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Under review as a conference paper at ICLR 2027

NearestPDE: Structured Backward Error for Ambiguity-Aware PDE Diagnosis

Abstract

We introduce NearestPDE, a post-hoc framework for diagnosing computed partial differential equation (PDE) fields through structured backward error. It ranks admissible coefficient, source, boundary, and geometry changes using physically scaled residual sensitivities, retaining indistinguishable explanations in a set. We establish conditions for unique recovery and limits of point diagnosis under observational overlap. Split-conformal calibration provides finite-sample marginal coverage under exchangeability within the declared dictionary. A disjoint residual grid selects a corrective re-solve without test-time reference solutions. Controlled tests recover all 1,980 identifiable cases and flag all 240 collinear controls. On nonlinear finite-difference fields, top-1 accuracy averages 100% across three noise levels, versus 78% for matched orthogonal matching pursuit (OMP). Contextual screening recovers three-cause supports with up to 1,023 localized atoms; OMP remains stronger in several transfer settings. Independent re-solves reduce forward error in 1,820/1,824 one-dimensional transfer cases. The framework separates ranked explanations, calibrated uncertainty, and testable model corrections within the declared perturbation dictionary.

Primary area:
interpretability and explainable AI
Keywords:
backward error analysis, PDE diagnosis, conformal prediction, uncertainty quantification, sparse recovery, model correction

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_9kBcOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
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Soundness
2
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Paper summary

This paper asks what nearby PDE could explain a solver's output. It ranks physically scaled changes to coefficients, forcing, boundaries, and geometry. When causes overlap, the method returns an explanation set. A separate residual grid chooses a candidate for re-solving. I like the workflow, though the strongest guarantees need closer scrutiny.

Critical strengths

The ambiguity treatment is the best part for me. Indistinguishable causes remain together in the output. The exact-collinearity controls make that behavior concrete.

I appreciate the matched residuals, dictionaries, and independent re-solves. The paper also separates repeated solver seeds from independent PDE instances. That makes the empirical comparisons more credible.

Critical weaknesses

The dictionary still carries a lot of prior knowledge. A small remainder means the declared mechanisms explain the field. I'd want real debugging cases before treating that as evidence of the actual fault.

The certified method sometimes says nothing. Every RFM certificate cell has zero accepted diagnoses. That's a serious practical limit, even though abstaining is the honest response.

The search costs substantially more without winning consistently. Median inference takes 0.0467 seconds versus OMP's 0.0019 seconds. I'd struggle to justify roughly 25 times the cost in transfer settings where OMP is stronger.

Questions for authors

Does the nonlinear FDM advantage survive numerically stabilized BIC and stopping rules? Please explain why adding noise raises OMP accuracy from 36.5% to 98.8%. That could materially change my assessment.

Are explanation-set scores calibrated per task or per independent PDE? I'd want one randomized task per PDE or a valid grouped-calibration argument. The selective-risk certificate doesn't automatically establish explanation-set coverage.

How does Theorem 1 handle nested supports and noisy admissibility boundaries? Please distinguish constrained fitting from fitting first and rejecting afterward. I'd need the guarantee aligned with the implemented procedure.

Where does set-based action selection outperform OMP with the same validation layer? I'd want an unplanned solver-fault case where retaining several explanations changes the intervention.

2 comments
AuthorsOpenReview ↗

Official Comment by Authors

Thank you for recognizing the ambiguity treatment and matched evaluation. Your comments helped strengthen the comparisons and clarify their limits.

W1: Dictionary prior knowledge and debugging evidence.

Thank you for emphasizing application evidence. A small remainder means compatibility within the dictionary. New public-source tests cover FiPy's face-coefficient cutoff, scikit-fem's plane-stress formula and FiPy's flux/gradient configuration, alongside SciPy. Direct reproductions and controlled adaptations are labeled separately. FiPy stabilization is proposed, not upstream-merged. Dictionaries/action catalogues still encode prior knowledge. These are retrospective tests, not blind production faults (Appendix O.1, p. 48).

W2: RFM abstention.

