Comparing Traditional and Reinforcement-Learning Methods for Energy Storage Control

Elinor Ginzburg; Itay Segev; Sarah Keren; Yoash Levron

REVIEW 6 major objections 5 minor 25 references

Comparing Traditional and Reinforcement-Learning Methods for Energy Storage Control

T0 review · 6 major / 5 minor · reviewed 2026-08-07 · deepseek-v4-flash

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Pith's one-line read When the physical model is known, classical optimization yields far better storage-control policies than model-free reinforcement learning, and the simplest ideal-storage case is the one RL handles worst.

desk verdict Useful three-case comparison of classical vs RL storage control, but the LS evidence that RL can match classical rests on an inconsistent baseline formulation. read the letter →

arxiv 2506.00459 v1 pith:NQSQKB7K submitted 2025-05-31 cs.LG cs.AI

Elinor Ginzburg , Itay Segev , Yoash Levron , Sarah Keren This is my paper

classification cs.LGcs.AI MSC 68T0549K1590C39

keywords energystoragecontrolmicrogridreinforcementlearningoptimalmodel-freepolicyshortestpathPontryaginminimumprinciplestateofcharge

verification ladder T0 review T1 audit T2 compute T3 formal

The pith

A machine-rendered reading of the paper's core claim, the machinery that carries it, and where it could break.

The reading

This paper asks how much performance is lost when a model-free reinforcement-learning policy replaces a traditional optimal-control solution for operating a microgrid battery. It compares three settings of increasing complexity—ideal storage, lossy storage, and lossy storage with quadratic transmission losses—using shortest-path search, Pontryagin's minimum principle, and dynamic programming as the classical baselines, and SAC, PPO, and TD3 as the learning baselines. The central claim is that when the physical model is known, classical optimization yields far better results than statistical learning, and that RL can be comparable in some lossy cases but not in the simplest ideal-storage case. The paper matters because it gives energy and AI researchers a concrete picture of where generative RL policies pay off and where they do not.

What carries the argument

The comparison is carried by paired formulations of the same microgrid. Classically, the ideal-storage problem is posed as a shortest-path search over discretized generated-energy states $E_g(t)$, with edge weights equal to the convex fuel cost $f(P_g)$; the lossy-storage problem is solved with Pontryagin's minimum principle on storage power $P_s$ with a penalty $c(E_s)$ for violating capacity; and the transmission-loss problem is solved by discretized dynamic programming. The RL side recasts each case as an MDP with state (state of charge, hour, net load), action equal to energy added to the battery, and reward $-f(P_g)$, trained with SAC, PPO, or TD3. The load-bearing mechanism is the normalized MSE between the RL policy and the classical policy over the same 100-episode test set, which converts "how different are the policies" into the paper's headline performance-loss measure.

What would settle it

Re-run Case Study II with the classical baseline computed from the stated objective $\int_0^T f(P_g(t))\,dt$ and an explicit power balance $P_s(t)=P_g(t)-P_L(t)$ (or its lossy equivalent); if PPO and TD3 no longer show near-zero normalized MSE against this baseline, the paper's lossy-storage result is an artifact of the mismatched objective.

Watch

Extended reading notes

Core claim

On the paper's own terms, the discovery is that the value of knowing the physical model is large and unevenly distributed across problem difficulty. In the ideal-storage case, where the only constraint on the battery is its capacity, none of the three RL methods learned a policy close to the shortest-path optimum; the normalized MSE to the classical policy was largest there. In the lossy-storage case, PPO and TD3 produced policies nearly identical to the Pontryagin-based baseline, and in the transmission-loss case PPO came closest. The authors interpret this as evidence that classical methods should be preferred when a model of the microgrid is available, and that embedding storage and transmission dynamics in the simulator can sometimes substitute for an analytical solution, but model-free RL still needs retraining for every new scenario and cannot be assumed to transfer from one household to another.

Load-bearing premise

The paper's comparison stands or falls on treating the classical optimization baselines as the true optimal policies, which in the lossy-storage case requires a power-balance relation between generator, load, and storage power that the paper never explicitly states.

