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Withdrawn from ICLR 2027

Beyond Forecast Accuracy: Evaluating Neural Operators for Differentiable PDE Control

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Neural operators learn mappings between function spaces and are inexpensive to evaluate and differentiate, making them a natural choice of surrogate for controlling systems governed by partial differential equations (PDEs), where repeated numerical solves render online optimization expensive. Differentiable predictive control (DPC) exploits both properties: it trains a neural feedback policy offline by differentiating a control objective through surrogate rollouts, so deployment reduces to a single forward pass. The surrogate thus plays a dual role, predicting the consequences of actions and supplying the sensitivities that drive policy updates. Our framework trains a neural-operator surrogate on open-loop trajectories, freezes it, optimizes the policy through predicted closed-loop rollouts, and deploys it on the numerical solver. We compare Fourier, Recurrent, and Time-integrated DeepONet operators with single- and multi-step training on stabilization across linear, nonlinear, dispersive, and chaotic PDEs. We find that forecast accuracy alone is an insufficient proxy for controller quality: surrogates with comparable prediction errors can yield policies that differ by orders of magnitude in terminal tracking error. A policy-dependent transfer bound and a counterexample in which vanishing forward-model error coexists with persistent policy-gradient error formalize why this can occur. With multi-step training, DPC outperforms model-free reinforcement learning while avoiding the online cost of model predictive control.

Primary area:
learning on time series and dynamical systems
Keywords:
PDE Control, Neural Operators, Differentiable Predictive Control

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_KX8cOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
2
Soundness
1
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Paper summary

This paper investigates whether the open-loop forecast accuracy of neural operators reflects the quality of controllers trained through them using differentiable predictive control. The authors follow an existing DPC pipeline and compare four configurations: FNO₁, FNO₅, RNO, and TI-DON. The main finding is that forecasting and control performance rankings do not always agree, with FNO₅ being the most consistent configuration among those tested. The paper also presents a policy-dependent transfer error bound and a counterexample in which the forward-model error tends to zero while the policy-gradient error remains nonzero.

Critical strengths

The research question is relevant, and the evaluation separates useful quantities. Distinguishing predictive accuracy, control performance within the surrogate, and control performance on the numerical plant helps avoid equating better prediction with better downstream control.

Critical weaknesses
  1. The paper follows an existing DPC pipeline, so its value depends primarily on whether the comparative experiments yield reliable and generalizable new insights. However, all tasks involve one-dimensional periodic PDEs with fixed actuator layouts, constant reference targets, and low-dimensional families of initial conditions. The paper does not compensate for this limited scope with sufficiently in-depth controlled analysis and, overall, reads more like an exploratory comparison of configurations.

  2. Confounding factors in the key comparisons make attribution difficult. FNO₁ and FNO₅ differ not only in supervision horizon but also in learning-rate schedule, number of training epochs, training-window construction, and checkpoint-selection criterion. These results are therefore better interpreted as comparisons between specific configurations rather than sufficient evidence for the effects of the training mechanisms or the relative merits of the methods.

  3. The connection between theory and empirical results is weak, and one theoretical inference is unsupported. The transfer error bound and gradient counterexample explain why predictive accuracy cannot provide general control guarantees, but they do not adequately explain the observed performance differences across the models evaluated in this paper.

Questions for authors
  1. Controlled comparisons.

Do the main advantages of FNO₅ over FNO₁ persist when optimization settings, training budgets, and checkpoint-selection protocols are controlled? For PPO, which conclusions remain valid after aligning the training objectives and specifying comparable budgets?

  1. Mechanistic explanation.

For the TI-DON failure on Cahn–Hilliard, what evidence distinguishes the roles of Jacobian error, closed-loop distribution shift, and policy-optimization failure? Can a targeted controlled experiment support the proposed explanation, rather than relying only on associations observed at selected trained checkpoints?

2 comments

Thank you for the assessment. We clarify the benchmark’s physical scope and the rationale for the training configurations below.

Benchmark scope. The six PDEs span nonlinear advection, phase separation, dispersion and chaos. Across all PDEs, the dynamics surrogates use a common data-generation procedure with bounded multisine controls sampled across five temporal frequency bands. Fixed actuator layouts simplify the analysis of forecast–control discrepancies. Zanotta et al. (ICML 2026) demonstrate PDE control with variable actuator configurations using DeepONet policies. Our study examines how learned dynamics affect policy training and controller performance.

Section 5.4 extends evaluation beyond the original initial-condition draws through amplitude scaling from 0.5 to 2, additive Gaussian perturbations and noisy burn-in. We report where controller performance holds or degrades under these shifts. We considered randomly sampled reference states but retained constant references because these tasks already expose the forecast–control discrepancies under investigation. Generalization across reference states remains untested.

