acceptodds
Under review as a conference paper at ICLR 2027

Learn or Refine? Predicting When Neural PDE Correction Is Worth Training

Abstract

Learned error correctors repair the output of a cheap classical PDE solver, but training one costs high-fidelity data and optimization. Before paying that cost, one would like to know whether the corrector will beat the classical alternative of refining the grid. Accuracy against a fixed reference cannot answer this, because refinement spends the same resource the corrector spends on training data. We formulate the question as a prospective matched-cost decision: a corrector is worth training only if its achievable error beats both a ridge control and the best refinement affordable within its own budget. The hard part is that the achievable learned error is unknown before training. We show that the pilot-to-full remaining learning gain is strongly family-dependent, so a fixed pilot-to-full calibration does not transfer reliably across families; but the gain is predictable from the pilot's early learning progress. This yields a two-feature estimator and a Learn-or-Refine rule costing about of full training. In leave-one-family-out evaluation over 74 prior regimearchitecture cases it has the lowest cross-family decision regret among competing estimators; after freezing the estimator it decides correctly on 9 of 10 regimes of an unseen Allen–Cahn family with zero decision regret. The method decides whether a specified corrector recipe is worth completing relative to matched-cost classical refinement.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
scientific machine learning, PDE solvers, learned error correction, algorithm selection, cost-aware learning, learning dynamics, hybrid numerical methods, partial differential equations

Reviews

Among:
Shape:
1234this paper, Bottom 1%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.00 over 3 reviews, above 0% of the others.
Reviewer_9ScsOpenReview ↗
Rating
1
Confidence
2
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

The paper studies the decision problem of whether to train a neural error corrector for a coarse PDE solution or refine that solution classically. For a given number of deployments, classical methods are considered affordable if their total computational cost does not exceed the end-to-end cost of the learned corrector, including reference-data generation, training, and inference. The corrector is worth training only if it outperforms both the best affordable classical method and a cheap linear regression baseline. However, this requires knowing the corrector's final error upfront, which is precisely what training would reveal. Therefore, the authors propose estimating the corrector's final performance from a small pilot run, using its early learning progress to predict the remaining improvement. The coefficients of this predictor are fitted on historical PDE problems and evaluated using leave-one-family-out validation, followed by a prospective evaluation on an unseen PDE family.

Critical strengths
  1. The paper studies a practical problem of choosing a performance-optimal method given a constrained budget.
Critical weaknesses
  1. Lack of contextualization within existing literature. The paper insufficiently positions its main contribution within the established literature on learning-curve-based performance prediction, extensively reviewed by Mohr & van Rijn (2024, Learning Curves for Decision Making in Supervised Machine Learning: A Survey). Moreover, the authors' distinction between predicting remaining learning gain and extrapolating final error is not convincing. Writing g^=w0+w1log⁡(e1/e2)+w2log⁡(e2/e3)\hat g = w_0 + w_1\log(e_1/e_2) + w_2\log(e_2/e_3), their estimator is algebraically equivalent to $ \log\hat e_{\mathrm{full}} = -w_0-w_1\log e_1+(w_1-w_2)\log e_2+(1+w_2)\log e_3, $ i.e., a constrained linear regression on intermediate log-errors, where the regression coefficients (excluding the intercept) sum to one. A more thorough contextualization is needed to clarify the methodological novelty of the proposed estimator beyond its application to cost-aware PDE solver selection.

  2. Limited methodological contribution and insufficient experimental evidence. The paper reads more like an empirical case study than a mature methodological contribution to machine learning. Beyond the matched-cost formulation, the proposed method is a relatively simple linear predictor, and its broader significance remains unclear. The experimental evaluation further weakens the contribution: most baselines are either trivial heuristics or alternative estimators proposed by the authors. In particular, there is no convincing comparison with established learning-curve prediction methods under comparable computational budgets. Moreover, the presentation of results is somewhat misleading. Table 1 emphasizes aggregate performance, whereas the per-family breakdown in Table 6 reveals that the proposed estimator matches B2-d10 on three of the four PDE families, with its entire improvement concentrated on Burgers. This considerably weakens the evidence for generalizable methodological progress. The prospective evaluation on only ten regimes from a single additional PDE family provides limited further support. More generally, the manuscript is repetitive and would benefit from a more concise presentation, clearer separation of empirical observations from methodological contributions, and a more critical examination of the results. I would strongly recommend moving Table 6 to the main text, potentially replacing Table 1. Overall, the work appears more appropriate for a specialized computational PDE venue than for a general machine learning conference.

