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Under review as a conference paper at ICLR 2027

Your Physics Prior Might Be a Constant: Controls for Physics-Informed Learning

Abstract

Physics-informed machine learning injects a physical law into training and credits the physics when accuracy improves. On a public wildfire-spread benchmark, we show that this attribution can fail, and that two inexpensive checks expose the failure. The first is a pre-training diagnostic: rank the cells the prior is supposed to discriminate and score the ranking against the class prior. The standard fire-spread law (Rothermel) scores 0.210 against 0.193, nearly uninformative at the data's resolution, which correctly predicts that an eikonal physics loss changes nothing. The second is a set of post-training controls. Distilling a calibrated Rothermel teacher into a U-Net gains +0.104 AP over our reproduced Dice baseline on 12 of 12 folds, a result the standard two-arm design would credit to physics. Yet an information-free constant teacher reproduces the gain, a plain Dice+BCE loss reaches +0.095 with no teacher at all, and a genuinely informative learned prior (a 13k-parameter neural cellular automaton) gains less than a constant at the label base rate. The gain comes from a constant-target regulariser whose strength is set by the target level and not by the prior's information. Compared with an information-free control at its own level, the learned prior transmits a small amount of information (+0.03) and the physics prior none. We propose both checks as standard practice for physics-informed claims.

Primary area:
neurosymbolic & hybrid AI systems (physics-informed, logic & formal reasoning, etc.)
Keywords:
physics-informed machine learning, knowledge distillation, neural cellular automata, interpretability

Reviews

Among:
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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_XUpcOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper studies a potential confound in evaluating physics-informed machine learning: an apparent improvement from introducing a physics prior does not necessarily imply that useful physical information has been transferred to the model.

The paper demonstrates this phenomenon on a wildfire-spread prediction benchmark. Distilling a Rothermel-based physics teacher into a U-Net substantially improves average precision over a Dice-loss baseline. However, the authors show that the Rothermel prior itself has very little predictive information at the spatial and temporal resolution of the benchmark. More importantly, replacing the physics teacher with an information-free constant teacher reproduces almost the entire improvement, while simply modifying the supervised loss to include BCE also captures most of the gain. The authors attribute the apparent physics-informed improvement primarily to a regularization effect that prevents saturation under the original Dice objective, rather than to information contained in the physical prior.

Based on this observation, the paper proposes two controls for physics-informed learning: first, evaluate whether the physical prior itself contains task-relevant information before training; second, compare physics-informed auxiliary objectives against information-free, level-matched controls.

The paper additionally develops a compact neural cellular automaton as an informative learned prior, analyzes the WildfireSpreadTS benchmark in detail, and extracts and compares learned wildfire-response rules.

Critical strengths
  1. I like the central experimental observation. The result that a seemingly substantial "physics-informed" gain can be almost completely reproduced by an information-free constant teacher is a useful caution for evaluating physics-informed methods. The comparison against constant and shuffled teachers is particularly informative.

  2. The paper makes a good methodological point about attribution. A comparison between "with physics" and "without physics" is not sufficient to establish that physical information caused an improvement if introducing the physics term simultaneously changes the optimization or regularization properties of the objective.

  3. The authors perform a relatively extensive set of controls. In particular, they separate the effect of the teacher's output level from the information carried by its spatial variation, and investigate the optimization mechanism behind the improvement.

  4. I also appreciate that the paper attempts to construct an actually informative learned prior as a positive control, rather than only comparing the physics teacher against completely uninformative baselines.

  5. More broadly, the paper raises a useful question for AI-for-science evaluation: when incorporating scientific knowledge improves a model, what experiment is necessary to establish that the scientific information itself, rather than an incidental change in the learning objective, produced the gain?

Critical weaknesses

My main concern is that the scope of the paper's claims appears substantially broader than what is established by the experiments.

The empirical result convincingly demonstrates a failure mode for one physical prior on one wildfire benchmark, especially when the prior is introduced through teacher distillation or an auxiliary soft-target objective. In this setting, the Rothermel teacher contains little usable predictive information at the benchmark resolution, and its apparent benefit can largely be reproduced by an information-free constant target. I find this result convincing.

