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Under review as a conference paper at ICLR 2027

Neural Conditional Simulation for PDE Refinement

Abstract

Refining a cheap coarse PDE solution to high fidelity is a conditional simulation problem, not a regression one. Under squared-error loss the optimal predictor is the conditional mean, which by the law of total variance discards all conditional variability and so cannot serve as a realization of the fine field. For Gaussian fields the answer is classical. Kriging supplies the conditional mean, and Matheron's construction adds an innovation drawn from the Schur-complement covariance to produce an exact sample in one pass. The fields that matter in practice, such as turbulence, stochastically forced dynamics, and precipitation, break these assumptions with innovations that are input-dependent, heteroscedastic, and heavy-tailed. We introduce Neural Conditional Simulation (NCS), which keeps the classical recipe but learns the innovation. NCS is initialized at the exact Gaussian simulator, trained end to end with strictly proper scoring rules, and samples through a coarse-to-fine cascade at one network pass per level. Because the Gaussian simulator is embedded as a zero-correction fallback and reported as a baseline, every result isolates the nonlinear conditional-simulation gain, which highlights the improvement that learning adds beyond exact Gaussian conditioning. On the near-Gaussian Allen-Cahn and Navier-Stokes benchmarks, this gain is small, as expected, and NCS matches the calibration of the best classical baseline to within a few percent. On the GARD-LENS precipitation ensemble, where the Gaussian assumptions break, NCS is the only method that is globally variance-calibrated at competitive CRPS and spectral error (Fortin-corrected ): across noise-schedule settings of the diffusion baselines, every setting with has higher CRPS and more than twice the spectral error. The heavy precipitation tail, however, is under-reproduced by NCS trained with the energy score (); tuned consistency models reach it only while under-dispersed (). Our supply-versus-reach diagnostic attributes this deficit to the objective rather than the source. A scale-free flatness term closes of an analogous deficit on a controlled system. On GARD-LENS, where the deficit depends on amplitude, an amplitude-conditional objective recovers most of the tail while keeping calibration and spectrum within their guards. With the same backbone and no more parameters than CorrDiff, NCS matches multi-step diffusion baselines such as EDM and CorrDiff in accuracy and proper score while using two network passes instead of which reduces per-member wall-clock time by -.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
conditional simulation, multi-fidelity learning, stochastic PDEs, proper scoring rules, kriging, probabilistic downscaling

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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_eL2gOpenReview ↗
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Paper summary

This paper proposes Neural Conditional Simulation (NCS), a framework for refining coarse PDE solutions into high-resolution stochastic fields. It combines classical Gaussian conditional simulation with a learned nonlinear innovation to capture structures that Gaussian assumptions cannot represent. The method uses a coarse-to-fine cascade with one network evaluation per level. Experiments on stochastic Allen–Cahn, Navier-Stokes, and GARD-LENS precipitation demonstrate competitive accuracy, uncertainty calibration, and spectral properties compared with diffusion models, at substantially lower inference cost.

Critical strengths

Building on classical kriging and Gaussian conditional simulation is a well-motivated approach. Rather than learning the entire conditional distribution from scratch, the method learns the correction to an existing statistical model. The Gaussian simulator provides a meaningful baseline, making it possible to assess what the neural network actually contributes. I find this particularly interesting. The evaluation covers several stochastic systems and compares against classical methods, neural operators, and diffusion models. The authors examine CRPS, energy score, ensemble spread, spectral properties, and extreme statistics. The results are encouraging, particularly the ability to obtain competitive probabilistic performance with substantially fewer network evaluations. The controlled experiments investigating where the Gaussian assumptions fail also strengthen the contribution.

Critical weaknesses

Although NCS achieves good overall calibration, the standard energy-score model substantially underestimates the heavy-tailed increment statistics on GARD-LENS, with a kurtosis ratio of 0.17. The authors address this using an amplitude-conditional objective, which is encouraging, but it shows that the standard formulation does not fully capture important extremes. Since these are particularly relevant for precipitation applications, this limitation deserves more emphasis. Can you please elaborate this? It would be nice addition to the paper. Maybe in the camera ready version add this.

Questions for authors
  1. The amplitude-conditional objective substantially improves the precipitation tails. Would you recommend this as the default NCS formulation for strongly non-Gaussian fields? How does its CRPS compare with the original NCS model?

  2. Could you clarify how the common coarse conditioning is constructed from the GARD-LENS ensemble members? How sensitive might the approach be to biases in independently generated coarse-resolution inputs?

3 comments

Weakness and Q1: The 0.17 kurtosis ratio deserves more emphasis. Should the amplitude-conditional objective be the default for strongly non-Gaussian fields? How does its CRPS compare?

We agree, and we answer both together because the second is the remedy for the first. Default NCS trained with the energy score is calibrated in spread (σ/s\sigma/s 0.98) and competitive on CRPS and spectrum, yet its lag-2 increment-kurtosis ratio is 0.21 on all 128 test conditions (0.17 on the 64 of Table 1), which means that NCS's predictions of small-scale fluctuations are far less heavy-tailed than the data's. The cause is the objective, not the sampler. The energy score is dominated by the bulk of the distribution, and rare intense cells contribute little to it. On GARD-LENS, the deficit is intensity-dependent. The ensemble is 3.8×3.8\times over-dispersed at low rain rates and 0.87×0.87\times under-dispersed in the tail, and an aggregate score cannot see that pattern.

Following this diagnosis, we changed only the objective and kept the model fixed. Each row below adds one amplitude-conditional term to the default energy score: amplitude-stratified ES (L2) or K62 slope matching (L4):

MethodRMSEESCRPSCorrected σ/s\sigma/slogPSDκ/κdata\kappa/\kappa_{\mathrm{data}}
NCS-Drift+ES1.158±0.0191.158 \pm 0.019460.7±0.3460.7 \pm 0.31.571±0.0101.571 \pm 0.0100.982±0.0140.982 \pm 0.0140.131±0.0140.131 \pm 0.0140.21±0.040.21 \pm 0.04
NCS-Drift+ES + L21.159±0.0181.159 \pm 0.018460.7±0.3460.7 \pm 0.31.554±0.0051.554 \pm 0.0050.981±0.0140.981 \pm 0.0140.143±0.0130.143 \pm 0.0130.70±0.040.70 \pm 0.04
NCS-Drift+ES + L41.151±0.0211.151 \pm 0.021460.8±0.3460.8 \pm 0.31.573±0.0091.573 \pm 0.0090.976±0.0140.976 \pm 0.0140.058±0.0020.058 \pm 0.0020.84±0.030.84 \pm 0.03

L4 matches how fluctuation size grows with local intensity. It raises the kurtosis ratio from 0.21 to 0.84 and more than halves logPSD at unchanged ES, CRPS and spread. Among the original-recipe baselines, only multi-step consistency sampling reaches a comparable tail (up to 1.10), and only when strongly under-dispersed (σ/s≤0.57\sigma/s \leq 0.57).