Minor weaknesses:

  • Figure presentation. Several figures have readability issues:
    • Figure 2: The legend overlaps with the local-linear/global-phase annotation.
    • Figure 4: The Fisher–KPP family is included in the legend and discussed in the caption, but its points are not visible.
    • Figure 5: The logarithmic y-axis makes zero-regret results for Fisher–KPP and Helmholtz invisible, potentially misleading the reader.
    • Figure 7: Several method labels overlap, making the low-cost region difficult to interpret.
  • Incomplete notation and terminology. The error metric (e), central to the proposed method, is not explicitly defined in the main text (relative L2L_2 error is only specified in Appendix D). The abbreviations M1b, M0c, and B2-d10 are also introduced without explanation. Furthermore, Appendix C uses L∗L^* to denote the full learned cost, whereas Eq. (1) introduces ClearnC_{\mathrm{learn}}, without clarifying their relationship.
  • Method presentation. Section 3.6 provides a lengthy numerical example, whereas a concise pseudocode description of the complete decision procedure would make the proposed method easier to understand and reproduce.
  • Insufficient presentation of deployment-volume sensitivity. Section 6.6 and Appendix N only describe the changes in decisions as the number of deployments NN varies. A table or figure showing the corresponding decisions or breakeven points would better substantiate these claims.
  • Unclear reference to earlier work. Section 6.3 describes B2-d10 as a calibration developed in the authors' "earlier work," but does not provide a corresponding reference or explain the origin of this method.
Questions for authors

I would like to emphasize that the answers to the questions below are unlikely to change my overall assessment of the paper, which is primarily driven by the more fundamental concerns outlined above. Nevertheless, I noted these questions while reading the manuscript and share them in the hope that they will help the authors clarify and strengthen the work in future revisions or submissions.

  1. Evaluation protocol and reference solutions (Section 3.2–3.4). How exactly are eclse_{\mathrm{cls}} and eridgee_{\mathrm{ridge}} estimated before making a decision? How many validation instances are used, and where do their high-fidelity reference solutions come from? Are these the same instances used for training the pilot corrector, or a separate validation set? More generally, are e5%e_\text{5\%}, e10%e_\text{10\%}, and e20%e_\text{20\%} measured on the same fixed validation set? How is the cost of obtaining these references accounted for?

  2. Cost accounting (Section 3.1, Appendix C). The paper reports computational costs in seconds and as fractions of full training cost. What hardware and software environment was used to obtain these measurements, and how were costs across numerical solvers and neural training made comparable? Moreover, when the decision is to refine classically, is the cost already spent on the pilot subtracted from the available refinement budget?

  3. Role of the ridge baseline (Section 3.2, Section 3.5). Why is the ridge corrector treated solely as an eligibility criterion rather than as a third deployable alternative? If it outperforms both the neural corrector and the classical refinement, the proposed decision rule still selects Refine. How is this justified from an operational cost–accuracy perspective?

  4. Ridge regressor specification (Section 3.2, Section 6.1). The ridge baseline is described as ridge regression on local stencil features, but its regularization is not specified. Is an L2L_2 penalty actually applied? If so, what is the regularization coefficient, and how is it selected? Is the coefficient fixed across PDE families, or tuned separately for each problem?

  5. Choice of pilot configuration (Section 3.3, Section 6.1). What motivates the particular selection of 10% of training pairs, 20% of the epoch budget, and an 8-channel CNN? Likewise, why are the progress features evaluated at 5%, 10%, and 20%? Has the sensitivity of the decision quality and computational cost to these choices been investigated? If so, could it be presented as an ablation study?

  6. Data preprocessing and training (Section 6.1, Appendix B). Are the inputs and regression targets normalized when training the neural correctors? Are the stencil features used by the ridge regressor normalized? The appendix also states that the pilot is trained on the first 26 training pairs. Are the pairs randomly ordered, and has the sensitivity to their selection been investigated?

4 comments
AuthorsOpenReview ↗

Response to Reviewer 9Scs (1/3)

We thank the reviewer for their comments.

The prospective set is ten regimes, eight of them Refine

"The headline result of 9/10 correct decisions is based on only ten regimes from one unseen PDE family. Moreover, the test set contains only two Learn cases and eight Refine cases, introducing substantial class imbalance."

All three reviews converge here, and the paper reports the prospective result against the 8/10 majority policy rather than as a headline accuracy. The interval is [0.60, 0.98], attached to a ten-regime check on one unseen family rather than to a general claim (Section 6.5). The rule catches both Learn cases (AC04, AC14), and its single error is AC11, where efulle_{\text{full}}, eclse_{\text{cls}} and eridgee_{\text{ridge}} are within 5% and the regret is zero (Section 6.5; Table 6). Against never training the paired counts are 2 to 1, exact p=1.0p=1.0 (Table 3). Five planned regimes were dropped or replaced before any outcome was observed, which leaves the set at ten (Section 6.5; App. P).

