- Rating
- 2
- Confidence
- 2
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 2
Read review
Paper summary
The paper examines how cross-field coupling structure affects neural-operator learning at different data scales. Structural interventions compare PDE-derived graphs with dense, uncoupled, and mismatched alternatives. A proposed initialization procedure uses short pathway-specific probes to set interaction strengths before joint training. The experiments report improvements in several regimes and evaluate the frozen procedure on an additional physical system.
Critical strengths
-
The structural controls are a useful part of the study. Holding the edge budget fixed makes mismatched graphs more informative than an arbitrary architecture comparison. The pathway-removal results also show why equally sized graph changes can have very different predictive consequences. This is a concrete observation that could guide model design.
-
The method is accompanied by relevant ablations, including uninformed gates and frozen probe initialization. Reserving a further system for evaluation after the procedure was fixed adds evidence beyond the development settings. I also appreciated the explicit reporting of a stronger external baseline in one regime.
Critical weaknesses
-
The main interpretation goes beyond what the comparisons identify. The prior-fidelity measure in Section 3.2 compares the PDE graph with deliberately mismatched graphs. Increasing separation can reflect growing harm from a wrong structure, without showing increasing benefit from a correct prior over a flexible model. The paper itself reports a different trend for the latter comparison. There is a related issue with “trust”: the adaptive method considers the full candidate set, and a gate can be compensated by rescaling its kernel. Useful predictions do not make the gate a uniquely interpretable measure of reliance on PDE knowledge. I see stronger evidence for an initialization strategy and a misspecification study.
-
The reliability and cost of the additional method benefit need a fairer comparison. The proposed procedure uses auxiliary probe training beyond the baselines' main optimization budget, while the low-overhead statement emphasizes the final run. A baseline with comparable auxiliary training or validation-guided initialization would be more informative. Evaluation also relies on few independent test configurations, and some reported improvements are small relative to training variability. The stronger scarce-data results are encouraging, but they do not settle whether the full adaptive procedure is consistently preferable to simpler initialization choices.
Questions for authors
- Can the scaling conclusions distinguish PDE-versus-Dense benefit from PDE-versus-mismatched-graph separation? Which claimed findings require each contrast?
- Is there any normalization or functional contribution measure that makes gate values interpretable as trust? If not, how should their physical interpretation be limited?
- What is the complete cost per regime, including the self-only model, all pathway probes, validation, and final training?
- Were equally budgeted training or initialization controls run? Existing results would help determine whether the auxiliary evidence, rather than additional optimization opportunity, explains the gain.
- Can paired per-seed and per-test-configuration differences be reported against the strongest fixed baseline? Any existing alternative-split results would help assess sensitivity to the small test set.
4 comments
Response to Reviewer tBGr (2/2)
Q1: Which contrast each claim needs
"Can the scaling conclusions distinguish PDE-versus-Dense benefit from PDE-versus-mismatched-graph separation? Which claimed findings require each contrast?"
Yes, and each claim now names its contrast (Section 3.2, Table 13).
- A correct prior loses value as data grows: this rests on the PDE-versus-Dense contrast.
- The cost of a wrong prior depends on the system: this rests on the PDE-versus-mismatched contrast.
- The harm of a wrong graph follows the pathway it removes: this rests on the leave-one-pathway-out interventions (Section 3.3).
Q2: Can gate values be read as trust?
"Is there any normalization or functional contribution measure that makes gate values interpretable as trust? If not, how should their physical interpretation be limited?"
We found no normalization that does this, because the kernel can absorb the scale. On Active Matter the D->U gate ends at 0.27, while removing that pathway costs 64% at abundant data (Appendix F, Table 5). The revision limits the interpretation where the gate is defined: is an initial pathway scale set from probe evidence (Fig. 1 caption, Section 4.1). The functional importance of a pathway is measured by its removal effect (Section 3.3).
Q3: Complete cost per regime
"What is the complete cost per regime, including the self-only model, all pathway probes, validation, and final training?"
Per regime the method runs one self-field model and six single-pathway probes, 2,000 steps each. This is 14,000 raw steps, or 70% of the 20,000-step full run, and 30% in full-model-equivalents. One 20,000-step final run follows. It takes 1,111 s on one RTX 3090, against 1,276 s for dense coupling (Appendix N). Validation is not a separate stage: each probe is scored on the validation split within its 2,000 steps, and checkpoint selection uses the validation split for every arm.
Q4: Equally budgeted controls
"Were equally budgeted training or initialization controls run? [...]"
Yes. The three controls under W2 cover this (Table 7; Appendix T, Tables 15 and 16).
- Equal budget without evidence (M2) shows no gain.
