acceptodds
Under review as a conference paper at ICLR 2027

Let's Do Turbulence Right: In Space and Time!

Abstract

The three-dimensional Navier–Stokes equations govern fluid turbulence, a chaotic and non-linear physical phenomenon characterized by complex eddies interacting across vast spatial and temporal scales. A numerically accurate modeling of this multi-scale energy cascade requires fully resolving both the fine spatial structures and the continuous temporal evolution of the flow field. In this paper, we leverage massive, time-resolved direct numerical simulations, which exceed 28 TB per run, to assess how numerical choices govern the resolved -dimensional physics of turbulent flows. Building on this analysis, we study how neural networks represent the recorded turbulent motion. Our results highlight that spatial and temporal assessments can disagree for both numerical records and learned representations. We therefore call on the machine learning community to treat -dimensional turbulence as a four-dimensional phenomenon.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
numerical turbulence, direct numerical simulation, DNS, representation, neural networks, spatiotemporal

Reviews

Among:
Shape:
1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_PjHYOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
3
Read review
Paper summary

Using a massive time-resolved direct numerical simulation (28.9 TB reference trajectory), this paper studies how numerical choices — spatial resolution, solver floating-point precision (FP64 down to FP4), coupled space–time filtering, and record quantization — shape the spatial structure (energy spectrum, enstrophy, gradient moments) and temporal evolution (correlation time, joint wavenumber–frequency spectra) of (3+1)-dimensional turbulence records. It then compares two neural representation families (SIREN and additive Gaussian fields) under two fitting procedures (joint space–time fitting vs. independent snapshot fitting) at matched parameter budgets. The central finding is that spatial and temporal assessments can disagree: records and fits that look acceptable under spatial diagnostics can fail temporally (e.g., FP8 evolution freezes into a verified fixed point; independent fits decorrelate too quickly while joint fits over-correlate). The authors call on the ML community to treat (3+1)D turbulence as a four-dimensional phenomenon and pledge to release filtered DNS records at multiple coupled space–time bandwidths with construction metadata.

Critical strengths

S1. A genuinely consequential, previously untraced analysis: the simulation → recording → neural-fitting pipeline treated as a single information channel. This is the consideration that most drives my recommendation. ML work on turbulence — closures, emulators, generative models, neural compression — consumes DNS records as if they were ground truth, yet the community has had no systematic account of what information those records actually retain. This paper supplies that account at an unusual level of rigor: solver precision down to FP4 (with two distinct, well-verified failure modes: the frozen FP8 fixed point and the FP4 initialization failure), a physically calibrated coupled space–time filtering operator, and byte-exact storage accounting. The demonstrated disagreements between spatial and temporal diagnostics are not rhetorical: they are documented failure modes (quantization adds apparent small-scale energy while shortening correlations; fitting attenuation can be harmful for resolved records yet beneficial for quantized ones) that would silently contaminate downstream training and evaluation. If the community is to build learned models on turbulent data responsibly, this kind of audit is foundational, and I am not aware of prior work tracing these effects end-to-end into neural representations. S2. Exemplary experimental rigor and reproducibility, including honest treatment of negative cases. The engineering behind the study is rare even among strong empirical papers: a 28.9 TB time-resolved reference simulation; compensated-arithmetic emulation of low-precision formats with rounding specified at the level of individual FFT butterflies; matched parameter budgets across families (within 0.2%); an explicit, measurable stopping criterion; seed-sensitivity checks (Table 13); matched-MSE temporal comparisons (Table 14); and per-run manifests with SHA-256 checksums. Equally important, the authors label the under-resolved coarse-grid runs as non-DNS, retain the failure controls in their accounting, and qualify their claims (e.g., "convergence means this measured plateau, not a demonstrated global minimum"). This level of methodological discipline makes the paper's findings trustworthy and its promised dataset release credible — and it is precisely the standard a "data-centric" contribution must meet.