Should it be the default? For fields whose tail arises from intensity-dependent variability, such as precipitation, yes: L4, or L2 if CRPS is the priority. We would not make it the default for all non-Gaussian fields, because it targets one mechanism. If the tail is intrinsic (e.g., Student-t innovations with amplitude-independent scale), RvarR_{var} is flat and L4 has nothing to match. In such a case a scale-free flatness term is the right choice (SHE-PAM, 93% closed). RvarR_{var}, computed on the default model, distinguishes the two cases before the added term is chosen (step 3 of the protocol in our answer to HC6i W6).

Whether the improved pooled tail translates into better conditional extremes is a separate question, which yLXT also raised. Please see the conditional exceedance, coverage, FSS and object diagnostics in our answer to yLXT Q4.

[REVISION] We state the default model's tail deficit and its cause in the main results and limitations and add the L4 row with CRPS to the main text and present L4 as the recommended objective for precipitation-like fields.

Q2: How is the common coarse condition built? Sensitivity to bias in independently generated coarse inputs?

We will describe it more precisely in Appendix D.1. For each day, the condition is the ensemble mean of the high-resolution members, block-averaged by 4×4\times (1282→322128^2 \rightarrow 32^2). The same condition is used for all members and by every method. Data are split by day, so no test day is seen during training. Two consequences, which we will state in Sec. 4, Appendix D.1 and the limitations:

  • The condition is shared across members, so all between-member variability must be generated by the model. The task is therefore conditional reconstruction given a consistent coarse field.
  • Robustness to coarse-model bias is untested on GARD-LENS, because the dataset has no independently produced coarse field. On our synthetic test cases, the coarse condition is a separate noise-free solve on the coarse grid, not a coarsening of the fine members, so those results already exercise an independent coarse solve.

As a controlled sensitivity test we offer a condition-member mismatch sweep on Navier-Stokes. Our Navier-Stokes simulator allows us to set how far the members' large scales drift from the condition. We sweep it from the training value (τ=1\tau = 1) through weaker settings (τ=4,16\tau = 4, 16) to fully free, and add one setting that is similar to GARD-LENS. All settings share the same random seeds, so the conditions are identical across settings. The members differ in their large scales and, slightly, in their fine-scale statistics; in particular, power in the finest resolved band is up to about 15% higher when free. We take the models trained on the current dataset and evaluate them, without retraining, on every setting. This measures how a deployed model responds to a coarse input that does not match the members it was trained against. The mismatch mm is the relative distance between each member's coarsened large scales and the test conditions, which gives the sweep a model-independent axis.

ES (mean over 3 seeds; σ/s\sigma/s in parentheses)

SettingmmNCSCorrDiffEDMConsistencyGCSPNO
GARD-style0.14310.8 (0.98)309.0 (1.00)310.7 (1.00)310.5 (1.02)312.4 (1.01)336.6
τ=1\tau=10.19312.6 (0.97)310.9 (1.00)312.8 (0.99)312.9 (0.93)314.8 (1.00)341.6
τ=4\tau=40.39345.2 (0.89)342.9 (0.91)343.7 (0.91)345.4 (0.87)344.8 (0.92)374.3
τ=16\tau=160.50369.7 (0.83)367.0 (0.85)367.1 (0.86)369.6 (0.82)367.7 (0.86)398.5
free0.54380.9 (0.81)378.1 (0.83)378.0 (0.83)380.9 (0.78)378.4 (0.84)409.8

The table shows that all methods degrade by the same amount. From τ=1\tau = 1 to free, ES rises by 20.0-21.9% for every arm including GCS (NCS +21.9%, Consistency +21.7%, CorrDiff +21.6%, EDM +20.8%, GCS +20.2%, PNO +20.0%), and σ/s\sigma/s falls by 16-17% for all. The degradation is graceful, and no learned method is disproportionately fragile when the coarse input stops matching the members. Since the conditions are identical across settings, a frozen model sees the same input and is scored against different targets, so the rise reflects both the condition's loss of information and a small shift in the members' fine-scale statistics. Furthermore, we are generating a precipitation dataset with independently simulated coarse fields. Unfortunately, this requires substantial GPU resources and is not yet finished, so we cannot report results from it in this rebuttal.

[REVISION] We state clearly construction and consequences in Sec. 4, Appendix D.1 and the limitations. Additionally, we add the sweep to the appendix with the framing above.

AuthorsOpenReview ↗

Follow-up on our response

Dear Reviewer eL2g,

Thank you for your positive and constructive review. In our response (Parts 1 and 2 above) we added the CRPS comparison for the amplitude-conditional objectives, stated when we recommend them, described how the GARD-LENS coarse condition is constructed, and added a condition–member mismatch sweep on Navier–Stokes.

As the discussion period ends on 18 November, we would be grateful to know whether this answers your questions and whether it has strengthened your view of the paper. We are happy to clarify anything further.

Reviewer_HC6iOpenReview ↗
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Paper summary

The paper combines classical conditional simulation with a neural network. The network learns to correct the random part of the output. The goal is to generate conditional samples with fewer network passes than multi-step generators. This aims to keep useful detail while reducing sampling time.

