- Rating
- 1
- Confidence
- 4
- Informativeness
- 1
- Presentation
- 2
- Soundness
- 1
Read review
Paper summary
The paper proposes OceanFlow, a probabilistic data-driven model for global ocean simulation and forecasting. A deterministic backbone, the Factorized Dynamics Operator (FDO), is run on Perlin-perturbed initial states to produce a reference ensemble. A learned correction then adjusts the ensemble mean, and a flow matching step reshapes the residuals around it, with a velocity conditioned on ensemble statistics. A final recentering keeps the ensemble mean at the corrected value. The claimed contributions are this coherent flow matching framework, the FDO architecture, and a short theoretical result on the resulting conditional law. The model is trained on GLORYS12 coarsened to 1 degree with ERA5 forcing: five ocean variables, four of them on 23 levels, giving 93 channels. Experiments cover simulations up to 120 days with reanalysis forcing and forecasts up to 30 days with OneForecast forcing, on 2020 and 2024. OceanFlow is compared with SimVP, GraphCast, CirT, WenHai, NeuralOM and DSLCast, some of them turned into Perlin-noise ensembles. Evaluation uses RMSE, ACC, CRPS, spread-skill ratio, rank histograms, coverage, a Nino-3.4 analysis, spectra, physical diagnostics and ablations. The authors report improvements in accuracy, probabilistic reliability and physical consistency over all baselines.
Critical strengths
The paper addresses a relevant problem: moving from deterministic prediction to ensembles, which is a natural next step for data-driven ocean models, and uncertainty estimates are needed for most practical uses. Separating the ensemble center from the spread around it is a simple and reasonable design. The evaluation goes beyond RMSE, with CRPS, spread-skill ratio, rank histograms and coverage, which is the right set of tools for judging an ensemble. Beyond this, the contribution is limited, for the reasons below.
Critical weaknesses
-
In Appendix E.8, the member conditions for the next day are taken from the deterministic reference ensemble, not from the transported members. The flow and the mean correction are applied to each day's reference output and then thrown away, so what remains is a Perlin-perturbed deterministic ensemble with a learned post-processing step on top. The residual noise is also redrawn at every transition and the context reset every day (E.4), so the learned part of member m on one day has nothing to do with member m on the next, and members can't be used as trajectories. Both learned components are also trained only on one-step transitions from true states, with a spread target taken from the one-day error. I don't see how this can represent uncertainty at 90 or 120 days, or how a one-step correction can fix drift built up over months. My guess is that long-lead spread comes mostly from the divergence of the Perlin reference and the hand-designed spread floor. None of this supports the "coherent state-conditioned pathwise law" claim, and no diagnostic looks at member trajectories or at where the spread actually comes from.
-
Reading Appendix E.4, each member's training target is built from the same noise it starts from: mostly that noise scaled up or down, with only 5% coming from the actual error pattern. So the flow mainly learns how much to stretch or shrink the noise at each grid point. That's useful, but it isn't learning a distribution, and learned residual keeps the shape of the generic smooth noise. With only two flow steps, the continuous-time theory describes an idealized version, not the actual model. The ablation points the same way. Removing the learned flow moves CRPS from 0.371 to 0.379 and RMSE from 0.684 to 0.697, and most of the gain over FDO+Perlin comes from the calibration steps around it. The headline contribution adds a little on its own.
-
Lemma 1 says that subtracting the ensemble mean and adding µ gives an ensemble with mean µ. This is true by construction, and the authors admit it says nothing about calibration or skill. The FDO is mostly standard components with new names: "factorized dynamics" is gated multi-branch mixing with FiLM-style conditioning, and the "state-conditioned response" is a learned residual connection. The deterministic FDO is also clearly weaker than NeuralOM (RMSE 0.825 vs 0.682 at 90 days), so it can hardly be called an accurate deterministic reference.
-
Several relevant data-driven ocean models are neither discussed nor compared against, including Njord, Samudra (1° and 1/4°), GLONET, Neptune, ORCAst and the GNN-based model of Hirabayashi et al., as well as regional efforts such as SeaCast and MedFormer. Njord and Neptune already produce probabilistic ensembles. Others are trained on the same GLORYS data, and some are public models that could serve directly as baselines. As written, the related work gives a misleading picture of the field, and the claim that probabilistic ocean modeling is "underexplored" needs more context.