However, I do not see why this case study is sufficient to motivate the proposed checks as general controls for "physics-informed learning." Physics can enter machine learning in substantially different ways: as a predictive teacher, as a soft target, as a differential constraint, as an architectural inductive bias, or through conservation laws and symmetries. The mechanism identified in this paper seems especially relevant to the first two cases.

For example, consider a standard Physics-Informed Neural Network in which a known PDE is imposed through a residual loss. The value of the PDE is not primarily that it independently predicts or ranks individual labels. Rather, it restricts the admissible function space by requiring the learned solution to satisfy a known differential relation. It is therefore unclear how the paper's notion of "prior informativeness," which is operationalized here through predictive performance of the prior, should be applied to this canonical physics-informed setting.

The paper does include an experiment using the physical law as a residual, but this still demonstrates only that this particular physical model is uninformative at this particular dataset resolution. It does not establish that the proposed diagnostic generalizes to physics-informed learning more broadly. I think the paper should either substantially narrow its claims or demonstrate the proposed controls across several qualitatively different mechanisms for incorporating physical knowledge.

A second major concern is presentation. The central message of the paper is actually quite simple and potentially useful: a physics teacher appears to improve performance; an information-free control reproduces the improvement; the improvement can be explained by the optimization/regularization effect of the loss; therefore physics-informed gains require appropriate controls. However, this message is obscured by a very large number of secondary experiments, benchmark-specific details, numerical results, and side analyses.

In particular, the extensive discussion of the neural cellular automaton, rollout averaging, parameter counts, wildfire response curves, individual environmental variables, benchmark variance, and other implementation details makes it difficult to identify the hierarchy of claims. Many of these analyses may be individually reasonable, but they substantially dilute the main scientific argument. I believe the paper would benefit from aggressive compression around the central causal story, with many of the secondary analyses moved to the appendix.

Relatedly, I found the paper unusually difficult to read despite the central idea being relatively straightforward. Individual paragraphs contain many details and qualifications, but the paper does not consistently distill these details into a small number of conceptual conclusions. As a result, I frequently found myself losing track of which experiments were essential for establishing the main claim and which were supplementary observations.

Finally, once the paper is reduced to its central argument, I am somewhat uncertain about the level of novelty. The observation that an auxiliary loss can improve optimization or act as a regularizer independently of the information contained in its target is not itself surprising. The interesting contribution is applying information-free and level-matched controls to physics-informed claims. I would therefore like the authors to clarify whether they view the primary contribution as a new scientific phenomenon, a methodological recommendation for a particular class of physics-informed methods, or a broader evaluation framework for AI-for-science.

Questions for authors
  1. What is the intended scope of the proposed controls? Are they primarily intended for physics-informed methods in which physics enters as a teacher, pseudo-label, or auxiliary prediction target, or do the authors intend them to apply to physics-informed learning in general?

  2. How should Check One be defined for a standard PINN in which the physics prior is a known governing PDE? A PDE does not naturally provide a standalone ranking of examples analogous to the wildfire prior used here. Its information instead comes from restricting the admissible solution space through a differential constraint. What would constitute an "information-free" or "level-matched" control in this setting?

  3. More generally, how would the proposed framework handle other common forms of physical knowledge, such as conservation laws, equivariances, symmetries, or physics-informed architectures? These seem qualitatively different from distillation from a physics teacher.

  4. The current evidence comes from one physical law and one benchmark. What evidence supports recommending these checks as standard practice beyond this setting? I would find experiments across qualitatively different physics-informed mechanisms substantially more convincing.

  5. What do the authors consider the primary scientific contribution of the paper? Is it the discovery of the constant-target regularization mechanism in this wildfire experiment, the proposal of information-free controls for physics-informed evaluation, or a broader claim about physics-informed learning? Clarifying this hierarchy would make the paper much easier to evaluate.

  6. How essential are the extensive NCA experiments to the central contribution? I understand its role as an informative positive-control prior, but much of the subsequent NCA analysis appears orthogonal to the main methodological claim. Could the main paper be substantially simplified by retaining only the NCA results necessary for the control experiment and moving the remaining analysis to the appendix?