Editorial extensions

If this is right

If the physical model and load forecast are known, classical optimization is the safer choice; RL should not be assumed to close the gap.
The simplest environment is not necessarily the easiest for RL: the ideal-storage case produced the worst relative performance, so problem simplicity cannot be used as a proxy for learning difficulty.
In the lossy-storage setting, model-free RL (PPO and TD3) can closely match an optimal control baseline, so the lossy case is a plausible target for data-driven control.
A generative RL policy that works for one microgrid cannot be assumed to transfer to another load profile without retraining, whereas classical solutions work per instance.
Embedding accurate storage and transmission dynamics in the training simulator can substitute for an analytical solution in some cases, pointing toward model-based or hybrid approaches.

Reading between the lines

Editorial extensions of the paper, not claims the author makes directly.

Editorial inference: a likely reason for the ideal-storage failure is that lossless dynamics create many near-tied trajectories, so the reward signal is too flat for model-free exploration; one could test this by adding tiny charging and discharging losses and checking whether RL immediately improves.
Editorial inference: the practical takeaway is to reserve RL for populations of heterogeneous microgrids or for settings where the model is unknown, and to use classical optimal control whenever a per-instance model and forecast exist.
Editorial inference: if the missing power-balance relation in Case Study II is not the assumed $P_s = P_g - P_L$, then the classical baseline solves a different objective and the near-zero losses reported for PPO and TD3 in the lossy case would need to be recomputed.

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Editorial analysis

A structured set of objections, weighed in public.

Desk editor's note, referee report, and a circularity audit.

Desk Editor's Note

read the letter

Short version: this is a legible, honest comparison of shortest-path/Pontryagin/DP baselines against SAC/PPO/TD3 on three micro-grid storage cases. The IS result — RL failing on the simplest ideal-storage case — is genuinely counter-intuitive and worth explaining. The LS claim, that PPO and TD3 almost match the classical solution, is the part I do not trust.

What is new: nobody has laid out this particular three-case comparison for storage control with both classical and model-free RL, including explicit MDP formulations. That is useful for practitioners. The formulations for IS and LT are clear enough to work from, and the IS failure mode is a real observation, even if the paper does not fully explain it.

The soft spots are concentrated in Case Study II. Equation (5) minimizes the integral of f(P_s(t)) dt, but the stated objective everywhere else is the integral of f(P_g(t)) dt. With the natural balance P_g = P_s + P_L, the integrand should be f(P_s + P_L). The optimality condition in Eq. (7) contains P_L, which cannot come from the problem as Eq. (5) is written. Either Eq. (5) is a typo and the reported near-zero LS errors come from solving the corrected problem, or the baseline solves a different problem and the "RL can be comparable in certain cases" conclusion is unsupported. The paper needs to state the power-balance relation explicitly and rerun or confirm the LS numbers.

Other issues are real but minor by comparison: normalized MSE is never defined, there are no error bars or variance across seeds, and the dataset description says both 100K and 10K episodes. The code and data are promised in the supplementary but not present in the preprint. The self-citations to the authors' own baselines are fine; those are external solvers with stated assumptions.

The qualitative takeaway — with a perfect model, classical optimization beats statistical learning, and with enough data RL can be comparable but not everywhere — is plausible and consistent with the IS and LT results. But the LS evidence is the load-bearing example for "comparable in certain cases," and right now that evidence is not established.

This paper is for practitioners who want a benchmark-style comparison of off-the-shelf RL against classical solvers. I would send it to review with a request for major revision, not desk-reject: the comparison is worth having, and the fixes are within reach. A careful referee should demand the corrected LS derivation, a definition of the metric, and the code.

Referee Report

6 major / 5 minor

Summary. The paper compares classical optimal-control methods (shortest path, Pontryagin's minimum principle, dynamic programming) with model-free reinforcement learning methods (SAC, PPO, TD3) for controlling a storage device in a simplified microgrid. Three case studies of increasing complexity are considered: ideal storage, lossy storage, and lossy storage with transmission losses. The empirical evaluation reports a 'normalized MSE' between RL and classical policies on a test set of 100 episodes, with the stated conclusions that classical methods are far superior when the physical model is known, that RL results can be comparable in some lossy settings but not in the ideal-storage case, and that model-based or model-informed approaches are preferable. The manuscript also provides formulations intended to make the storage-control problem accessible to AI researchers.