-
OceanBench is built on the same GLORYS reanalysis, with defined metrics, protocols and published scores, and already includes models this paper compares against or cites (WenHai, XiHe, LangYa). The authors neither use nor mention it, and OceanForecastBench is only cited in passing. Their numbers can't be checked against published scores, and there's no way to tell whether their re-evaluation of WenHai matches what is reported there. Choosing a custom protocol when a standard one exists on the same data, with some of the same models, needs a clear justification.
-
Samudra uses a convolutional UNet, is publicly available, and has shown stable and skillful long rollouts. That is hard to square with the convolutional results here: SimVP has ACC 0.088 at 90 days, and the plain convolutional ablation reaches RMSE 1.054. CirT also looks broken, with normalized RMSE around 2.8, ACC near zero and a member spatial-std error of 1.02. The retrained baselines seem poorly tuned, which inflates the gains.
-
NeuralOM alone already matches OceanFlow's ensemble mean (0.682 vs 0.681, within the std), yet it's the only strong baseline never given a perturbation ensemble. Perturbation averaging lowered DSLCast's RMSE by about 0.13, so a NeuralOM ensemble would very likely beat OceanFlow. NeuralOM is also missing from Figure 4, and DSLCast is called "the strongest perturbation-based baseline" in Section 3.4 only because NeuralOM was never perturbed. More broadly, OceanFlow tunes its perturbation amplitude and spread against CRPS, while the baselines get untuned Perlin noise and are badly under-dispersed (SSR sown to 0.22). Any CRPS-trained calibration would improve CRPS and calibration error, so this says little about the method. FuXi-ONS (discussed but not run), a CRPS-trained noise-injection model, or simple spread inflation on the baselines would make a fairer comparison. It's also unclear how the pretrained models (WenHai, NeuralOM, DSLCast) were evaluated in this setting: different resolutions, forcing..
-
The 20 initial conditions are 20 consecutive days starting January 1, 2020 (Appendix F), and the 2024 test uses 10. These aren't independent samples, they cover a single season, and the tiny standard deviations in the tables are misleading. The Nino-3.4 analysis suffers most: with only 10 initial conditions, whose dates are not given, nothing can be said about ENSO skill. The correlation metric is defined but never reported.
-
The paper talks about "93 ocean variables", but these are five physical variables, four of them on 23 levels, so 93 channels. Every main table averages over all of them in normalized space, which hides a lot. Ocean variability is very uneven: some regions, such as western boundary currents, the equatorial band or the Southern Ocean, are highly energetic, while others change very little over a few months. Depth levels respond to forcing on different timescales, and the variables themselves differ widely in how much they vary. A single averaged score can therefore improve because of how a model does on part of the channels or regions, while saying little about the rest. The calibration numbers may be an example of this: an SSR of 0.71 indicates clear under-dispersion, yet a CalibErr of 0.032 indicates near-perfect coverage, which suggests the coverage statistic is dominated by a subset of points. per-variable results cover only five surface fields and three subsurface levels, only against the Perlin baselines, with no regional breakdown.
-
Section 3.5 argues that the ensemble mean shouldn't be read as a physical state, then evaluates two of its three physical diagnostics on the ensemble mean. The diagnostics are thin anyway: a global-mean SST tendency, a correlation of correlations between SSH and currents, and an amplitude ratio. There are no budget checks for heat, salt or volume, no member-level balance checks and no stratification checks. The member spectra may also look closer to the truth partly because of the smoothing applied in the residual branch rather than better physics.
-
The gain in the two-way coupling experiment (Table 5) comes from better atmospheric forcing produced by another system, and DSLCast isn't run with the same forcing, so it says little about OceanFlow. Section 3.7 is called "efficiency analysis" but gives no runtime, even though inference needs a deterministic step plus two flow evaluations per member and per day. The "fewest trainable parameters" claim probably excludes the frozen backbone and leaves out the pretrained baselines?
-
Minor issues:
- RMSE goes down from 90 to 120 days in several rows, unexplained.
- The years used for the ACC climatology are not given.
- The non-fair empirical CRPS is used with only 10 training members, which favors under-dispersion.
- Ensemble statistics fed to the velocity use 10 members in training but 20 at evaluation.
- The "w/o State Response" ablation has a huge variance (ACC 0.072 +- 0.090), suggesting unstable training or a single seed.
- A more direct description of the method, with less specialized terminology, would help readability.
Some of the cited papers:
- Holmberg, Daniel, et al. "Accurate Mediterranean Sea forecasting via graph-based deep learning." Scientific Reports 15.1 (2025): 45051.
- Holmberg, Daniel, et al. "Njord: A Probabilistic Graph Neural Network for Ensemble Ocean Forecasting." arXiv preprint arXiv:2605.15470 (2026).
