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Under review as a conference paper at ICLR 2027

STREAM: Dynamic Channel Graphs with Autoregressive State Propagation for Multivariate Forecasting

Abstract

Real-world multivariate series involve multiple dependencies: each chan- nel has its own dynamics, channels interact through spatial or physical structure, and these interactions can change across regimes. Yet standard benchmarks fix the channel set and lookback, allowing models that ignore inter-channel dependencies to remain competitive and leaving their value insufficiently tested. In deployment, sensors may fail, become noisy, or be added, while longer histories accumulate. We therefore evaluate dependency modeling through a controlled robustness protocol that expands the channel set along a sensor graph while scoring a fixed core set, and independently extends the lookback. We then present STREAM, which models channel dependency within each temporal patch using a sparse graph re-estimated from the patch, and models temporal dependency with a linear-time selec- tive state-space recurrence. Its bounded neighborhoods limit the effect of added channels, while the recurrence supports longer contexts with linear cost and patch-by-patch forecasting beyond the trained horizon.

Primary area:
learning on time series and dynamical systems
Keywords:
Time Series Forecasting

Reviews

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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_c5BVOpenReview ↗
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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

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).

AuthorsOpenReview ↗

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.

AuthorsOpenReview ↗

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. N(0,1)\mathcal{N}(0, 1) 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 c0c_0 and two extra channels c1c_1 and c2c_2; f=1/8f = 1/8 gives c0c_0 alone and f=1f = 1 all three channels, scored on the core (L=H=96L = H = 96, 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-τ\tau). c1c_1 leads the target by τ\tau steps. As τ\tau 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 c1c_1 (correlation 0.10) is 3.7 times its reliance on the control c2c_2, 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). c1c_1 and c2c_2 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 k=8k = 8, so top-kk selects every channel; the selectivity here comes from the attention weights within the neighbourhood, not from top-kk sparsification. We did not run adversarially constructed noise in this revision.

Distant channels on real data. STREAM uses no adjacency: the top-kk 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 kk 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 f=1/4f = 1/4 (+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 (f=1/8f = 1/8 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-kk 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.

Reviewer_EoiyOpenReview ↗
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Paper summary

The paper investigates when inter-channel dependencies help multivariate time-series forecasting, particularly when the available channel set changes, sensors become noisy or fail, and the lookback window increases.

The proposed model, STREAM, constructs a top-k channel graph separately within each temporal patch and models temporal dependencies using a per-channel Mamba recurrence with shared parameters. A global graph stream summarizes patch representations and broadcasts its recurrent output to all channels. Training combines a Huber forecasting objective with an auxiliary next-block prediction (NBP) objective applied at intermediate positions. The model also supports autoregressive forecasting with cached states.

The evaluation includes nine spatio-temporal datasets for channel-set and lookback experiments, plus five conventional forecasting datasets for horizon extension. The channel protocol grows spatially contiguous subsets while evaluating a fixed core, distinguishing informative additions, noisy additions, and test-time failures.

Critical strengths

S1. Evaluating channel expansion on a fixed core is a useful experimental idea.

Section 3.1 keeps the prediction target set fixed as additional channels become available. This avoids confounding changes in prediction accuracy with changes in the intrinsic difficulty of the scored channels. Breadth-first expansion over a physical graph also provides a more spatially meaningful setting than independently sampling arbitrary channel subsets.

S2. The architectural decomposition has a practical motivation.

Separating spatial interaction within a patch from temporal recurrence across patches provides an understandable approach to spatio-temporal modeling. Cached recurrent states are also suitable for incremental generation. Appendix G includes a comparison between caching and re-encoding on the same network, which provides direct evidence for the computational value of caching.

S3. Several reported results are competitive.

Under scenario A with all input channels, STREAM achieves an MSE of 0.123 on PEMS07, compared with 0.161 for TimeFilter, and 0.671 on METR-LA, compared with 0.694 for TimeFilter (Table 1). Table 3 reports an average rank of 3.25 across lookbacks for STREAM, compared with 3.39 for TimeFilter. These are encouraging results, although their interpretation remains subject to the evaluation-consistency concerns below.

