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Under review as a conference paper at ICLR 2027

Identifiability before Optimization: Sparse Observation Design for PDE Search

Abstract

A vanishing physics residual can coexist with large solution error when the exposed partial differential equation (PDE) specification leaves the target ambiguous. We isolate this information failure by removing a public condition while keeping the hidden target fixed. For finite-dimensional linear operators, sparse observations restore identifiability exactly when they have full rank on the operator's nullspace; their conditioning controls reconstruction stability. We extend the analysis to estimated ambiguity spaces and local nonlinear problems. Motivated by these conditions, a target-independent portfolio selects observation locations before querying their values. Across seven controlled symbolic-search families, omitting initial data yields a perfect proxy optimum with relative L2 error of 1.000; nine public observations reduce mean error to 0.088, versus 0.074 with the full condition. On 16 PDE libraries, using ten observations with 5% representation mismatch and 1% Gaussian noise, the portfolio achieves mean error of 0.0587, improves on uniform placement in 15/16 tasks, and meets an absolute 0.01 non-inferiority margin to A-optimal design. Independent neural-solver experiments reproduce the omission–repair gap: eight observations improve all 24 paired DeepXDE runs, although Allen–Cahn remains inaccurate. These results distinguish information sufficiency from optimization success and show how ambiguity analysis can guide sparse observation design.

Primary area:
learning theory
Keywords:
identifiability, sparse observations, experimental design, PDE search, inverse problems, scientific machine learning

Reviews

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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_J5EoOpenReview ↗
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2
Confidence
2
Informativeness
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2
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Paper summary

This paper distinguishes insufficient information from optimization failure in PDE solving. It characterizes when sparse observations restore identifiability through nullspace rank and conditioning, and proposes a target-independent observation-selection portfolio. Experiments cover symbolic search, finite-dimensional reconstruction, and neural PDE solvers.

Critical strengths
  1. The distinction between information sufficiency and optimization success offers a useful perspective on why small physics residuals may coexist with large solution errors.
  2. The analysis connects observation count, ambiguity, and stability, supported by paired experiments across multiple solvers and random seeds.
Critical weaknesses
  1. Strong dependence on finite-dimensional representations. The main portfolio benchmark uses a predefined eight-dimensional solution library with ten observations. Successful recovery therefore relies heavily on the assumed representation. Although the theoretical scope is acknowledged, its relevance to richer PDE solution spaces remains unclear. The authors should distinguish representation-level identifiability from PDE-level uniqueness and evaluate larger libraries and stronger representation mismatch.
  2. Limited validation beyond controlled settings. The DeepXDE experiments use fixed uniform observations, demonstrating the benefit of additional information rather than the proposed portfolio. The authors should evaluate the complete selection-and-reconstruction pipeline on more complex settings, such as PhySense benchmarks, using a common reconstruction model and equal observation budgets. Comparisons should include classical and learning-based placement methods, with explicit reporting of information requirements and estimation costs.
Questions for authors

See Weaknesses.

1 comment
AuthorsOpenReview ↗

Official Comment by Authors

Thank you for recognizing the distinction between information sufficiency and optimization success. Your questions led us to test richer representations, evaluate the full external pipeline and report information and cost requirements explicitly.

W1: Representation dependence, larger libraries and mismatch.

We agree that representation-level identifiability is not PDE-level uniqueness. The revised rank/local results retain their assumptions. POD/RFF reconstruction spaces are not asserted exact nonlinear-PDE kernels. Three independent-reference PDEs use 96 historical training trajectories, 12 ID/12 OOD targets, POD/RFF dimensions 8/16/32/64 and 1%/5% noise. We separate fixed k=10 from k=2q. At q=64,k=10, 54 feature directions remain unresolved. With k=128, POD ID errors [Burgers,Allen–Cahn,2D RD] are [.10319,.02672,.02110], but OOD errors remain [.67664,.16228,.89622] with projection floors [.61464,.14201,.81433]. These evaluation-only floors show persistent mismatch. Larger libraries do not ensure recovery. All methods, unstable cases and actual solver-rank diagnostics remain, with repeats averaged within target. The continuum appendix separately proves a conditional approximation bound, not unrestricted uniqueness (Secs. 3.1/7, Appendix E.7 (p. 27), Table 55 (p. 48), Figures 7–8, pp. 49–50, Appendix K (p. 43)).