- Structure selection with the probe's step budget and the same validation split is behind M3 on every seed, on AM-scarce (five seeds) and on RBC-scarce (five seeds).
- A simpler initialization with the same probe evidence, the gate-free arm, matches M3 in all four scarce and medium cells of AM and TRL.
The auxiliary evidence therefore explains the gain.
Q5: Paired differences per seed and per test configuration
"Can paired per-seed and per-test-configuration differences be reported against the strongest fixed baseline? [...]"
Both are reported. Per seed, Appendix Q (Table 11) compares M3 with the PDE graph, the strongest fixed baseline on AM-scarce: 6.468% against 6.766%, a reduction of 0.298 pp (95% CI [0.010, 0.586], 3/3 seeds). On RBC-scarce the strongest fixed baseline in the paper is dense coupling, and the paired reduction is 0.0041 (95% CI [0.0021, 0.0060], 3/3 seeds; Appendix T, Table 17). Per test configuration, Section 5.6 reports the paired changes over the 21 held-out AM configurations, and Table 14 lists all nine TRL configurations one by one. The splits are fixed for all arms, and the 21 and 9 held-out configurations are the sensitivity evidence.
If the revision addresses your concerns, we would appreciate it if you would consider updating your score.
Follow-up to Reviewer tBGr
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 reliability and the cost of the gain. The revision adds seed-paired tests on AM-scarce (a reduction of 0.298 pp, 95% CI [0.010, 0.586]) and on RBC-scarce (0.0041, 95% CI [0.0021, 0.0060]). It also adds the equally budgeted control that you asked for. A selection baseline with the probe's step budget reaches 7.40% on AM-scarce against 6.44% for M3, and M3 is lower on every seed (Appendix T, Tables 15 and 17). The rebuttal also covers the reading of the gate, which the paper now describes as an evidence-initialized pathway scale (Section 4.1). We hope these additions give a fuller picture of the work.
We would also like to highlight the main result of the paper. PDE-derived coupling structure is already a common inductive bias in neural operators for multi-field systems, and such models are usually compared with an unconstrained baseline. Our design holds the backbone, the edge budget and the evaluation fixed, and each cross-field pathway can be imposed, removed or replaced. It shows that the value of a coupling graph comes from individual pathways. One pathway per system dominates and grows with data (Active Matter D->U: +10.6% -> +64.4%; turbulent radiative layer U->R: -0.8% -> +31.4%), and the harm of a wrong graph follows which pathway it removes (Spearman 1.00 on TRL). The method that follows from this study was frozen before it was tested on Rayleigh-Benard convection, where it is 4.7% below the best fixed structure at scarce data. These results are, to the best of our knowledge, new in the literature on physics-guided neural operators. Your review notes that holding the edge budget fixed makes mismatched graphs more informative than an arbitrary architecture comparison, 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.
Official Comment by Reviewer tBGr
Thanks to the author for the rebuttal. After reading the rebuttal carefully, I will maintain the score.
Response to Reviewer tBGr (1/2)
We thank the reviewer for a careful review. Its main suggestion is to read the paper as a misspecification study together with an initialization strategy, and the revision now presents it that way.
W1: What the comparisons identify, and the trust reading
The revision separates the two contrasts that the review distinguishes (Section 3.2, Table 13):
The span S(N) is the second contrast normalized by the Dense error, and the Fig. 2 caption now says that the panel plots S(N) only. The claim of the paper is the one these comparisons support: the amount of data alone does not determine the cost of a wrong prior.
On the gate: it multiplies a linear spectral weight, so the kernel can absorb its scale. The revision describes it as an evidence-initialized pathway scale (Fig. 1 caption, Section 4.1) and presents the method as an initialization strategy. A new control supports that reading (Appendix T, Table 16). We removed the gate and initialized each operator at its probe-based scale. This gate-free arm matches M3 in all four scarce and medium cells of AM and TRL, on the same three seeds: 6.445% against 6.468% (AM-scarce), 3.981% against 3.972% (AM-medium), 10.48% against 10.46% (TRL-scarce) and 8.51% against 8.47% (TRL-medium).
W2: Reliability and cost of the gain
Cost. The probe is seven 2,000-step runs per regime, which is 70% of a full run in raw steps and 30% in full-model-equivalents (Section 4.5, Appendix N). Section 4.5 now limits the no-overhead statement to the final run.
Comparable controls. Three controls separate the probe evidence from extra optimization. The second and third are new (Appendix T, Tables 15 and 16).
Reliability. The revision reports four checks.
On AM-medium the gain is 0.09 pp on 3/3 seeds. TRL-medium is a tie, and the two abundant cells are 0.07 and 0.08 pp behind the PDE graph. The abstract and Section 5.2 now say so.