S4. The detailed appendix makes the empirical claims inspectable.

Tables 10–13 report errors for individual channel fractions and lookback lengths, rather than only aggregate rankings. Figure 6 documents changes in selected neighborhoods across patches. The conclusion also acknowledges relevant limitations, including separate retraining for each channel configuration, sensitivity to failures with few channels, and rollout performance below the best direct forecasters.

Critical weaknesses

W1. Nominally identical experimental conditions produce substantially different results without an explanation.

This is my most significant concern.

Section 3.1 states that scenario B corrupts only channels outside the fixed core. At f=1/8f=1/8, the input contains only the core, so there are no added channels to corrupt. Scenarios A and B should therefore represent the same experimental condition at this point, assuming the stated training configuration, preprocessing, and seed conventions are held fixed.

Nevertheless, Tables 10 and 11 report substantial differences:

Dataset / modelScenario A, f=1/8f=1/8Scenario B, f=1/8f=1/8
ERA5-t2m / TimeFilter0.1610.311
ERA5-t2m / MambaTS0.1710.318
PEMS03 / PatchTST0.2871.484
PEMS03 / iTransformer0.5451.060

The defined corruption intervention cannot explain these differences because it is absent at this fraction. This matters directly for Equation (1), which normalizes each curve by its error at f=1/8f=1/8.

A second discrepancy concerns the shared anchor. Section 3.2 explicitly states that the lookback-axis point at L=96L=96 is the full-channel point of Axis 1. However, the corresponding results differ:

Dataset / modelTable 10: scenario A, full channelsTable 13: L=96L=96
PEMS04 / STREAM0.1620.698
PEMS08 / STREAM0.3081.032
Air Quality / DLinear1.1373.685

One possible explanation is that the lookback experiment scores all channels whereas the channel experiment scores only the core. If so, this distinction needs to be stated explicitly, and the claims of a shared anchor and fixed prediction target need to be revised. The current text does not establish whether the differences arise from evaluation masks, training configurations, preprocessing, or result aggregation.

These discrepancies do not establish misconduct or identify a particular implementation error. They do, however, prevent the reader from verifying that the central comparisons follow the stated protocol.

W2. The scaling slope measures the benefit of expansion, but does not by itself establish failure robustness.

Table 2 ranks methods by the slope of log MSE against successive doublings of the monitored area. This is a valid measure of spatial-scaling behavior, but a steep negative slope can arise because a model performs extremely poorly at the smallest fraction and then recovers.

For example, Table 12 reports the following STREAM errors:

  • METR-LA: 7.216 → 0.731 → 0.733 → 0.717.
  • PEMS07: 3.455 → 0.213 → 0.174 → 0.571.

For METR-LA, most of the improvement occurs in the first expansion. For PEMS07, the error at the final expansion increases by approximately 3.28 times relative to the preceding fraction, despite a favorable overall slope. At full size, its MSE of 0.571 is also considerably higher than the 0.210 reported for TimesNet.

The paper acknowledges poor performance with few channels, which is useful. Nevertheless, the strongest conclusions need to distinguish expansion benefit, absolute prediction accuracy, and the additional error caused by failure. The best average slope rank does not establish the best absolute accuracy under failure or consistent compensation as the network grows.

The statements that STREAM does not degrade with noisy additions are also too broad. In Table 11, STREAM increases from 0.178 to 0.257 on PEMS03 and from 0.506 to 0.669 on ERA5-sp as the channel fraction grows. A negative slope averaged across datasets does not establish robustness on each dataset or at each expansion step.

A more informative analysis would compare scenarios B and A at the same fraction. For scenario C, clean and failed inputs should be scored on the same surviving-core mask, so the reported degradation isolates the failure intervention.

W3. The claim that channels interact only through the top-k graph is inconsistent with the global graph stream.