The pilot inside the matched budget

"Moreover, when the decision is to refine classically, is the cost already spent on the pilot subtracted from the available refinement budget?"

The pilot is charged inside ClearnC_{\text{learn}} rather than subtracted from the refinement budget: Eq. 1 carries it as a fourth term, so a classical arm is affordable when its per-rollout cost times NN stays within that same budget (Section 3.1; the same accounting answers Reviewer gTYB's Q1). Charging the 63.7 s pilot moves 0 of 84 decisions across the 74 historical and ten prospective cases (abstract; Section 7). The decision cost on Allen-Cahn is 14.7%, against 4.9% for the classical-only probe, which trains no pilot (App. C; Table 3). The pilot is a separate 8-channel network and the full corrector is wider (Section 6.1), so no pilot parameter is reused and nothing is amortized into the corrector.

Where the decision-time references come from

"How exactly are eclse_{\mathrm{cls}} and eridgee_{\mathrm{ridge}} estimated before making a decision? How many validation instances are used, and where do their high-fidelity reference solutions come from?"

Every decision-time error is scored on nval=12n_{\text{val}}=12 pilot-evaluation episodes drawn from a separate RNG stream, and that cost is charged inside CpilotC_{\text{pilot}} (Section 3.1; Eq. 1; this is the protocol behind Q1 below). The 26 pilot pairs are training data, and the held-out test set supplies the labels that score a decision, so the references are not the pairs that trained the pilot. The three progress checkpoints are read from one pilot run, so e_{5\\%}, e_{10\\%} and e_{20\\%} are measured on the same fixed episodes (Section 3.1; App. C).

What is new, and the curve baseline at matched cost

"Moreover, the authors' distinction between predicting remaining learning gain and extrapolating final error is not convincing."

The estimator is a damped log-linear extrapolation and the paper states its form, with a fitted slope of 1.613 against the analytic 2.322 (Section 5). The two-feature form is a constrained linear regression on intermediate log-errors, as you show; the claim is the damping and the matched-cost decision it feeds, not a new extrapolation law (Section 5). Section 2 now positions it against the learning-curve literature (Mohr & van Rijn, 2024; Domhan et al., 2015; Li et al., 2017), where the decision is which learned configuration to keep or when to stop it, not whether to learn at all. The matched-cost curve fits that two reviews asked for are the comparison reported in the general response, and Table 8 lists the fits.

AuthorsOpenReview ↗

Response to Reviewer 9Scs (2/3)

W1: Literature and what the estimator is

"The paper insufficiently positions its main contribution within the established literature on learning-curve-based performance prediction, extensively reviewed by Mohr & van Rijn (2024, Learning Curves for Decision Making in Supervised Machine Learning: A Survey)."

The measured part of the distinction is that a frozen absolute calibration scores 0.879 against 0.970 for the raw pilot on 33 cross-family cases, on a classical-dominated transfer set where the majority policy is also 0.970 (Section 6.4). Revision. Section 2 and Section 5.

W2: Contribution and the per-family evidence

"In particular, there is no convincing comparison with established learning-curve prediction methods under comparable computational budgets."

Answered above under What is new, and the curve baseline at matched cost for the baseline half and under The prospective set is ten regimes, eight of them Refine for the prospective half; for the per-family point, the table you read as Table 6 moves into the main text as Table 2, beside the aggregate in Table 1. The two estimators tie on advection-diffusion at 0.132 and on Fisher-KPP and Helmholtz at zero, and the difference is Burgers, 0.022 against 0.042. On the advection-diffusion fold 27 of 32 cases are Learn and the rule is correct on 27, with 4 false positives and 1 false negative. The margin over the frozen calibration is one case in 74, macro regret 0.038 against 0.044, and we report it as a one-case margin (Section 6.4; Table 1). On the venue question we have no measurement to offer; Section 6.2 now separates development, model-selection and prospective evidence, and the Discussion is compressed.

Minor weaknesses

"Figure 2: The legend overlaps with the local-linear/global-phase annotation."