Thank you for highlighting this limit. We retain original abstention and align the set score with the existing point null gate before independent study B. With mean-five width-384 RFM, 512 certificate and 384 test PDEs, certified acceptance is 357/384 at all three noise levels. A joint 108-rule audit gives risk upper bounds 6.72/6.70/7.30%, with 18/17/18 accepted-test errors. OLS with the same score has comparable acceptance. Low-fidelity physical-score rules still fail certification. This modified pipeline requires higher fidelity and does not retroactively certify the old rule (Table 39, pp. 45–46).

W3: Search cost.

Thank you for requesting complete costs. We retain the 24.6-fold legacy search ratio and tight-budget failures (Table 34, p. 41). New small-dictionary RFM search medians are 2.97/1.15 ms for structured/OMP. Set/path validation plus re-solving take 94.57/92.53 ms, including assembly and search, excluding input/reference construction (Table 42, p. 47). Matching physical-score OLS has lower search cost. We recommend selection by regime and budget (Sec. 6, pp. 9–10).

Q1: Stabilized baselines and the noise anomaly.

Thank you for requesting this check. Stabilized BIC removes the original noiseless FDM advantage. The legacy baseline refits each extension (OLS-style), although labeled OMP. Near-roundoff RSS makes logarithmic BIC over-select. Noise avoids this regime rather than improving identifiability. Three floors raise 210/576 to 576/576, while noisy cells remain 569/576 (eight tasks on 72 PDEs). Actual stopping tests on 512 fresh PDEs give 100% noiseless accuracy for stabilized OLS and structured selection (Table 26, p. 35 and Table 32, p. 39). New complete-path correlation OMP with the same physical score gives 306/384 versus structured 360/384 in M5, but OLS also reaches 360/384 (Table 35, p. 42).

Q2: Calibration unit and coverage target.

Thank you for this distinction. Each A/B study has 128/256/512/384 independent tuning/calibration/certification/test PDEs, one pre-randomized task each. Profiles/noise are paired. Scores, generators and gates are fixed before calibration. High-fidelity B coverage is 95.31–95.57%, mean size 1.00. Low-fidelity coverage is 90.10–90.63%, mean size 1.39–1.61 (Table 37, p. 44). Missing truths receive infinite excess scores, without deletion. Legacy pooling is descriptive. Per-PDE maxima target simultaneous task coverage (Table 31, p. 38). Risk certification does not establish set coverage.

Q3: Nested supports and noisy admissibility.

Thank you for identifying this gap. Fits now optimize within joint physical bounds. Theorem 1 (p. 5) uses feasible residual images. Nested supports can have zero separation, requiring an actual penalty preference. Non-null output also must pass the fixed null gate. On 128 paired PDEs, the closest-boundary/highest-noise joint case reduces true-support exclusions from 54 to 0 and raises correct diagnoses from 70 to 119 (Table 30, p. 37). The old rejection rule additionally needs an interior margin accounting for noise amplification and ridge bias (Proposition 6, p. 32). Old fits do not inherit the new guarantee.

Q4: Sets versus OMP with the same validation.

Thank you for requesting matched interventions. The new external tests do not establish superiority over full OMP with the same validation. In the flux adaptation both repair 24/24, with OMP cheaper (0.0668 versus 0.3725 s). In SciPy extensions, sets rescue structured point selection from 16/24 to 24/24, while OMP also repairs 24/24 (Table 43, p. 49 and Table 45, p. 50). RFM repair-success counts also match. Identical complete sets/validation give identical actions. The supported benefit is retaining and testing alternatives, with blind production debugging still open.

Thank you again for your careful review and constructive suggestions.

Thank you for the detailed response and the revised manuscript. The constrained fitting procedure and updated recovery proof address my concerns about physical admissibility, and using one randomized task per independent PDE resolves my concern about the calibration unit. The stabilized BIC experiments also explain the original noiseless FDM anomaly. OMP with the same validation still matches the reported repair success rates, so the practical advantage remains unclear. I will raise my score in light of the substantive revisions and additional evidence.

Reviewer_9JFyOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper uses structured backward error and calibrated explanation sets to identify plausible physical changes behind a computed PDE field and uses a separate residual grid to select a model correction that is tested through a new solve.

Critical strengths
  1. The problem is useful for checking numerical PDE solutions. The method turns residuals into physical explanations within a declared dictionary. I like that it keeps several explanations when the available field cannot distinguish them. The physical scaling also makes the comparison between different types of changes more meaningful.