The contribution statement and Figure 3 describe the sparse graph as the only route for cross-channel mixing. Section 4.2, however, also defines a global summary and broadcasts its recurrent representation to every channel:

\qquad g_p = \operatorname{LN}\!\left(g_p^{\mathrm{in}}+\operatorname{SSM}_g(g^{\mathrm{in}})_p\right), \qquad h_{p,c}\leftarrow h_{p,c}+g_p.$$ This creates an additional communication path from all channels to each channel. A noisy channel can therefore influence a core prediction through the graph stream even when it is not selected into that core channel's top-k neighborhood. Moreover, fixing $k$ bounds the number of selected neighbors; it does not guarantee that irrelevant additions cannot displace useful neighbors. The statement in Section 4.1 that uninformative channels are out-competed for the available slots requires empirical support. The architecture may still work well, but the present results cannot be directly attributed to isolation by bounded neighborhoods. Comparisons with and without the graph stream, with a fixed versus a per-patch graph, and with different neighborhood sizes would directly test this explanation. ### W4. Channel expansion changes the training supervision as well as the available context, and the ablations do not isolate the central mechanism. Section 3.1 describes added channels as providing context, but Equation (6) trains on targets from all $C$ channels. Scenario B also modifies both inputs and targets of corrupted channels. Increasing the channel fraction therefore changes the auxiliary prediction tasks and the relative weight of core-channel supervision in the total objective. This distinction also affects the interpretation of channel-independent baselines. A model with no cross-channel path at inference can still change its core predictions after retraining on additional channels if its parameters are shared across channels. Consequently, differences between separately trained models cannot be attributed solely to the presence or absence of an inference-time neighbor-to-target path. Table 5 primarily ablates the temporal backbone, Huber loss, and NBP objective. It does not directly establish the contribution of the dynamic sparse graph that motivates the paper. Figure 6 shows that neighborhoods change, but does not establish that those changes improve forecasting or track useful regime changes. A limited set of matched comparisons on representative datasets would be sufficient: a channel-independent version with the same backbone and losses, a fixed graph versus per-patch reconstruction, and a core-only prediction-loss control. These would validate existing claims without requiring a substantially different study. ### W5. The causal interpretation of NBP needs qualification because normalization uses the entire lookback. Appendix B explicitly states that intermediate NBP positions use instance-normalization statistics computed over the entire lookback. Thus, for an intermediate position $p<P$, its representation depends on observations later in that lookback: $$z_p = F\!\left( X_{\leq pP_s}; \mu(X_{1:L}), \sigma(X_{1:L}) \right).$$ Some of those later observations belong to the prediction target of the intermediate NBP task. The recurrence may be causal with respect to the normalized tokens, but the complete training computation is not a function of the raw prefix alone. This does not imply that the final forecast has access to future test targets: the full lookback is legitimately observed for the main prediction. It does, however, qualify the analogy with strictly causal next-token prediction and the description of every intermediate state as a summary of its raw prefix. The normalization convention during cached rollout also needs to be specified. If statistics are updated with the sliding window, how are previously cached states kept consistent with the new coordinate system? If they remain fixed, how does this differ from the re-encoding baseline? A comparison using prefix-only normalization or fixed training-set statistics would clarify whether the NBP and rollout gains depend on this choice. ### W6. The efficiency analysis does not fully account for graph construction and readout costs. Table 9 correctly reports $O(PC^2d)$ computation for channel similarity scoring, but lists graph memory as $O(PCk)$. Retaining only top-k edges does not establish the same bound for peak memory if the full similarity matrix is materialized before selection. A tiled implementation could avoid that intermediate allocation, but the implementation strategy and memory measurements are needed to support the claim. Equation (4) also reads the most recent $\kappa$ states, with $\kappa=\operatorname{round}(P/2)$. The cache therefore includes $O(C\kappa D)$ historical states in addition to the recurrent state, and the readout cost depends on $\kappa$. This does not invalidate constant cost per rollout step for a fixed trained configuration, but the description of each new patch as requiring only a graph step and a state update omits part of the computation. Appendix G reports relative speedups and growth factors. Absolute latency, the precise GPU model, and peak memory across channel counts would make the practical efficiency claim easier to assess. ### W7. Rollout performance depends strongly on the decoding mode, and the comparison settings need clarification. Table 4 shows substantial benefits from fine-grained decoding on ECL and Traffic, but the effect is not consistent. On Solar, STREAM's MSE increases from 0.505 with block-wise decoding to 2.532 with fine-grained decoding. On Weather, it increases from 0.356 to 0.406. The claim of outperforming AutoTimes on four of five datasets needs an explicit comparison convention. It holds when taking each model's best MSE across the two modes. Under block-wise decoding alone, STREAM is better only on Weather. If the decoding mode is selected separately for each dataset, the paper should explain whether that choice is made on validation data. There is also a relevant implementation question. The AutoTimes paper uses a segment length of 96 in its multivariate experiments, whereas STREAM uses patch lengths of 4 or 16 on the general benchmarks (Table 7). The manuscript should specify AutoTimes' training segment length, the actual fine-grained decoding increment, any training adjustments, and timestamp handling. Without these details, it is difficult to assess what using the "same" decoding modes entails.
Questions for authors
  1. At f=1/8f=1/8, scenarios A and B contain no different corruption intervention. Why do several three-seed averages differ substantially? Are preprocessing, core selection, and hyperparameters identical?
  2. Do the full-channel entries in Table 10 and the L=96L=96 entries in Table 13 use the same scoring mask? If not, how should the shared-anchor statement in Section 3.2 be interpreted?
  3. At a fixed channel fraction and with matched scoring masks, how does STREAM's additional error under noise or failure compare with TimeFilter and channel-independent baselines?
  4. Do the channel-expansion and failure results persist without the global graph stream? What is the performance difference between a fixed graph and per-patch reconstruction?
  5. Do the NBP and rollout benefits persist with prefix-only normalization? What normalization rule is used during cached generation?
  6. Does top-k graph construction avoid materializing the full similarity matrix? How do peak memory and per-step latency scale with CC and LL when all caches and the readout are included?
  7. What segment length, decoding increment, and timestamp treatment are used for AutoTimes? Is decoding-mode selection based on validation performance?
11 comments
AuthorsOpenReview ↗