Significance. If the empirical comparison were fully supported, the paper would be a useful benchmark for the energy-storage RL community: it evaluates standard off-the-shelf RL algorithms against classical baselines on a hierarchy of controlled microgrid models and quantifies the generalization gap. Strengths include the explicit formulation of three increasing-complexity use cases, the use of standard RL libraries, and the attempt to compare generative policies with problem-specific optimizers. However, the central quantitative claims are currently undermined by an internal inconsistency in the Case Study II baseline, an undefined evaluation metric, missing statistical variability, and contradictory dataset statements. The paper's main conclusion is plausible but not yet established by the reported evidence.

major comments (6)

[Case-Study II: Lossy Storage Devices, Eq. (5) and Eq. (7)] Eq. (5) minimizes ∫ f(P_s(t)) dt, but the problem stated in Eq. (1) and the RL reward minimize ∫ f(P_g(t)) dt. With the power-balance relation P_s = P_g − P_L from Case Study I, the correct integrand is f(P_s(t) + P_L(t)), not f(P_s(t)). As printed, Eq. (5) defines a different optimization problem from the one the paper claims to solve. Moreover, the optimality condition in Eq. (7) contains P_L in the expression for \hat P_s; this cannot be a necessary condition for the cost in Eq. (5), since P_L does not appear there. The appearance of P_L suggests that the baseline actually solves the corrected objective. If Eq. (5) is implemented literally, the lossy-storage comparisons in Table 1 and the claim that RL can be comparable in some cases are unsupported. If it is a typo, the manuscript must state the intended objective, provide the full Pontryagin derivation, and confirm that the reported numbers correspond to the corrected problem. No code or derivation is supplied in the preprint to resolve this.
[Empirical Evaluation, Table 1] The normalized MSE reported in Table 1 is never defined. It is unclear what quantity is averaged, what the reference denominator is, and whether the error is computed on per-step generation power, per-episode cost, or something else. Without this definition, the values 1.00, 0.83, 0.027, and 0.19 cannot be interpreted, and the main quantitative evidence for the paper's conclusions is not checkable. The manuscript should define the metric explicitly, report absolute expected costs for both classical and RL methods, and include standard errors or confidence intervals.
[Dataset] The dataset section states both 'We examined 100K episodes' and 'extracted from the dataset (with its 10K episodes) a test set of 100 episodes.' These numbers cannot both be correct. The distinction matters because the conclusion that RL results are comparable 'when using large amounts of data' depends on the actual number of training episodes. Please clarify the total number of episodes, the training/validation/test split, and the number of environment steps used for RL training.
[Results, Table 1 and Figure 3] All quantitative comparisons are based on a single evaluation of a single training run per RL algorithm, with no error bars, seeds, or statistical tests. RL training is stochastic, and the observed normalized MSE values such as 0.027 vs. 1.00 could easily be within run-to-run variability. The single-day policy plots in Figure 3 are anecdotal. The manuscript should report means and standard deviations over multiple seeds, and if claiming that PPO/TD3 match the classical baseline in the lossy-storage case, provide a statistical basis for that claim.
[Case-Study III, Eqs. (9)-(10)] The terminal constraint E(T)=0, which appears in Eqs. (2) and (5), is missing from the Case Study III formulation: Eq. (9) has only E(0)=0 and Eq. (10) has only E_0=0. Without a terminal condition, the dynamic-programming baseline solves a different horizon-end problem and may deplete the storage at the final interval, which is not comparable to the previous case studies. Additionally, the dynamic programming algorithm used to solve Eq. (10) is not described (no grid resolution, discretization of the energy state, or convergence criterion), so the optimality of the LT baseline is not established. The missing terminal constraint and the DP implementation details should be supplied.
[Case-Study I, Solution Approaches] The Dijkstra baseline is optimal only on the discretized graph, but the manuscript does not report the discretization resolution of the energy variable. It says the space is 'transferred into discrete points by grid-based uniform discretization with N=T possible states at each time t,' but N is the number of time steps, not the number of energy levels. If the energy grid is coarse, the classical baseline is suboptimal and the conclusion that classical methods are 'far superior' in the ideal-storage case may be partly an artifact of the discretization. Please report the number of energy levels per time step and demonstrate convergence of the baseline as the grid is refined.

