acceptodds
Under review as a conference paper at ICLR 2027

KoopFM: Base-Anchored Flow Matching for Long-Term Emulation of Forced Dynamical Systems

Abstract

Long-term rollouts of chaotic dynamical systems are critical across computational science, from turbulence to climate projection. Under time-varying external forcing the problem shifts from an initial-value to a boundary condition one, in which long-run statistics are set by the forcing trajectory. Neural operators are increasingly being used in this setting, but deterministic models are spectrally biased and may drift, whereas generative ones fix the spectra issue but transport mass from isotropic Gaussian noise. Thus, the vector field must rebuild global structure, forcing response and fine-scale turbulence at once, at many network evaluations per step. Motivated by scale separation and the Mori–Zwanzig formalism, we propose KoopFM, which couples a Koopman-autoencoder base model with base-anchored flow matching, where we replace the standard Gaussian source of the probability path with a source centered on the base prediction, so the residual travels a much shorter path. We identify the source variance σ as the central mechanism, as it prevents degeneracy and determines that path length, as well as the correction range of the flow. Across three chaotic dynamical systems, we show that the anchoring construction has two main advantages. First, whenever the one-step conditional is narrow, inference needs as few as two NFEs without any distillation. Second, the damped, forcing-aware Koopman anchor improves the out-of-distribution forcing response on the chaotic Lorenz–96 system, and on forced Rayleigh–Benard convection the anchored model outperforms vanilla flow matching beyond the training range of the forcing, up to a metric-dependent limit.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
flow matching, Koopman operator, dynamical systems emulation, generative surrogate models, out-of-distribution generalization

Reviews

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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_eirROpenReview ↗
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2
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2
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2
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2
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Paper summary

The paper proposes a generative emulator that combines a forcing-aware Koopman-style predictor with conditional flow matching. The basic idea is to initialize the flow-matching process around the deterministic prediction, so that the generative model only needs to account for the residual. The experiments on Lorenz–96, Kolmogorov flow, and Rayleigh–Bénard show promising performance at low NFE, and some robustness to changes in the forcing.

Critical strengths
  1. Anchoring flow matching around a deterministic prediction is intuitive and can reduce the number of function evaluations.
  2. The source-variance and anchor experiments provide interesting evidence that the best generative anchor is not necessarily the most accurate one-step predictor.
  3. The experiments with varying and stochastic forcing clarify the method succeeds and where its advantage starts deteriorating.
  4. The combination of a physical/Koopman anchor with conditional generative refinement is technically well motivated.
Critical weaknesses
  1. The core idea of using a deterministic prediction as an anchor for generative residual refinement is closely related to existing diffusion/flow-based residual forecasting and PDE-refinement approaches. My impression is that the main novelty is the combination with a forcing-aware Koopman model, rather than a fundamentally new generative mechanism. It would be useful to more clearly position the method relative to this existing line of work.
  2. The experiments do not establish that KoopFM is competitive with the broader state of the art. Comparisons with closely related residual generative methods (beyond PDE-Refiner) and stronger external Koopman baselines are missing. The advantage appears stronger in NFE efficiency rather than overall generative quality.
  3. Several ablations are provided, but they do not cleanly isolate the contributions of anchor initialization, explicit anchor conditioning, the Koopman architecture, forcing conditioning, and source variance. It is unclear how much of the gain comes from generic anchoring versus the Koopman structure.
  4. The benchmarks are useful but relatively controlled, and there is little evidence of scaling to substantially larger state dimensions or higher-resolution systems. The method is also demonstrated only as a discrete-time physical emulator.
  5. Since the central claim is that the generative model recovers structure missing from the deterministic anchor, visual comparisons of the generated fields, residuals, and spectra would be valuable. The current aggregate metrics do not fully establish that KoopFM produces better fields.
Questions for authors
  1. How does KoopFM compare with other closely related residual generative approaches beyond PDE-Refiner, particularly flow/diffusion methods that condition on deterministic forecasts or model their residuals?
  2. The anchor ablation suggests that the Koopman anchor provides an advantage beyond simply using a more accurate deterministic predictor. Can the authors further disentangle the benefit of the Koopman representation from the generic benefit of anchor-centered flow matching?
  3. Can the authors ablate explicit anchor conditioning, forcing conditioning, and source initialization independently?
  4. How does the method scale to substantially larger spatial/state dimensions?
2 comments