W2(a): Complete external pipeline and matched comparisons.

We agree that fixed uniform DeepXDE points test added information. The complete PhySense SST evaluation instead compares portfolio/A/Predictive A/QR/spatial/random/published PGD with the same frozen 19,059,980-parameter reconstructor, 15/25/50-value budgets and paired flow seeds on all 366 released test frames. Classical acquisition uses 9,843 historical fields and public calendar/mask inputs, not current target fields. For q=16 without added measurement noise, the mean relative L2 errors averaged over the three budgets and paired flow seeds are portfolio .07911, A .06654, QR .06452 and PGD .04368. The learned-model placement baseline remains better. Post-hoc paired moving-block sensitivity uses four block lengths and both release-row and calendar-label orderings. Label alignment is assumed, not independently certified. The intervals do not create independent-year or calibrated significance evidence. This is one previously examined dataset/fold, not a new blind dataset (Table 4 (p. 9), Table 40 (p. 31), Table 56 (p. 51)).

W2(b): Information requirements and estimation costs.

We added an information-requirements summary covering 19 experiment–method combinations and separated historical preprocessing, basis/pilot estimation, design and reconstruction. Geometry-only placement need not use POD, although every SST arm shares the history-trained backbone. Scalar budgets do not equate hardware or pixel-access costs. A continuous PGD query can interpolate four pixels. Recorded SST design-work medians are portfolio 210.492 s, A 3.4095 s, Predictive A 3.3689 s and QR .06003 s. Individual A/Predictive A include their QR initializer. Basis/pilot and reconstruction are separate, nested totals are not added, and cache/batched timings are not standalone latency. Original backbone-training and PGD-placement costs remain explicitly unknown, not zero. We therefore do not claim an end-to-end cost advantage (Sec. 5.6, Appendix L.3 (p. 50), Tables 57–59, pp. 52–53).

Reviewer_9fLcOpenReview ↗
Rating
2
Confidence
3
Informativeness
3
Presentation
2
Soundness
2
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Paper summary

This paper studies the identifiability problem in PDE solving. It shows that a small physics residual does not always mean an accurate solution, especially when the given PDE constraints are insufficient. The authors introduce an omission–repair protocol to study this problem. They provide theoretical analysis of identifiability and stability based on the null space of PDE operators. They also propose a target-independent observation-design portfolio. It combines existing design methods to select informative observation points.

Experiments are conducted on symbolic PDE search, finite-dimensional PDE libraries, and neural solvers. The results show that sparse observations can greatly reduce errors caused by missing information. The proposed portfolio achieves comparable performance to existing optimal-design methods.

Critical strengths
  1. The paper studies an important problem in PDE solving. It clearly separates information insufficiency from optimization failure. The omission–repair experiments provide direct evidence of this problem.

  2. The paper provides theoretical conditions for identifiability and reconstruction stability. It also considers estimated ambiguity spaces and local nonlinear problems. These results help explain why sparse observations can improve reconstruction.

  3. The authors conduct experiments with different PDE problems, observation budgets, and noise settings. They also compare against strong baselines, including A-optimal, D-optimal, and Pivoted QR. The experiments provide evidence for the proposed identifiability analysis.

  4. The authors test the information-repair mechanism with symbolic search, PINNs, and DeepXDE. This shows that the observed failure is not limited to one specific solver.

Critical weaknesses
  1. Most identifiability failures are artificially created by removing initial conditions or using synthetic problems. These cases are closely related to classical PDE well-posedness. Also, the sparse observations in DeepXDE are computed from the known initial condition. In real applications, such information may not be available. The paper does not sufficiently study naturally under-specified PDE problems or how to obtain additional observations in practice. Can the authors clarify the practical scenarios where the original conditions are unavailable but additional observations can still be obtained? Can the method be tested on naturally under-specified PDE problems?

  2. The necessity of the proposed portfolio is insufficiently justified. The proposed portfolio does not outperform strong baselines such as A-optimal and Predictive A. In Table 3, A-optimal achieves a lower mean error than the portfolio. The paper also lacks direct ablation studies for the components and weights in Equation (6). Therefore, the additional benefit of using this portfolio instead of existing methods remains unclear. What is the main advantage of the proposed portfolio over directly using A-optimal or Predictive A? Can the authors provide ablation studies to justify the design choices in Equation (6)?

