acceptodds
Under review as a conference paper at ICLR 2027

Better Reconstruction, Worse Transfer: Probing Representation Geometry in Cross-Reynolds Generalisation

Abstract

Neural PDE surrogates degrade sharply when the governing physical parameter shifts. How the degradation distributes across the components of the pipeline has not been measured, so improvement effort is allocated by intuition. We address this on a zero-shot cross-Reynolds task in forced 2D Navier-Stokes, using a retrieval predictor as a diagnostic instrument, not because it is competitive, but because it is decomposable: its encoder, database, selection rule and autoregressive loop permit nested diagnostic substitutions. In seed 42, these give a 16.2% encode-decode reference, a 5.7-point reference-to-refreshed-oracle gap and a 14.0-point state-refresh gap; neither contrast distinguishes error injection from dynamical amplification. Holding representation and output path fixed, retrieved increments transfer better than the two tested learned-transition implementations, though by smaller margins than the equal-width PCA-ConvAE contrast; this does not make the increment mechanism irrelevant. Representation interventions then decouple reconstruction from transfer. A random projection of equal width yields 99.42% error, level with its own 99.27% reconstruction reference error, so reducing dimension is not by itself sufficient. A linear encoder of equal width reconstructs the target regime better (10.99% against 16.20%) yet transfers worse (41.93% against 38.30%, paired CI [3.26, 4.00]), a reversal that holds for all three autoencoder training seeds, so reconstruction fidelity does not determine transfer ordering. Widening that linear family from 64 to 512 improves the reconstruction reference error 3.16-fold while leaving transfer error unimproved, so capacity does not determine it either. Tested nonorthogonal invertible linear reparameterisations preserve reconstruction to numerical tolerance but increase mean deployment error by up to 4.75 points, showing that transfer depends on the retrieval coordinate frame even when reconstruction is held fixed. On the physical-output route, a fourth encoder trained with no reconstruction objective transfers 11.92 points worse (paired CI [11.30, 12.54]) while passing its encoder collapse diagnostics, so a non-reconstruction objective is not by itself sufficient either. Eight further candidates have mixed outcomes, including beneficial database expansion, a nonsignificant curvature-proxy association and an untested phase-alignment control. The established result is a decoupling between reconstruction fidelity and deployment ordering; organisation is a suggested explanation still to be identified. All claims are scoped to this benchmark and a tenfold parameter shift. We do not present a method: no tested diagnostic variant beats its canonical baseline.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
neural PDE surrogates, operator learning, out-of-distribution generalisation, representation geometry, turbulence, retrieval-based prediction, error decomposition, diagnostic analysis, zero-shot transfer, autoregressive rollout

Reviews

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1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_MwS2OpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
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Soundness
3
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Paper summary

This paper is a diagnostic study of cross-Reynolds generalization failure in neural PDE surrogates, explicitly positioned as a measurement contribution rather than a new method. Working on zero-shot transfer from ν=10⁻³ (Re≈1,000) to ν=10⁻⁴ (Re≈10,000) in forced 2D Navier–Stokes (64×64 vorticity fields, 500 target trajectories, 10-step rollouts), the authors adopt a retrieval-based (analog/RIDE-style) predictor as a decomposable instrument: its encoder, database, selection rule, and autoregressive loop permit nested oracle substitutions that localize the deployment error (38.30%) into an encode–decode reference (16.20%), a +5.66 pp gap to a refreshed-base direction oracle, a dominant +14.01 pp state-refresh (compounding drift) gap, and a +2.44 pp selector gap. The central finding is a decoupling between reconstruction fidelity and deployment ordering: at equal latent width and a common output route, PCA-64 reconstructs better than ConvAE (10.99% vs 16.20%) yet transfers significantly worse (41.93% vs 38.30%); widening PCA from 64 to 512 improves reconstruction 3.16-fold without improving deployment; a random-projection control and an opposite-direction JEPA intervention (11.92 pp worse despite passing collapse checks) further rule out dimensionality, capacity, and non-reconstruction objectives as sufficient explanations. A fidelity-preserving reparameterization intervention shows that invertible linear changes to the retrieval coordinate frame leave reconstruction unchanged to numerical tolerance while nonorthogonal frames degrade deployment by up to 4.75 pp, indicating that retrieval geometry matters even at fixed fidelity. An inventory of eight candidate explanations (mismatch growth, temporal context, database coverage, similarity metric, curvature, phase coordinates, dynamics objective, step-1 anomaly) yields mixed evidence without identifying a responsible mechanism, and a paired spectral-norm audit shows metric weighting only mildly affects method ordering. The authors emphasize scope limits (one benchmark, one tenfold shift, exploratory design with paired bootstrap intervals), retain dual records and pre-registered expectations, and state plainly that no tested variant beats its canonical baseline.