W1/Q1, positioning relative to residual generative models. We agree that the generative mechanism is closely related to other methods and say so in Sections 3 and 4.2, where the construction is identified with residual generative models (ResShift, inversion by direct iteration, CorrDiff, ArchesWeatherGen). The closest method beyond PDE-Refiner, ArchesWeatherGen, is now in the comparison through its construction, the U-Net forecast anchor under our recipe (Table 7 row (g); see our answer to Reviewer W13Y, W1), and at the Koopman σ (row (h)), where it matches KoopFM except on W1(p). The contribution we claim is the forcing-aware anchor plus the σ analysis plus the evaluation (our answer to Reviewer b3ub, W1), and we have restructured the text so that this is said once, up front, and tabulated: the new Table 1 in Section 3 places KoopFM next to Cohesion, PDE-Refiner, ResShift, CorrDiff and ArchesWeatherGen, and its last column names the closest row of our ablations.

W2, state of the art and Koopman baselines. Three Koopman-flavoured baselines are now explicit: the Cohesion-style construction (Gaussian source guided by the Koopman prior through conditioning) is cell (a) of Table 9; the Koopman autoencoder rolled out alone is the "base predictor alone" row (Table 21); Koop-Res is the deterministic residual on the same anchor. We did not add a larger standalone Koopman model: the paper makes no claim about Koopman models as emulators on their own, and the anchor is deliberately low-capacity and not meant to compete alone (Section 4.1, "Capacity").

On whether the advantage lies in NFE efficiency rather than in overall generative quality: this is partly true, and we do not claim otherwise. On Rayleigh–Bénard KoopFM is not uniformly best at each model's own budget (Table 2): it leads on W1(p) and is ahead of Vanilla CFM on LSD(p), but Vanilla CFM matches or leads on the fluxes and PDE-Refiner has the best LSD(p). The clearest gain there is the budget: two solver steps match Vanilla CFM at 25. The second gain is the forcing response. On Lorenz–96 KoopFM has the lowest response error on the slow and the fast variables, with a margin that grows for F > 12, outside the training range (Section 5.1; this needs five or more solver steps, App. C.6), and on Rayleigh–Bénard it holds the pressure statistics and the Re response up to 30–40% above the training ceiling (Table 27).

W3/Q2/Q3, clean isolation. Table 9 varies source initialisation, anchor conditioning and forcing conditioning one at a time with the same anchor and backbone. App. C.6 repeats these cells on Lorenz–96, where the forcing response is measured directly: hiding the forcing from the flow raises the high-forcing response error of the slow tier from 2.74 to 9.01 in all three seeds, so the flow needs the forcing as well as the anchor. Table 7 varies the anchor at fixed σ and σ at fixed anchor, with a persistence anchor as the generic-anchoring control (numbers in our answer to Reviewer b3ub, Q2).

How much is Koopman and how much is generic anchoring (Q2):

  • Anchoring alone is not enough. A persistence anchor at a near-matched σ is 3× worse on W1(p) and 60% worse on LSD(p); on Lorenz–96 it diverges.
  • σ does not repair a wrong forcing response. The FNO anchor at the Koopman σ matches the spectra but not the forcing-dependent metrics.
  • A sound generic anchor at the right σ is enough. The U-Net forecast anchor at the Koopman σ matches KoopFM on every metric except W1(p), where KoopFM stays significantly ahead in both schedules.

So most of the benefit is generic to an anchor with a sound forcing response and a wide enough source. The Koopman anchor's specific contribution is that it delivers this with a 55× smaller network and that its own residual already gives the working width. App. B.2 now says this.

W4/Q4, scaling. We do not have results at larger state dimension and now say so in Section 6. On the cost side, the anchor adds 0.16 M parameters and a fraction of one network evaluation per step, the flow runs at 2–10 NFE instead of 25, and both stages are convolutional, so the per-step cost scales with the backbone like any U-Net-based emulator; the open question is whether a low-capacity anchor remains forcing-aware at higher resolution. The reviewer is also right that KoopFM is demonstrated only as a discrete-time emulator with a fixed time step, like the baselines we compare against. A continuous-time formulation is outside the scope of this paper, which Section 6 now also states.