minor comments (5)

[Results, Figure 3] The text refers to 'T3D' in the discussion of the lossy-storage case; this should be 'TD3'.
[Case-Study I, RL formulation] The action set is written as A={a=∆E, 0≤∆E≤E_L+E_max}, which does not depend on the current state of charge or on the remaining capacity. The valid charge action should be bounded by both the current SOC and the battery capacity, e.g., max(−E_s, ...) ≤ ∆E ≤ min(E_max−E_s, ...). This is likely a notation error, but it makes the MDP formulation imprecise.
[Abstract and Introduction] The abstract describes the third use case as 'lossy storage devices with convex transmission losses,' while the introduction calls it 'lossy storage devices with non-convex cost functions.' The body of the paper should state clearly whether the transmission-loss setting is convex or non-convex, since this affects the choice of solution method.
[Dataset] There is a typo in 'pyhton implementation'; also, the code and datasets are said to be in the supplementary materials but are not included in the preprint, so the experiments cannot be reproduced from the current version.
[Case-Study III, Eq. (8)-(9)] The notation switches between P and P_g without clear definition in Eqs. (8)-(9). In particular, Eq. (8) uses P for the load-side power, while Eq. (9) uses P(t) for the storage power in the constraint dE/dt = η(E(t))·P(t). Please disambiguate these symbols.

Circularity Check

0 steps flagged · score 0.0 of 10

No circularity: the comparison is a held-out empirical benchmark against implemented classical solvers; the main caveat is baseline correctness, not circularity.

full rationale

The manuscript compares classical optimal-control baselines (Dijkstra shortest path, Pontryagin, dynamic programming) against model-free RL policies (SAC, PPO, TD3) on three storage-control cases. The central result is an empirical comparison: classical solutions are computed by implementing published algorithms (Levron and Shmilovitz 2010; Zargari, Levron, and Belikov 2019) and RL policies are trained on a training split and evaluated on a held-out test split. No fitted parameter is renamed as a prediction; hyperparameters are tuned on a separate validation set and fixed before evaluation. The self-citations to prior work by Levron and coauthors supply the baseline algorithms and the data simulator, but these are external, code-reproduced mathematical methods with stated assumptions, not results that include the paper's comparison outcome. The RL reward is the negative of the same cost function minimized by the classical methods, which is a shared task definition rather than a circular reduction. Therefore no claimed prediction reduces by construction to an input. The reviewer's concern about Case Study II (Eq. (5) minimizing ∫ f(P_s) while the stated objective Eq. (1) is ∫ f(P_g)) is a potential baseline-correctness flaw, but it is not an instance of circularity: it does not make the output equivalent to the input; it makes the baseline possibly solve a different problem. Score 0 for circularity.

Assumptions & free parameters 2 free parameters · 5 assumptions · 0 invented entities

The comparison rests on several modeling choices inherited from prior work: strictly convex generation cost, deterministic load and PV knowledge for baselines, a quadratic penalty to enforce battery bounds in Case Study II, and a short-line quadratic-loss approximation. The only hand-tuned parameter explicitly introduced by the paper is the penalty coefficient Q, and the RL hyperparameters are tuned on a 10-episode validation set. No invented entities are added; the micro-grid components are standard.

free parameters (2)

Q (capacity penalty coefficient) = not reported
Introduced in Eq (6) to enforce battery bounds by penalizing E_s below 0 and above E_max in the Pontryagin baseline; the text says a large Q implies the bounds, but no value or sensitivity study is given.
RL hyperparameters per method (learning rates, discount factors, network sizes) = not reported in preprint
Tuned in preliminary tests on a 10-episode validation set and then fixed across case studies; the actual values and tuning protocol are promised in supplementary material but absent from the arXiv v1.