The paper fixes two of the four figure points and leaves two: Fig. 4 now draws the Fisher-KPP points that its caption discusses, Fig. 5 uses a symlog axis so the eight zero cells in Table 2 sit on the zero line, Fig. 2's legend still covers part of the diagonal annotation, and Fig. 7's labels still crowd the low-cost region. On notation, M1b, M0c and B2-d10 are now defined in Section 6.3 and named in the Table 1 rows, App. C uses ClearnC_{\text{learn}}, the same symbol as Eq. 1, and the error is relative L2L_2, stated in the Table 5 caption and App. D, though still not in Section 3. On method presentation, no pseudocode box is added: the procedure is Eq. 3-Eq. 6 plus the Section 3.4 paragraph, and Section 3.6 keeps the worked example. On deployment volume, Section 6.6 and App. N give the decisions across N∈{10,100,103,104,105}N \in \lbrace 10, 100, 10^3, 10^4, 10^5\rbrace, several regimes move from Refine to Learn as NN grows and none move back, and no breakeven table is added, though Table 5 lets a reader recompute a flip point. On the earlier-work reference, Section 6.3 now defines B2-d10 as a log-linear power-law map from pilot error to full error, fit once on advection-diffusion and never refit, and since it is our own earlier calibration there is no third-party reference to add.

Q1: Evaluation protocol and reference solutions

"Are these the same instances used for training the pilot corrector, or a separate validation set?"

eclse_{\text{cls}} and eridgee_{\text{ridge}} come from the classical frontier at the affordable resolutions, epilote_{\text{pilot}} from the pilot run, and all three are scored on the same 12 episodes (Section 3.1). Across nval=6/12/24n_{\text{val}}=6/12/24 the calibrated estimate moves by 17.3% and stays above the true full error; that check is reported here only.

AuthorsOpenReview ↗

Response to Reviewer 9Scs (3/3)

Q2: Cost accounting

"What hardware and software environment was used to obtain these measurements, and how were costs across numerical solvers and neural training made comparable?"

The second half of your question is answered above under The pilot inside the matched budget; on hardware, the paper reports wall-clock seconds per arm (Table 7) and does not add a hardware table, and App. C defines the denominator of every reported fraction.

Q3: The ridge baseline as a gate

"Why is the ridge corrector treated solely as an eligibility criterion rather than as a third deployable alternative? If it outperforms both the neural corrector and the classical refinement, the proposed decision rule still selects Refine."

The ridge is a learned control fitted to the same training pairs, not a classical arm, so the budget comparison cannot price it as refinement (Section 3.2; Section 6.1). The ground-truth winner is defined as the gate winner, so a ridge-best regime is one where the corrector should not be trained at all (Section 3.5). The gate winner and the better arm differ in 1 of 84 decisions, AC11, where all three errors are within 5% and the regret is zero (Section 3.5; Section 6.5). Revision. Section 3.5 states the two-arm oracle and the gate.

Q4: The ridge regressor

"Is an L2L_2 penalty actually applied? If so, what is the regularization coefficient, and how is it selected?"

It is an L2L_2-penalized fit on local stencil features [1, u, uxu_x, uxxu_{xx}] (Section 3.2). The paper does not report the coefficient or how it was selected, and Table 5 gives the resulting error per regime. The control is a floor that any corrector must beat, not a tuned competitor, so a coefficient search is not part of the decision rule.

Q5: The pilot configuration

"What motivates the particular selection of 10% of training pairs, 20% of the epoch budget, and an 8-channel CNN? Likewise, why are the progress features evaluated at 5%, 10%, and 20%?"

The pilot is set at 10% of the training pairs and 20% of the epoch budget, which puts the decision at about 15% of full training (Section 3.4). The choice is not a single point: a 3x3 grid over width {8, 16, 24} and budget fraction {0.10, 0.20, 0.30} gives a calibrated estimate between 0.025 and 0.048, monotone in budget and flat across width (0.04785 at every width), against a true full error of 0.016 (App. B.2). The 5%, 10% and 20% checkpoints come from that one run and define pearlyp_{\text{early}} and platep_{\text{late}} in Eq. 4; the grid bounds the estimator's input rather than selecting a favorable cell. Revision. App. B.2 reports the grid.

Q6: Preprocessing and pair order

"The appendix also states that the pilot is trained on the first 26 training pairs. Are the pairs randomly ordered, and has the sensitivity to their selection been investigated?"

The pilot takes the first 26 pairs in a fixed order, and the full corrector takes all 256 (App. B.2). A second seed with a shuffled pair order moves the pilot estimate by 6.2%, and both estimates stay above the true full error; that check is reported here only. On normalization, the paper states only that training minimizes MSE on the reference residual (App. B.4) and does not report input or target scaling. Revision. App. B.2 states the pair order.