W5, visual comparisons. New Appendix "Qualitative comparison": fields of the reference and four models at two Ra (Fig. 5), the anchor, the true residual, the sampled residual and the spectra of anchor, reference and samples (Fig. 6: the flow restores the mid-range content that the anchor lacks), and the holdout pair at 1.2× the ceiling (Fig. 7).

Reviewer_eirROpenReview ↗

response

Thank you for your comments and clarifications. I will retain the score as marked.

Reviewer_W13YOpenReview ↗
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2
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4
Informativeness
2
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2
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2
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Paper summary

This paper proposes KoopFM, a two-stage generative emulator for long-term simulation of forced chaotic dynamical systems. A forcing-aware Koopman autoencoder first produces a coarse prediction, which serves as the center of the source distribution for conditional flow matching. This reduces the transport distance and allows the generative model to focus on unresolved dynamics. Experiments on Lorenz–96, Kolmogorov flow, and Rayleigh–Bénard convection demonstrate improved sampling efficiency under narrow one-step conditionals, as well as gains in selected long-term statistics and forcing extrapolation.

Critical strengths
  1. Anchoring flow matching to a physically meaningful prediction is an intuitive and computationally efficient approach. The strong results at only 2 NFEs are compelling, particularly for deterministic Kolmogorov flow and Rayleigh–Bénard convection.

  2. The paper covers three dynamical systems, includes competitive deterministic and generative baselines, and evaluates long autoregressive rollouts rather than relying solely on short-horizon prediction accuracy.

  3. The observed degeneracy at zero source noise and the counterintuitive finding that a more accurate anchor can produce worse long-term statistics are interesting and potentially valuable insights beyond this particular architecture.

Critical weaknesses
  1. Limited novelty and insufficient mechanism isolation. Forecast-centered residual generative models already exist, including ArchesWeatherGen. More importantly, KoopFM changes both the source distribution and the network conditioning relative to vanilla CFM. The claimed efficiency mechanism is therefore not cleanly isolated. A shorter Euclidean transport distance alone also does not guarantee lower ODE integration complexity.

  2. The extrapolation evidence is less conclusive than the framing suggests. In Rayleigh–Bénard convection, part of the advantage already exists within the training range, the high-Ra holdout uses only one training run per configuration, and the benefit disappears at different thresholds across metrics (e.g., around 1.14× for Nusselt bias). Both models eventually deteriorate severely. This limits the evidence for a robust extrapolation advantage.

  3. Long-term physical fidelity remains incompletely established. The strongest Rayleigh–Bénard result relies heavily on W1(p), a location-invariant marginal pressure metric that retains the hydrostatic component. This does not fully characterize spatial coherence or physical consistency. Moreover, KoopFM underperforms vanilla CFM under strong stochastic forcing, remains under-dispersed in autoregressive ensembles, and exhibits constraint-related heat-flux errors under extrapolation.

Questions for authors
  1. Can the authors disentangle the contributions of source anchoring, explicit anchor conditioning, and source variance? In particular, a controlled ablation varying source initialization and anchor conditioning independently, with matched networks, would better substantiate the proposed mechanism.

  2. Does the advantage of the Koopman anchor persist when source variance is controlled independently of anchor prediction error? In Table 5, better predictors automatically receive smaller source variance, confounding anchor quality with the flow's correction capacity.

  3. Can the authors strengthen the extrapolation and physical-fidelity evidence? Multiple training seeds for the high-Ra holdout, uncertainty estimates for extrapolation thresholds, and spatial/physics-aware diagnostics (e.g., divergence, two-point correlations, and flux consistency) would help establish whether the reported pressure-statistics gains reflect more faithful long-term dynamics.

3 comments
AuthorsOpenReview ↗

Part 1/2: W1, W2

W1, novelty, mechanism isolation, path length vs. ODE complexity. The controlled ablation the reviewer describes is the new Table 9 (Section 5.3, App. B.3): source and anchor conditioning varied independently, with matched networks and the same frozen anchor. We also measured the geometry of the sampling path (App. A.2, Table 4; 50 Euler steps on 210 test pairs per model): how far the flow travels from its source draw to the generated sample, and how straight that path is (length travelled divided by the straight-line distance; 1 is a straight line).