Response to Reviewer Eoiy

Thank you for the exceptionally careful review. Checking our tables against the stated protocol exposed real errors, and your points on what the slopes do and do not establish have changed how we state our results. We respond to every weakness and question; where a weakness and a question raise the same issue we answer them together.

[W1/Q1] "At f = 1/8, scenarios A and B contain no different corruption intervention. Why do several three-seed averages differ substantially?"

You are right. At f=1/8f = 1/8 the input is the core alone, scenario B has nothing to corrupt, and the two scenarios are the same condition, so differences of the size you list cannot come from the intervention. They were reporting errors in the submitted tables (G1(a) of the general response). We corrected the values: Tables 10 and 11 are revised, and all slopes in Table 1 are recomputed from the corrected values.

In the revised tables, STREAM's entries at f=1/8f = 1/8 are identical in the two scenarios. Small differences remain for some baselines, at most about 3% (for example TimeFilter on ERA5-t2m, 0.166 against 0.171), because GPU training is not fully deterministic even at a fixed seed (the selective-scan kernel of Mamba, cuDNN algorithm selection with cudnn.benchmark = True, and non-deterministic floating-point accumulation). We treat differences of this size as run-to-run variation.

[W1/Q2] "Do the full-channel entries in Table 10 and the L = 96 entries in Table 13 use the same scoring mask? If not, how should the shared-anchor statement in Section 3.2 be interpreted?"

They do not, and you are right that the shared-anchor statement was therefore incorrect. Table 10 is scored on the core V1/8V_{1/8} and Table 13 on all channels. In checking this we also found that Table 13 mixed the two scoring masks. Every entry of Table 13 is now obtained on all channels and Table 3 is recomputed; Section 3.2 no longer describes a shared anchor, and every table states its scoring mask (G1(b)).