Critical strengths

S1. A genuinely novel diagnostic methodology with one cleanly controlled causal-style demonstration. Using a retrieval predictor not as a competitor but as a decomposable instrument — with nested substitutions (reconstruction reference → refreshed-oracle → free-running-oracle → deployment) that localize the transfer deficit into conditional components — is, to my knowledge, a new experimental design in neural-PDE evaluation. Within it, the fidelity-preserving reparameterization experiment is the standout: orthogonal transforms leave deployment unchanged to ~10⁻⁶ pp (5,000/5,000 index agreement, as cosine invariance analytically requires), while nonorthogonal frames degrade deployment monotonically with index-agreement loss (up to +4.75 pp under whitening) — all with reconstruction held fixed to numerical tolerance. This is as close to an interventional identification of "retrieval coordinate frame matters" as one can get without retraining, and the equal-width PCA–ConvAE reversal (10.99% vs 16.20% reconstruction, yet +3.63 pp worse deployment, paired CI excluding zero) is a well-controlled demonstration that reconstruction fidelity cannot order deployment. This strength is consequential to my assessment because it is the paper's real claim to a lasting contribution: a measurement methodology and a cautionary result that should change how the community screens representations for cross-regime deployment. S2. Audit discipline of a standard rarely seen in this literature. Pre-registered expectations are confronted with outcomes (four of five expectations falsified, including the whitening reversal, and reported as such); a pre-specified Stage-3 gate was not met and the stage was not run, explicitly flagged as "not a null result"; paired bootstrap intervals with pinned seeds throughout; numerical validation against analytic targets (affine PCA decoder checks within 1.9×10⁻⁶); dual records preserved rather than silently reconciled. This is consequential because the paper's genre — an exploratory diagnostic study — lives or dies on the credibility of its negative and reversal claims, and this rigor is what makes the central reversal believable rather than anecdotal. It also gives the paper reusable value (retained arrays, protocols, stopping rules) independent of its conclusions.

Critical weaknesses

W1. The headline claim is demonstrated only on a knowingly non-competitive retrieval instrument, and its portability to learned predictors — the systems readers will assume it concerns — is entirely untested. Within the retrieval pipeline, "transfer" means borrowing source-regime increments: deployment error never passes through any learned dynamics, so the reconstruction–transfer decoupling is, mechanistically, a statement about retrieval geometry and neighbour selection under distribution shift. The title and abstract invite the broader reading (neural PDE surrogates generally — FNO, U-Net, ConvAE-GRU), yet no learned-transition pathway is subjected to the same reconstruction-vs-deployment ordering test. This is consequential because it caps the paper's significance: the finding may be specific to analog-style prediction rather than a property of representation learning for PDE dynamics. Combined with the single benchmark, single grid (64×64), single forcing mode, and single tenfold viscosity shift (with the more discriminating boundary regime disqualified by the resolution audit), the evidence supports a narrower claim than the framing asserts. W2. The study fails on its own stated goal: no mechanism is identified, and the key quantitative pillars rest on fragile foundations. The paper sets out to probe what property of representation geometry drives transfer, but the eight-candidate inventory ends in mixed or inconclusive evidence; the coordinate-frame intervention establishes that the frame matters while explicitly not identifying which property is responsible; and the most informative anomaly (whitening's unexpected +4.75 pp degradation, against a pre-registered expectation of improvement) is not pursued to a mechanistic follow-up. Meanwhile the load-bearing numbers are weaker than the presentation suggests: the oracle ladder — the paper's error-localization backbone — exists only for seed 42, while seed-to-seed spread in the reconstruction reference (13.89%–16.20%) implies the ladder's absolute magnitudes may vary materially; the selection×refresh factorial is incomplete; the JEPA contrast uses a seed-42 physical baseline rather than a three-versus-three control; and several headline-adjacent records remain unreconciled (U-Net 34.72% vs 34.668555%; deployment 38.300117% vs 38.300047%). This is consequential because a diagnostic paper whose diagnostics are single-seed and whose mechanism hunt comes home empty delivers less than its framing promises — this, jointly with W1, is what places the paper below the acceptance line for me.