AuthorsOpenReview ↗

Follow-up to Reviewer 9Scs

We would like to follow up on our rebuttal before the author-reviewer discussion closes on Nov. 18 at 11:59 p.m. AoE. The rebuttal answers each of your comments in detail. In particular, it covers the learning-curve baselines at matched cost. At the same pilot cost, three-point power-law and ensemble curve fits reach 62/74 correct decisions, against 66/74 for the two-feature estimator (Section 6.4, Table 8). The rebuttal also covers the pilot, which is now charged in Eq. 1 and leaves all 84 decisions unchanged (Section 7), and the reference protocol behind every decision-time error (Section 3.1). We hope these additions give a fuller picture of the work.

We would also like to highlight the main result of the paper. Learned correctors for PDE solvers are already widely studied, and they are usually judged by their accuracy against a fixed reference after training. Refining the grid spends the same resource that the corrector spends on training data. Our paper formulates this as a matched-cost decision. The Learn-or-Refine rule decides before the full training cost is paid, at about 15% of full training. Over 74 earlier regime-architecture cases it decides 66/74 correctly in leave-one-family-out evaluation. After the estimator was frozen, it decides 9 of 10 regimes of an unseen Allen-Cahn family correctly, with zero mean and zero worst-case decision regret. These results are, to the best of our knowledge, new in the literature on learned PDE correction. Your review notes that the paper studies a practical problem, the choice of the best method under a constrained budget, and we hope the new controls complete this picture.

We would be very grateful if you could read the rebuttal before the discussion closes and tell us what you think. If it resolves your concerns, we kindly ask you to consider raising your score. If anything remains open, please let us know and we will answer right away.

Thank you for your time and consideration. We look forward to your reply.

Reviewer_gTYBOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

This paper formulates the decision of whether to train a neural PDE error corrector or refine a classical numerical solver as a prospective algorithm-selection problem under matched computational budgets. The authors propose Learn-or-Refine, a lightweight decision framework that predicts the full corrector's achievable error using early learning progress from a partially trained pilot model and compares it against classical refinement and a ridge-regression baseline.

Critical strengths
  1. The paper is well motivated. The paper addresses an important question in scientific machine learning: whether investing in neural PDE correction is more cost-effective than improving an existing classical numerical solver. Unlike approaches that analyze computational efficiency only after training, the proposed framework aims to predict whether training will be worthwhile before the full computational investment is made.
Critical weaknesses

The headline result of 9/10 correct decisions is based on only ten regimes from one unseen PDE family. Moreover, the test set contains only two Learn cases and eight Refine cases, introducing substantial class imbalance. That means, a simple strategy of choosing Refine would make 8/10 correct rate. The paper reports a Wilson 95% confidence interval of approximately [0.60, 0.98], which reflects considerable uncertainty. In addition, five originally planned Allen–Cahn regimes were dropped or replaced due to computational limitations. Although these amendments were documented before observing the outcomes, they further restrict the strength of the prospective evidence.

Questions for authors

The proposed method requires training an additional pilot corrector before deciding whether to complete full training. However, Equation (1) defines the learned-computation budget without explicitly including this pilot cost. Since the pilot uses a smaller architecture and fewer training pairs, its parameters cannot necessarily be reused for the full corrector. Could the authors clarify how this additional computational expense is incorporated into the matched-cost comparison and whether including it changes the optimal classical refinement frontier or the final decisions?

2 comments
AuthorsOpenReview ↗

Response to Reviewer gTYB

We thank the reviewer for their comments.

W1: Ten regimes, one family

"The headline result of 9/10 correct decisions is based on only ten regimes from one unseen PDE family."

The paper now states that the ten-regime result is a prospective check on one family and not a generalization claim (Section 6.5; Section 7). Revision. Section 6.5 and the design-scope paragraph in Section 7.

W2: Two Learn cases against eight Refine cases

"Moreover, the test set contains only two Learn cases and eight Refine cases, introducing substantial class imbalance."

The majority policy is the reference row in Table 3, and the rule's claim rests on the regret columns rather than on the accuracy margin. Revision. Table 3 reports mean and max regret beside accuracy for every method.

W3: The interval

"The paper reports a Wilson 95% confidence interval of approximately [0.60, 0.98], which reflects considerable uncertainty."

The paper reports the interval beside the point estimate and does not describe the ten-regime result as precise. Revision. Section 6.5 reports the interval with the result.

W4: Five regimes dropped or replaced

"In addition, five originally planned Allen-Cahn regimes were dropped or replaced due to computational limitations. Although these amendments were documented before observing the outcomes, they further restrict the strength of the prospective evidence."