We understand that these errors prevented you from verifying the central comparisons, and we thank you for identifying them precisely.

[W2] "The scaling slope measures the benefit of expansion, but does not by itself establish failure robustness."

We agree in part. The slope answers one question: how the error changes as the monitored area grows. As you show for METR-LA and PEMS07, a favourable slope can come from a very poor start at the smallest fraction, so the slope alone establishes neither absolute accuracy under failure nor robustness on each dataset or at each expansion step. The revision therefore distinguishes three quantities, as you suggest: the benefit of expansion (the slope), the absolute error at each fraction, and the additional error caused by the intervention at a matched fraction and scoring mask. Section 5.2 is revised accordingly.

AuthorsOpenReview ↗

Response to Reviewer Eoiy

[W2/Q3] Noise: scenario B against scenario A at the same fraction.

A and B are scored on the same core V1/8V_{1/8}, which B never alters, so the scoring masks match. The table below reports the additional error of B over A at each fraction for STREAM, TimeFilter and the channel-independent baselines (%, computed from Tables 10 and 11; f=1/4f = 1/4 / 1/21/2 / full).

DatasetSTREAMTimeFilterDLinearPatchTSTTiDE
ERA5-t2m+68 / +57 / +1−8 / +1 / +2+2 / +4 / +60 / +1 / +1−1 / 0 / +1
ERA5-d2m+83 / +33 / +1+2 / −2 / −1+4 / +5 / +30 / 0 / 00 / 0 / 0
ERA5-sp+12 / +4 / −4+1 / 0 / +1+2 / +3 / +4+1 / +1 / +10 / 0 / 0
Air Quality0 / +1 / +8−1 / −2 / −1+6 / +6 / +12−16 / −21 / −190 / 0 / −1
PEMS03+1 / +4 / +44+6 / +4 / −50 / 0 / 0+20 / +14 / +220 / +1 / +1
PEMS040 / −8 / −12−2 / −6 / −6+1 / +2 / +3+1 / −1 / −30 / 0 / 0
PEMS07+22 / −5 / +1−2 / −6 / −9+1 / +1 / +20 / +1 / +10 / +1 / +1
PEMS08+7 / −11 / −11−11 / +1 / −2+1 / +1 / +2+10 / +8 / +60 / 0 / 0
METR-LA0 / 0 / 0+1 / 0 / +10 / 0 / 00 / +4 / −10 / 0 / 0

Three things can be read from the table. First, with all channels the additional error of STREAM is within 2% or negative on seven of the nine datasets even with noise channels mixed in; the exceptions are Air Quality (+8%) and PEMS03 (+44%). Second, in absolute error STREAM has the lowest MSE under scenario B with all channels on five of the nine datasets (ERA5-t2m, ERA5-d2m, PEMS04, PEMS07, METR-LA), more than any baseline (TimeFilter three, PatchTST one; Table 11). On these five datasets STREAM with noise channels is 3–23% better than the best baseline under clean scenario A. Third, the penalty is large at intermediate fractions: +68% and +83% on ERA5-t2m and ERA5-d2m and +22% on PEMS07 at f=1/4f = 1/4, and still +57% and +33% on ERA5-t2m and ERA5-d2m at f=1/2f = 1/2.

The additional error B − A is also smaller the less a model gains from added channels, as for channel-independent (CI) models. TiDE, for example, barely changes with the fraction under scenario A, and its B − A is within ±1% in every cell. This measure should therefore be read together with the absolute error.

Nevertheless, we agree that "does not degrade" was too broad as written: as you point out, STREAM's error under B rises from 0.178 to 0.257 on PEMS03 and from 0.506 to 0.669 on ERA5-sp as the fraction grows. Section 5.2 and the conclusion no longer make a general robustness claim for noisy channels.

