- Rating
- 2
- Confidence
- 3
- Informativeness
- 2
- Presentation
- 3
- Soundness
- 2
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Paper summary
This paper proposes STREAM, a multivariate forecasting model that separates channel dependency and temporal dependency. Within each temporal patch, the model constructs a sparse top-k channel graph that is re-estimated dynamically, while temporal information is propagated across patches using a selective state-space recurrence applied independently to each channel. The paper also introduces a robustness-oriented evaluation protocol that varies the channel set, lookback length, and autoregressive rollout horizon. Experiments are conducted on nine spatio-temporal datasets with physical graphs, with additional rollout experiments on standard long-term forecasting benchmarks. The main claim is that selective local channel mixing is more robust to added, noisy, or failing channels, while the state-space recurrence better exploits longer temporal contexts.
Critical strengths
The strongest aspect of the paper is the evaluation framework itself. The authors do not rely only on a single fixed benchmark setting, but test channel expansion, noisy channels, sensor failures, longer lookbacks, and autoregressive rollout. This gives a more operational view of model robustness than standard leaderboard comparisons. The paper also includes several useful structural comparisons with TimeFilter, MambaTS, and other channel-mixing families, and the efficiency analysis shows a practical benefit of caching recurrent states during rollout.
Critical weaknesses
The main weakness is that the evidence for STREAM’s architectural choices is less clean than the paper suggests. First, the channel robustness protocol is not architecture-neutral: graph-based contiguous expansion and i.i.d. noisy non-core channels create conditions where a local top-k graph has an obvious structural advantage. Second, the lookback results are mixed rather than consistently supporting the proposed temporal mechanism; STREAM does not monotonically improve on several datasets, and in the aggregate lookback table TimeFilter is often comparable or better on traffic benchmarks. Third, the autoregressive rollout comparison is difficult to interpret because direct forecasters are evaluated under block-wise self-feeding even though they were not trained for autoregressive use, while STREAM has an architecture explicitly designed for cached patch-wise rollout. The paper acknowledges this asymmetry, but it still uses the rollout results as evidence of a broader robustness advantage.
Questions for authors
My main question is how much of STREAM’s advantage remains under stress tests that are less aligned with its inductive bias. For example, what happens if the added channels are spatially distant but predictive, or if noisy channels are correlated or adversarial rather than i.i.d.? I would also like clarification on the rollout claim: since STREAM is explicitly designed for recurrent patch-wise decoding while many baselines are not trained to consume their own outputs, should the H=720 experiment be interpreted as a model-quality comparison or primarily as an architectural capability comparison?
5 comments
Response to Reviewer c5BV
A note on the comment of 13 November. The Official Comment posted on 13 Nov 2026 discusses OU-WSP, a Gaussian flow-matching baseline, MIMIC-IV forecasting tasks and TSFlow. None of these appear in our submission, and the comment replies to a rebuttal that we had not yet posted. We believe it was intended for another submission and kindly ask you to check. Our response to your review of this submission follows.
Thank you for the thoughtful review. Your three weaknesses each question whether our evidence is as clean as the paper suggested, and in each case we have narrowed the claim or added evidence.
Response to Reviewer c5BV
[W1/Q1] "The channel robustness protocol is not architecture-neutral ... what happens if the added channels are spatially distant but predictive, or if noisy channels are correlated or adversarial rather than i.i.d.?"
We agree with the point on noise: i.i.d. noise is uncorrelated with every real channel and is the easiest case. On real data, moreover, the usefulness of a channel is unknown, so a change in the core error cannot be attributed to the model or to the channel. We therefore built synthetic tasks whose ground truth is known in closed form and tested both of your questions directly (Appendix H).
Setup. Each task has the target and two extra channels and ; gives alone and all three channels, scored on the core (, three seeds). The processes are linear-Gaussian, so least squares on the same 96-step window is Bayes-optimal. We use it as an oracle and report the normalized gain, the fraction of the achievable improvement from the extra channels that a model obtains. No model is tuned on these tasks.