assumptions (5)

domain assumption The generation cost function f is twice differentiable and strictly convex; experiments use f(x)=x^2.
Invoked in the model description and used by the shortest-path and Pontryagin baselines and by the RL reward function.
domain assumption Classical baselines have exact, deterministic knowledge of the load and PV profiles over the horizon.
The Dijkstra solution requires a deterministic P_L(t); this is stated in the Solution Approaches for Case Study I and underlies the comparison, since RL samples episodes from a distribution instead.
ad hoc to paper Battery capacity constraints can be replaced by the quadratic penalty c(E_s) with sufficiently large Q without changing the optimum.
Eq (6) introduces c(E_s) and the text says a large Q implicitly guarantees the bound, but no proof or sensitivity analysis is provided.
domain assumption Short transmission lines satisfy |V| approximately equal to |V_g|, giving quadratic losses P_g approximately P plus (R/|V_g|^2)P^2.
Used to build the Case Study III objective; the paper cites Hobbs et al. (2008) and describes the model as an analytical model developed by the authors.
domain assumption The 100-episode test set drawn from the Chowdhury et al. simulator represents the load and PV distribution.
All reported errors are averaged over this set; the paper gives no details on how episodes were sampled, why 100 episodes is sufficient, or how the test and training split was made.

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Cite this review

Pith. "Pith review of Comparing Traditional and Reinforcement-Learning Methods for Energy Storage Control." pith.science (2026). https://pith.science/paper/NQSQKB7K

@misc{pith2026250600459,
  author       = {Pith},
  title        = {Pith review of: Comparing Traditional and Reinforcement-Learning Methods for Energy Storage Control},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/NQSQKB7K}},
  note         = {Machine review of arXiv:2506.00459}
}

read the original abstract

We aim to better understand the tradeoffs between traditional and reinforcement learning (RL) approaches for energy storage management. More specifically, we wish to better understand the performance loss incurred when using a generative RL policy instead of using a traditional approach to find optimal control policies for specific instances. Our comparison is based on a simplified micro-grid model, that includes a load component, a photovoltaic source, and a storage device. Based on this model, we examine three use cases of increasing complexity: ideal storage with convex cost functions, lossy storage devices, and lossy storage devices with convex transmission losses. With the aim of promoting the principled use RL based methods in this challenging and important domain, we provide a detailed formulation of each use case and a detailed description of the optimization challenges. We then compare the performance of traditional and RL methods, discuss settings in which it is beneficial to use each method, and suggest avenues for future investigation.

Figures

Figures reproduced from arXiv: 2506.00459 by the authors.

**Figure 2.** Average load [top] and PV generation [bottom] [PITH_FULL_IMAGE:figures/full_fig_p006_2.png] view at source ↗

**Figure 3.** Single day generation policy for the classical and RL approaches for the three study-cases. [PITH_FULL_IMAGE:figures/full_fig_p007_3.png] view at source ↗

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Reviewed August 7, 2026 · model on record in the stance chip above.

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, " * write output.state after.block = add.period write newline

ENTRY address archivePrefix author booktitle chapter edition editor eid eprint howpublished institution isbn journal key month note number organization pages publisher school series title type volume year label extra.label sort.label short.list INTEGERS output.state before.all mid.sentence after.sentence after.block FUNCTION init.state.consts #0 'before.a...

[2] [2]

write newline

" write newline "" before.all 'output.state := FUNCTION n.dashify 't := "" t empty not t #1 #1 substring "-" = t #1 #2 substring "--" = not "--" * t #2 global.max substring 't := t #1 #1 substring "-" = "-" * t #2 global.max substring 't := while if t #1 #1 substring * t #2 global.max substring 't := if while FUNCTION word.in bbl.in capitalize " " * FUNCT...

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Bui, V.-H.; Hussain, A.; and Kim, H.-M. 2019. Double deep Q -learning-based distributed operation of battery energy storage system considering uncertainties. IEEE Transactions on Smart Grid, 11(1): 457--469

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Chowdhury, N. R.; Ofir, R.; Zargari, N.; Baimel, D.; Belikov, J.; and Levron, Y. 2021. Optimal Control of Lossy Energy Storage Systems With Nonlinear Efficiency Based on Dynamic Programming and Pontryagin's Minimum Principle. IEEE Transactions on Energy Conversion, 36(1): 524--533

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Haarnoja, T.; Zhou, A.; Abbeel, P.; and Levine, S. 2018. Soft actor-critic: Off-policy maximum entropy deep reinforcement learning with a stochastic actor. In International conference on machine learning, 1861--1870. PMLR

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