FNO comparison. We compare complete training configurations under an approximate budget of 12 hours per dynamics model on one A100. FNO₁ and FNO₅ share the architecture and source trajectories, with identical policy-training and evaluation horizons. Their subscripts denote the dynamics-model supervision horizon.

FNO₅ penalizes prediction errors across five autoregressive steps and backpropagates through predicted states, accounting for accumulated rollout error. We selected optimization settings for each objective within the computational budget. Both configurations showed little further loss reduction toward the end of training under their respective schedules. This supports the chosen training durations. Persistence under identical optimization and checkpoint-selection settings remains untested, so we attribute the results to the complete configurations.

FNO₅ achieves the lowest nominal terminal tracking error on five of six PDEs and comes within approximately 7% on the sixth. Its advantage does not extend to every perturbation setting: under the largest tested CH perturbations, the policy trained through FNO₅ fails from some initial conditions, while the FNO₁ policy retains tracking.

PPO comparison. PPO uses the same tracking and control-effort stage cost as DPC, with the same targets, actuator bounds and evaluation horizons. We initially targeted approximately 12 hours of PPO training and extended runs where needed to allow training to stabilize. Recorded CPU training times range from 8.57 to 36.52 hours.

FNO₅-based DPC achieves lower terminal tracking error than these PPO policies on all six PDEs, by 0.94–3.72 orders of magnitude. This comparison includes the PPO runs that received additional training beyond the intended budget. The timings document the resources used; CPU and A100 hours do not establish equivalent total compute.

Connection between theory and experiments. Could you clarify which theoretical inference you consider unsupported, and whether your concern is with the derivation itself or its use in interpreting the empirical results? A reference to the relevant statement or proof step would help us address this precisely.

TI-DON failure on Cahn–Hilliard. We agree that the current evidence does not separate the causal roles of Jacobian error, closed-loop distribution shift and policy optimization. TI-DON’s poor tracking within its own surrogate shows that transfer to the numerical plant alone cannot explain the failure. The observed state-sensitivity mismatch does not establish the cause.

We are running a targeted policy-training experiment on two additional, independently trained TI-DON dynamics models. We reduce the policy learning rate to one-third of its original value while holding policy initialization, update budget and other settings fixed. This tests sensitivity to that optimization choice; it does not fully separate the competing mechanisms.

Thank you for the clarifications. I appreciate your acknowledgment that the results concern complete training configurations and that the diagnostics do not establish causality. These qualifications are helpful, but several substantive concerns remain.

  1. Controlled comparisons. The approximately matched training time does not isolate supervision horizon from optimization and checkpoint-selection choices. Do the FNO₅ advantages persist under controlled settings? For PPO, matching the stage cost is insufficient: Eq. (14) adds an intermediate-state tracking penalty to DPC that is absent from PPO. Which conclusions remain after accounting for this difference?

  2. Robustness and practical significance. Please provide the completed independent-surrogate-seed results, particularly for the smaller ranking differences. Given the reported cumulative-cost differences below 1% among FNO/RNO policies, what practical benefit do the endpoint improvements establish?

  3. TI-DON failure. Does the proposed learning-rate experiment resolve the failure within the surrogate, and does the result persist across surrogate seeds? This would clarify optimization sensitivity, although attributing the failure specifically to Jacobian error would still require additional evidence.

Reviewer_uRLYOpenReview ↗
Rating
1(−1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
3
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Paper summary

This paper trains neural network approximations for systems governed by PDEs and then asks whether training a controller on the surrogate NN approximation of the true PDE yields poor performance. The papers' main contributions are (1) a policy-dependent sim-to-real transfer bound, (2) a simulation lemma style bound which decomposes a difference in policy performance into a transfer gap and an optimization gap, and (3) an example of how forecast accuracy does not guarantee gradient similarities. The authors conduct experiments on a set of 1-dimensional PDEs, with several different methods for learning surrogate dynamics used.

Critical strengths

The introduction and setup to the paper are well written and the claims are easy to follow. The paper investigates a critical question regarding the use of learned differentiable dynamics surrogates to provide gradients for offline policy training, which is widely applicable to multiple downstream fields, as the authors themselves note. The theoretical results themselves are more a re-synthesis of existing, known results, but I think the paper both explores interesting questions and gives a nice framework for thinking about simulation. With clearer connections to the claims and clearer experiments, I think the paper could be a valuable contribution.

Critical weaknesses

On a minor note: I think it might be cleaner to start with Claim 2, the simulation-lemma style bound and then introduce Claim 1 and Claim 3 as results pertaining to the δopt\delta_{\textrm{opt}} and Δ(π)\Delta(\pi) terms respectively.