  3. The theoretical guarantees mainly focus on finite-dimensional linear problems and local nonlinear settings. However, real PDE solution spaces can be infinite-dimensional. The portfolio is also mainly evaluated on predefined low-dimensional PDE libraries. In the DeepXDE experiments, the authors use fixed observation points instead of the proposed portfolio. Therefore, it remains unclear how the theoretical analysis and the proposed selection strategy can be effectively applied to practical nonlinear PINNs. Can the proposed portfolio be directly evaluated on nonlinear PINNs and compared with existing selection methods?

  4. The improvements of the guarded design are not consistent across different settings. In Table 9, only the clean setting shows a statistically significant improvement over uniform sampling. The results under noisy settings are not statistically conclusive. In Table 12, the guarded hybrid also does not show a significant improvement over uniform sampling under equal-budget and equal-weight settings.

Questions for authors

See weakness.

2 comments
AuthorsOpenReview ↗

Official Comment by Authors

Thank you for distinguishing classical well-posedness from practical acquisition and for highlighting the limits of the portfolio evidence. We have added direct tests and revised the claims accordingly.

W1: Practical acquisition and naturally incomplete data.

We agree that deleting an initial condition is not a new PDE phenomenon, and known-initial-value measurements do not establish practical availability. The controlled omission tests isolate information from optimization. We added published wave-tank records with three occluded camera views and no complete initial state or boundary forcing: four historical runs and eight held-out runs, with locations committed before allowed values are queried. All methods share a history-selected, approximate dispersive-wave model. Original-score/Predictive-A means at 64 values are both .3006. The different-budget 459-value control is .2550. This is retrospective assimilation, not deployment, gap recovery or exact nonlinear-wave uniqueness (Appendix J (p. 40), Table 50 (p. 43)). We also evaluate simulated late acquisition without initial values in the nonlinear PINN study below.

W2: Portfolio benefit, ablations and weights.

We agree that the mixed score is not necessary for sparse information repair and is not uniformly better than A/Predictive A. We added single-term/deletion ablations and a fixed 16-setting weight grid. Full/RMS-only means are .05874/.05655, with paired difference interval [-.00548,.00054]. These results do not establish component necessity. Gaussian squared risk and worst-direction amplification can trade off (full/A ratios 1.0474/.9706), but the original weights 0.25/d0.25/\sqrt{d} and 0.100.10 remain empirical. A separately labeled historical-risk selector uses extra historical selection information. Its laboratory ratio versus A is .9006 (primary-family Holm p=.046875), without established improvement over Predictive A or stronger history-aware designs. This extension does not validate the original weights (Sec. 3.1, Table 26 (p. 24), Table 28 (p. 25), Table 30 (p. 26), Table 51 (p. 44)).

W3: Infinite-dimensional scope and complete nonlinear PINNs.

Finite-library rank and local Jacobian conditions do not certify unrestricted PDE uniqueness or optimizer convergence. We added full proofs that finite linear observations leave ambiguity in an infinite kernel. For a declared L-Lipschitz transport class on an interval of length D with noise bounded by epsilon, the fixed-design exact minimax uniform error is Lh+epsilon, where h is the fill distance in characteristic coordinates. If every coordinate in the interval is attainable, the optimal k-point error is epsilon+LD/(2k). The regularity/noise bounds require independent justification (Appendix K (p. 43)). We also completed public-pilot acquisition, committed late-window sampling and nonlinear PINN training, comparing portfolio/A/Predictive A/QR/spatial/random under common networks, losses, paired initialization and observation budgets. Each model uses 4000 Adam steps followed by independent L-BFGS with strong-Wolfe line search, capped at 500 iterations. There are 672 models but only six private targets per fixed PDE. Portfolio/Predictive-A errors are .53187/.47430 for Burgers and .40273/.38774 for Allen–Cahn. Target-level Holm tests do not establish superiority. Allen–Cahn and full-initial controls remain difficult. Richer POD/RFF and OOD diagnostics are also retained. They do not enlarge the theorem's scope. Physical pilots lack the inputs for the separate uncertainty certificate (Table 38 (p. 30), Table 39 (p. 30), Appendix E.7 (p. 27), Appendix H (p. 35) and Appendix L.1 (p. 48)).

W4: Guarded-design statistical evidence.

