constructing these metrics, and also presented practical recommendations for the measurement of reliability for RL.
Additionally, we presented examples of applying these metrics to common RL algorithms and environments, and showed that these metrics can reveal strengths and weaknesses of an algorithm that are obscured when we only inspect mean or median performance.
A A SSUMPTIONS AND D EFINITIONS
Reinforcement Learning algorithms vary widely in design, and our metrics are based on certain notions that should span the gamut of RL algorithms.
Policy A policy π Θ ( a i | s i ) is a distribution over actions a i given a current (input) state s i .
We assume policies are parameterized by a parameter Θ .
Agent An agent is deﬁned as a distribution over policies (or equivalently a distribution over parameters Θ ).
In many cases, an agent will be a single policy but for population-based RL methods, the agent is a discrete set of policies.
Window A window is a collection of states over which the agent is assumed to have small variation.
A window could be a sequence of consecutive time steps for a sequential RL algorithm, or a collection of states at the same training step of a distributed RL algorithm with a parameter server (all agents share Θ ).
Performance The performance of an agent is the mean or median per-epoch reward from running that agent.
If the agent is a single policy, then the performance p ( π Θ ) is the mean or median per-epoch reward for that agent.
If the agent is a distribution D (Θ) of policies, then the performance is the median of p ( π Θ ) with Θ ∼ D .
Training Run A training run is a sequence of updates to the agent D (Θ) from running a reinforcement learning algorithm.
It leads to a trained agent D final (Θ) .
Multiple training runs share no information with each other.
We cannot directly measure performance since it is a statistic across an inﬁnite sample of evaluation runs of an agent.
Instead we use windows to compute sample medians to approximate performance.
B D ETRENDING BY DIFFERENCING
Typically, de-trending can be performed in two main ways (Nelson & Plosser, 1982; Hamilton, 1994).
Differencing (i.e. y t (cid:48) =
y t − y t − 1 ) is more appropriate for difference-stationary (DS) processes (e.g. a random walk: y t
=
y t − 1 + b + (cid:15) t ), where the shocks (cid:15) t accumulate over time.
For trend-stationary (TS) processes, which are characterized by stationary ﬂuctuations around a deterministic trend, e.g. y t = a + b ∗ t + (cid:15) t , it is more appropriate to ﬁt and subtract that trend.
We performed an analysis of real training runs and veriﬁed that the data are indeed approximately
DS, and that differencing does indeed remove the majority of time-dependent structure.
For this analysis we used the training runs on Atari as described in 5.2.
Before differencing, the Augmented
Dickey-Fuller test (ADF test, also known as a difference-stationarity test; Said E. Said & David A.
Dickey (1984)) rejects the null hypothesis of a unit root on only 72% of the runs; after differencing, the ADF test rejects the null hypothesis on 92% of the runs (p-value threshold 0.05).
For the ADF test, the rejection of a unit root (of the autoregressive lag polynomial) implies the alternate hypothesis, which is that the time series is trend-stationary.
Therefore, our training curves are better characterized as an accumulation of shocks, i.e. as DS processes, rather than as mean-reverting TS processes.
They are not actually purely DS because the shocks (cid:15) t are not stationary over time, but because we compute standard deviation within sliding windows, we can capture the non-stationarity and change in variability over time.
Thus, we chose to detrend using differencing.
As a further note in favor of detrending by differencing, it is useful to observe that the standard deviation is deﬁned relative to a mean, as σ = (cid:112) E
[( X − µ ) 2 ] .
On the raw data (without differencing), the standard deviation would be deﬁned relative to µ as average performance, so that any improvements in performance are included in that computation of variance.
On the other hand, if we compute variance on the 1st-order differences, we are using a µ that represents the average change in performance, which is a more reasonable baseline to compute variance against, when we are concerned with the variability of those changes.
A ﬁnal beneﬁt of differencing is that it is parameter-free.
C I LLUSTRATIONS OF P ERMUTATION T EST P ROCEDURES
We illustrate the procedure for computing permutation tests to compare pairs of algorithms on a speciﬁed metric, in Figs.
3 (for per-run metrics) and 4 (for across-run metrics).
D R AW TRAINING CURVES FOR O PEN AI M U J O C O TASKS
In Figure 5, we show the raw training curves for the TF-Agents implementations of continuouscontrol algorithms, applied to the OpenAI MuJoCo tasks.
These are compared against baselines from the literature, where available (DDPG and TD3: Fujimoto et al.
(2018), PPO: Schulman et al.
SAC: Haarnoja et al.
E H YPERPARAMETER SETTINGS
For the continuous control experiments, hyperparameters were chosen on a per-environment basis according to the black-box optimization algorithm described in Golovin et al.
The hyperparameter search space is shown in Table 2.
For the discrete control experiments, hyperparameter selection is described in (Castro et al., 2018).
Hyperparameters are shown in Table 8, duplicated for reference from https://github.com/google/dopamine/tree/master/baselines.
[Table]
F P ER - TASK METRIC RESULTS
Metric results are shown on a per-task basis in Figs.
6 to 8 for the OpenAI Gym MuJoCo tasks, and
Figs.
9 to 23 for the Atari environments.
Note that because we are no longer aggregating across tasks in this analysis, we do not need to convert the metric values to rankings. Metric values Metric rankings
[Figure]
[Figure]
[Figure]
Raw values
Evaluate per-run metrics for each run e.g. 3 runs per (task, algo) algoA algoB algoC task task task permuted null distribution actual difference 1, 6,5, 8,3, 2,7, 5,6, 9,2, 1,3, 7,5, 6,8, 1,
Permuted rankings tasks
[Figure]
Comparing algorithms on per
[Figure]
metrics
3 algorithms, 3 tasks, and 3 runs per (task, algo) pair.
To compute the difference in average rankings for two algorithms, follow the gray arrows.
To compute a null distribution of difference in average rankings (by permuting the runs), follow the blue arrows a number of times (e.g. 1,000 times).
Once the null distribution has been computed, the actual value of the difference can be compared with the null distribution to obtain a p-value.
[Table]
Metric values
[Table]
l
[Table]
r i t h m
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a l go r i t
h m s
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[Table]
r i t
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[Table] [Figure] [Table] [Table]
[Table] [Table] [Table]
[Table]
[Figure] [Figure] [Figure] [Figure]