Critical strengths
  1. The classical part is clear and easy to inspect. The reader can see what the neural part adds. This makes the starting point easy to understand. It also separates the learned part from the fixed part.
  2. The method has a clear structure. Each part has its own role. The steps are easy to identify. This makes the overall design easier to follow.
  3. The paper clearly states the limits of its theory. This helps readers understand what the method can and cannot guarantee.
Critical weaknesses
  1. Most components already exist in earlier work. The main new part seems to be how they are combined. The paper could better show why this combination is useful.
  2. The paper explains many design choices in detail. This sometimes makes the main contribution harder to follow. A shorter explanation could make the key idea clearer.
  3. Much of the theory builds on known results. The paper offers few new theoretical results. It would help to state the theoretical contribution more clearly.
  4. The theory shows that a suitable transport exists. It does not guarantee that the chosen network can learn it. This gap could be explained more clearly.
  5. The source relies on a stationary spectral model. This may limit how it handles spatially changing patterns. The paper could explain how learning handles this limit.
  6. The paper separates two types of limits. But the line between them is not fully clear. A clearer rule would make the framework easier to use.
  7. The cascade uses independent noise at each level. It is not clear when this is enough to capture the full distribution across scales.
Questions for authors

Could the authors explain what NCS adds beyond earlier methods? Which part of the design matters most? How does it differ from related approaches? A brief comparison would clarify its contribution and intended use.

10 comments

W1, W3, Q: What does NCS add beyond earlier methods? Which part matters most?

The guiding principle of NCS is to learn only what classical theory cannot already provide. Stochastic systems range from near-Gaussian to strongly non-Gaussian, and the current default is to learn the whole conditional law with a diffusion model. That spends network capacity and compute on structure that Gaussian conditional simulation gives in closed form, and it gives no anchor in the regime where the correct answer is known. NCS takes the opposite route. It is built on top of existing literature like kriging or Matheron's construction and we will highlight this in Section 3 more. NCS's motivation is rooted in the fact that classical conditional simulation is exact but cannot learn while neural generators can learn but start from nothing. NCS joins the two: it samples δ^=Kc+gθ(ε,c)\hat{\delta} = \mathcal{K}c + g_\theta(\varepsilon, c), where the kriging mean Kc\mathcal{K}c and the spectrally fitted innovation ε\varepsilon carry everything Gaussian theory provides, and the transport gθg_\theta, initialized at the identity, learns only what that theory misses. Training therefore starts from a correct answer rather than from noise. At initialization NCS is Gaussian conditional simulation, exact for Gaussian fields with known covariance (Prop. 2), and already optimal for the training score in population (Cor. 3). As a consequence, NCS has three unique properties:

  1. The value of learning is measurable. Because the untrained model is a meaningful baseline rather than noise, we report in every table exactly what learning added. The gain is small where the field is near-Gaussian and large where it is not (CRPS, GCS →\rightarrow NCS: Allen-Cahn 0.425→0.4090.425 \rightarrow 0.409, Navier-Stokes 0.976→0.9690.976 \rightarrow 0.969, GARD-LENS 2.460→1.5712.460 \rightarrow 1.571). We are not aware of a learned refiner that reports this paired difference.
  2. Calibration comes from the anchor and not from a noise schedule. On GARD-LENS, NCS is calibrated at its standard recipe (σ/s\sigma/s 0.98) at one network pass. NCS leads against its closest one-pass relative PNO on ES (460.7 vs. 462.4), CRPS (1.571 vs. 1.592) and spectrum (logPSD 0.13 vs. 0.55). Diffusion baselines reach comparable spread only after target standardization and validation-tuned sampling (EDM σ/s\sigma/s 0.44→0.900.44 \rightarrow 0.90).
  3. Our Supply-Reach taxonomy and the modular design says which part to change. The source, transport and objective act on different properties (Table 12): the source sets the spectrum (logPSD 1.31.3-1.7→0.11.7 \rightarrow 0.1-0.50.5), the transport the proper score (ES −11-11 to −12-12%), and the objective the tail (a flatness term closes 93% of the kurtosis deficit on SHE-PAM; an amplitude-conditional term raises the lag-2 kurtosis ratio from 0.21 to 0.84 on GARD-LENS, with source and architecture unchanged).

So, to the question "which part matters most": no single part does. It depends on which property fails, and the protocol in our answer to W6 is how we decide.

[REVISION] Add this statement and the GCS →\rightarrow NCS comparison to the introduction; mark classical results.

W4: The theory shows a transport exists, not that the network can learn it.

Agreed. Lemma 3 is an existence result and the paper does not guarantee that a finite network trained on finite data finds the transport. We will move this caveat from the appendix into Section 3. The limitation is shared by every learned sampler. What differs is how much must be learned. In NCS, the Gaussian part is supplied in closed form and the network learns the departure. Empirically, on controls with a known answer, the learned correction reaches it: 1.00×1.00\times of the closed-form ceiling on the nonstationary control (see W5 for what was tested), and CRPS 0.60 vs. 1.13-1.16 for every classical arm when the conditional mean is nonlinear.

W5: Stationary spectral source and spatially varying patterns.

Both the source and the kriging mean are stationary, so any nonstationarity must come from the learned part. In Appendix C.6 we test this on a Gaussian control which is built so that every stationary predictor must fail. In this experiment, the exact conditional mean mixes two disjoint frequency bands with a spatially varying weight. Because the control is Gaussian the best achievable result is known, and the stationary filter's gap is 78% of the local-variance error. Fraction of that ceiling recovered:

ArmRecovered
Locally stationary filter0.54×0.54\times
Per-pixel rescaling0.51×0.51\times
Season-stratified filter−0.15×-0.15\times
Learned correction (Appendix C.6)1.00×1.00\times

On GARD-LENS, where no ceiling exists, the same correction improves on the global filter by 61-68%. In the default cascade the transport can vary in space through the coarse condition cc; however, we haven't measured to which extent, and we add this to the limitations.

[REVISION] Move this result into the discussion of the source, with the attribution above.

W6: The supply/reach line is not fully clear.

We agree the line needs a sharper definition, and we will add one. The two classes ask different questions about a deficit. Supply-limited: can the model produce the structure at all? Reach-limited: the model can produce it, but does the training objective ask for it? In practice, we use the following protocol to distinguish between the two:

Protocol.