- Garcia, Pierre, et al. "Orcast: Operational high-resolution current forecasts." Artificial Intelligence for the Earth Systems 4.4 (2025): e250002.
- Epicoco, Italo, et al. "MedFormer: a data-driven model for forecasting the Mediterranean Sea." Earth Science Informatics 19.8 (2026): 129.
- El Aouni, Anass, et al. "GLONET: Mercator's end‐to‐end neural Global Ocean forecasting system." Journal of Geophysical Research: Machine Learning and Computation 2.3 (2025): e2025JH000686.
- Donno, Davide, et al. "Neptune: An AI model for Global Ocean Subseasonal Prediction." arXiv preprint arXiv:2609.08606 (2026).
- Li, Jinxin, et al. "OceanGraph: Adaptive Mesh-Grid Coupling for Multiscale Ocean State Prediction." IEEE Journal of Selected Topics in Applied Earth Observations and Remote Sensing (2026).
- Dheeshjith, Surya, et al. "Samudra: An AI global ocean emulator for climate." Geophysical Research Letters 52.10 (2025): e2024GL114318.
- Yuan, Yuan, et al. "Samudra 2: Scaling Ocean Emulators across Resolutions." arXiv preprint arXiv:2606.02610 (2026).
Questions for authors
Please refer to the weaknesses summarized above.
9 comments
Response to Reviewer VBBh — Part 2/9
Q2. Reading Appendix E.4, each member's training target is built from the same noise it starts from: mostly that noise scaled up or down, with only 5% coming from the actual error pattern. So the flow mainly learns how much to stretch or shrink the noise at each grid point. That's useful, but it isn't learning a distribution, and learned residual keeps the shape of the generic smooth noise. With only two flow steps, the continuous-time theory describes an idealized version, not the actual model. The ablation points the same way. Removing the learned flow moves CRPS from 0.371 to 0.379 and RMSE from 0.684 to 0.697, and most of the gain over FDO+Perlin comes from the calibration steps around it. The headline contribution adds a little on its own.
A2. The endpoint construction is deliberately structured, but the observation enters both its amplitude and its error-pattern component, and training also scores the generated ensemble directly against observations. Specifically, is the next-day GLORYS12 reanalysis field and is its error relative to the anchor. The 95% component uses a spread target derived from the channel-wise ocean RMS of this error; the remaining 5% introduces its spatial pattern. Thus, 5% is not the fraction of the target informed by reanalysis. The shared source noise defines a source-target coupling for flow matching, rather than an independent target sample. We agree that this is a constructed residual target, not an observed ensemble of alternative futures. Its purpose is to provide tractable transport supervision. The terminal ensemble is additionally optimized through empirical CRPS against , with gradients propagated through the integrated residual paths. Mean, member-error, and spread objectives provide complementary supervision. Consequently, the model is not trained only to reproduce a fixed rescaling of smooth noise. Even learned conditional amplitude changes alter a distribution, while the spatial velocity network and ensemble context allow departures from that restricted transformation. We will distinguish this modeling capacity from claims of recovering an unrestricted true conditional law.
Two numerical updates are used for both distributional training and inference. The implemented composition defines a finite-step conditional ensemble map; the mean-preservation and member-relabeling properties do not require it to equal the exact solution of a continuous ODE. The continuous formulation describes the transport construction, not a claim of negligible discretization error. The no-flow comparison is particularly informative for reliability. Using the original ablation table:
| Metric | w/o learned pathwise flow | OceanFlow |
|---|---|---|
| CRPS↓ | 0.379±0.002 | 0.371±0.002 |
| RankDev↓ | 0.109±0.001 | 0.088±0.000 |
| CalibErr↓ | 0.081±0.002 | 0.032±0.000 |
Removing transport raises the calibration error from 0.032 to 0.081. Equivalently, retaining it reduces CalibErr by approximately 60.5% and RankDev by 19.3%, alongside a 2.1% CRPS improvement. The modest incremental CRPS change therefore does not capture the full reliability difference. We do not regard mean control as incidental machinery outside the contribution: the core idea is to learn the residual distribution around an explicitly controlled center. The no-mean-control and no-flow variants test these complementary roles. Because these components are optimized together, their gains need not add independently. The results support the complete mean-anchored transport formulation, rather than attributing all improvement to flow integration alone.