Critical weaknesses

W1. The central prescriptive claim lacks downstream closure. The paper's headline message — treat turbulence as a 4D phenomenon; match representation and fitting choices to application-relevant temporal dynamics — is argued entirely at the level of diagnostics on records and fits. No experiment shows that the documented spatial–temporal disagreements actually matter for what the community does with these representations: training emulators, learning closures, or compressing data for analysis. A joint fit that over-correlates and an independent fit that decorrelates too fast might produce equally good (or equally bad) downstream models; without this link, the "call to action" rests on the plausibility of the diagnostics rather than demonstrated consequence. This is consequential to my assessment because the paper's contribution type is prescriptive — it asks the community to change practice — and prescriptive claims require evidence that current practice leads to measurably worse outcomes. A single small downstream study (e.g., training one temporal emulator on joint vs. independent fits, or on FP16 vs. FP8 records, and comparing rollout error or energy-transfer statistics) would substantially strengthen the paper; its absence is the main reason I do not recommend a clear accept. W2. Statistical and architectural scope limit the generality of the conclusions. Every numerical comparison rests on a single realization of one flow configuration, and turbulence statistics (gradient moments, correlation times) are known to fluctuate across realizations; the three-seed check (Table 13) covers training randomness, not flow variability. Moreover, the resolution study and the precision/quantization study use different physical setups (Re_λ ≈ 280 vs. ≈ 65), so cross-comparison generalization is asserted rather than shown. On the learning side, only two representation families, pure-MSE fitting, and a single binary axis of temporal parameter sharing (joint vs. independent) are tested; hybrid schemes (shared backbone + per-frame residuals, temporal embeddings), feature-grid INRs, and derivative-aware losses — all common in practice — are absent, while the text occasionally implies broader applicability than this evidence supports. This matters to my recommendation because the paper's value is as a community reference; if its qualitative conclusions are specific to one realization, one solver implementation (unscaled compensated arithmetic), and two architectures, the reference's authority is correspondingly narrower than the framing suggests.

Questions for authors

Q1. (Clarification, potentially score-changing) Can you provide any evidence — even at small scale — that the spatial–temporal disagreements you document propagate to a downstream learning task? For example: does a temporal emulator trained on an independent fit produce statistically worse rollouts than one trained on a joint fit of matched spatial MSE? Even a negative result would sharpen the paper's message. This directly addresses W1 and is the single most important factor in my final assessment. Q2. (Clarification) How robust are your headline numerical findings to realization variability? Specifically: for the resolution and precision studies, would the qualitative ordering of effects (energy pile-up at coarse N, FP8 freezing, FP4 failure) survive across 3–5 independent initial conditions? If you have run such replicates, please report the realization-to-realization spread of S, F, and τ_e; if not, please state explicitly which conclusions are single-realization observations. Q3. (Clarification) The coupled filtering operator (Eq. 12) calibrates the temporal bandwidth via a sweeping-based relation with α set to a pooled 99% spectral-energy quantile. How sensitive are the released filtered records — in particular their correlation times — to this calibration? Since the released dataset carries this design choice, please report the effect of α (e.g., 90% vs. 99.9% retention) and of the assumed scaling (k⁻¹ sweeping vs. k⁻²ᐟ³ Kolmogorov) on the records' temporal statistics, and document the choice in the data card. Q4. (Clarification) The quantization learning targets are stored in FP32, which — as you note — can mask differences between the FP64/FP32/FP16 records, and indeed the corresponding fits are nearly identical (Tables 9–10). Do you agree that the quantization comparison among these three formats is therefore effectively vacuous for the neural study, and would you revise the claims in §5.2 accordingly? Q5. (Clarification) What is the concrete commitment and timeline for releasing the filtered records, construction metadata, and manifests? The dataset is a named contribution (#3) and part of what justifies acceptance; a specific release plan (hosting, formats, license, expected size) would materially affect my confidence in that contribution. Q6. (Future work, not score-relevant) Have you considered a hybrid temporal parameter-sharing scheme (e.g., shared backbone with per-frame low-rank residuals) or a derivative-aware fitting loss, and do you expect these to change the joint-vs-independent trade-off you observe?

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

In this paper, the authors present a diagnostic study of turbulence governed by the three-dimensional Navier–Stokes equations. They explore the effects of resolution, filtering, solver precision, and record quantization on numerical simulations, as well as how neural representations capture spatial and temporal properties of turbulence. In their experiments, they use large-scale simulations. They compare joint fitting, which means training a single model to represent the whole space-time sequence, and independent fitting, which means training a separate model for each time snapshot. They show that good spatial accuracy does not necessarily mean good temporal accuracy. For example, joint fitting can preserve temporal correlations for too long, while independent fitting can lose them too quickly. They also evaluate different physical properties, such as energy spectra, enstrophy, gradient statistics, and temporal correlations.

Critical strengths
  • The paper studies an interesting and important problem using large-scale three-dimensional turbulence simulations rather than limiting the experiments to simpler two-dimensional problems. The evaluation also goes beyond a single reconstruction error and considers several physical quantities. In particular, separating errors introduced during numerical simulation from those introduced by filtering, quantization, and neural fitting is interesting and provides useful insights.

  • The comparison between joint and independent fitting is interesting. The authors show that two representations can have similar spatial reconstruction errors but different temporal behavior.

Critical weaknesses
  • Limited novelty is one of the main weaknesses of this paper. The paper does not introduce a new architecture, training approach, or loss function. Although the diagnostic study provides some useful observations, the main conclusion, which is "We therefore call on the machine learning community to treat (3 + 1)-dimensional turbulence as a four-dimensional phenomenon," is somewhat obvious from a physical perspective. Maybe a practical downstream experiment demonstrating how these findings can improve neural models would strengthen the novelty and contribution of the paper.