  2. The experimental study is quite detailed. The comparisons use matched residual observations and candidate dictionaries. The ablations examine the score components and the search procedure. The paper also tests transfer across solvers and changes in derivative accuracy. It clearly reports cases where competing selectors are stronger and uses independent solves to evaluate the selected corrections.

Critical weaknesses
  1. My main concern is the handling of physical constraints. The method first fits the coefficients without these constraints and then rejects a candidate if the fitted coefficients are invalid. However, the same candidate may have another coefficient choice that is physically valid and still explains the residual well. For example, noise can push an estimated diffusion coefficient outside the positive range even when the true coefficient remains positive. Rejecting the whole candidate can therefore remove the correct explanation. The recovery argument assumes that the generating coefficients are valid but does not establish that the fitted coefficients remain valid. This leaves a gap between the stated guarantee and the actual procedure.

  2. I am also not clear how the explanation sets are calibrated in the experiments. The coverage guarantee requires exchangeable calibration examples. Several perturbation tasks are generated from the same PDE instance, so these examples share information. The paper gives an independent-instance sampling rule for the separate risk certificate but does not clearly state the sampling unit for the explanation-set threshold. If related task rows are simply pooled, the ordinary calibration argument may not apply. This is not enough to conclude that the reported coverage is incorrect. However, the current description does not clearly connect the experimental calibration procedure to the stated guarantee.

Questions for authors
  1. Could the authors compare rejecting invalid unconstrained fits with fitting under the physical constraints? A focused test with coefficients close to their admissibility limits would be helpful. Please check whether noise causes a valid explanation to be rejected and how this affects diagnosis and the explanation set. If the current procedure is kept, please clarify the additional assumption needed for the recovery result.

  2. What is the sampling unit used to calibrate the explanation sets? Please explain how tasks from the same PDE instance enter the calibration threshold. If the current procedure pools related tasks, please check coverage using a rule that accounts for this dependence. Reporting set size together with coverage would help show the practical effect. Please distinguish this procedure from the separate risk certification step.

4 comments
AuthorsOpenReview ↗

Official Comment by Authors

Thank you for recognizing the physical explanations, ambiguity handling and experimental design. Your questions helped us align the fitting procedure, recovery statement and calibration protocol.

W1 & Q1: Physical constraints and recovery.

Thank you for identifying this gap. Feasible generating parameters do not ensure feasible unconstrained estimates under noise. We now optimize within the joint physical feasible set. A feasible unconstrained optimum is retained. Otherwise the same support receives a constrained quadratic fit, rather than being discarded. Constraints apply to combined global/local coefficients (Sec. 3.1, pp. 3–4 and the procedure in Appendix A, p. 16).

The paired boundary experiment uses 128 independent PDEs, identical observations/dictionaries/scores, four diffusion slacks, four residual-noise levels, and constant or joint diffusion changes. At relative slack 0.0005 and noise 0.01, joint-diffusion true-support exclusions fall from 54/128 to 0/128, while top-1 rises from 70/128 to 119/128. Fixed-gap inclusion rises from 74/128 to 128/128, with mean size 2.02 to 3.00. Constant-diffusion exclusions fall from 49/128 to 0/128. Table 30 (p. 37) retains all 32 settings, including remaining exact-support errors. Gap-0.03 inclusion is descriptive, not calibrated coverage.

Revised Theorem 1 (p. 5) uses distances to physically feasible residual images and applies to constrained fitting. Nested competitors may have zero separation, so uniqueness requires the actual penalty gap. Non-null recovery by the implemented point rule also requires passing its fixed null gate. For the old rejection rule, Proposition 6 (p. 32) gives the additional interior margin: with zero ridge, full column rank and noise norm at most ε\varepsilon, feasibility is ensured by dist⁡(z∗,ZS∗c)>∥XS∗+∥2ε\operatorname{dist}(z_*,Z_{S_*}^{c})>\lVert X_{S_*}^{+}\rVert_2\varepsilon. Ridge requires accounting for bias as well. Legacy fits retain their labels and do not inherit the revised guarantee.

W2 & Q2: Calibration units, dependence and set size.