We agree that noisy and equal-budget results do not establish consistent guard benefits. Submitted Table 9 is now Table 10 (p. 16): only the controlled clean interval is strictly below zero. The 1%/5% Gaussian and contamination intervals include zero. Submitted Table 12 is now Table 13 (p. 17): equal-budget/equal-weight uniform and guarded means are .11370/.11626, difference +.00256 with 95% interval [-.00088,+.00581]. Nine of fourteen case wins do not override that endpoint. The original geometric gate is not an MSE guarantee. A separately declared historical-risk gate guarantees no worse loss than uniform only for its historical scenarios/mixtures. Its held-out guard/uniform ratio .8154 has secondary-family Holm p=.1875. We retain these inconclusive results without claiming equivalence or general superiority (Sec. 7, Table 51 (p. 44), Appendix J.4 (p. 42)).

The rebuttal period is close to the end. But I did not see the revisions in the paper, as the author says. (Appendix J (p. 40), Table 50 (p. 43), Sec. 3.1, Table 26 (p. 24), Table 28 (p. 25), ...). I remind the authors to upload the revised version. I will keep my score for now.

Reviewer_ey9ZOpenReview ↗
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2
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2
Informativeness
2
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Paper summary

This paper studies the problem of PDE solution identifiability, which consists of finding the correct solution among those that satisfy the PDE, which is known to be a hard problem. As illustration, they show that removing initial conditions of the PDE can lead to trivial yet correct solutions that respect the PDE. This paper proposes to use a few observations ("anchors") to guide the search for a solution; in particular, they focus on how to choose those observation points to maximize information gain and reduce the ambiguity. To choose which measurements most help, they exploit the nullspace of the PDE to find ambiguous directions and deduce which observations would most help. Additionally, the authors propose a "public portfolio" which serves as a tool to select from existing methods for choosing useful observation points; the choice of preferred method is based on a score that combines reconstruction stability and spatial coverage. They show that adding these few observations can reduce reconstruction error without having to improve the PDE solver itself.

Critical strengths
  • This paper presents a new score that combines error amplification and spatial coverage. This combination and its usage for building a portfolio is a useful practical contribution.
  • The authors evaluate the identifiability problem across different PDE families, using different numbers of anchors, noise, and types of solvers. The experiments demonstrate that low residual for PDE does not always imply an accurate solution.
Critical weaknesses
  • The public portfolio does not outperform individual methods (A-optimal, predictive A) in average reconstruction error. The absence of direct ablation of the portfolio scoring components makes it difficult to understand the benefit of the proposed score (see questions for authors). The portfolio is also not clearly evaluated end-to-end for symbolic PDE search.
  • For this work, theoretical foundations rely largely on existing and well-established concepts from nullspace analysis and optimal experimental design. It appears that the method relies on applying these existing ideas to proxy-driven PDE search and combining existing criteria for observation selection rather than introducing a new framework.
Questions for authors
  • I would be interested in how each component of the score (Eq. 6) affects the performance: is the spatial coverage more important than the amplification terms or the opposite? Also linked to the public portfolio, I would like to see how often the proposed portfolio selects each existing method within that portfolio (especially since some of the methods perform better than the portfolio on average). Could the authors evaluate the public portfolio directly in the symbolic PDE-search experiments, comparing it with A-optimal, Predictive A, and QR under identical observation budgets and optimization settings?

  • I am also interested in how robust the portfolio is to errors in the estimated ambiguity space N_hat ? And how does the performance of the portfolio compare with individual methods when we change the levels of error for subspace estimation / when we change pilot noise?

2 comments
AuthorsOpenReview ↗

Official Comment by Authors

Thank you for recognizing the value of the information audit and for requesting direct evidence on the portfolio. We have added the requested comparisons and clarified the contribution and its limits.

W1 & Q1(a): Score components and weights.

We agree that the submitted averages do not establish portfolio superiority. At the original setting (16 fixed-library tasks, d=8, k=10, 5% mismatch, 1% Gaussian noise), full-score/RMS-only errors are .05874/.05655. The paired 95% interval for RMS-only minus full is [-.00548,.00054]. We added single-term and leave-one-out ablations and a fixed 16-setting weight grid without test-based retuning. These do not establish that every component is necessary. Gaussian mean-square risk and bounded-energy worst noise address different objectives: full/A ratios are 1.0474 for Gaussian squared risk and .9706 for worst-direction amplification. Coverage needs a justified residual envelope. The original weights remain empirical, and single-objective designs remain appropriate when that objective is specified (Secs. 3.1/5.6, Table 26 (p. 24), Table 28 (p. 25), Table 30 (p. 26)).