Questions for authors

Clarification requests (answers could materially change my rating): Q1. Can you run the reconstruction-vs-deployment ordering test on at least one learned-transition pathway — e.g., the same ConvAE encoder paired with (a) retrieval transitions and (b) the trained GRU transition module — and report whether the PCA–ConvAE reversal (or its absence) reproduces? A positive result would directly address W1 and raise my score; a clearly scoped negative result, with claims re-titled to retrieval-based deployment, would partially address it. Q2. Can you replicate the nested oracle ladder on the other two training seeds (123, 7) and report seed-level spread of the three gaps (5.66 / 14.01 / 2.44 pp)? The state-refresh dominance is the paper's most actionable attribution; its robustness across seeds materially affects how much weight it can bear. Q3. Regarding the whitening reversal (+4.75 pp, against your prior expectation): did you examine whether whitening suppresses precisely the low-variance directions that align with the enstrophy-containing spectral band? A dose–response analysis of deployment change against κ(A) or index agreement across your seven frames, plus this one spectral-alignment check, would convert your most intriguing anomaly into a falsifiable mechanistic hypothesis — which would substantively address W2. Q4. Please reconcile or adjudicate the dual records that touch headline comparisons (U-Net 34.72% vs 34.668555%; deployment 38.300117% vs 38.300047%), stating which is authoritative for each claim and what the provenance difference turned out to be. The paper's credibility model is "all records retained"; it needs one designated authoritative value per claim to be interpretable. Suggestions for future work (not required for acceptance; not part of my rating): Q5. Extending the instrument to a second shift magnitude (e.g., fivefold) and a second forcing scale to map how the reversal strength scales with distribution distance; nonlinear intrinsic-dimension estimators (you cite but do not run TWO-NN/MLE) to test whether the curvature-proxy null is estimator-specific; and completing the phase-aligned control. These would strengthen a follow-up but exceed what I consider necessary for this submission.

3 comments
AuthorsOpenReview ↗

Response to Reviewer MwS2 (1/3): summary and Q1

We thank the reviewer for an exceptionally careful review, and we apologise for replying so close to the end of the discussion period: we chose to answer the clarification requests by running them, and the experiments took most of the available time.

The reviewer's two central criticisms were fair. Before this round, our evidence could not show whether the reconstruction–transfer reversal extends beyond retrieval (W1), and our error attribution rested on a single seed (W2). Both now have experimental answers. Every new pipeline was first required to reproduce an existing number, and every classification was pre-registered before the corresponding run. The revised PDF has been uploaded. Because of the length limit, our response is split into three comments.

Summary

RequestAnswerRevised PDF
Q1 / W1: reversal under a learned transitionYes, and transfer-specific by a pre-registered difference-in-differences testSec. 5.3, Table 5; App. I.1
Q2: ladder on seeds 123 and 7State refresh is the largest gap in every seed (14.01–14.89 pp)Sec. 4.1, Table 3; App. F.1
W2: selection × refresh factorialThe direction-oracle advantage appears only after the state has driftedSec. 4.1, Table 2; App. F.1
Q3: whitening mechanismDirection-specific at fixed dose, in both directionsSec. 6, Table 6; App. I.2–I.3
Q4: dual recordsAdjudicated; the two U-Net values were two different metricsTable 1; App. J; App. C
W2: JEPA controlThree versus three: ranges do not overlap (≥ 11.37 pp)Sec. 5.2; App. I.5
Q5Intrinsic dimension estimated; second shift and phase control remain future workSec. 5.1; App. I.4

Q1 / W1. Does the reversal reproduce under a learned transition? Yes, and it is transfer-specific.