  1. Diagnose. Score the trained model against the GCS floor on spread, spectrum, the increment-kurtosis ratio and the amplitude-binned variance ratio RvarR_{var} (Appendix D.3). If all of them match the data, stop.
  2. Test supply. Keep the energy score and vary the source (Gaussian →\rightarrow Nataf) and the transport (identity →\rightarrow affine →\rightarrow full), as in the factorial of Table 12.
  3. Classify and fix.
    • 3a. The deficit responds →\rightarrow supply-limited. The fix is the source or transport that moved it. Examples from the paper: on Allen-Cahn only the Nataf source reaches the tail (κ/κdata\kappa/\kappa_{data} 1.1 vs 0.7-0.8); with a nonlinear conditional mean only the learned transport helps (CRPS 0.60 vs 1.13-1.16).
    • 3b. No source ×\times transport cell moves the deficit →\rightarrow reach-limited. The fix is an added objective term, and RvarR_{var} decides which one: a scale-free flatness term if RvarR_{var} is flat across amplitude (homogeneous deficit), or an amplitude-conditional term (e.g., amplitude-stratified ES or K62 slope matching) if RvarR_{var} crosses one. Each term is dosed at the smallest weight that moves the tail, keeping nRMSE, σ/s\sigma/s and logPSD inside fixed guards. Examples from the paper: on SHE-PAM the Gaussian source reaches κ=3.99\kappa = 3.99 against 38.3 and the deficit is homogeneous, and a flatness term closes 93%. On GARD-LENS RvarR_{var} crosses one (3.8×3.8\times over-dispersed at low amplitude, 0.87×0.87\times in the tail), so a flatness term cannot bend it; amplitude-conditional terms do: K62 slope matching (L4) closes 80% of the kurtosis deficit and amplitude-stratified ES (L2) 62%.

Step (1) is the one that should not be skipped. On GARD-LENS, default NCS passes every aggregate check (σ/s\sigma/s 0.98, competitive CRPS and spectrum) while reproducing only 21% of the increment kurtosis.

[REVISION] Add this protocol to Sec. 4.1 as the definition of the taxonomy.

W7: Independent noise per cascade level.

Independent noise does not make the levels independent. Each level l+1l+1 is conditioned on the full sample produced at level ll, so whatever the coarser levels generated is passed on through that conditioning field. Independent per-level noise is therefore exact when the finer level depends on the coarser history only through the current level's sample (Eq. 29). It can fail when innovations at two levels are correlated in a way the intermediate sample does not carry, for example cross-scale coupling that bypasses the resolved field. On our benchmarks we find no sign of this and the dependent-noise alternatives below do not improve finest-level quality. In addition, the cascade is trained end to end, so each level's network can compensate for dependence the noise does not carry.

We tested this directly in the Appendix. We replaced the independent noise with three dependent alternatives: (i) a shared latent projected across levels, (ii) latents with the empirically fitted cross-level covariance, and (iii) an autoregressive latent in which each level's noise is conditioned on the previous level's innovation. On Allen-Cahn and Navier-Stokes with three seeds, none of them improves finest-level quality (energy score, nRMSE, σ/s\sigma/s and logPSD are unchanged within seed variance). The shared and fitted-covariance latents do slightly tighten consistency between levels (restriction error 0.096→0.0740.096 \rightarrow 0.074 on Navier-Stokes). But independent noise already exceeds the data's cross-level coherence (0.944 vs 0.905), and dependent noise raises it further (0.966). So dependent noise brings no gain where it matters, and independent noise remains our default.

[REVISION] State the sufficiency condition and the untested case in Sec. 3 and the limitations.

Reviewer_yLXTOpenReview ↗
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Paper summary

This paper proposes Neural Conditional Simulation (NCS) for generating fine-resolution PDE fields conditioned on a coarse solution. Its motivation is that squared-error refinement estimates a conditional mean and therefore misses unresolved variability. NCS combines a fixed kriging/Wiener predictor with a learned, condition-dependent transformation of a spectrally fitted innovation. An identity initialization embeds classical Gaussian conditional simulation, which is exact under joint Gaussianity with exact covariance information. Sampling proceeds through a coarse-to-fine cascade with one network evaluation per level, using drifting pretraining followed by end-to-end energy-score optimization.

The main contribution is a framework that makes gains beyond Gaussian conditioning measurable. A second contribution is a diagnostic distinction between “supply-limited” errors requiring changes to the source or transport and “reach-limited” errors requiring a different training objective. The theoretical analysis establishes Gaussian exactness under ideal conditions and population identification through proper scoring, without guaranteeing finite-sample convergence or exactness of the full cascade.

Validation combines stochastic Allen–Cahn and Navier–Stokes benchmarks, GARD-LENS precipitation ensembles, and controlled Gaussian and non-Gaussian experiments. Comparisons cover deterministic refiners, classical simulators, probabilistic neural operators, consistency models, and diffusion methods. Evaluation includes proper scores, ensemble calibration, spectral errors, tail statistics, cross-scale consistency, and runtime, supported by component and objective ablations.

Reported gains over classical methods are modest on near-Gaussian benchmarks but larger for precipitation, where NCS achieves a spread–skill ratio of 0.96 at competitive CRPS and spectral error. Sampling is reported to be 17–36 times faster than 35-evaluation diffusion baselines. Energy-score training alone substantially underestimates heavy tails; an amplitude-conditioned objective recovers approximately 78% of the precipitation increment-kurtosis deficit without degrading global calibration.

Critical strengths

A useful connection between classical conditional simulation and learned refinement. NCS retains an explicit kriging predictor and learns a conditional transformation of the innovation, with Gaussian conditional simulation available as an identity-map baseline. This gives the neural component a meaningful statistical reference against which its contribution can be measured. The theoretical discussion also distinguishes population guarantees from the approximations introduced by estimated covariances and finite neural networks. Although the individual ingredients are established, their combination provides an interpretable approach to stochastic refinement. This supports acceptance because the formulation helps identify when learning adds value and when a simpler classical simulator already performs adequately.