Q1(b): Candidate-selection frequency.

In the order [A,D,E,Predictive A,Predictive E,QR,spectral-logdet], the counts over the same 16 tasks are:

k=8: [6,0,7,1,2,0,0] k=10: [1,1,6,0,7,0,1] k=12: [2,0,7,1,4,0,2] k=16: [0,1,8,2,3,0,2].

Different names can yield identical coordinates, so these counts alone do not establish better recovery (Table 27 (p. 24)).

W1 & Q1(c): Complete symbolic search.

Seven controlled search-surrogate tasks each use 12 paired runs with different random seeds, matched grammar/optimization budgets and absolute noise SD .01. Statistical comparisons use task-level means after averaging the paired runs within each task. Errors [portfolio,A,Predictive A,QR] are [.1382,.1269,.1453,.1553] at k=8 and [.1376,.1426,.1415,.1583] at k=12. Task-level Holm tests do not establish superiority. A separately declared true-residual Burgers/Allen–Cahn extension uses eight targets per PDE, three paired repeats and a richer 128-function bank. At k=16 the corresponding means are [.6763,.7103,.7087,.7016] and [.9075,.9068,.9064,.9048]. Primary target-level Holm tests again show no advantage. Full-initial controls also remain inaccurate after optimizer diagnostics. The bank change and poor recovery are explicit, rather than treated as an unchanged, successful replay (Table 4 (p. 9), Table 29 (p. 25), Appendix I (p. 38), Tables 46–49 (pp. 39–40)).

W2: Contribution relative to established work.

We agree that nullspace analysis, optimal design and perturbation bounds are established. Relative to reduced-basis sparse sensing and gappy-POD stability analysis, our contribution is a matched PDE information audit: hold target, representation and optimizer fixed, vary available constraints, and test sparse repair together with representation and solver controls. The abstract, contribution paragraph, related work and conclusion now state this scope. We do not claim a new general optimal-design theory (Secs. 1/3/6/7, Appendix F (p. 31)).

Q2: Estimated ambiguity spaces and pilot noise.

We distinguish controlled subspace error from noisy-pilot estimation. At angle sine .1, portfolio/A and portfolio/Predictive-A MSE ratios are .9011/.9036 (Holm p=.0438/.0020). At zero error, the portfolio is worse than Predictive A (ratio 1.1335, p=.0429). The six-family noisy-pilot study supplies the true dimension. With 16d pilot rows and nominal pilot perturbation parameter nu=.1, mean relative L2 errors [portfolio,A,Predictive A,QR] are [.017968,.020621,.020621,.017733], without a family-level Holm advantage. Here nu controls a matrix perturbation and is not a relative measurement-noise percentage. The prediction-bias bound requires correct dimension, full rank and valid feature-error bounds. The separate observable diagnostic requires a trusted systematic-bias bound. Certifying positive exact nullity additionally needs a justified nonzero-gap prior. Repeats cannot supply those assumptions. Missing inputs yield an unclassified outcome, and the physical nonlinear pilots remain uncertified (Table 31 (p. 26), Table 32 (p. 27), Eq. 7 (p. 5), Appendix H (p. 35)).

I thank the authors for the detailed response and for running the additional experiments.

The new experiments improve the empirical evaluation of the portfolio (the end-to-end comparisons and the sensitivity analysis regarding subspace estimation errors). I acknowledge that these address some gaps in the original submission. However my main concern regarding the contribution of the portfolio remains: the new results do not show a consistent advantage over individual existing methods; the score ablations also suggest that the different components are not always necessary. I understand that the portfolio combines different objectives, but its practical advantage over simpler alternatives remains somewhat unclear to me. As for the novelty, framing the contribution as a controlled "PDE information audit" rather than a new optimal-design framework could make the scope of the paper clearer, but it does not fully remove my concern about the methodological novelty. I am not entirely convinced that the proposed portfolio offers a strong and novel contribution beyond the existing methods. For those reasons, I will maintain my original rating.

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

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