We paired the same encoders (ConvAE seeds 42/123/7; PCA-64 as in the paper) with the GRU transition module, using an identical architecture and training protocol for both, trained on the source regime only. To separate a transfer effect from a difference in fit quality, we evaluated on the target regime and on held-out source trajectories (4500–4999, unseen by both encoders and GRUs). Pre-registered criterion: the reversal counts as transfer-specific only if PCA is worse on the target and the target gap exceeds the source gap, with CIs excluding zero in every seed.

SeedΔ target, PCA − ConvAE (pp)Δ source (pp)DiD (pp)
42+3.03 [2.72, 3.35]−0.61 [−0.79, −0.43]+3.65 [3.28, 4.02]
123+2.72 [2.36, 3.08]−1.03 [−1.20, −0.86]+3.76 [3.35, 4.15]
7+2.63 [2.26, 2.99]−0.77 [−0.96, −0.58]+3.40 [2.98, 3.81]

The ordering flips between regimes: on held-out source data PCA-64 is better in every seed, consistent with its better reconstruction; on the target it is worse in every seed. The criterion is met. The result holds with 3× training (seed 42, 30 epochs: Δ target +2.84 [2.57, 3.11], DiD +2.40 [2.11, 2.70]). Per-dimension standardisation of the PCA latent performs worse still (50.55 / 50.43 / 50.40%).

So, within this benchmark, reconstruction fidelity fails to order deployment for a learned transition as well as for retrieval, by a similar margin (3.63 pp for retrieval). We have revised the framing accordingly while keeping the scope explicit: one learned transition architecture, one benchmark, one tenfold shift.

AuthorsOpenReview ↗

Response to Reviewer MwS2 (2/3): Q2, factorial, Q4 and JEPA

Q2. Is state-refresh dominance robust across seeds? Yes.

We parameterised the ladder and reran it for seeds 123 and 7 (no retraining), after reproducing seed 42 to within 10⁻³ pp with identical oracle indices.

SeedRef.RefreshedFree-runningDeployedRef.→refreshedState refreshSelector
4216.2021.8535.8638.305.66 [5.56, 5.76]14.01 [13.91, 14.11]2.44 [2.27, 2.60]
12313.8921.1035.9738.297.21 [7.08, 7.35]14.87 [14.75, 14.99]2.31 [2.13, 2.49]
714.0521.2236.1138.447.17 [7.04, 7.30]14.89 [14.78, 15.01]2.33 [2.14, 2.51]

Levels (%) are rounded for display; gaps (pp) and paired 95% CIs are computed from per-trajectory arrays. State refresh is the largest gap in every seed. As the reviewer anticipated, magnitudes move with the seed: the reference-to-refreshed gap is about 7.2 pp for seeds 123 and 7, so the seed-42 value understated it. Deployment is stable (38.29–38.44%).

W2. The selection × refresh factorial. We ran the missing cell, canonical selection with true-state refresh (N_RIDE = 3 unchanged). For seed 42: canonical 38.30 (generated state) / 21.69 (refresh); direction oracle 35.86 / 21.85. Under refresh, canonical is slightly better than the oracle in every seed: −0.16 [−0.19, −0.13], −0.17 [−0.21, −0.13], −0.22 [−0.26, −0.19] pp. The oracle's advantage (2.31–2.44 pp) therefore appears only after the state has drifted; the ladder's selector gap is conditional on drift, not an independent component. The direction oracle is thus not an upper bound on selection, which the revision now states (Table 2).

Q4. Dual records, adjudicated.

  • Deployment (38.300117% vs 38.300047%). The 5,000 selections are identical; the difference is float32 versus float64 aggregation. Three independent code paths agree with 38.300047% to about 10⁻⁸ pp, which we designate authoritative (38.30% in the main text).
  • U-Net (34.72% vs 34.668555%). These were two different metrics, not a provenance discrepancy: 34.668555% came from the spectral-weighting evaluation, which excludes the k = 0 mode, while Eq. (1) gives 34.7156%. Re-running all three checkpoints reproduces the cached fields elementwise. The revision removes the "unreconciled" statements, labels the spectral evaluation explicitly, and recomputes the stepwise U-Net errors under Eq. (1). We now report the sample SD (0.74); the earlier ±0.60 is the population SD of the same three seeds.