Critical weaknesses
  1. The comparisons do not fully establish the practical quality–cost advantage. The paper includes useful baseline and sampling-budget studies, but several comparisons remain difficult to interpret. The GARD-LENS diffusion sweep changes the inference-time noise ceiling and step count while keeping the training noise distribution unchanged (Appendix F.6). It therefore does not establish whether the reported underdispersion persists after tuning the training setup for this heavy-tailed dataset. Similarly, the headline 17–36× speedup is measured against 35-evaluation diffusion, although the sampling-budget study reports that the iterative methods approach their best scores at roughly 8–11 evaluations. The timing study also uses the smaller Navier–Stokes problem, whereas the main accuracy table uses the larger one. These choices do not invalidate the reported measurements, but leave the advantage at comparable quality and resolution less certain. Section 5.4 also acknowledges a batch-size difference in the threshold-weighted ablation despite Table 13 describing objective-only changes. Since efficiency and diagnostic attribution are central contributions, latency measurements at the best validated sampling budgets and a matched-batch objective ablation are important to my assessment.

  2. Validation of reliable conditional tail simulation remains incomplete. The precipitation experiments demonstrate that global variance calibration can coexist with substantial tail errors. The main energy-score model reaches an increment-kurtosis ratio of only 0.17, and the amplitude-conditioned extension improves this to approximately 0.81–0.83 (Tables 1 and 15). This correction is encouraging, and the authors acknowledge the remaining deficit. However, improved pooled kurtosis at two lags does not establish accurate conditional exceedance probabilities or the spatial organization of extremes. More direct evaluation of these properties for the corrected model would be consequential given the paper’s motivation in uncertainty-sensitive scientific simulation. Furthermore, GARD-LENS conditions are constructed by coarsening the high-resolution fields, rather than using an independently generated coarse forecast (Appendix D.1). This is a valid conditional reconstruction task, but it leaves robustness to coarse-model bias untested on the main non-Gaussian application. Consequently, the evidence supports a promising refinement method under the evaluated conditions more strongly than broad practical reliability. Conditional extreme-event diagnostics and an independently conditioned precipitation benchmark would help determine whether the reported improvements extend to the setting motivating the application.

Questions for authors

These clarification requests could materially change my assessment:

  1. Baseline tuning and efficiency. Table 19 varies sampling parameters while keeping the training noise distribution fixed. How was that distribution selected for GARD-LENS? Was training-time tuning investigated? What speedups remain at the best validated sampling budgets, using comparable quality targets and resolutions?

  2. Objective attribution. Section 5.4 mentions a smaller batch for the threshold-weighted objective, while Table 13 describes objective-only changes. Which settings differed? Is there an existing matched-batch comparison showing whether the reported tail and spectral gains persist?

  3. Evaluation protocol. Table 3 lists 128 GARD-LENS test conditions, whereas Table 19 refers to 64. Is this a fixed subset, how was it selected, and were NCS and all baselines evaluated on precisely the same conditions?

  4. Conditional tail reliability. For the amplitude-conditioned model in Table 15, are conditional exceedance probabilities or coverage results available beyond pooled increment kurtosis? Such diagnostics would help determine whether the correction improves extreme-event reliability across intensity levels.

Evaluating independently generated coarse forecasts would be useful future work. For the current submission, clarifying the limitations imposed by target-derived conditioning would be sufficient to establish the intended scope of the precipitation results and their relevance to deployment.

6 comments

Q1. How was the diffusion training noise distribution chosen for GARD-LENS? Was training-time tuning investigated?

EDM and CorrDiff were trained with the published EDM recipe: σdata\sigma_{\mathrm{data}} from the training residuals, training noise ln⁡σ∼N(−1.2,1.22)\ln \sigma \sim \mathcal{N}(-1.2, 1.2^2). We did not tune the training-time distribution for GARD-LENS, and Table 19 varies sampling-time settings only, which could be swept from existing checkpoints (132 settings). The reviewer is right that this left open whether the under-dispersion persists after training-time tuning; it partially does.

We retrained EDM, CorrDiff and Consistency on GARD-LENS with the residual target standardized by training-split statistics (exact inverse at evaluation), three seeds, everything else unchanged. Sampling settings (σmax⁡\sigma_{\max}, σmin⁡\sigma_{\min}, steps: 180 settings for EDM and CorrDiff, 70 for Consistency) were selected on the validation conditions by a rule fixed in advance: σ/s∈[0.85,1.15]\sigma/s \in [0.85, 1.15], logPSD at most twice the best passing value, then lowest CRPS. The selected settings were then sampled once on all 128 test conditions. Seed means and 95% condition-bootstrap intervals:

ArmSettingESCRPSσ/s\sigma/slogPSDκ/κdata\kappa/\kappa_{\mathrm{data}}NFE
EDMold: paper checkpoint, default sampler497.00 [472.21, 522.28]1.509 [1.427, 1.603]0.442 [0.430, 0.455]0.312 [0.288, 0.336]0.19 [0.14, 0.25]35
EDMtuned, default sampler469.15 [445.55, 492.48]1.486 [1.406, 1.565]0.859 [0.856, 0.905]0.102 [0.086, 0.127]0.61 [0.45, 0.83]35
EDMtuned, val-selected (35 NFE)468.84 [444.36, 492.99]1.487 [1.407, 1.566]0.901 [0.879, 0.927]0.094 [0.081, 0.121]0.63 [0.47, 0.85]35
EDMtuned, val-selected (17 NFE)468.97 [444.43, 492.24]1.487 [1.407, 1.566]0.897 [0.873, 0.924]0.095 [0.082, 0.120]0.57 [0.42, 0.77]17
CorrDiffold: paper checkpoint, default sampler491.44 [466.15, 517.36]1.521 [1.432, 1.610]0.530 [0.515, 0.546]0.113 [0.098, 0.134]0.14 [0.11, 0.19]35+1
CorrDifftuned, default sampler475.93 [453.10, 499.10]1.493 [1.413, 1.573]0.796 [0.770, 0.826]0.092 [0.074, 0.115]0.51 [0.37, 0.69]35+1
CorrDifftuned, val-selected (grid edge)475.19 [452.73, 498.14]1.496 [1.416, 1.576]0.881 [0.851, 0.912]0.093 [0.074, 0.114]0.49 [0.35, 0.66]17+1
Consistencyold: paper checkpoint, default sampler497.01 [471.85, 522.74]1.550 [1.460, 1.642]0.433 [0.419, 0.448]0.448 [0.422, 0.474]0.26 [0.19, 0.35]2
Consistencytuned, default sampler471.82 [449.22, 494.74]1.508 [1.427, 1.588]0.744 [0.723, 0.765]0.213 [0.188, 0.239]0.54 [0.34, 0.84]2
NCS-460.71 [438.61, 483.31]1.571 [1.487, 1.655]0.982 [0.960, 1.006]0.131 [0.111, 0.154]0.21 [0.15, 0.29]1
NCS+L2-460.71 [438.59, 483.32]1.554 [1.471, 1.636]0.981 [0.959, 1.005]0.143 [0.121, 0.166]0.70 [0.64, 0.75]1
NCS+L4-460.78 [438.67, 483.36]1.573 [1.489, 1.657]0.976 [0.954, 1.000]0.058 [0.045, 0.078]0.84 [0.80, 0.89]1
GCS-490.28 [468.32, 512.80]2.460 [2.374, 2.548]0.959 [0.912, 1.010]0.023 [0.013, 0.061]0.01 [0.01, 0.01]0