The authors use Claim 1 to argue that sim-to-real transfer is policy conditioned, and therefore training on the open-loop trajectories used to model the surrogate does not necessarily yield a bound on the policy-dependent surrogate error of Claim 1. While this is true, with slightly stronger stability requirements on the policy used for simulator rollouts (see e.g. https://arxiv.org/abs/2205.14812, which pertains to offline imitation learning and bounds on-policy rollouts using offline-collected data via an adversarial condition), it may be possible to bound the on-learned-policy error effectively. The bound the authors derive is an upper bound, not a lower bound: open-loop forecast accuracy may in fact bound the sim-to-real transfer for a learned policy in practice, particularly with sufficient data coverage.

Claim 3, that predictive accuracy does not mean that accuracy of simulator gradients, relies on an extreme counterexample where the difference between the surrogate and true plants is an error term whose frequency blows up as the error goes to zero. As the authors themselves note, when curvature is bounded (as is likely the case for any reasonably trained surrogate), then prediction accuracy does bound the Jacobian error. Furthermore, that poor or noisy gradients of the simulator leads to bad optimization outcomes (e.g. large δopt\delta_{\mathrm{opt}}) also does not follow directly.

I think the experiments section is quite difficult to follow--the discussion repeats the numbers given in the tables directly (take e.g. lines 361-377) but do not suggest to the reader how the experiments line up with the claims made earlier in the paper. It is very difficult to make any concrete takeaways from the experimental results as a consequence.

I think with significant cleanup of the experiments and clear, hypothesis driven experiment design I would be willing to increase my score despite the limited 1-dimensional PDEs used. I think the introduction/setting questions are important, even if the experiments section is of poor quality.

Questions for authors

It is difficult to make sense of the experiments: the authors suggest that forecasting and control favor different choices of surrogates, yet the log-endpoint MSEs reported in Table 2 suggest that forecasting and control are fairly well correlated between the different methods used, with perhaps the exception of TI-DON on CH?

I think it would be helpful if the authors could explain what the experimental hypotheses are and how the experiments line up with the claims made earlier in the paper. The experiments section is a flood of numbers and of jargon (that reads as LLM-generated?) and it is unclear what results matter or what the conclusions are. For instance Section 5.3 seems to ask whether surrogates report their own controllers' performance, which is a good question, but as a reader it is unclear what the conclusion is or what even I should be looking at.

You introduce this counter-example system in Claim 3 to show how forecast accuracy does not yield stable gradients. Do you have any experiments showing poor training when introducing error of this form into the plant disrupts training?

2 comments

We agree that the Experiments section needs a hypothesis-driven rewrite with clearer links to the theoretical claims.

Claim ordering. We agree that the performance-gap decomposition is a clearer starting point. We will present Claim 2 first, separating the surrogate optimization gap from the policy-dependent transfer gaps. Claim 1 will then explain how on-policy model error and closed-loop stability affect transfer. Finally, Claim 3 will illustrate why accurate forward predictions need not yield accurate gradients for policy training. This identifies a potential optimization difficulty but does not establish poor controller performance.

Stability and coverage. We agree that additional stability and coverage assumptions can support transfer guarantees. Stronger stability assumptions can bound how errors accumulate through the rollout. We will cite TaSIL as a related example. Our sampled forecast errors and hard action limits alone do not establish the required uniform error bound.

1. Forecast accuracy and control performance. Forecast accuracy is useful: the best forecaster produces the best controller on four of six PDEs. We will narrow the claim to the control differences between similarly accurate dynamics models. Policy training using independently trained surrogate seeds is underway to test whether these comparisons persist; we will report the completed evaluations in the updated PDF.

2. Experimental hypotheses and Section 5.3. The experiments examine whether forecast and sensitivity errors predict plant-side tracking, and whether a surrogate correctly estimates its trained policy’s plant performance. The gradient counterexample motivates the sensitivity diagnostics; the transfer bound motivates comparing surrogate-side and plant-side performance. We will distinguish the empirical terminal tracking metrics from the cumulative-cost quantities in the theory.

Section 5.3 shows that accurate performance assessment does not imply successful control. TI-DON on CH yields poor tracking in both the surrogate and numerical plant, whereas RNO underestimates its policy’s plant-side error. FNO₅ gives the most consistent estimates, agreeing within a factor of two across the six PDEs. We will state these conclusions before the ratios and include the absolute tracking errors.

3. Counterexample and policy training. We agree that Claim 3 establishes a theoretical limitation, not a policy-training failure. The construction relies on increasing curvature as prediction error vanishes; uniform curvature bounds and appropriate domain assumptions can restore a relationship between prediction and gradient accuracy (Appendix G.3). Neither the counterexample nor our measured Jacobian discrepancies establish that inaccurate gradients caused the observed controller failures. We have not performed the suggested training experiment and will clarify these limitations in the revision.