W2. JEPA, three versus three. Per-trajectory JEPA arrays were not retained, so no paired interval is available. At the seed level, JEPA gives 50.77 / 50.48 / 51.29% and the physical-route ConvAE baseline 38.93 / 39.07 / 39.11%. The ranges do not overlap; the most conservative difference is 11.37 pp (vs 11.92 pp in the original seed-42 pairing). We report this as an unpaired n = 3 comparison.

AuthorsOpenReview ↗

Response to Reviewer MwS2 (3/3): Q3, Q5 and a question

Q3. Is the whitening degradation due to its direction, or only its conditioning? Its direction.

Dose–response across the seven frames. Deployment error rises with κ(A) and falling index agreement, and the curve is strongly convex: at κ = 2, about 38% of selections change, yet deployment moves by only +0.01 pp (CI includes zero), consistent with many near-equivalent neighbours.

Fixed dose, varied direction. This experiment was designed in direct response to the reviewer's question. Cosine similarity is invariant to a left orthogonal factor, so A = UΣVᵀ affects retrieval only through Σ (the dose) and V (the direction); dropping U reproduces all 5,000 whitening selections exactly. We held whitening's spectrum fixed (κ = 56.35) and changed only V:

Frame (same Σ)Δ deployment vs identity (pp)
Source whitening+4.75 [4.30, 5.21]
Random orientations (5 draws)+0.92 to +1.30
Reversed whitening−0.36 [−0.49, −0.22]

Whitening is worse, and reversed whitening better, than every random orientation, with all pairwise CIs excluding zero (pre-registered: direction-specific in both directions). Generic distortion at this conditioning costs about 1 pp; the remaining ~3.5 pp is direction-specific.

The spectral hypothesis. One correction: whitening up-weights, rather than suppresses, low-variance directions. In the seed-42 ConvAE latent, low source-variance directions are both the most shifted between regimes (ρ = −0.85 with the target/source variance ratio; permutation p ≈ 10⁻⁴) and decode to higher wavenumbers (ρ = −0.44; p ≈ 10⁻⁴). Whitening raises the distance-weight share of the most-shifted quartile from 0.0247 to 0.2500; reversed whitening lowers it to 0.0040. This is correlational; the causal evidence is the fixed-dose test.

Scope. This uses one encoder seed, and a pre-registered check shows the account does not extend across encoders: PCA-64 places less weight on its most-shifted directions than ConvAE (0.0026 vs 0.0244–0.0268), yet transfers worse. Shift weighting explains frame effects within an encoder, not the PCA–ConvAE reversal; the revision keeps the two separate. Reversed whitening uses source statistics only, so it is a valid zero-shot frame, and it means one diagnostic variant now beats its baseline. We have corrected that statement (Sec. 8) and report the frame as a direction test, not a method (one seed, 0.36 pp).

Q5. We ran TWO-NN and Levina–Bickel MLE, validated on a synthetic 5-dimensional manifold in 64 dimensions. For both representations, target-regime intrinsic dimension exceeds the source (ConvAE about 4.6–4.9 vs 6.1–6.3; PCA-64 4.4–4.8 vs 6.1–6.6). This is descriptive and does not test the curvature–error association. A second shift magnitude and the phase-aligned control need new simulation data and remain future work.

A note on process. Our first reproduction gate for Q1 caught a genuine bug in the adapted training script (a different random-number call order). After the fix, the adapted script matched the original to 0.0002 pp, within the paper's pre-existing 0.01 pp tolerance. Numbers produced before the fix were discarded, and all deviations are logged in our experiment records.

We are genuinely grateful for this review. Its questions could be answered by experiment, and answering them changed the paper: the reversal now holds beyond retrieval, the ladder is robust across seeds, and the whitening anomaly is now a direction-specific result with a testable account. We will respond promptly to any follow-up.