ModelSourceAnchor as inputDistance source → sampleStraightness (1 = straight)One-step L2 error, 2 NFEOne-step LSD(p), 2 NFERollout LSD(p), 2 / 25 NFE
Vanilla CFMN(0, I)no7791.00010.0230.651.01 / 0.61
(a)N(0, I)yes7791.00010.0240.620.99 / 0.58
(b)anchoredno961.00140.0280.290.63 / 0.37
KoopFM (ours)anchoredyes961.00130.0260.270.59 / 0.37

One-step LSD(p) is teacher-forced at Ra ≈ 1e7; rollout LSD(p) is pooled over both schedules.

  • The mechanism is the source. (b) reproduces KoopFM and (a) behaves like Vanilla CFM; conditioning the network on the anchor changes LSD(p) by between 0 and 7%, depending on the cell and the budget.
  • The reviewer is right about path length. The anchored path is 8× shorter, but every path is straight to within 1% and the one-step L2 error at 2 NFE is no better for the anchored models. Neither path length nor ODE complexity in state-space norms explains the low-NFE result.
  • The advantage is spectral, and those norms, dominated by the energetic large scales, do not see it: the anchored cells reach at 2 NFE the LSD(p) that the Gaussian-source cells reach at 25, already at one step and again in rollouts. Section 4.2 now says that the low-NFE gain is not explained by path length alone, and the conclusion no longer credits the short path.

On ArchesWeatherGen: its construction is now in the paper as an anchor, i.e. the U-Net 1-step forecast with flow matching on its residual under our exact Stage-2 recipe (Table 7 rows (g), (h)); this is a re-implementation of the design on our data, not the original model. At its own σ it is 50% worse on LSD(p); pinned at the Koopman σ it is level with KoopFM on every metric except W1(p). The paper says so and states what the Koopman anchor then contributes: the same quality with a 55× smaller anchor and a σ that comes from its own residual (App. B.2; numbers in our answer to Reviewer b3ub, Q2).

W2, extrapolation evidence. We accept all three points and changed the text. (i) The in-range part of the gap was already stated and is kept. (ii) We trained two more Stage-2 seeds per holdout arm (the anchor is shared) and regenerated Table 27 with a bootstrap over initial conditions. The table gives the forcing level, as a multiple of the training ceiling, up to which KoopFM is ahead of Vanilla CFM:

MetricSeed 1Seed 2Seed 3Pooled [95% CI]
W1(p)1.501.251.381.35 [1.34, 1.35]
LSD(p)1.281.28> 1.601.33 [1.30, 1.36]
LSD(E)1.201.141.501.26 [1.17, 1.32]
Re bias1.331.411.431.41
Nu bias1.14≤ 1.00≤ 1.00not robust

(iii) The Nusselt bias is the exception the reviewer pointed at, and the seeds show it is not a result: two of the three KoopFM seeds are behind Vanilla CFM on Nu already inside the training range, and KoopFM's Nu bias varies across training seeds by 4–16 times its spread across initial conditions. We have withdrawn the Nu claim in Sections 5.3 and 6 and now state that the advantage that survives a change of seed is confined to the pressure statistics and the Re response, up to 30–40% above the ceiling. We do not count LSD(E): its crossover is above the ceiling in every seed, but the pooled ratio stays between 0.93 and 1.02 up to 1.3× and is significant at one rung only, so we report it as a tie. Both models deteriorate severely beyond that, as the paper says.

AuthorsOpenReview ↗

Part 2/2: W3, Q1–Q3

W3, physical fidelity and W1(p). The new appendix "Physical consistency" (Table 29) reports the diagnostics the reviewer names, on the whole-trajectory rollouts and on the DNS with the same stencil.

