- Rating
- 3(+1)
- Confidence
- 4
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 2
Read review
Paper summary
The paper investigates how training and prediction formulations affect zero-shot out-of-distribution (OOD) trajectory prediction in pretrained neural PDE solvers. The authors develop a lightweight spatiotemporal ViT and compare four formulations: local-history autoregressive rollout, full-history autoregressive rollout, teacher forcing, and non-autoregressive full-trajectory prediction. The models are pretrained on six fluid dynamics datasets and evaluated without finetuning on five OOD tasks involving different initial-condition distributions within the same PDE families. The experiments show that the choice of formulation can substantially affect OOD performance, with teacher forcing generally outperforming full-history autoregressive training despite the training-inference mismatch. The authors further investigate the effect of teacher forcing using a smaller ViT and an FNO. Finally, they report that their 25M-parameter ViT achieves substantially lower errors than the much larger Poseidon-L on two OOD tasks, even when Poseidon uses direct prediction.
Critical strengths
Systematic comparison of training and prediction formulations. The paper compares four formulations within the same ViT architecture, including local-history autoregressive rollout, full-history autoregressive rollout, teacher forcing, and full-trajectory prediction. The comparison between autoregressive training and teacher forcing is further extended to a smaller ViT and an FNO, providing a useful empirical analysis of how training strategy and temporal conditioning affect zero-shot OOD performance across different architectures.
Critical weaknesses
-
Misleading baseline comparison in the central motivation. A central motivation of the paper is the surprisingly strong performance of a lightweight ViT compared with the much larger Poseidon-L model. However, the initial comparison in Table 1 evaluates Poseidon using autoregressive rollout, despite direct prediction being an established inference strategy for Poseidon. In fact, the original Poseidon paper (Herde et al., 2024, Appendix D.6.2) explicitly mentions comparing both strategies and selecting the better one for each task. It is therefore not surprising that using a less suitable inference strategy can substantially degrade Poseidon's performance. Indeed, the authors' own results show that direct prediction reduces Poseidon-L's error from 1.2350 (Table 1) to 0.2576 (Table 3) on NS-BB and from 1.4902 to 0.7152 on NS-VS. Although the paper later reports comparisons using direct prediction, the much larger performance gaps under autoregressive rollout receive considerable emphasis in motivating the work. This weakens the central narrative because part of the observed advantage comes from the baseline's inference strategy rather than the proposed pretraining design.
-
Limited scope of OOD generalization. The paper investigates how pretraining design affects zero-shot OOD performance, but the evaluation is limited to distribution shifts within the same governing equation families. Specifically, all five OOD tasks retain the compressible Euler or incompressible Navier–Stokes equations, as well as the same physical variables and computational domain as the pretraining datasets, and primarily differ in their initial-condition distributions and resulting flow patterns (Section 4; Appendix C). While this is a meaningful form of OOD generalization, it provides limited evidence of whether the observed benefits of different pretraining formulations extend to more substantial shifts in the underlying physics. Evaluating additional settings involving different governing equations, physical parameters, or geometries would help establish the generality of the conclusions.
Questions for authors
Questions:
-
Choice of inference strategy for Poseidon and framing of the paper. The original Poseidon paper (Herde et al., 2024, Appendix D.6.2) discusses both direct prediction and autoregressive rollout and selects the better strategy for each downstream task. Given that direct prediction substantially improves Poseidon-L's performance in your experiments, what motivated the decision to use autoregressive rollout in the initial comparison in Table 1? More importantly, since this comparison plays a central role in motivating the paper, I am concerned that it creates a misleading impression of the performance gap between the models.
I suggest reconsidering the central framing to place greater emphasis on the investigation of training and inference strategies, rather than primarily on outperforming Poseidon. For example, the paper could first highlight how the same pretrained Poseidon model performs substantially differently under autoregressive rollout and direct prediction. This observation could then motivate a broader investigation into how training and inference strategies affect zero-shot OOD performance. The authors could present their controlled comparisons within the proposed ViT architecture, followed by a comparison with Poseidon using appropriate inference strategies. This would better reflect the paper's main empirical contribution.
-
Selection of training duration. Section 5 uses 80 epochs for the controlled comparisons because longer training improves source-domain accuracy. However, the final comparison in Table 6 uses a teacher-forced ViT trained for 40 epochs. Could the authors clarify the rationale for this choice and report the corresponding results for the 80-epoch teacher-forced model? In particular, what criterion was used to select the training duration for the final comparison?