  • The conclusions are based on limited experimental settings. For example, although the authors consider two Reynolds-number regimes, they do not systematically investigate how their conclusions change across different Reynolds numbers. Also, the experiments are limited to turbulence in a periodic domain, with only one initial realization for each numerical setting. More complex boundary conditions and different initial conditions could help establish the generality of the findings. The authors also perform a three-seed experiment in Appendix E.5, but it is limited to one representative record, while most other experiments use a single seed. Furthermore, only two neural representation families are considered, which makes it unclear whether the observed behaviors generalize to other architectures.

Questions for authors
  • How would these conclusions change when the Reynolds number changes systematically? Would the differences between joint and independent fitting still hold?

  • Even though the authors train the neural representations using supervised reconstruction, why are the errors in some physical quantities still relatively high? For example, can the authors clarify whether these errors are mainly caused by limited model capacity, optimization, or the use of an MSE-only loss function?

  • Can the authors show the effect of model capacity on the results? Although the parameter budgets are reported and matched between joint and independent fitting, it is unclear whether increasing model capacity would reduce the observed spatial and temporal errors.

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

This paper investigates how numerical simulation, recording, and neural representation choices affect the spatial and temporal fidelity of three-dimensional turbulence. It first examines spatial resolution, solver precision, space–time filtering, and record quantization. It then compares joint space–time fitting with independent snapshot fitting using SIRENs and additive Gaussian fields under approximately matched total parameter budgets. Evaluation includes energy spectra, enstrophy, gradient statistics, correlation times, and joint space–time spectra. The main finding is that similar spatial statistics or snapshot reconstruction errors do not imply equally faithful temporal behavior. The task concerns representation and reconstruction of observed flow sequences rather than forecasting.

Critical strengths

The paper clearly separates errors introduced during numerical evolution from changes introduced during recording, evaluating both through a consistent set of spatial and temporal diagnostics. For example, low-precision evolution can retain a structured spatial field while becoming temporally frozen, whereas post-hoc quantization can introduce spurious small-scale energy and shorten correlations. These results demonstrate why spatial appearance or energy spectra alone are insufficient to assess the fidelity of recorded dynamics. This is a practically useful contribution for research that relies on numerical data to train models.

Critical weaknesses
  1. The robustness of the physical statistics across observation windows is not sufficiently established. Appendices D.1–D.3 describe one initial realization per numerical setting, with the main measurements taken over a common window of length 2.476. Using the scales in Table 4, this corresponds to only approximately 1.6–2 large-eddy turnover times for the reference flows; some spatial statistics use just 16 frames within that window. Table 13 examines training randomness, but not finite-window variability in the DNS data. Consequently, it remains unclear whether smaller differences in precision, gradient statistics, and correlation-time rankings persist across other windows. This matters for a paper whose main contribution is quantitative diagnosis.

  2. The temporal boundary convention of the Gaussian representation may affect the temporal statistics being studied. Appendix E.4 wraps the time coordinate periodically in the joint Gaussian model, although the supplied movie is an interior segment of a longer trajectory and need not have matching endpoints. SIREN has no equivalent constraint. Since temporal correlations and frequency distributions are central to the analysis, this choice may influence the joint Gaussian model’s temporal bias, complicating attribution to temporal parameter sharing alone. The tapering check in Appendix E.6 addresses endpoint leakage in spectral estimation, but does not replace an ablation of the model’s imposed temporal periodicity. This requires clarification rather than establishing that the reported results are incorrect.

Questions for authors
  1. Could the authors evaluate several disjoint observation windows from the existing trajectories and report variability or confidence intervals for the key gradient-statistic and correlation-time comparisons? Which conclusions remain stable across windows, and which differences are comparable to finite-sample fluctuations?

  2. Do the correlation-time findings and joint-versus-independent differences persist when temporal wrapping is removed from the joint Gaussian model, or when evaluation excludes a temporal boundary region? This control would help distinguish the effects of temporal parameter sharing from those of the imposed boundary convention.

  3. Appendix E.4 states that only the first layer uses sin⁡(Mh)\sin(Mh), while subsequent layers use sin⁡(h)\sin(h), yet subsequent weights are initialized within ±6/din/M\pm\sqrt{6/d_{\mathrm{in}}}/M. Is an additional frequency scaling omitted from the description, or is this a deliberate variant? The official SIREN implementation pairs the reduced initialization scale with a frequency multiplier in the hidden activations. If the reported formulation is intentional, do the spectral and gradient-statistic differences persist under that paired parameterization?

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

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