Model (increase / increase-decline)Divergence (%)Mass flux (10⁻³)Wall NuW1(p̄)LSD(p′)
DNS0.37 / 0.350.01 / 0.0112.40 / 13.42––
Vanilla CFM5.7 / 4.74.3 / 3.712.00 / 13.172.48 / 2.140.83 / 0.62
U-Net4.1 / 4.12.5 / 2.112.70 / 13.712.09 / 1.901.00 / 0.79
PDE-Refiner3.1 / 2.82.8 / 2.412.75 / 13.892.09 / 1.850.57 / 0.43
Koop-Res (residual)5.3 / 4.72.2 / 2.112.98 / 13.702.05 / 1.780.91 / 0.72
KoopFM (ours)5.6 / 4.72.3 / 2.110.95 / 11.991.87 / 1.680.63 / 0.46
  • Divergence and mass flux: no model is divergence-free; all are about 10× the stencil error of the DNS. On divergence KoopFM is level with Vanilla CFM and Koop-Res and significantly behind the U-Net and PDE-Refiner; on mass flux it is level with the U-Net, PDE-Refiner and Koop-Res and at about half the value of Vanilla CFM.
  • Two-point correlations of w and b at two heights are indistinguishable from the DNS for every model (integral scales agree to the third digit; not tabulated here).
  • Flux consistency: KoopFM matches the bulk Nusselt number but underestimates the wall value by 11% (boundary layer 12% too thick), significantly worse than all four baselines. This is now stated in Section 6. The ablation cells narrow it to the combination of the Koopman anchor with the wide source: it does not change with NFE, and neither the Koopman anchor at a narrow σ nor other anchors at the wide σ show it. We have not identified the mechanism.
  • W1(p): split into the mean profile p̄(z) and the fluctuation p′, the W1(p) advantage sits in the hydrostatic profile (KoopFM significantly best on W1(p̄); W1(p′) is equal across models), so the reviewer's caution is justified and Section 5.3 now says where the gain is. The spectral result does not depend on the profile: LSD on p′ keeps the ordering of LSD(p).

In summary, KoopFM's gains are in the pressure statistics, the spectra and the Re response, not in the heat flux: the wall flux is 11% too low, we no longer claim a Nusselt advantage (W2, part 1), and the heat-flux error beyond the training ceiling that the reviewer points to remains (App. E.13; listed as a limitation in Section 6).

Q1–Q3. Q1 is Table 9 for the source and the conditioning, and rows (d)/(e) of Table 7 (Table 5 of the submission) for the source variance, each varied independently; App. C.6 repeats the cells on Lorenz–96. Q2 is the matched-σ cross (our answer to Reviewer b3ub, Q2): the Koopman anchor's advantage on the forcing-dependent metrics persists at matched σ against the FNO but not against a U-Net forecast anchor; its spectral advantage is the σ prescription. Q3 is W2 (part 1) and W3 above.

Thank you for the detailed response and substantial additional experiments. The controlled ablations in Tables 7 and 9 address my concerns about mechanism isolation and the confounding effect of source variance. However, the comparable performance of the U-Net anchor at matched σ suggests that the distinct contribution of the Koopman component is primarily computational efficiency, leaving my novelty concern only partially resolved.

The additional training seeds strengthen the extrapolation analysis, but the crossover thresholds vary considerably across seeds, and the improvements remain limited to selected metrics and forcing ranges. Moreover, the new physical diagnostics confirm that the W1(p) advantage largely comes from the hydrostatic mean profile, while the significant wall heat-flux bias and physical consistency issues remain unresolved.

Therefore, I intend to maintain my score.

Reviewer_b3ubOpenReview ↗
Rating
3(+1)
Confidence
4
Informativeness
2
Presentation
2(+1)
Soundness
3
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Paper summary

This paper proposes KoopFM for long-term emulation of forced chaotic dynamical systems. A forcing-aware Koopman autoencoder first provides a deterministic next-state prediction. A conditional flow-matching model then generates the next state from a Gaussian source centered on this prediction, with its noise scale estimated from the anchor's prediction residuals. Experiments investigate long-term statistics, forcing-response extrapolation, and sampling efficiency across Lorenz–96, Kolmogorov flow, and Rayleigh–Bénard convection.

Critical strengths

The experimental evaluation is extensive. The paper examines long autoregressive rollouts, forcing-response statistics, different sampling budgets, and several choices of anchor and source noise. I particularly appreciate the comparison between observed and unobserved forcing in Kolmogorov flow, which identifies a setting where anchoring does not help. The anchor and noise-scale ablations also provide useful observations beyond aggregate forecasting scores. Overall, the experiments offer substantial evidence about both the potential benefits and limitations of the approach.

Critical weaknesses

1. The methodological contribution and its connection to Mori–Zwanzig are not sufficiently established.

The method appears primarily to combine a Koopman predictor with a conditional generative correction model. This can be useful, but the manuscript does not clearly establish what is gained beyond existing predictor–corrector and residual generative modeling approaches.