App. P names the amendment, with three fine-grid regimes replaced and two large-ϵ\epsilon regimes dropped before any of their outcomes were observed. The set is ten, and Section 6.5 reports the amendment where the result is reported. Revision. Section 6.5 and App. P.

Q1: The pilot cost

"The proposed method requires training an additional pilot corrector before deciding whether to complete full training. However, Equation (1) defines the learned-computation budget without explicitly including this pilot cost."

The pilot cannot be reused for the full corrector, so it enters Eq. 1 as its own term and the affordable classical frontier is recomputed under the enlarged ClearnC_{\text{learn}} (Section 3.1). Revision. Eq. 1, the abstract and Section 7.

AuthorsOpenReview ↗

Follow-up to Reviewer gTYB

We would like to follow up on our rebuttal before the author-reviewer discussion closes on Nov. 18 at 11:59 p.m. AoE. The rebuttal answers each of your comments in detail. In particular, it covers the size of the prospective test. Section 6.5 and App. P now give the Wilson interval, the two Learn cases and the protocol amendments. The matched-cost comparison over the 74 earlier cases is reported next to it, where the estimator decides 66/74 correctly (Section 6.4, Table 1). The rebuttal also covers the pilot cost. The 63.7 s pilot is now charged in Eq. 1, and it leaves all 84 decisions unchanged (Section 7, Table 8). We hope these additions give a fuller picture of the work.

We would also like to highlight the main result of the paper. Learned correctors for PDE solvers are already widely studied, and they are usually judged by their accuracy against a fixed reference after training. Refining the grid spends the same resource that the corrector spends on training data. Our paper formulates this as a matched-cost decision. The Learn-or-Refine rule decides before the full training cost is paid, at about 15% of full training. Over 74 earlier regime-architecture cases it decides 66/74 correctly in leave-one-family-out evaluation. After the estimator was frozen, it decides 9 of 10 regimes of an unseen Allen-Cahn family correctly, with zero mean and zero worst-case decision regret. These results are, to the best of our knowledge, new in the literature on learned PDE correction. Your review notes that the paper addresses an important question in scientific machine learning and that the framework predicts before the full investment is made, and we hope the new controls complete this picture.

We would be very grateful if you could read the rebuttal before the discussion closes and tell us what you think. If it resolves your concerns, we kindly ask you to consider raising your score. If anything remains open, please let us know and we will answer right away.

Thank you for your time and consideration. We look forward to your reply.

Reviewer_5ivFOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

This paper proposes Learn-or-Refine, a method for predicting whether training a neural PDE corrector is more cost-effective than using classical numerical methods, such as grid refinement or Richardson extrapolation, with the extra compute budget. The authors formulate this as a matched computational budget decision problem. The proposed method trains a smaller pilot neural network on a fraction of the full training budget, then uses a two-feature linear model based on early training progress to predict the final error of the fully trained corrector. This prediction is then compared against classical refinement and a simple ridge regression baseline to decide whether to proceed with larger-scale training. The authors evaluate the method using leave-one-out PDE family validation across 74 configurations, followed by a held-out evaluation on 10 Allen-Cahn regimes. They report improved decision regret over baseline estimators, achieving 9/10 correct decisions with zero regret on the held-out family, at approximately 15% of the full training cost.

Critical strengths
  • The problem is important. The work focuses on determining whether it is worthwhile to train a neural corrector vs. allocating the same computational resources to a classical solver with higher-fidelity data.
Critical weaknesses
  • Limited novelty. The paper combines two existing ideas: using partial training + learing curve statistics to predict eventual performance at the end of training, and comparing neural solvers vs. classical alternatives using total compute cost.
  • The method's extrapolation assumption is neither theoretically or empirically justified. The pilot uses a smaller model trained on substantially less data, and assumes that the early learning dynamics can reliably predict the final performance of a much larger model on more data. However, there is no theoretical justification, and in practice the coefficients are empirically fitted to a small precomputed pool. There is little evidence that the proposed method generalizes. The authors validate the estimator with leave-one-family-out evaluation over four PDE families tested on ten Allen-Cahn regimes, but this only uses five PDE families, and the Allen-Cahn test contains only two examples where training the neural model is the right option (i.e. the task yields 80% accuracy by default).
Questions for authors
  • Computing e_ridge, e_cls, and e_pilot for a new PDE problem requires a high-fidelity numerical reference, which is exactly the expensive computation the problem is intended to avoid if unnecessary. In the paper, how are the reference solutions used to estimate these errors produced? Are they drawn entirely from the 26 pilot training pairs or are additional held-out high-fidelity reference solutions needed?
  • It remains unclear under what conditions the proposed estimator can be expected to generalize to new PDE families -- in particular, the relationship between early training progress and final corrector performance may depend strongly on properties of the underlying PDE, the numerical discretization, the neural network architecture, and the structure of the resulting approximation error. Could the authors provide further insight into which properties determine whether this relationship transfers across PDE families, or whether there are identifiable settings in which it is likely to fail? Additional evaluations on qualitatively different PDEs would also help establish the generality of the proposed approach.
3 comments
AuthorsOpenReview ↗

Response to Reviewer 5ivF

We thank the reviewer for their comments.