Thank you for requesting the sampling unit. Each independent calibration PDE contributes one excess score from one pre-randomized task. Dictionary, fitting, score and task policy are fixed beforehand. Calibration and test PDEs are disjoint and use the same policy. Legacy pooled-task frequencies are explicitly descriptive. The separate risk certificate does not establish set coverage.

For the dependence control, Table 31 (p. 38) fixes legacy fits/scores on 24 calibration and 72 evaluation PDEs, each with eight tasks. At RFM noise 0.0005, one-task calibration covers 64/72 randomized tasks, with mean size 5.36. Per-PDE maxima cover all eight tasks on 72/72 PDEs, with mean random-task size 6.17. The targets are marginal random-task and simultaneous cluster coverage, respectively (Appendix H, pp. 32–33). With only eight independent scores, nominal 90% requires an infinite threshold and all 15 labels. We retain these information costs and below-nominal realizations. The theorem is marginal over calibration/test draws, not conditional on every split.

The new A/B studies each use 128/256/512/384 disjoint tuning/calibration/certification/test PDEs, one task per PDE. Profiles and noise levels are paired repeats. A exposed a mismatch between the point null gate and ungated set scores. We retained A, fixed the score change before B, and compared both policies on entirely fresh B PDEs. The revised score uses the same observable null rule before calibration. Its exchangeable-score rank argument is given in Appendix N.2 (p. 43).

In B, high-fidelity set coverage is 95.31/95.57/95.31%, with mean size 1.00. Low-fidelity coverage is 90.63/90.63/90.10%, with sizes 1.54/1.61/1.39 (Table 37, p. 44). Missing truths are assigned infinite excess scores, not deleted. Complete OMP paths omit enough calibration truths to produce an infinite threshold and all 15 labels. This preserves coverage while reporting the loss of discrimination.

Acceptance gates are frozen using tuning data, then assessed on independent certification PDEs. Under the joint 108-rule audit, high-fidelity structured scoring accepts 357/384 test PDEs, with risk upper bounds 6.72/6.70/7.30% and 18/17/18 accepted-test errors. OLS with the same physical score gives comparable results. Low-fidelity rules still fail certification (Table 39, pp. 45–46). These risk bounds control error conditional on accepting a point diagnosis. They are distinct from true-explanation inclusion, and neither result extends beyond the stated exchangeable task family.

Thank you again for your careful review and for helping us make the implementation, assumptions and calibration evidence more precise.

I acknowledge your current work. But from my perspective, there is the huge gap between the original method and current method. and all our experiment should be reset to support your current algorithm. And now my concerns is that current experiment is not enough to support revised method. and I keep my score.

AuthorsOpenReview ↗

Official Comment by Authors

Thank you for your follow-up and for emphasizing that the experimental evidence must support the algorithm described in the revised paper. We have now completed a unified re-evaluation of the original experimental configurations and previous rebuttal studies, together with additional independent-PDE validation, and updated the corresponding manuscript tables and figures.

The revision retains the original NearestPDE framework. Its structured backward-error formulation, physically scaled perturbation dictionary, ambiguity-aware explanation sets, and validation-and-re-solve workflow remain in place. The corrections are limited in scope: enforcing joint physical constraints during fitting, aligning set scores with the existing null-output rule, and using independent PDEs as the calibration unit. The recovery statement is aligned with constrained fitting. The updated experiments distinguish the revised implementation from explicitly labeled ablation controls.

1. Re-evaluation of the original experiments. The evaluation covers all 47 registered original configurations and the previous rebuttal cohorts. With the original configurations retained, we recomputed diagnosis, explanation-set, certification and correction decisions under the frozen implementation. Unchanged forward fields were reused only after configuration and payload checks. The controlled study again identifies all 1,980 identifiable cases and flags all 240 collinear controls. In the original one-dimensional transfer study, independent re-solves improve 1,820/1,824 cases (Table 4, p. 18).

2. Direct validation near physical boundaries. The paired experiment uses 128 independent PDEs and retains all 32 combinations of diffusion slack, noise and constant/joint changes. In the closest-boundary, highest-noise joint-diffusion setting, true-support exclusions decrease from 54/128 to 0/128 and correct diagnoses increase from 70/128 to 119/128. Fixed-gap truth inclusion increases from 74/128 to 128/128, with mean size increasing from 2.02 to 3.00. This is descriptive inclusion, not calibrated coverage. Ties and remaining exact-support errors are also retained (Table 25, p. 31).