At the level of the graph, Figure 9 (Appendix E) shows that on PEMS08 the noise channels rarely enter the neighbourhood of a core channel; we discuss this in Part 3.

[W2] Failure: absolute accuracy under scenario C.

We agree that the best average slope rank does not establish the best absolute accuracy under failure. The per-fraction errors are in Table 12, and Section 5.2 notes that STREAM's absolute error at f=1/8f = 1/8 is high.

This high error, however, is concentrated in the core-only setting. On the graph-based traffic datasets STREAM's error falls sharply once the monitored area grows to f=1/4f = 1/4 (for example METR-LA 7.216 to 0.731, PEMS07 3.455 to 0.213 and PEMS04 2.655 to 0.265). Across the 15 settings with f≥1/4f \geq 1/4 on these five datasets, STREAM has the lowest MSE in 7, more than any baseline (TimesNet 6, PatchTST 2; Table 12), and on METR-LA it ranks first at every fraction from f=1/4f = 1/4.

Figure 10 (Appendix E) shows where this difference comes from: on PEMS08, with only the core available, three of its 21 channels fail and channel 1 loses part of its nearest neighbours (test MSE 1.053); as the monitored area grows it finds surviving neighbours, and its error falls to 0.681 at f=1/2f = 1/2.

On ERA5 and Air Quality, by contrast, STREAM's absolute error under failure is higher than that of the baselines at most fractions. The revised Section 5.2 reports the absolute errors next to the slope.

[W2] "For scenario C, clean and failed inputs should be scored on the same surviving-core mask."

Scenario C is already scored on the same surviving-core mask. The failed set EE is drawn once per dataset with a fixed generator, and the indices of its core channels are stored and shared by every model and every fraction of that dataset. The MSE and MAE of scenario C are therefore always computed on the same mask V1/8∖EV_{1/8} \setminus E, the core without these channels (Section 3.1, Appendix A).

AuthorsOpenReview ↗

Response to Reviewer Eoiy

[W3/Q4] "The claim that channels interact only through the top-k graph is inconsistent with the global graph stream."

We agree.

The description. Section 4.2 defines the graph stream as one of the two causal streams along the patch axis: the channel average sps_p and its change enter a one-layer recurrence, and the output gpg_p is added to every channel. In this decomposition, channel mixing, that is, which channel exchanges information with which (Eq. 2), is done only by the top-kk graph, and the graph stream is a patch-level temporal context that is identical for every channel. You are right, however, that the average includes every channel, so a noisy channel contributes to gpg_p with weight 1/C1/C even when it is in no core channel's top-kk set. The contributions and the caption of Figure 3 are revised to make this distinction.

"Out-competed for the available slots" requires support. A fixed kk bounds the number of selected neighbours, not their identity, so we now test this directly (Appendix E). Figure 8 follows channel 0 of PEMS08 through the four models of scenario A on the same test window: part of its kk slots move to the newly added channels, while three core neighbours (channels 1, 3 and 13) are selected by all four models at the same patches. Figure 9 repeats the analysis for the models of scenario B. The noise channels take 4 of the 96 neighbour slots of channel 0 (12 patches ×\times k=8k = 8) at f=1/4f = 1/4 and none at 1/21/2 and full, although they make up 7%, 11% and 17% of the available channels, and 91 of the 96 selections are identical to those made on the clean window. Figure 10 does the same for test-time failures (scenario C): failed channels are not removed from the neighbourhood, since the model cannot recognise them, but they do not take over free slots either (14, 15, 12 and 14 of the 96 slots under failure, against 14, 11, 14 and 19 for the same channels in the clean window). This is one channel on one dataset, and the additional error of B over A in Part 2 shows that noise is not excluded on every dataset; Section 4.1 no longer makes this claim.

Ablations. Table 5 now contains the comparisons you ask for (relative MSE change in % with respect to the full model, positive = worse; L=H=96L = H = 96; ETTh1 and Solar on all channels, the others on the core of scenario A).