In particular, let at=x^t+1a_t=\hat{x}_{t+1} denote the base prediction and rt+1=xt+1−atr_{t+1}=x_{t+1}-a_t its residual. The proposed interpolation can be written as

xτ=(1−τ)(at+σ⊙ϵ)+τxt+1,x_\tau=(1-\tau)(a_t+\sigma\odot\epsilon)+\tau x_{t+1},

or, equivalently,

xτ−at=(1−τ)σ⊙ϵ+τrt+1.x_\tau-a_t=(1-\tau)\sigma\odot\epsilon+\tau r_{t+1}.

Thus, at the level of the probability path and regression target, the construction is flow matching on prediction residuals expressed in shifted coordinates. The paper acknowledges related constructions in Section 3, but the specific advance beyond these approaches remains insufficiently isolated. Is the main contribution the forcing-aware Koopman parameterization, the source-noise prescription, or the empirical findings about long-term behavior? The paper would benefit from a sharper statement of this contribution and evidence that distinguishes these possibilities.

The Mori–Zwanzig motivation also seems more heuristic than the abstract and introduction suggest. In practice, Stage 2 learns a conditional transition model,

pθ(xt+1∣xt,x^t+1,ut),p_\theta(x_{t+1}\mid x_t,\hat{x}_{t+1},u_t),

with x^t+1\hat{x}_{t+1} itself determined by (xt,ut)(x_t,u_t). This is a reasonable generative forecasting formulation, but the manuscript does not establish how the learned correction corresponds to the memory or orthogonal-dynamics terms in Eq. (3). I acknowledge that the authors explicitly do not parameterize the memory kernel and instead condition on the full generated state. My concern is therefore not the absence of an explicit memory model, but the lack of a concrete connection between the MZ interpretation and the implemented algorithm. The authors should distinguish an interpretation that motivates the architecture from a closure relationship actually established by the method.

2. The presentation makes the main argument unnecessarily difficult to follow.

The methodology contains useful ideas, but its organization obscures the central algorithm and its justification. Section 4.1 combines the latent transition parameterization, stability qualifications, vector versus field representations, spatial parameter sharing, training–inference mismatch, and input-noise augmentation in one long paragraph. These are different aspects of the method and should be presented separately.

Similarly, Section 4.3 moves rapidly from the zero-noise construction to an algebraic shortcut, sampling failure, adaptive noise estimation, correction range, and anchor expressiveness. The observation in Eq. (7) is useful, but the derivation, empirical evidence, and practical prescription for choosing σ\sigma need to be distinguished more clearly. In particular, statements about the effective correction range should be separated from what is mathematically implied by the source distribution.

Although the appendix provides pseudocode, the main text should first give a compact end-to-end description of one forecasting step and then explain the individual design choices. A clearer separation between the algorithm, its physical motivation, and the evidence supporting each claim would substantially improve the paper.

I would be willing to raise my recommendation to 3 if the rebuttal clarifies the specific contribution, provides convincing responses to the central design questions, and presents a clearer account of the method and the scope of its physical interpretation.

Questions for authors
  1. Why perform generative correction in physical space rather than latent space? Since the method already learns a compressed Koopman representation, could flow matching be performed around the predicted latent state and decoded only once, potentially reducing the cost of each vector-field evaluation? Is physical-space correction necessary because the current encoder–decoder cannot represent the small-scale structures that Stage 2 must restore? Please clarify this accuracy–cost trade-off.

  2. Can the contribution of the Koopman anchor be separated from the source-noise scale? Appendix B.2 compares Koopman and FNO anchors, but σ\sigma is estimated separately from each anchor's residuals. Consequently, changing the anchor also changes the source distribution. Do the Koopman anchors retain their long-term advantages when the noise scales are matched, or when σ\sigma is selected independently for each anchor under the same validation protocol? This would help determine whether the observed benefit comes from the Koopman structure or from its interaction with the noise prescription.