One question for our follow-up work: would the reviewer consider a second shift magnitude on this benchmark (e.g., fivefold) or a second system with a parameter-driven regime change (e.g., Burgers with vanishing viscosity, as Reviewer 4Ffu suggests) more informative?

Reviewer_4FfuOpenReview ↗
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Paper summary

The paper is extremely hard to understand. So I will try my best to write the summary based on my understanding.

The paper seems to be investigate why neural PDE surrogates degrade when some physical parameters of the underlying physical systems changes, by using a retrieval predictor as a diagnostic tools. The data is 2D Navier Stokes and the key physical parameter is the Reynolds number. Then the attempt to explain the degradation seems to be feeding a pre-trained surrogate with data of varying Reynolds numbers.

Critical strengths

It is crucial and new to explain why PDE surrogates can degrade when key physical parameters of the underlying physical systems change. These changes can sometimes causes significant change of behavior of the physical system, so the degradation of prediction is not necessarily only a learning or genearalization issue, but a modeling limitation. This paper picks a good research question.

Critical weaknesses

Despite spending hours trying to understand the paper, I simply couldn't make sense of it, mostly due to the writing. This includes broken structures, jumping logics, missing information, etc. I am afraid that regardless of the results, this draft is not ready for publication.

  1. The justification of the chosen tools. Explaining PDE surrogates is not entirely new. For example, steering [1] and sparse probing [2] have been used to explain the behaviors. It is unclear what new information is obtained by the analysis in this paper. It seems that the ability to transfer is an important criterion where multiple alternative methods were tested. However, it is hard to see what explainability this brings.

  2. The chosen problem is too narrow. Reynolds number is one important indicator for e.g. turbulence formation, but there are many physical systems with similar behavioral changes due to the change of key parameters, e.g. visosity approaching zero in Burgers, or Hopf bifurcation in flow past a cylinder. The specific chosen example might not be a good example showing prediction degradation due to physical parameter change.

  3. Writing is a big issue. I have to say I was lost from reading the Abstract. Too many terms and references are presented without explaining them first. For example, 'In seed 42', 'encode–decode reference', 'PCA–ConvAE contrast' and coutless many other. I am afraid this goes beyond the possibility of the lack of necessary background for a reader, and is mainly a writing issue itself.

[1] Physics Steering: Causal Control of Cross-Domain Concepts in a Physics Foundation Model [2] Sparse probes and murky physics: a case study of interpretability challenges in a foundation model for continuum dynamics

Questions for authors

I do not have any questions as the writing is hard to understand, to the point that it is already challenging to form meaingful questions.

1 comment
AuthorsOpenReview ↗

Response to Reviewer 4Ffu: setting, positioning and scope

We thank the reviewer for the review and for the comments on the research question. We agree that the submission was difficult to read; the manuscript has been revised throughout (see the general response). Since the reviewer noted that the draft made it hard to form questions, we first summarise the paper, then address the three points.

Summary of the paper.

  • Setting. All models and retrieval databases are built on forced 2D Navier–Stokes at Re ≈ 1,000 only and evaluated zero-shot on Re ≈ 10,000. No model is trained or tuned on the target regime; we do not feed a pre-trained surrogate data of varying Reynolds numbers.
  • Instrument. A retrieval (analog) predictor encodes the current state, finds the most similar source-regime state, and borrows what happened next. Each component (encoder, database, selection rule, rollout loop) can be replaced independently, which is what lets us locate where the transfer error arises.
  • Findings. (i) Reconstruction fidelity does not order transfer: at equal width, PCA reconstructs the target better than a convolutional autoencoder but transfers worse, with retrieval and with a learned GRU transition. (ii) The largest diagnostic gap is state drift during rollout. (iii) With reconstruction held fixed, changing only the retrieval coordinate system changes transfer by up to 4.75 pp, depending on the direction of the change.

1. Writing. The abstract and introduction are rewritten around these findings. The terms flagged in the review ("In seed 42", "encode–decode reference", "PCA–ConvAE contrast") are removed from the abstract or defined at first use; Sec. 3 describes the predictor and its two output routes in prose; and one term is used per concept throughout.