W1: Novelty

"Limited novelty. The paper combines two existing ideas: using partial training + learing curve statistics to predict eventual performance at the end of training, and comparing neural solvers vs. Classical alternatives using total compute cost."

Both ingredients are in the paper, and the claim is the decision they support rather than a new curve model. Revision. Section 2 and Section 5.

W2: The extrapolation assumption and the five families

"The method's extrapolation assumption is neither theoretically or empirically justified."

The assumption is stated as one: Section 5 gives the estimator's form and says the empirical content is the damping and the decision it feeds. The paper adds three measurable conditions under which the relation holds, a low-frequency nonlinear residual (99% of its energy below k=4k=4; CNN correlation 0.998, ridge relative L2L_2 0.19), slow refinement at matched cost (h/4h/4 leaves 0.096), and a non-degenerate pilot slope, plus one measured failure (Section 4; Section 6.6). That failure is D8, where a corrector becomes strong after the pilot has plateaued and the gain is underestimated (Section 6.6; App. O). Five families are studied; the fifth, Allen-Cahn, was unseen during fitting and selection, and transfer beyond them is untested (Section 7). Your Allen-Cahn denominator point is the shared concern answered in the response to Reviewer 9Scs, under The prospective set is ten regimes, eight of them Refine.

Q1: Reference provenance

"In the paper, how are the reference solutions used to estimate these errors produced? Are they drawn entirely from the 26 pilot training pairs or are additional held-out high-fidelity reference solutions needed?"

The references are the 12 held-out pilot-evaluation episodes, not the 26 pilot pairs, and their cost is inside CpilotC_{\text{pilot}} (Section 3.1).

Q2: Conditions for transfer and further PDEs

"Could the authors provide further insight into which properties determine whether this relationship transfers across PDE families, or whether there are identifiable settings in which it is likely to fail?"

The properties are the three conditions under W2 above, and the identifiable failure is the corrector that becomes strong after its pilot has plateaued (D8, App. O). A sixth family is not added: the evaluated scope is five families, Allen-Cahn is the prospective one, and transfer beyond them is untested (Section 7). The paper states that scope instead of extrapolating it.

AuthorsOpenReview ↗

Follow-up to Reviewer 5ivF

We would like to follow up on our rebuttal before the author-reviewer discussion closes on Nov. 18 at 11:59 p.m. AoE. The rebuttal answers each of your comments in detail. In particular, it covers novelty. The learning-curve baselines are now run at matched cost. Three-point power-law and ensemble curve fits reach 62/74 correct decisions, against 66/74 for the two-feature estimator at the same pilot cost (Section 6.4, Table 8). The rebuttal also covers the provenance of the references (Section 3.1) and the conditions under which the relation transfers, together with the D8 failure case (Section 4, Section 6.6). We hope these additions give a fuller picture of the work.

We would also like to highlight the main result of the paper. Learned correctors for PDE solvers are already widely studied, and they are usually judged by their accuracy against a fixed reference after training. Refining the grid spends the same resource that the corrector spends on training data. Our paper formulates this as a matched-cost decision. The Learn-or-Refine rule decides before the full training cost is paid, at about 15% of full training. Over 74 earlier regime-architecture cases it decides 66/74 correctly in leave-one-family-out evaluation. After the estimator was frozen, it decides 9 of 10 regimes of an unseen Allen-Cahn family correctly, with zero mean and zero worst-case decision regret. These results are, to the best of our knowledge, new in the literature on learned PDE correction. Your review notes that the problem is important, and we hope the new controls complete this picture.

We would be very grateful if you could read the rebuttal before the discussion closes and tell us what you think. If it resolves your concerns, we kindly ask you to consider raising your score. If anything remains open, please let us know and we will answer right away.

Thank you for your time and consideration. We look forward to your reply.

Thank you for clarifying which reference solutions the pilot uses and for adding the matched-cost baselines. I’m maintaining my rating for three reasons.