5 comments
AuthorsOpenReview ↗

Part 1/2: W1, W2

W1, contribution and Mori–Zwanzig. We agree with the reviewer's claim: at the level of the probability path and the regression target, the construction is flow matching on the anchor residual in shifted coordinates, and Section 4.2 already cites ResShift, inversion by direct iteration and ArchesWeatherGen for it. We have sharpened what we claim as new into three items, each with its evidence: (i) the anchor, which is frozen, damped, forcing-aware and re-encoded from the generated state at every step, and which at its own σ is ahead of more accurate FNO and U-Net anchors at theirs on W1(p) and LSD(p) (App. B.2, Table 7), being matched only by a U-Net anchor pinned at the Koopman σ (row (h); Q2 in part 2); (ii) the analysis of the source width: the training degeneracy at σ → 0 (Section 4.3, Table 5), the anchor-matched prescription being near-optimal (App. B.1), and the new matched-σ cross that shows σ, not anchor accuracy, sets the spectral fidelity (App. B.2); (iii) the evaluation, i.e. climate metrics with paired tests, NFE ladders and a forcing-range holdout with a data-volume control and, now, training seeds and metric-resolved limits (Section 5.3, Table 27). On Mori–Zwanzig we accept the point entirely: the identity motivates the split into a resolved Markovian part and a learned remainder and nothing more. We have therefore removed the displayed identity (Eq. (3) of the submission): Section 2 now carries it as one sentence of prose under "Scale separation", states that a Koopman model captures only the Markovian term and that Stage 2 absorbs the remainder without parameterizing the memory kernel or the orthogonal noise; the abstract and introduction say "motivated by scale separation"; and Section 4.2 adds that Stage 2 is a learned one-step conditional whose only closure-type comparison is Koop-Res against KoopFM, and that on the resolved grid the map is deterministic so the sampled spread is epistemic.

W2, presentation. Section 4 now opens with a box that gives one forecasting step end to end (anchor, source, flow, repeat) with pointers to the design choices. Section 4.1 is split into labelled parts (latent transition, stability, vector vs. field latents, parameter sharing, train–test gap, capacity). Section 4.3 is split into three titled paragraphs: the σ = 0 shortcut (the algebra and the σ = 0 run), the choice of σ (EMA of the anchor residual, 1–3× near-optimal) and the correction range (now with the matched-σ evidence).

AuthorsOpenReview ↗

Part 2/2: Q1, Q2

Q1, physical- vs. latent-space correction. We ran the ablation the question implies, and without re-encoding the rollout fails. Same weights, 10 NFE, 19 initial conditions, whole trajectory; the anchor is either re-encoded from the generated state at every step (the paper) or rolled out in its own latent space.

KoopFM (increase / increase-decline)W1(Nu)W1(Re)W1(p)LSD(p)
Anchor re-encoded every step (paper)0.31 / 0.285.3 / 3.22.2 / 2.10.43 / 0.34
Anchor rolled out in latent space19.8 / 21.5689 / 78342 / 521.23 / 1.34

The latent operator is stable by construction (rotation-decay blocks), and run open-loop it loses the fluctuations: within about ten steps the field RMS of the rollout falls to roughly a fifth of its re-encoded counterpart and afterwards only follows the forcing. The flow, trained on anchors one step away from the truth, does not restore the missing amplitude. Re-encoding is therefore the part of the design that keeps the anchor informative (the "Re-run" column of the new Table 1). On cost: the anchor is 0.16 M parameters and a small fraction of one U-Net evaluation, so the per-step cost is set by the NFE of the flow. A latent-space flow would have to represent the small-scale content that the 64 × 8 × 32 latent cannot (the anchor is spectrally deficient by design, Table 21), trading a cheap anchor step for a decoder that must generate what the flow now generates.

Q2, anchor vs. noise scale. We pinned σ at training time to cross the two factors (revised App. B.2). Short answer: σ, not the anchor architecture, sets most of the long-run quality; the Koopman anchor keeps a W1(p) advantage and is the cheapest way to get there.

Anchor (parameters)σ (mean)W1(Nu)W1(Re)W1(p)LSD(p)
Koopman, own σ = KoopFM (ours; 0.164 M)0.1190.294.32.110.39
(e) Koopman at the FNO σ0.0190.275.42.220.91
FNO, own σ (8.61 M)0.0193.1515022.50.63
FNO at 2× its σ0.0381.577010.80.41
FNO at 3× its σ0.0571.806710.90.42
(d) FNO at the Koopman σ0.1190.5417.83.310.35
(g) U-Net forecast, own σ (9.03 M)0.0130.235.22.500.60
(h) U-Net forecast at the Koopman σ0.1190.224.72.290.38

Autoregressive, whole trajectory, 10 NFE, pooled over both schedules (n = 19).