Response to Reviewer VBBh — Part 3/9
Q3. Lemma 1 says that subtracting the ensemble mean and adding µ gives an ensemble with mean µ. This is true by construction, and the authors admit it says nothing about calibration or skill. The FDO is mostly standard components with new names: "factorized dynamics" is gated multi-branch mixing with FiLM-style conditioning, and the "state-conditioned response" is a learned residual connection. The deterministic FDO is also clearly weaker than NeuralOM (RMSE 0.825 vs 0.682 at 90 days), so it can hardly be called an accurate deterministic reference.
A3. We appreciate this distinction between a structural statement and a performance guarantee. Lemma 1 characterizes the generated conditional ensemble law; it does not prove calibration or forecast skill. Centering preserves the empirical mean by construction, and existence under the stated regularity assumptions is standard. The useful connection is that ensemble-conditioned transport, reference composition, and recentering together define one conditional map on the member set, without dependence on arbitrary member labels. We will state this modest role directly and streamline the proof accordingly. FDO's architectural contribution lies in organizing factorized evolution and state-conditioned response within one conditional transition operator. Learned projections form factor subspaces that undergo separate transformations, followed by cross-factor interactions with state-dependent selection. The output response then uses the original condition to adapt the decoded transition. This organization provides separate parameterizations for the deterministic reference and residual-flow velocity within the mean-anchored framework. The deterministic ablations evaluate this design by replacing the complete factorized block, removing the state response, or replacing it with a fixed state addition. Their results support the combination of structured factor evolution and a learned response, beyond a fixed input shortcut.
We also agree that the standalone FDO does not outperform NeuralOM at 90 days. “Accurate reference” should describe its role in the ensemble construction, not imply that it is the strongest deterministic model. NeuralOM is a substantial comparator: its published configuration uses 0.5° data, staged residual modeling, and multi-step fine-tuning, whereas our deterministic stage uses daily 1° data and 50 training epochs. These are differences in training protocol, not grounds for dismissing its stronger result. Crucially, our probabilistic result does not rely on claiming a superior deterministic backbone. With the same FDO reference, CRPS improves from 0.403 to 0.371, RankDev from 0.204 to 0.088, and CalibErr from 0.225 to 0.032 when learned OceanFlow refinement is introduced. The main 20-IC comparison also reports essentially tied 90-day RMSE for NeuralOM and OceanFlow, while OceanFlow provides an evaluated ensemble distribution. We will distinguish the structural lemma, the supporting architecture, and the empirical contribution of mean-anchored distribution learning more clearly.
Response to Reviewer VBBh — Part 1/9
Dear Reviewer VBBh,
Thank you for the detailed review and for identifying points that require clearer definitions and evaluation context. We respond below with clarifications, the existing controlled comparisons, and an additional independent retraining experiment.
A1. Thank you for examining the inference procedure closely. OceanFlow learns a conditional ensemble law at each ocean transition, not a fully flow-driven joint law over an entire multi-month trajectory. The deterministic reference advances the member conditions in physical time; the learned mean correction and residual transport determine the ensemble that is saved and evaluated at that transition. Their outputs are therefore not discarded from the forecast, although they are not fed back as the next day's member conditions. Here, pathwise refers to residual evolution in auxiliary flow time within a transition. Coherent refers to member updates being jointly conditioned on the evolving ensemble, with final recentering preserving their common anchor. Resetting the residual noise and context does not remove this within-transition interaction. It does mean that a fixed transported-member index should not be interpreted as a validated stochastic trajectory across days. We will make this scope explicit in the main method and inference description.
The long-lead condition comes from the evolving reference rollout, rather than repeatedly restarting from the initial state. OceanFlow learns to transform that reference ensemble using its current state and forcing. Applying this one-step-trained transformation at long leads is an empirical generalization question; we do not claim that the training objective guarantees removal of arbitrary accumulated drift. The 90-/120-day experiments evaluate precisely whether this transformation remains useful under those rollout conditions. The same-reference ablations provide evidence beyond the presence of Perlin spread or a floor. At 90 days over 10 ICs:
FDO+Perlin supplies the same deterministic backbone and perturbation reference without learned distributional refinement. The no-flow variant retains mean control and the reference-based output construction but removes learned residual transport. Its weaker calibration shows that the full result is not recovered by the reference and mean-control mechanisms alone. These comparisons establish the usefulness of learned ensemble refinement, although they do not constitute a variance-budget decomposition of every source of spread. Our contribution is thus reference-guided, mean-anchored ensemble transport with improved conditional reliability at the evaluated lead times. Temporally coherent stochastic trajectories and feedback of transported members are distinct extensions, rather than properties implied by the current coherent-law claim.