  • The rebuttal still doesn’t explain when to trust the pilot. Slow refinement helps explain why a fully trained neural corrector might beat the classical solver. My question was how we can tell that from a small pilot trained on 26 examples. D8 illustrates the problem. The pilot appeared to plateau, yet the full corrector achieved roughly 3.8 times lower error than refinement. Given that pilot curve, what could a user have observed before full training to distinguish D8 from a case where training really would be a waste?
  • The main example does not establish that the correction is nonlinear. In the advection–diffusion example, the coarse and fine solvers are both linear in the initial data. The CNN also sees a wider neighborhood than the ridge model. A wider linear filter could therefore explain the CNN’s advantage. The paper needs a comparison against a linear filter with the same spatial reach to support its interpretation. The related claim about Richardson extrapolation has a separate problem. Richardson relies on how error changes as the grid is refined. A good ridge fit at one resolution tells us nothing about that scaling.
  • The results support a narrower claim than the paper makes. The rule gets one more decision right than the frozen calibration across the 74 cases used for model selection. On the unseen family, it correctly identifies both cases where training pays off. That is encouraging, but two successes in one family give us little basis for predicting when the same relationship will hold on a new PDE. I see evidence for a useful heuristic and still see the proposed explanation for its transfer as unsubstantiated.

Comments on the paper

2 comments
AuthorsOpenReview ↗

General Response to All Reviewers

We thank the reviewers for their constructive feedback and valuable insights. The reviews converge on one question, whether the prospective test on ten Allen-Cahn regimes and the estimator behind it can carry the claim, and on two accounting points, the pilot inside the matched budget and a stated reference set behind every decision-time error, both now explicit in the revision.

The strongest verified result is the matched-cost comparison over the 74 historical regimexarchitecture cases: the two-feature estimator decides 66/74 correctly against 65/74 for the frozen single-pilot calibration, and the three-point power-law and ensemble curve fits that the submission was missing reach 62/74 against 66/74 at the same pilot cost (Section 6.4; Table 1; Table 8).

On the frozen ten-regime Allen-Cahn set the same estimator decides 9 of 10 correctly, with zero mean and zero worst-case regret against 8/10 for never training (Table 3), and Section 6.5 and App. P give the Wilson interval, the two Learn cases and the five pre-outcome regime amendments. That is one family and one prospective check, and the paper states the limit where the result is reported.

The pilot is a fourth term in Eq. 1 and Section 7, the reference protocol is in Section 3.1, the per-family split is in Table 2, and the conditions under which the relation holds, with the D8 failure, are in Section 4 and Section 6.6.

Revisions are marked in blue in the revised PDF.

AuthorsOpenReview ↗

Summary of the Rebuttal for the Area Chair and Reviewers

We thank all the reviewers and the Area Chair for reviewing our paper, and for being active in the rebuttal phase. Here we address the comments common to the reviews and summarize the corresponding changes.

Our revision is uploaded. Our main contribution is proposing a matched-cost decision — whether a specified corrector recipe beats classical refinement within the same budget — and a rule that costs about 15% of full training. The rule decides 66/74 historical cases in leave-one-family-out evaluation and 9/10 regimes of an unseen Allen–Cahn family after freezing. On the prospective set it has 0.000 mean and 0.000 worst-case regret, against 8/10 with 0.040 mean and 0.203 worst-case for the majority policy.

The key point is that the paper's primary metric is decision regret, not accuracy. Moreover, we would like to clarify why accuracy alone is insufficient here: real problem sets are class-imbalanced, so the paper evaluates by decision regret, the payoff lost relative to an oracle. For a fair comparison, the majority policy must be scored by the same regret. We would also like to note that the 8/10 baseline is achieved by missing both Learn cases, while the rule's single error is zero-regret. B2-d10 is not directly comparable on accuracy alone: its worst-case regret is 0.523 against 0.000 for the rule. At 14.7% of full training, the rule is the only method that both catches every Learn case and avoids the costly false positive.

Please note that the five protocol amendments were made before any of their outcomes were observed. The current main limitation is scope: five families, two architectures, and two classical arms.

Below, we summarize the changes: (i) curve baselines at the same pilot cost reach 62/74, against 66/74; (ii) the 63.7 s pilot is charged in Eq. 1 and changes 0 of 84 decisions; (iii) the prospective test reports the Wilson interval, the two Learn cases, and the protocol amendments; (iv) every decision-time error now has a stated reference protocol, with per-family results in Table 2; (v) the conditions and the D8 failure are stated in §4 and §6.6.

We hope our response adequately addresses your points and restores your confidence in the work. We look forward to hearing your thoughts.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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