3. Independent validation across five PDE families. The additional study contains 6,400 independent PDEs spanning one-dimensional elliptic, unanchored two-dimensional elliptic, interface, large-dictionary and parabolic problems. Each family has disjoint sets of 128/256/512/384 tuning/calibration/certification/test PDEs. Solver profiles and noise levels are paired measurements. In the new noiseless one-dimensional elliptic FEM and RFM settings, structured selection identifies 384/384 test PDEs. The full results also retain harder FDM and large-dictionary settings where cheaper baselines are stronger (Table 1, p. 8; Table 52, pp. 53–54).

4. Independent-PDE calibration, with set size reported. Each calibration PDE contributes one pre-randomized task, with the dictionary, fitting and score policy fixed beforehand. In independent study B, high-fidelity inclusion is 95.31–95.57%, with mean size 1.00; lower-fidelity inclusion is 90.10–90.63%, with mean size 1.39–1.61 (Table 42, pp. 45–46). These explanation-set results are evaluated separately from selective-risk certification. Study C also reports the limits: lower-fidelity inclusion is 82.81–83.07%, and its broader 4,096-rule risk audit requires abstention for the primary structured rules. These outcomes remain in Tables 54–55 (pp. 57–59), with the coverage and certification assumptions stated explicitly.

The revised manuscript therefore provides both a re-evaluation of the original experiments and independent tests of the current implementation. We have kept the framework’s original scope and report where the revised implementation succeeds, where baselines match or exceed it, and where uncertainty prevents an informative or certified output.

Thank you again for your careful review and for prompting us to strengthen the consistency between the method, its theoretical statements and its empirical evidence.

I do not agree that the latest changes amount to a straightforward re-evaluation. The fitting procedure, recovery statement, and calibration protocol have all been revised, while the earlier performance claims have been narrowed. In my view, this substantially changes the method and the paper’s central argument.

And I could accept a huge of additional experiment is done to support the original contribution, but now the storyline is changed, and huge amount of experiment is to support new storyline, which looks like to support a new paper.

I believe the paper could be accepted in the future, but for the current version, I will keep my score.

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

NearestPDE diagnoses a computed PDE field by asking which nearby physical problem could explain it. It ranks changes from a predefined perturbation dictionary using physically scaled residual sensitivities. When several changes are indistinguishable, it returns an explanation set rather than forcing a single answer. The authors study identifiability, calibrate set coverage under stated assumptions, and test selected corrections by re-solving the inferred PDE.

Critical strengths
  1. The treatment of ambiguity is the strongest part of the paper. Different physical changes can produce the same residual pattern, so a confident single label can be misleading. The collinear controls in Figure 1 illustrate why retaining a set of explanations is more appropriate than reporting only top-1 accuracy.

  2. The evaluation goes beyond cause labels and checks whether the diagnosis leads to a useful re-solve. The results also identify settings where structured selection helps, notably nonlinear finite-difference fields and large dictionaries with multiple simultaneous causes. This gives the framework value beyond a residual-ranking exercise.

Critical weaknesses
  1. The benefit of the framework should be distinguished from that of its structured selector. OMP is stronger in several transfer settings (Table 1), and matched selectors produce similar correction results (Section 5.5). The uncertainty and correction components can also be paired with OMP. Structured search has clear successes, but costs more, so the evidence does not support treating it as the default choice across all the tested regimes.

  2. The practical scope remains limited by the declared dictionary and the manufactured test problems. An explanation is a nearby PDE consistent with the observed residual, not necessarily the actual physical cause of an error. The paper acknowledges this distinction, but the results give limited evidence for how a user would construct and calibrate the dictionary for a new application. I view this as a limit on applicability rather than a flaw in the backward-error formulation.

Questions for authors
  1. When would you recommend structured selection over OMP combined with the same explanation-set and correction layers? Can that choice be guided by diagnostics available without the true cause labels?

  2. For a new PDE application, how should the perturbation dictionary and physical scales be chosen before the cause of the discrepancy is known? Please clarify which choices can be reused and which require application-specific calibration.