Tuning removes most of the diffusion baselines' under-dispersion. EDM's spread rises from σ/s\sigma/s 0.44 to 0.90, and with it CRPS (1.509→1.4871.509 \rightarrow 1.487), spectrum (logPSD 0.31→0.090.31 \rightarrow 0.09) and tail (κ/κdata\kappa/\kappa_{\mathrm{data}} 0.19→0.570.19 \rightarrow 0.57). CorrDiff improves similarly (σ/s\sigma/s 0.53→0.880.53 \rightarrow 0.88) and Consistency improves (0.43→0.740.43 \rightarrow 0.74) but stays outside the window. The comparison with NCS is therefore a tradeoff rather than a ranking:

  1. Tuned EDM is better on CRPS (1.487 vs. 1.571) and spatial structure (logPSD 0.095 vs. 0.131).
  2. NCS is better on the multivariate score and spread: ES 460.7 vs. 469.0, σ/s\sigma/s 0.98 vs. 0.90.
  3. With the amplitude-conditional objective (L4), NCS reproduces the tail best (κ/κdata\kappa/\kappa_{\mathrm{data}} 0.84 vs. 0.57) and has the best spectrum (logPSD 0.058 vs. 0.095), at unchanged ES and spread. Its CRPS (1.573) remains behind tuned EDM.

NCS does this with one network pass per member against 17 for the selected EDM setting, and without a noise schedule to set. We withdraw the statement that NCS is the only calibrated method on GARD-LENS, and revise the abstract and Sec. 5.2 to describe this tradeoff.

[REVISION] We replace the GARD-LENS diffusion comparison in the abstract, introduction and Sec. 5.2 with this tradeoff. We add the E1 table and the validation-selection table to the appendix. We keep Table 19 but relabel it as the original-recipe sweep.

Q1b, Q1c. Speedup at the best validated budgets; timing on small vs. large Navier-Stokes.

The 1717-35×35\times figure is at the default schedule (35 NFE). The budget sweep shows that EDM reaches its own quality floor at about 9-11 NFE on Allen-Cahn and Navier-Stokes, and its best-CRPS GARD-LENS setting uses 17 NFE (Table 19). We therefore define the matched-quality budget as the smallest budget at which the baseline reaches its own best score. Measured per-member latency at those budgets, on the same GPU and in the same session:

SystemNCS (ms)EDM, validated budget: ms (NFE)SpeedupEDM, 35 NFE: msSpeedup
Allen-Cahn0.863.76-4.55 (9-11)4.44.4-5.3×5.3\times14.3616.7×16.7\times
Navier-Stokes 32→12832 \rightarrow 1280.946.76-8.25 (9-11)7.27.2-8.8×8.8\times26.1527.8×27.8\times
Navier-Stokes 64→25664 \rightarrow 2563.4424.27-29.65 (9-11)7.17.1-8.6×8.6\times94.2527.4×27.4\times
GARD-LENS0.7412.72 (17)17.2×17.2\times26.1935.3×35.3\times

CorrDiff costs the same as EDM within 1% at every budget. EDM's cost scales almost exactly linearly with NFE (fixed per-sample overhead is below 0.1 ms), so the validated-budget speedups are roughly the 35-NFE figures scaled by the step ratio.

[REVISION] We provide the validated-budget speedup as the headline, with the 35-NFE numbers secondary.

Q2. Batch size in the threshold-weighted ablation.

Thank you for catching this. The threshold-weighted arm was fine-tuned end to end at batch 1 because its tail-weight dose was calibrated at that batch; changing the batch shifts the effective dose by about 20% and would have required recalibration. The energy-score control and the other arms ran at batch 4. Appendix G wrongly states batch 1 for the energy-score stage. Architecture, source, pretraining, epochs, ensemble size and learning rate were identical. The Table 13 caption ("objective-only changes") is therefore inaccurate and will be corrected, as will Appendix G.

To remove the confound we retrained the energy-score arm with the threshold-weighted arm's exact recipe, with only the threshold terms deleted: batch 1, the same pretraining and fine-tuning epochs, learning rate, ensemble size, source and number of optimizer updates. This is a full retrain, three seeds. All nine runs (three arms ×\times three seeds) are scored on byte-identical conditions and targets.

Panel A

ArmESCRPSσ/s\sigma/slogPSD
ES, batch 4312.6 [311.3, 313.8]0.969 [0.965, 0.973]0.973 [0.969, 0.977]0.364 [0.341, 0.392]
ES, batch 1 (matched control)312.9 [311.6, 314.2]0.970 [0.966, 0.974]0.969 [0.965, 0.973]0.342 [0.338, 0.348]
twES, batch 1312.8 [311.5, 314.1]0.970 [0.966, 0.974]0.973 [0.969, 0.977]0.208 [0.201, 0.217]

Panel B: tail (standardized lag increments; data value in the last row)

Armκ1\kappa_1κ2\kappa_2Δζ4\Delta\zeta_4q99q_{99}q99.9q_{99.9}
ES, batch 46.49 [6.11, 6.84]3.63 [3.58, 3.69]−0.119-0.119 [−0.128-0.128, −0.112-0.112]2.00 [1.95, 2.04]2.87 [2.79, 2.94]
ES, batch 1 (matched control)6.18 [5.98, 6.43]3.54 [3.50, 3.60]−0.102-0.102 [−0.111-0.111, −0.096-0.096]2.02 [2.00, 2.03]2.88 [2.85, 2.91]
twES, batch 14.79 [4.63, 4.95]4.04 [3.91, 4.13]−0.334-0.334 [−0.368-0.368, −0.303-0.303]3.04 [3.01, 3.06]4.24 [4.18, 4.28]
Data4.164.02−0.341-0.3412.903.99

κ2\kappa_2 is the lag-2 increment kurtosis, Δζ4\Delta\zeta_4 the fourth-order structure-function exponent departure, and q99q_{99}/q99.9q_{99.9} the far quantiles of the standardized increments.