  7. Could the authors reorganize the paper around the central causal chain: apparent physics-informed gain -> information-free control reproduces the gain -> loss-level mechanism explains the gain -> methodological recommendation? I think this would substantially improve readability and make the scientific contribution easier to assess.

1 comment

We thank the reviewer for a detailed and constructive report. We agree with the two main concerns, and we would like to respond to them directly.

The reviewer is right about the scope, and we will narrow the claims. The controls are intended for methods in which physics enters as a training signal: a teacher, a pseudo-label, a soft target, or an auxiliary loss term. Our evidence supports them for that class, and we will state that in the title subtitle, the abstract, and the introduction. We do not claim they cover architectural priors, symmetries, or conservation laws built into the model, and we will state this explicitly.

We agree that a governing equation does not rank examples, and that "check one", as we implement it, does not transfer unchanged. However, we propose that the idea behind it does: before training, measure on held-out observations whether the law holds better than a null alternative at the data's resolution. For a residual loss, this is the residual of the law evaluated on observed data, compared with the residual of a deliberately wrong law. The matching control for "check two" is to train with that wrong law, for example with shuffled or constant coefficients, which keeps the form of the loss and removes the physics. We have not tested these forms, and the revision will present them as a proposal and not as a result. Our own residual experiment supports only the narrow statement that this law is uninformative at this resolution.

We view our contribution as a methodological recommendation for the class above, supported by one fully worked case. We agree that an auxiliary loss acting as a regulariser is not surprising in itself. What we add is the demonstration that it can account for an entire physics-informed gain on every fold of a public benchmark, and the level-matched controls that separate the two effects. The finding was not planned: we set out to improve wildfire prediction with a physics prior, and our own controls refuted the result.

We accept the criticism on presentation and will reorganise the paper around the chain the reviewer describes: the apparent gain, the information-free control that reproduces it, the loss-level mechanism, and the recommendation. The learned prior will stay in the main text only in its role as the positive control. Its capacity study, rollout analysis, and rule extraction will move to the appendix, and each section will end with a single stated conclusion.

On evidence beyond this setting, we agree that one law and one benchmark is a limitation. Additional experiments are in progress and will be included in the final version if the paper is accepted.

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

This paper considers the physics-informed learning problem and claims that for the wildfire-spread benchmark injecting physical prior does improve the learning accuracy. For this the paper compares the training with and without physics and shows that physical knowledge may not necessary lead to an improvement in the accuracy.

Critical strengths

The idea of the paper is interesting, and it boils down to the question: is a physical prior always useful? Which is a fair question to ask and investigate in physics-informed learning. However, the paper is a little confusing to me, with lots of terminologies that could be better motivated and introduced.

Critical weaknesses

Regarding the results, I think that it needs more validation compared to its one law on one benchmark. The authors also seems to be overlooking the literature on regularized empirical risk minimization and complexity dependent bounds for physics informed learning, where it is proved that a well aligned physical knowledge can speedup learning.

1. A. Scampicchio, LF. Toso, R. Rickenbach, J. Anderson, M. N. Zeilinger, “Physics-informed learning under mixing: How physical knowledge speeds up learning” ICLR 2026
2. Doumeche, N., F. Bach, G. Biau, and C. Boyer. “Physics-informed machine learning as a kernel method”. COLT 2024.
3. Diego Marcondes Complexity Dependent Error Rates for Physics-informed Statistical Learning via the Small-ball Method. 2025.
Questions for authors

This brings the following questions and comments:

Have the authors checked if the physical knowledge considered really aligns with the “ground truth” underlying model? If so, how this connects to the theoretical works listed above in the weaknesses?

How this observation would generalize to other back marks and physical laws? Given the fact that it may exist a physical law where you might actually be able to see the improvement in the accuracy.

I feel that the current version of the paper is missing theory and validation.

The paper claims would be improved if it can provide additional validation for physical laws and benchmarks. In addition, the writing could be improved by explaining terminologies in the text.

3 comments

Dear reviewer,

Thank you for the comments and additonal references.

We would first like to clarify the paper's claim, since the summary describes a comparison of training with and without physics. That comparison is the standard design, and in our case it shows a gain of +0.104 AP for the physics addition. Our point is that this design cannot tell where the gain comes from. When the physics teacher is replaced by a constant that carries no information, the gain remains (+0.102). The paper therefore does not claim that physical priors are not useful. It claims that a with/without comparison is not sufficient evidence that they are, and it proposes two inexpensive checks that are.