  • σ is tied to the spectra. At the FNO's narrow σ the Koopman anchor loses them (LSD(p) 0.91, worse than Vanilla CFM); at the Koopman σ both the FNO and the U-Net anchor gain them.
  • At matched σ, an FNO anchor still gets the forcing response wrong: where the forcing reverses it stays at W1(Re) 30 against 3.2.
  • A U-Net anchor at matched σ is on par with KoopFM: row (h) is level with KoopFM and ahead under teacher forcing. KoopFM stays ahead only on W1(p), in both schedules (paired +0.13 [0.06, 0.19] and +0.22 [0.16, 0.27]).
  • What the Koopman anchor contributes is therefore the same quality with a 55× smaller anchor (2 instead of 3 network evaluations per step at 2 NFE; the U-Net-anchored model trains 1.5× slower), and it is the only anchor here whose own residual already gives the working σ.

On selecting σ independently for each anchor: the Koopman anchor's σ was selected over {1, 2, 3}× its residual (App. B.1). The same ladder on the FNO halves its errors but leaves them an order of magnitude away; only the 6× wider value rescues it, so a 1–3× protocol would not have found the working width for the FNO. The paper now states this.

On Lorenz–96 the same cross gives the same picture (App. C.6): the Koopman anchor at the FNO's narrow σ degrades (joint energy distance 0.08 → 0.60 at 50 NFE), and the FNO (BPTT-4) anchor at the Koopman σ is ahead of the Koopman anchor on the forcing response, so there too the anchor need not be a Koopman model.

Thank you for the detailed rebuttal and the additional experiments. I appreciate the authors' efforts to address the reviewers' concerns. In particular, the new controlled ablations help clarify the respective roles of source anchoring, source variance, and the choice of base predictor. I also appreciate the authors' willingness to clarify the methodological contribution and revise the Mori–Zwanzig motivation and presentation.

The responses have addressed several of my initial concerns. However, I still have two questions that I would appreciate further clarification on.

1. On the selection and interpretation of the source noise scale σ\sigma.

The new matched-σ\sigma experiments are informative, and I appreciate the authors' efforts to disentangle the effects of the anchor architecture and source variance.

Nevertheless, I remain somewhat uncertain about the generality of the residual-based noise prescription. For example, the FNO anchor performs poorly when using its own residual-based σ\sigma, while the U-Net anchor achieves reasonably good long-term performance with an even smaller residual-based σ\sigma. Increasing σ\sigma substantially improves the FNO results, but the same adjustment does not appear necessary for the U-Net.

I understand that differences in the anchors' forcing-response behavior also contribute to these outcomes. However, this raises a broader question: under what conditions is the anchor's one-step residual RMS a reliable estimate of the appropriate source noise scale? Is there a practical criterion or diagnostic that could help determine when the residual-based σ\sigma is sufficient and when a larger noise scale is needed?

I understand that establishing a universal rule may be difficult, but a clearer discussion of the applicability and limitations of this prescription would help strengthen the generality of the proposed approach.

2. On the computational advantage of the Koopman anchor.

I appreciate the authors' clarification that the Koopman anchor is substantially smaller than the U-Net anchor and provides comparable performance at a lower computational cost.

However, I am still curious about the end-to-end inference efficiency. One attractive feature of Koopman-based modeling is the possibility of efficient multistep propagation through linear latent dynamics. In the proposed framework, however, each physical time step requires re-encoding the generated state, performing a Koopman update, decoding the prediction, and then applying flow-matching correction.

Could the authors provide a more explicit comparison of the end-to-end inference efficiency of the proposed prediction–correction framework against representative baselines, including inference time and computational cost under comparable settings? Since flow-matching correction is performed in the full physical space at every prediction step, such a comparison would help clarify the practical efficiency of the overall framework beyond the lightweight Koopman anchor.

Overall, I appreciate the substantial additional experiments and the thoughtful responses to the reviewers' concerns. The rebuttal has clarified several important aspects of the method and its contributions.

I would prefer to review the formally revised manuscript before making a final decision on whether to update my rating.

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