At batch 1, the energy-score arm behaves like the batch-4 arm on every tail statistic: its q99q_{99} is 2.02 against 2.00, with overlapping intervals, and both are far from the data's 2.90. The threshold-weighted arm, trained at the same batch, is clearly separated from both, by 47 times the standard deviation of the difference on q99q_{99} and by 7-14 times on κ2\kappa_2 and Δζ4\Delta\zeta_4. The tail gain therefore comes from the objective, not from the batch.

The same holds for the spectrum. logPSD barely moves between batch 4 and batch 1 (0.364 vs. 0.342, overlapping), while the threshold-weighted arm reaches 0.208. Since the comparison is now matched, we restore the attribution of the spectral improvement to the threshold-weighted score. None of this costs accuracy: ES, CRPS and σ/s\sigma/s overlap across all three arms.

[REVISION] We correct the Table 13 caption and Appendix G.

Q3. 128 vs. 64 GARD-LENS test conditions.

The 1024 GARD-LENS conditions are split at random (split seed 0) into 768 training, 128 validation and 128 test. Every GARD-LENS row in Table 1, the schedule sweep of Table 19 and the objective ladder of Table 15 was scored on the same 64 of the 128 test conditions: a random subset fixed by the split seed before any model was trained, identical for every arm and seed. Sampling settings in Table 19 were selected on validation conditions only. The cap was chosen to bound the sampling cost of the 35-step diffusion baselines at M=32M = 32.

To remove any doubt about the subset, we re-sampled every principal GARD-LENS row of Table 1 on all 128 test conditions, with the unchanged checkpoints and their default samplers. The standardized-target diffusion retrain with validation-selected settings is reported separately in Q1, already on 128 conditions. The conditions and targets are byte-identical across all 24 runs, and the first 64 are exactly the Table 1 conditions. Recomputed on those 64, the stored predictions reproduce Table 1 (e.g. NCS ES 473.7, CRPS 1.588; EDM 513.0, 1.535). Re-sampling reproduces it within seed noise.

Seed means; 95% condition-bootstrap intervals for the 128-condition values (2000 replicates, the same resample for every row, seeds not resampled):

Panel A: accuracy

ArmES (n=64n=64)ES (n=128n=128)CRPS (n=64n=64)CRPS (n=128n=128)
NCS474.4 [441.3, 507.7]460.7 [438.6, 483.3]1.590 [1.472, 1.708]1.571 [1.487, 1.655]
NCS+L2474.5 [441.4, 507.8]460.7 [438.6, 483.3]1.571 [1.454, 1.687]1.554 [1.471, 1.636]
NCS+L4474.5 [441.4, 507.8]460.8 [438.7, 483.4]1.592 [1.473, 1.710]1.573 [1.489, 1.657]
GCS505.8 [471.6, 540.5]490.3 [468.3, 512.8]2.499 [2.368, 2.634]2.460 [2.374, 2.548]
PNO476.2 [443.4, 508.9]462.4 [440.2, 485.8]1.610 [1.490, 1.727]1.592 [1.514, 1.681]
EDM513.0 [475.2, 549.9]497.0 [472.2, 522.3]1.536 [1.408, 1.664]1.509 [1.427, 1.603]
CorrDiff508.4 [469.3, 548.0]491.4 [466.2, 517.4]1.552 [1.422, 1.688]1.521 [1.432, 1.610]
Consistency514.4 [475.3, 553.2]497.0 [471.9, 522.7]1.583 [1.447, 1.722]1.550 [1.460, 1.642]

Panel B: calibration and spectrum

Armσ/s\sigma/s (n=64n=64)σ/s\sigma/s (n=128n=128)logPSD (n=64n=64)logPSD (n=128n=128)
NCS0.964 [0.939, 0.993]0.982 [0.960, 1.006]0.147 [0.115, 0.180]0.131 [0.111, 0.154]
NCS+L20.963 [0.937, 0.992]0.981 [0.959, 1.005]0.160 [0.127, 0.193]0.143 [0.121, 0.166]
NCS+L40.959 [0.933, 0.987]0.976 [0.954, 1.000]0.071 [0.048, 0.101]0.058 [0.045, 0.078]
GCS0.923 [0.859, 0.998]0.959 [0.912, 1.010]0.018 [0.015, 0.071]0.023 [0.013, 0.061]
PNO1.000 [0.964, 1.035]1.036 [1.004, 1.066]0.536 [0.498, 0.577]0.551 [0.525, 0.575]
EDM0.428 [0.414, 0.445]0.442 [0.430, 0.455]0.325 [0.286, 0.362]0.312 [0.288, 0.336]
CorrDiff0.514 [0.496, 0.535]0.530 [0.515, 0.546]0.120 [0.095, 0.154]0.113 [0.098, 0.134]
Consistency0.418 [0.400, 0.438]0.433 [0.419, 0.448]0.456 [0.416, 0.497]0.448 [0.422, 0.474]

Comments on the paper

3 comments
AuthorsOpenReview ↗

General response (all reviewers)

We thank the reviewers for careful and constructive reviews, and since rebuttal time is short, we offer an optional, anonymized 8-minute video recap of NCS (link) for anyone who would like a quick refresher on the method before reading our responses.

Three concerns were shared, and we address each with new evidence below and in the individual responses. Unless stated otherwise, all GARD-LENS numbers are now on all 128 test conditions, and kurtosis ratios are at lag 2.