-
Interpretation of the final comparison with Poseidon. Table 6 shows that the proposed ViT substantially outperforms Poseidon-L on two of the five OOD tasks (NS-BB and NS-VS), while Poseidon-L performs better on CE-RKH and NS-SL. On CE-RM, both models have relative L1 errors exceeding 1, meaning their errors are larger than those of a trivial zero-field predictor under the reported metric. These mixed results seem to provide more limited support for the paper's emphasis on outperforming Poseidon than the overall narrative suggests. Could the authors explain why the proposed ViT substantially outperforms Poseidon-L on some OOD tasks but performs considerably worse on others, particularly within the Navier–Stokes family, and discuss what this suggests about the generalization capabilities and limitations of the proposed approach?
-
Discussion of related work. The related work section could benefit from discussing Walrus: A Cross-domain Foundation Model for Continuum Dynamics (McCabe et al., ICML 2026). Walrus is particularly relevant given its focus on cross-domain pretraining and stable long-horizon prediction of physical dynamics. How do the findings of the present paper relate to the training and prediction strategies studied in Walrus?
Comments and Suggestions:
-
Clarify the use of "rollout" and "trajectory prediction." The paper frequently uses "rollout prediction" to describe the overall task, including in the title and Section 3. However, one of the four formulations, full-trajectory prediction, generates all future states jointly rather than through autoregressive rollout. This makes it somewhat unclear whether "rollout" refers specifically to autoregressive prediction or more generally to predicting a future trajectory. I suggest distinguishing these terms more consistently, using "trajectory prediction" or "emulation" for the general task and "autoregressive rollout" when referring to recursive prediction.
-
Clarity of Figure 1(b). Figure 1(b) is difficult to follow without consulting the subsequent sections and Appendix B, despite being the main figure introducing the four formulations. In particular, the relationship between the evolution blocks , their embedded representations, and the physical states is not immediately clear. The figure also mixes training and inference formulations without explicitly distinguishing them. For example, teacher forcing differs from full-history AR in whether ground-truth or predicted histories are used during training, but both use the same autoregressive inference procedure. I suggest replacing the equations in Figure 1(b) with schematic diagrams illustrating the inputs, predictions, and feedback connections for each formulation, using different colors or line styles to distinguish ground-truth and predicted states. The differences between training and inference should also be made explicit. The equations could instead be presented in the main text, following Equations 1-4. This would make the four formulations and the focus of the paper easier to understand.
-
Clarity and organization of experimental results. The organization of the results tables could be improved to make the purpose of each comparison clearer. Some tables combine multiple comparison factors, while closely related results are spread across different tables. For example, Table 2 mixes differences in architecture, training duration, and inference strategy, while assessing the effect of Poseidon's inference strategy requires comparing Tables 1 and 3. Similarly, the final comparisons involving ViT and FNO are separated between Table 6 and Appendix Table 14, and the different comparison settings in Tables 4 and 5 could be made more explicit. I suggest reorganizing or consolidating some of the tables around clearly defined experimental questions, making it clear which factors vary and which are held fixed. This would make the results easier to follow and interpret.
-
Inconsistency in source-domain results. The relative L1 and L2 errors for the 80-epoch ViT under local-history AR on CE-Gauss appear to be swapped between Tables 2 and 17 and Tables 10 and 11. Specifically, Tables 2 and 17 report 0.2289 (L1) and 0.1878 (L2), whereas Tables 10 and 11 report 0.1878 (L1) and 0.2289 (L2). Could the authors verify which values are correct and ensure consistency across the tables?
4 comments
Response to Reviewer UjBu
(Part 2/2)
Interpretation of the comparison with Poseidon (Q3). First of all, you are right that all models have errors above 1 on CE-RM. CE-RM is no longer marked in the revised tables. Secondly, the errors on the CE systems tend to be higher than those on the NS systems. In our early exploration, we also tried training separate foundation models for CE and NS, and the CE-only model did not converge well, which suggests that the CE tasks may be more challenging. On the three NS systems, the OOD performance is generally better.
In the revision, we also evaluated Poseidon-B and Poseidon-T under direct prediction, which we had not done in the original submission. To be honest, we had not noticed before how strong Poseidon-B is under direct prediction: it achieves a particularly low error on NS-BB, lower than our ViT, and with 158M parameters, it achieves lower error than the 629M Poseidon-L on four of the five OOD systems, which likely suggests that zero-shot OOD performance does not simply improve with model size. Meanwhile, our ViT achieves the lowest NS-VS error among all models (Table 1).
For NS-SL, we do not yet have a fully satisfactory explanation of why our ViT performs worse than Poseidon-L. Figure 9 suggests that our ViT does not capture well the small vortices emerging in the later stage of the shear-layer evolution, whereas Poseidon-L partially captures them. One possibility is that Poseidon's direct prediction, which maps the initial condition to each future time in a single step, helps preserve such small-scale structures. However, Figure 3 shows that the error gap between our ViT and Poseidon-L on NS-SL is already present in the first prediction steps, so error accumulation during AR rollout alone does not seem to explain it, and the fine-scale reconstruction of our patch-based ViT may also play a role.