Alignment with the ground truth is exactly what our first check measures. Before any training, we rank the cells where the law is supposed to act and compare that ranking with the observed outcome. For the Rothermel law at this benchmark's resolution, the alignment is close to chance (0.210 against a class prior of 0.193), while for a learned prior it is high (0.399). We see no conflict with the theoretical works the reviewer lists. As the reviewer notes, they show that well-aligned physical knowledge speeds up learning. Our results concern the complementary case: the knowledge is poorly aligned with the data, yet the standard experiment still reports a gain. Our checks are a practical test of the alignment premise those results rely on. We will cite and discuss these works in the revision.

We agree that the evidence is one law on one benchmark, and we state this as a limitation. We also agree that laws exist for which a real improvement would be seen, and the checks are designed to detect that case as well. The learned prior in our study passes both checks, which shows they do not only return negative answers. Additional experiments are in progress and will be included in the final version if the paper is accepted.

We will also define the terminology at first use, in particular front cells, level-matched controls, and the two checks, and add a short overview of the experimental design at the start of the paper.

We also thank the reviewer for these references and will cite them. They are complementary to our work and do not overlap with it. All three analyse a regression estimator with a physics residual penalty, and each speed-up is proved under a condition on the physics: Scampicchio et al. require the prior to be aligned, Doumèche et al. obtain faster rates "depending on the physical error", and Marcondes quantifies how the gain degrades under misspecification.

Our paper addresses the step that precedes these results in practice, which is whether that condition holds for a given law and dataset. Check One measures it before training. For the Rothermel law at this resolution, alignment is close to chance (0.210 against a class prior of 0.193), thus the theory predicts no gain, as confirmed by our residual experiment. Our second finding is outside their setting, as with a soft-target loss, a gain appears even though alignment is absent, because the auxiliary term regularises the network. No rate result predicts or excludes this, which is why, as we propose, empirical control is needed.

Reviewer_SbvNOpenReview ↗

Comment by Reviewer SbvN

I thank you the authors for the clarification, the response clarifies the contribution, but the current evidence shown in the paper still leaves open how reliably the proposed checks work across other physical priors and settings. I mean, other physical laws might be better aligned with the underlying dynamics, which might then show the improvements from adding the physics. I will keep my rating.

Reviewer_hDh1OpenReview ↗
Rating
3
Confidence
1
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper argues that the standard two-arm physics-informed experiment cannot distinguish a real physics contribution from a loss-form artefact. On WildfireSpreadTS the authors reproduce the published baselines, distil a calibrated Rothermel spread law into a Res18-U-Net, and get +0.104 AP on 12/12 folds. They then show that (i) a one-forward-pass pre-training diagnostic — AP of the prior's ranking of front cells against the class prior — finds the law nearly uninformative (0.210 vs 0.193) and correctly predicts that an eikonal residual changes nothing; (ii) an information-free constant teacher at 0.196 reproduces the gain (+0.102), plain Dice+BCE gets +0.095 with no teacher, and the physics arm beats the constant by only +0.003 [−0.009, +0.018]; (iii) a 13k-parameter NCA, a prior that genuinely carries information, passes both checks (+0.031 over its spatially shuffled copy). The conclusion is that the gain is a target-level regulariser, and that both checks should be standard.

Critical strengths
  1. The diagnostic is validated prospectively, in both directions. This is what lifts the paper above a post-hoc debunk. The same statistic that flags Rothermel as uninformative (0.210 vs 0.193) also flags the NCA as informative (0.399), and both predictions are confirmed downstream — the eikonal loss does nothing, the NCA beats its shuffled control. Validating an instrument on a positive and a negative case is the right design, and the cost asymmetry (~one inference pass vs ~30 GPU-hours of physics-loss runs) makes it adoptable.

  2. The level-matched controls give a clean attribution. Turning "+0.10 from physics" into "level effect + information effect" is the paper's real contribution, and the constant-teacher result is hard to argue with: 12/12 folds, per-fold, and consistent at the year level. This transfers to any auxiliary-loss claim, not just fire.