  1. The precipitation tail (eL2g, yLXT). Default NCS is calibrated in spread (σ/s\sigma/s 0.98) and competitive on CRPS and spectrum. However, it reproduces only 21% of the data's increment kurtosis. The cause is the objective. The energy score is dominated by the bulk of the distribution, and on GARD-LENS the deficit depends on intensity: the ensemble is 3.8×3.8\times over-dispersed at low rain rates and 0.87×0.87\times in the tail. We changed only the objective. Amplitude-conditional terms raise the kurtosis ratio to 0.70 (L2) and 0.84 (L4) with ES and spread unchanged. L4 also more than halves logPSD (0.131→0.0580.131 \rightarrow 0.058), and L2 improves CRPS (1.571→1.5541.571 \rightarrow 1.554).

  2. Construction of the GARD-LENS condition (eL2g, yLXT). The coarse condition is the block-averaged ensemble mean of the same high-resolution members that are refined. The task is therefore conditional reconstruction given a consistent coarse field. We state this in Sec. 4, Appendix D.1 and the limitations, and we restrict the precipitation claims to this setting. We also ran a condition–member mismatch sweep on Navier–Stokes (eL2g Q2). As the coarse input stops matching the members, every method degrades by a similar 20–22% in ES, including the untrained Gaussian anchor. An independently conditioned precipitation benchmark is in preparation but is not part of this rebuttal.

  3. Clarity of the contribution (HC6i, yLXT). We add a short statement of what NCS adds over classical conditional simulation and over learned refiners. We also define the supply/reach taxonomy operationally as a three-step diagnostic protocol (HC6i W6), and we move design detail to the appendix.

New evidence

  • Retrained diffusion baselines (yLXT Q1). We retrained EDM, CorrDiff and Consistency on GARD-LENS with a standardized target, using three seeds. Sampling settings were selected on validation conditions by a rule fixed in advance. This removes most of the baselines’ under-dispersion (EDM σ/s\sigma/s 0.44→0.900.44 \rightarrow 0.90). Tuned EDM is better than NCS on CRPS and spectral structure. NCS keeps the lower energy score, spread closer to one, and, with L4, the best tail among learned methods. We withdraw the claim that NCS is the only calibrated method on GARD-LENS, and we present the comparison as a quality–latency tradeoff.
  • Latency at validated budgets (yLXT Q1b/c). At each baseline’s best validated sampling budget, NCS is 4.44.4-5.3×5.3\times faster than EDM on Allen-Cahn, 77-9×9\times on Navier-Stokes and 17×17\times on GARD-LENS. At the default 35 steps the figures are 1717-35×35\times. The validated-budget figures become the headline.
  • Matched-batch control (yLXT Q2). We retrained the energy-score arm with the threshold-weighted arm’s exact recipe, at batch 1. Its tail and spectrum are unchanged, so both gains come from the objective, not the batch.
  • All principal GARD-LENS rows re-sampled on all 128 test conditions (yLXT Q3). The energy-score ordering is unchanged. On CRPS, Consistency moves ahead of NCS+L2, and PNO becomes slightly over-dispersed (σ/s\sigma/s 1.04).
  • Conditional extreme diagnostics (yLXT Q4). We report exceedance reliability, Brier score, coverage, fractions skill and object statistics, with uncertainty, on all 128 test conditions.
AuthorsOpenReview ↗

Summary of the discussion and new evidence

Dear Area Chair,

Thank you for handling our submission. We would like to briefly summarize the discussion. No reviewer identified an error in the theory or in the method: all theoretical results and the NCS algorithm stand as submitted, and two of the three reviews report no substantive soundness concerns. The reviewers' feedback has been very constructive, and it has strengthened the paper in the following ways.

Prompted by the reviews, we added the following new evidence:

  • retrained diffusion baselines (EDM, CorrDiff, Consistency) with standardized targets and validation-selected sampling,
  • latency at the baselines' validated sampling budgets, including the resolution of the main table,
  • a matched-batch control for the objective ablation,
  • all GARD-LENS results evaluated on the full 128-condition test set,
  • conditional exceedance, coverage, fractions-skill and object diagnostics for precipitation extremes.

We believe these additions have made the value of NCS considerably clearer. Against properly tuned diffusion baselines, NCS remains well calibrated with a single network pass, at 17 times lower per-member latency than the best validated diffusion setting on GARD-LENS. It places heavy rain more accurately and covers wet pixels better than every diffusion baseline. The matched control confirms that the tail improvement comes from the objective, and every table reports exactly what learning adds over the exact Gaussian simulator. This is the central idea of the paper, and the discussion has made it easier to see.

We also sharpened the presentation. The GARD-LENS comparison is now framed as a quality–latency tradeoff, the precipitation results are clearly scoped to conditional reconstruction, the theoretical section states precisely what NCS guarantees, and the supply–reach taxonomy now rests on a positive experimental test with an explicit "unresolved" outcome.

For a quick overview of the method, we provide an anonymized 8-minute video summary: https://osf.io/9wqxy/overview?view_only=d6aa818868cc4c23bd330384f0b39423

We have invited all reviewers to share their view of these additions, and we would warmly welcome any further feedback from Reviewers yLXT and eL2g before the discussion closes.

Thank you for your time and support.

Dear Area Chair,

We thank you and the reviewers for a constructive discussion. In our view, the paper's central claims hold and are now better supported than in the submitted version. In particular, we show where our work extends the literature and what advantage our approach provides over classical and diffusion baselines (theoretical advantages, comparison to baselines).

Reviewer yLXT listed requests that "could materially change my assessment". We provided every requested result (1, 2, 3). Together, these results support the paper's claims and strengthen the case for the method. On conditioning, the reviewer wrote that "clarifying the limitations imposed by target-derived conditioning would be sufficient". We did exactly this: the construction is now stated explicitly, and the precipitation claims are restricted to conditional reconstruction (construction, scope of claims). We therefore believe all of yLXT's requests have been addressed.

Reviewer HC6i raises no substantive soundness concerns. We answered the original question and all seven listed weaknesses. On 16 November, we also answered the three follow-up questions on the theoretical advantages of the construction, the evaluation set (1, 2), and the supply–reach classification.

Reviewer eL2g recommends weak acceptance and likewise raises no substantive soundness concerns. We answered both questions with new results (Q1, Q2).

No reviewer challenged the contributed theory or identified an error in the method. The discussion has left the paper's foundations intact and its evidence considerably stronger.

Sincerely, The Authors

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

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