Comments and suggestions.
- Terminology. We changed the text to use “trajectory prediction” for the general task and “autoregressive rollout” only for recursive prediction. As noted in the general response, the title is unchanged for now, as we are confirming whether it can be changed during the discussion period.
- Figure 1(b). We redrew Figure 1(b) to show the inputs, predictions, and feedback connections of each formulation, with separate training and inference columns and distinct ground-truth and predicted states. The equations are now in the main text (Eq. 5).
- Organization of results. Table 1 merges the original Tables 1, 3, and 6, and Table 3 consolidates the formulation comparisons across model sizes and training lengths together with FNO (original Tables 3, 4, 5, and 14). The captions state which factors vary.
- CE-Gauss values. Thank you for catching this. The correct values are 0.1878 (relative ) and 0.2289 (relative ). We corrected the tables and verified all reported values against our evaluation outputs.
Additional experiments and analyses. Beyond your suggestions, we also strengthened the empirical study:
- We added a 92M ViT, so the formulation comparisons now cover three model sizes (10M, 25M, and 92M).
- We report all formulations and model sizes, including FNO, at both 40 and 80 epochs, under both relative and (Tables 3 and 11) and on the source domain (Tables 7 and 8).
- We added a per-step error analysis (Figure 3 and "Where Do the Gains of Teacher Forcing Arise?" in Section 5), with the per-step errors of all formulations on all five OOD systems in Figure 8 (Appendix G).
We hope these revisions address your concerns, and we thank you again for your constructive suggestions.
I thank the authors for their detailed response and revisions. I believe they have largely addressed my concerns, particularly regarding the framing of the paper, the comparison with Poseidon, and the presentation results. I think the revisions have substantially improved the paper, and I am happy to upgrade my rating to weak accept.
We thank you very much for upgrading the rating and for being positive about our study! Thanks again for the constructive suggestions and comments.
Response to Reviewer UjBu
(Part 1/2)
We thank you for your detailed and constructive review! Your suggestions helped us substantially improve the paper, and we have revised it following most of them. As you suggested, the paper now starts from the observation that the same pretrained Poseidon checkpoint performs substantially differently under AR rollout and direct prediction, uses it to motivate the controlled comparisons of training and inference formulations, and compares with Poseidon under both inference modes. We have also revised the terminology, Figure 1(b), the organization of the tables, and the CE-Gauss values, as detailed at the end of this response.
Poseidon's inference strategies and Walrus (W1, Q1, Q4). We would like to add one clarification on Appendix D.6.2 of the Poseidon paper. In addition to selecting the better strategy for each task, it shows that after finetuning, neither AR rollout nor direct prediction is consistently better across downstream tasks. We also checked the released Poseidon codebase and found that finetuning is likewise performed with all2all training. This is why we initially evaluated Poseidon with AR rollout in Table 1, which also matches the inference procedure of our ViT. In contrast, our evaluation of the pretrained models themselves, without finetuning, shows a clear and consistent gap between the two inference mode. This difference from the finetuned models is the core motivation of our paper: the training and inference formulations can matter for the zero-shot OOD generalization of pretrained models, even when they make little difference after finetuning. This is also the main difference from Walrus, which we have added to the related work. Like Poseidon, Walrus evaluates OOD generalization after finetuning on the downstream tasks. Strictly speaking, after finetuning, the downstream task is no longer unseen by the model, whereas we evaluate the pretrained models on unseen tasks zero-shot. In addition, Walrus is trained with one-step prediction from ground-truth histories and uses patch jittering to improve rollout stability, but it does not directly compare teacher-forced and rollout-based training.
Scope of the OOD evaluation (W2). Our OOD setting follows from our research question, which focuses on the zero-shot generalization of the pretrained models themselves. The five OOD tasks keep the governing equation families, physical fields, and computational domain of pretraining, so all models can be evaluated without modification. Shifts to other governing equations, physical fields, or geometries would require modifying the input and output embeddings and finetuning the models, which would no longer evaluate the pretrained models themselves. We have clarified this in Section 4 and Appendix C. Extending the study to such settings is an interesting direction for future work.
Training duration (Q2). There was no specific criterion: in the original submission, we used 80 epochs for the controlled comparisons simply because the source-domain accuracy was still improving at that point. The revised paper reports all formulations at both 40 and 80 epochs (Table 3), and the conclusions are consistent across the two training lengths. For the comparison with Poseidon in Table 1, we use 40 epochs to match the released Poseidon-B and Poseidon-T checkpoints.