VariantETTh1SolarPEMS04PEMS07ERA5-t2mAvg.
w/o graph stream−1.8+0.2+14.2+1.60.0+2.8
Fixed graph−2.9−1.5+5.6+17.5+1.7+4.1
w/o graph (channel-independent)−3.9+7.9+103.9+85.5+1.9+39.1
  • "Do the channel-expansion and failure results persist without the global graph stream?" With clean inputs, the model without the graph stream is within 2% of the full model on four of the five datasets and 14.2% worse on PEMS04.
  • "What is the performance difference between a fixed graph and per-patch reconstruction?" Using a single graph for the whole window costs +17.5% on PEMS07, +5.6% on PEMS04 and +1.7% on ERA5-t2m. On ETTh1 and Solar the fixed graph is slightly better (−2.9%, −1.5%), so per-patch reconstruction helps on the road networks and not on the general benchmarks.
Reviewer_XZH9OpenReview ↗
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Paper summary

STREAM combines a sparse channel graph rebuilt at each patch with state-space models for temporal modeling. It evaluates forecasting under changes in channel sets, history lengths, and prediction horizons.

Critical strengths
  • The fixed-core evaluation provides a useful way to study whether additional channels help forecasting.
  • The model achieves competitive results, and the cached rollout shows clear speed benefits.
Critical weaknesses
  • The main graph choices need clearer ablations. Table 5 studies the temporal backbone and training losses, but does not isolate the benefits of rebuilding the graph at each patch or using a fixed top-k neighborhood. Comparing against a graph fixed over the window and dense channel attention, with the other components unchanged, would help explain where the gains come from.
  • The role of the global graph stream needs clarification. The paper states that channels interact only through the top-k graph. However, the graph stream pools information across all channels and broadcasts it back to each channel. This seems to provide another interaction path. Please clarify the description and consider an ablation without this stream to distinguish its contribution from local graph mixing.
Questions for authors

The conclusion acknowledges that the channel scenarios use separately trained models. Could you test changes in channel availability and history length using the same checkpoint, without retraining? The current separately trained models provide a controlled comparison, while this additional test would connect more directly to the deployment motivation. It would also be helpful to explain how channel embeddings and the readout handle these changes.

3 comments
AuthorsOpenReview ↗

Response to Reviewer XZH9

Thank you for the thoughtful review and for the concrete suggestions on ablations. We address each point below.

[W1] "The main graph choices need clearer ablations ... a graph fixed over the window and dense channel attention, with the other components unchanged."

We agree and have added both comparisons to Table 5. Each variant changes only the graph and keeps the backbone, losses and hyperparameters. Entries are the relative MSE change (%) with respect to the full model (positive = worse), L=H=96L = H = 96.

VariantETTh1SolarPEMS04PEMS07ERA5-t2mAvg.
Fixed graph−2.9−1.5+5.6+17.5+1.7+4.1
Dense (all channels)−2.8+7.7+10.9−5.0+1.5+2.5
w/o graph (channel-independent)−3.9+7.9+103.9+85.5+1.9+39.1
  • Per-patch rebuilding. "Fixed graph" estimates a single top-kk graph for the whole window and shares it across all patches. This costs +5.6% on PEMS04, +17.5% on PEMS07 and +1.7% on ERA5-t2m. On ETTh1 and Solar the fixed graph is slightly better (−2.9%, −1.5%). Per-patch rebuilding therefore helps on the road networks and is not needed on the two general benchmarks.
  • Fixed top-kk neighbourhood. "Dense" replaces the top-kk selection with attention over all channels. It is worse on Solar (+7.7%), PEMS04 (+10.9%) and ERA5-t2m (+1.5%), and better on ETTh1 (−2.8%) and PEMS07 (−5.0%); the average change is +2.5%.
  • Where the gains come from. Removing cross-channel mixing altogether roughly doubles the error on PEMS04 and PEMS07 (+103.9%, +85.5%). Most of the gain thus comes from having a channel graph at all.

[W2] "The paper states that channels interact only through the top-k graph. However, the graph stream pools information across all channels and broadcasts it back to each channel."