2 comments
AuthorsOpenReview ↗

Official Comment by Authors

Thank you for recognizing the ambiguity treatment and independent re-solves. Your comments helped us clarify which benefits come from the framework, which depend on the selector, and what a new application requires.

W1 & Q1: When should structured selection replace OMP?

Thank you for emphasizing this distinction. We agree that OMP can use the same explanation-set and correction layers. The revised discussion recommends choosing the selector by regime and total budget, without making exhaustive search the default (Sec. 6, pp. 9–10).

We also distinguish standard correlation OMP from the legacy baseline that refits every extension, recorded as OMP in the older tables. New studies A/B each use 384 independent test PDEs with identical observations, dictionaries, joint constraints and scores. In high-fidelity RFM without added noise, full structured scoring is correct on 360/384 versus 306/384 for complete-path standard OMP with the same physical score. Independent B gives 366 versus 313. However, OLS with that score reaches 360 and 368, respectively. Low-fidelity OLS+BIC can be stronger (Table 35, p. 42). We therefore attribute no exclusive benefit to exhaustive search when a cheaper selector matches it.

For a decision without test-time cause labels, the earlier router was frozen on 192 development PDEs before 384 test PDEs. It checks additional combinations when the greedy normalized remainder is at least 0.01. At 511 local atoms, accuracy rises from 56.25% to 100%, invoking full search on 43.75%. At 31 atoms both reach 100% without full search (Table 20, p. 30). This threshold is specific to the controlled family, and development uses known causes. It is not a universal deployment criterion.

We retain the 0.0467/0.0019-second legacy search costs and the tight-budget failures. In the new flux adaptation, complete OMP-path validation matches all 24 repairs at 0.0668 s versus 0.3725 s for the structured set (Table 45, p. 50). Point routing also does not remove full-set construction costs. These results support starting with a cheaper adequate selector and checking additional combinations when justified by the application and budget.

W2 & Q2: Choosing dictionaries and physical scales before knowing the cause.

Thank you for asking for a concrete procedure. The nominal PDE and inspectable coefficient, source, boundary and geometry settings define the candidate mechanisms. Independent material, measurement or engineering tolerances define their scales. The unknown target cause is not an input (Sec. 3.1, pp. 3–4 and Appendix D, p. 29).

For −au′′=f-a u''=f, include conductivity, source-amplitude and boundary-data changes together. If an independently specified conductivity tolerance is 5% of nonzero a0a_0, set sa=0.05∣a0∣s_a=0.05|a_0|. Source and boundary scales use their own uncertainties, including absolute tolerances where appropriate. The coordinates pg=Dgzgp_g=D_gz_g then compare dimensionless changes. This example specifies the inputs before knowing which mechanism occurred.

Sensitivity formulas, mechanism definitions and unit conversions can be reused for the same operator structure. Physical scales can be reused only while their tolerances remain applicable. Bounds, localization, residual weights and the observation/noise model require application-specific checks. The set threshold is a separate statistical quantity: freeze dictionary, score and gate, then calibrate on representative independent PDEs with one pre-randomized task each. Prespecified perturbations with a trusted solver can supply calibration labels. Reusing a threshold requires exchangeability. Without representative calibration, we report exploratory explanations rather than certified coverage.

The new null-gated set score is separately calibrated and confirmed on fresh B data, with its ungated control retained (Appendix N.2, p. 43). The public-source study includes the existing SciPy case and three additional mechanisms, explicitly separating direct reproductions from controlled adaptations (Appendix O.1, p. 48). These are retrospective cases with declared dictionaries and action catalogues, not blind unknown production faults. A small remainder establishes compatibility within that dictionary, not the actual physical or software cause.

Thank you again for your careful review and for helping us clarify the method's scope and practical setup.

I’d like to thank the authors for their thoughtful responses and additional experiments.

I believe that the authors’ responses and additional experiments have substantially addressed my previous concerns. The additional experiments demonstrate that Structured Selection can outperform OMP in certain complex settings, providing further support for the contribution of the proposed method.

Regarding Q2, the authors have provided a reasonable procedure for specifying the perturbation dictionary and physical scales in advance, based on the PDE structure and independently defined physical tolerances. Overall, I will maintain my original rating of 3 (Weak Accept).

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