As your response acknowledges, there gap between the theorem, claims, and experiments still remains to be resolved and requires a significant rework of the experiments section and new experiments.

The experimental side of this paper at a minimum needs a substantial rework and even in the updated draft, the text of the experimental section reads like LLM generated statistics with no good synthesis or presentation.

Please let me know if you end up updating the draft with additional experiments you mentioned in your response before the end of the author-reviewer discussion deadline.

Reviewer_E9WnOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

The paper compares FNO, RNO, and TI-DeepONet as surrogate models for differentiable PDE control. It asks whether better forecast accuracy leads to better controllers. Experiments cover six one-dimensional PDEs, with theoretical results explaining why accurate predictions do not generally guarantee accurate gradients.

Critical strengths

The question is relevant to choosing surrogates for control. Some comparisons are informative: RNO and one-step FNO have similar forecast errors on Burgers and KdV, but their endpoint control errors differ by about 9 and 7 times, respectively (Table 2).

Critical weaknesses
  1. The new insight is limited. Model-gradient accuracy in policy optimization was already studied by Li et al. (ICLR 2022), and the paper uses the DPC pipeline of Sarkar et al. (2025). Its main contribution is therefore the comparison of neural operators. I am not yet convinced that this comparison provides a substantial new understanding beyond the known distinction between prediction and gradient accuracy.

  2. The experiments leave the main conclusion uncertain. In Table 10, the best forecaster also gives the best controller on four of six PDEs; the remaining error ratios are 4.2 and 1.07. Each surrogate configuration is trained only once, so the robustness of the comparisons is unclear. The largest discrepancy involves TI-DeepONet on Cahn–Hilliard, but its controller also fails inside the surrogate (Table 12). The diagnostics do not establish why this happens.

Questions for authors
  1. What specific new conclusion about neural operators does this evaluation establish beyond prior work on prediction and model-gradient accuracy?

  2. Do the key Burgers, KdV, and Cahn–Hilliard comparisons persist across independently trained surrogates?

  3. Why does TI-DeepONet fail to train a successful controller even inside its own surrogate on Cahn–Hilliard? Does this result persist under a reasonable change of policy-training settings?

1 comment

Thank you for the careful assessment. We should explain more clearly what the analysis adds beyond comparing neural operators.

We build on Li et al.’s perspective of model-gradient error by examining how prediction and sensitivity discrepancies relate to the behavior of trained PDE controllers. Li et al. analyze policy-gradient bias and develop gradient-aware model training. Our procedure evaluates the surrogate and numerical plant at matching state–action pairs along each trained policy’s closed loop. It separates transition defects from actuator- and state-sensitivity mismatches and tracks their evolution through the rollout. Combining these diagnostics with surrogate-side and plant-side tracking also distinguishes poor control already present within the surrogate from degradation during transfer to the plant.

We agree that forecast accuracy provides useful guidance: the best forecaster produces the best controller on four of six PDEs. We will narrow the claim to the discrepancies observed between similarly accurate predictors.

  1. Conclusions beyond prior work: Our narrower empirical conclusion is that, at the evaluated checkpoints, smaller on-policy prediction defects and local Jacobian mismatches in the dynamics model do not consistently correspond to better plant-side terminal tracking by the policy trained through it (Sections 5.1–5.2 and Appendix I). For example for the dynamics surrogate, relative to FNO₁, FNO₅ reduces the measured local discrepancies on both CDR and KdV, yet control improves on CDR and slightly worsens on KdV. These observations show the limits of using local error magnitudes to select a surrogate for control. The PDE dynamics and feedback policy jointly determine how perturbations propagate through the closed loop. We therefore interpret the diagnostics within each PDE–policy pair and use them to formulate hypotheses about the observed differences. Establishing their causal role requires further investigation.

  2. Reliability of the comparisons: We are testing the Burgers, KdV and Cahn–Hilliard comparisons across two additional surrogate seeds, using a common policy initialization seed. Policy training is underway, so persistence of the control differences remains to be confirmed. We will report the seed-level control evaluations in the updated PDF.

  3. TI-DeepONet on Cahn–Hilliard: We agree that failure inside the surrogate means poor transfer alone cannot explain the result. The diagnostics identify a state-sensitivity discrepancy, but do not establish that it causes the failure. We are also comparing the original policy learning rate with one-third of that value for both additional TI-DON surrogate seeds. Each dynamics surrogate remains frozen, and we hold the policy initialization, update budget and remaining training settings fixed. This tests whether the failure is sensitive to that policy-training choice, which surrogate-seed replication alone cannot answer.

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