Critical weaknesses
  1. Scope versus framing. The evidence is one semi-empirical law on one benchmark at one daily/375 m resolution. The paper says so plainly in section 9, but the title and abstract read as a general claim about physics priors. More concretely, the Rothermel teacher is a per-pixel logistic of rate of spread, not a propagation model; the authors themselves write that a one-step level-set teacher "would be a fairer physics teacher and is future work." So part of the negative result may be a statement about this teacher rather than about the physics at this resolution. Check One is a decent defence, but it does not fully close this.

  2. The positive claim is underpowered. section 6's recipe (+0.011 over Dice+BCE) is single-seed, the measured seed spread is 0.006–0.024, one run collapsed to 0.043 against 0.309/0.311, and the fold-level p=0.043 does not survive Holm. Calling it a recipe overstates what the data support. Relatedly, the abstract's headline comparison of the NCA (+0.062) against a constant at 0.196 (+0.102) is exactly the level-unmatched comparison the paper spends five pages arguing against; the level-matched number is +0.031. This does not sink the negative result, but it weakens the rhetorical symmetry, and I would like to see the abstract use the matched number.

Questions for authors
  1. Could you add a spatially shuffled Rothermel teacher on the folds where t(x) actually varies (e.g. fold 11, 1–99th percentile span 0.135)? That is the exact analogue of your NCA control, and it would make the +0.003 less dependent on how "same level" is defined.

  2. Would a one-step level-set propagation teacher (ROS setting local advance from the observed mask) pass Check Two on the four probe folds? If it fails too, the "no information to transfer" conclusion becomes much stronger; if it passes, the boundary of the claim becomes much clearer.

  3. What AP lift counts as "informative enough" in Check One? A threshold derived from fold-level variance would make the diagnostic usable by others. Also, how does it extend to continuous priors or regression targets?

  4. Can you decompose the +0.104 into (a) adding a non-vanishing-gradient BCE term (+0.095), (b) the target level (~+0.01), (c) prior information (~0)? The phrase "a level effect worth up to +0.10" currently reads as if (b) alone were +0.10, which your own §6 contradicts.

  5. Would three seeds on the 12 folds (or at least on the four probe folds) justify keeping the word "recipe" in sec6?

1 comment

Dear reviewer,

Thank you for your careful reading, we agree with most points.

The result was found by chance: we set out to improve wildfire-spread prediction with an NCA and a physics prior, and the controls refuted our own positive result. We then chose to present the checks as a general method. We agree the evidence concerns one law, one teacher, and one resolution, and the abstract will say so. Check One is computed on the raw Rothermel rate of spread, before any teacher is built, so the missing ranking information (0.210 vs 0.193) does not depend on the per-pixel logistic. We agree that a propagation teacher is the open test.

Agreed on the recipe; the revision will no longer present it as a contribution. A weight-matched control, Dice + 2·BCE(y), reaches 0.4525 against 0.4542 (+0.0017, 6/12 folds), so the margin is a BCE-weight effect. Three seeds on the probe folds are now reported, and the word "recipe" will be removed.

We agree on abstract comparison. The abstract will report the level-matched number (+0.031 over the shuffled copy).

Shuffled Rothermel teacher is the right control. Existing evidence points the same way: across the 12 folds, the Rothermel-minus-constant difference does not grow with the teacher's spatial spread (Spearman −0.55) or with its Check One lift (+0.12, p = 0.71).

We have no principled threshold and will say so. A practical reference is the fold-to-fold range of the class-prior AP ([0.156, 0.233]): Rothermel's lift (+0.017) is well inside it the NCA's (+0.206) is far outside. For continuous targets a rank correlation can replace AP. we have not tested this.

Regarding the decomposition of +0.104, the reviewer's reading is correct, and our phrase is misleading. Any BCE term supplies a non-vanishing gradient on saturated pixels (+0.095 from BCE(y); +0.102 from a constant at 0.196; +0.050 at ≈0.002); stacking the two adds +0.01; the prior's information adds ≈0. We will rewrite the sentence.

The shuffled Rothermel teacher, a one-step level-set teacher, and additional seeds are in progress and will be included in the final version if the paper is accepted.

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

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