2. What the analysis adds, relative to steering and sparse probing. These methods ask what a representation encodes. Our question is different: where along a prediction pipeline error arises when the physical regime shifts. The analysis yields three results of this kind:

  • the largest part of the measured transfer gap comes from state drift during rollout (14.01–14.89 pp across three seeds; Sec. 4);
  • reconstruction quality, a direct measure of what a representation retains, does not predict deployment (Sec. 5);
  • the coordinate system in which neighbours are compared changes transfer even when the information content is identical (Sec. 6).

The two approaches are complementary: a probe can show that a quantity is decodable from a representation without showing that a predictor can use it in a shifted regime, which is what deployment-level interventions measure. A paragraph discussing both cited works has been added (Sec. 2).

3. Scope. We agree that a single system is a limitation, and the revision states it explicitly (Sec. 8). We chose the Reynolds number because it gives a large, controlled shift through a single parameter: target states lie about 18 times farther, in angle, from the source database than source states lie from one another, and the target regime has a higher local intrinsic dimension (Sec. 5.1). This bears on the reviewer's point that a parameter change can alter the behaviour of the system itself rather than only test generalisation. Vanishing viscosity in Burgers' equation and the Hopf bifurcation in cylinder flow would test whether the reversal generalises; we list both as future work.

The revised PDF has been uploaded, and we are happy to answer further questions.

Reviewer_tsG9OpenReview ↗
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Paper summary

The paper claims to study the gap between reconstruction error and representation quality. They make the observation that a low reconstruction error does not necessarily lead to correctly rolled-out dynamics. The work tests generalization using 2D forced Navier-Stokes solutions.

Critical strengths

The paper seems to evaluate on multiple different settings and tries multiple baseline methods.

Critical weaknesses

It is not clear what problem the paper is trying to solve beyond a few sentences in the introduction. It is not clear what problem the paper is trying to solve beyond a few sentences in the introduction. Overall, there is a serious lack of clarity. Some examples:

  • "Retrieval predictor" is never cited or explained in the methods or related work.
  • "Frames" is never defined in the introduction.
  • Table 1: certain methods are seeded while others are not. For example, "ConvAE-Relay, Physical" is only run for 1 seed.
  • Individual terms in equation 1 are not defined.
  • JEPA is cited but not explained, and the main text refers to "config2" without explaining what this is.
  • Fig. 1 caption: It is not clear what "chips" means in this context.
  • Section 4.2, L∗L^* and LdirL_{dir} are not defined. Similarly, a "diagnostic cache" is referenced without explanation.
  • ConvAE is not defined.
  • Section 6: The 8 candidates are not explained, nor are the stages, and it is not clear what "null-effect result" means.
Questions for authors

No questions.

1 comment
AuthorsOpenReview ↗

Response to Reviewer tsG9

We thank the reviewer for the review. The manuscript has been revised for clarity, and each listed point is addressed as follows:

PointChangeLocation
Problem unclearAbstract and introduction rewritten around the question, setting and three findingsAbstract; Sec. 1
"Retrieval predictor"Described in prose as an analog forecaster, with citationsSec. 3.2; Sec. 2
"Frames"Defined as a snapshot index; coordinate sense renamed "retrieval coordinate system"Sec. 3.1; Sec. 6
Table 1 seedsThree-seed results for all trained predictors; uncertainty convention stated per rowTable 1
Eq. (1) termsAll symbols definedSec. 3.1
JEPA; "config2"JEPA defined; configuration labels moved to the appendixSec. 3.3; App. B
"Chips"Figure 1 and caption revisedFig. 1
Sec. 4.2 symbols; "diagnostic cache"Replaced by a plain statement; provenance moved to the appendixSec. 4.2; App. J
ConvAEDefinedSec. 3.3
Candidates, stages, "null-effect"Each candidate stated as a hypothesis; stage details moved to the appendixSec. 7, Table 7; App. F.7

In addition, the main diagnostic analysis is now reported on three seeds (Sec. 4, Table 3). The revised PDF has been uploaded.

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

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