Distant but predictive channels (lead-). leads the target by steps. As grows from 12 to 48 and 96, its same-time correlation with the target falls from 0.55 to 0.10, while the information it carries about the target's future grows. STREAM obtains 92%, 71% and 51% of the achievable gain, TimeFilter, iTransformer and MambaTS at most 33%, and the channel-independent models at most 20%. On lead96, STREAM's reliance on the useful (correlation 0.10) is 3.7 times its reliance on the control , whereas TimeFilter and iTransformer weight the two almost equally (1.2 and 1.6 times). STREAM thus uses channels according to their information, not their similarity.
Correlated noise (corrnoise). and are strongly correlated with each other but carry no information about the target. STREAM degrades least (+1.2%), against +6.4% for TimeFilter and +11.4% for iTransformer; even the channel-independent models, which never read the extra channels, degrade because their weights are shared across channels (+2.5% PatchTST, +5.4% DLinear). When the extra channels are noisy copies of the target (redundant), iTransformer degrades by 9.3%, while all other models, STREAM included, stay within ±1.5% on average.
Scope. Each task has three channels, fewer than , so top- selects every channel; the selectivity here comes from the attention weights within the neighbourhood, not from top- sparsification. We did not run adversarially constructed noise in this revision.
Distant channels on real data. STREAM uses no adjacency: the top- neighbours of a channel are chosen by learned query–key scores among all channels present at that time, so a distant channel competes for the slots on the same terms as an adjacent one. Figure 8 (Appendix E) follows channel 0 of PEMS08 through the four models trained at fractions 1/8, 1/4, 1/2 and full on the same test window. With all channels it draws neighbours not only from the core but also from the 1/4 and 1/2 regions and from the full region (+85), the farthest in breadth-first order, and its MSE falls from 0.912 at 1/8 to 0.358 at 1/4 and 0.289 at 1/2 (0.301 with all channels).
The protocol does not mechanically favour STREAM. Several of its own results go against STREAM, and the revision states them plainly:
- On ERA5-sp, STREAM's core MSE rises as channels are added (0.506 to 0.697) and it is behind every baseline with all channels. On PEMS04 it also rises (0.135 to 0.162).
- Under noisy additions STREAM is not uniformly unaffected. With all channels its additional error under B over A is within 2% or negative on seven of nine datasets, but it is large on ERA5-t2m and d2m at (+68%, +83%) and on PEMS03 with all channels (+44%) (see our response to Reviewer Eoiy, Part 2).
- Under failure with few channels STREAM's absolute error is high ( in Table 12), as the paper notes; Figure 10 shows that this comes from losing nearby neighbours when only the core is available.
How much comes from sparse local mixing. The graph ablations (Table 5) show that removing the graph roughly doubles the error on PEMS04 and PEMS07 (+103.9%, +85.5%), and that replacing top- by dense attention over all channels is worse on Solar (+7.7%), PEMS04 (+10.9%) and ERA5-t2m (+1.5%) and better on PEMS07 (−5.0%). These are measured on clean data, so they do not depend on the noise model.
I appreciate the authors' additional experiments, particularly the completed context-only evaluation and the matched post-processing comparison. These additions address my original methodological concerns, but the revised results also raise questions about the actual contribution of the proposed framework. Under the corrected protocol, the substantial downstream improvements highlighted in the original submission are reduced to marginal differences against Gaussian FM, while the simpler OU-only variant actually outperforms OU-WSP on both MIMIC-IV forecasting tasks. This is particularly concerning because the context-adaptive Fourier residual is presented as a central methodological contribution, yet the new results do not establish that it consistently improves downstream utility beyond the structured OU anchor. The fidelity experiments reveal a similar distinction. OU-WSP achieves better spectral alignment, but this does not translate into consistently better distributional fidelity or temporal dependence, with the OU-only variant performing better on W1 across both datasets and Gaussian FM retaining substantially lower ACF discrepancies. These results suggest that the Fourier residual primarily improves a specific spectral objective rather than providing the broader improvements in conditional time-series generation implied by the paper. While the adapted TSFlow comparison is useful, outperforming that baseline does not resolve the more fundamental question of whether the additional complexity of OU-WSP is justified over its own simpler OU-only formulation. The rebuttal has improved the reliability of the evaluation, but the corrected evidence makes the central methodological contribution less convincing than originally presented. I therefore maintain my rating of 2 (Weak Rejection).