Section 4.2 ("Causal streams across patches") defines the graph stream as one of the two streams that carry time along the patch axis, next to the per-channel node stream. For each patch, the channel tokens are averaged into a single summary sps_p. This summary and its change from the previous patch, sp−sp−1s_p - s_{p-1}, enter a one-layer recurrence, and its output gpg_p is added to every channel before the node stream. As Section 4.2 states, it is "the path through which each channel sees how the dependency structure of the patch has been evolving". The architecture figure accordingly places gpg_p in step (iii), the causal recurrence across patches "conditioned on the graph-summary stream gpg_p", and not in step (ii), where channels mix.

We agree that the graph stream mixes information from all channels to some extent, since it is computed from the channel average. This is intended. Within a patch, channel mixing, that is, which channel exchanges information with which (Eq. 2), is done only by the top-kk graph. Across patches, Mamba scans each channel independently, so a channel on its own cannot see how the graph as a whole is evolving. The graph stream passes the state of the graph at that point in time to every channel as a patch-level context that is identical for every channel. The ablation without the graph stream shows its effect (Table 5, relative MSE change in %):

VariantETTh1SolarPEMS04PEMS07ERA5-t2mAvg.
w/o graph stream−1.8+0.2+14.2+1.60.0+2.8
w/o graph (channel-independent)−3.9+7.9+103.9+85.5+1.9+39.1

The graph stream matters on PEMS04 (+14.2%) and changes the error by less than 2% on the other four datasets. Local graph mixing remains the main source of the cross-channel benefit.

AuthorsOpenReview ↗

Response to Reviewer XZH9

[Q1] "Could you test changes in channel availability and history length using the same checkpoint, without retraining? ... explain how channel embeddings and the readout handle these changes."

Yes. Both more channels and a longer history can be evaluated with the same checkpoint, without retraining. We checked, for STREAM and each baseline, whether a trained checkpoint loads and runs a forward pass under each change:

ModelMore channelsLonger lookback
STREAM (learned channel ID)△ new channels have no learned ID row, which must be filled✓
STREAM (no channel ID)✓✓
iTransformer✓✗ Linear(L→D)\mathrm{Linear}(L \to D) embedding
PatchTST / DLinear / TiDE✓ (channel-independent)✗ linear head of size LL
MambaTS✗ C×CC \times C VAST matrix✗ head of size dmodel⋅L/patchd_{\mathrm{model}} \cdot L / \mathrm{patch}
TimeFilter✗ MoE gate of size (3,C)(3, C)✗ head of size dim⋅numpatches\mathrm{dim} \cdot \mathrm{num_patches}
TimesNet✗ Conv embedding with in_channels =C= C✗ predict_linear(L)(L)

STREAM is the only model that can be evaluated with the same checkpoint along both axes. The baselines fail for one reason: the number of channels CC or the length LL enters the size of a parameter. All parameters of STREAM are independent of CC and LL, with the single exception of the learned channel embedding.

Why this works. The computation and the size of each parameter are as follows (patch length PsP_s, hidden dimension DD):

  • Patching into [B,P=L/Ps,C,Ps][B, P = L/P_s, C, P_s] → patch embedding Linear(Ps→D)\mathrm{Linear}(P_s \to D), applied per patch and independent of CC and LL.
  • Channel embedding Embedding(Ctrain,D)\mathrm{Embedding}(C_{\mathrm{train}}, D), the only parameter tied to CC.
  • Graph layer: at every patch, the top-kk neighbours are selected by ⟨q,k⟩\langle q, k \rangle among the channels present; the qq, kk and vv weights are D×DD \times D.
  • Mamba backbone: a recurrent scan along the patch axis for each channel, with weights shared across channels and independent of length.
  • Readout: the states of the last κ\kappa patches are concatenated and mapped by Linear(κD→H)\mathrm{Linear}(\kappa D \to H), which is independent of LL once κ\kappa is fixed.

Channel embeddings: how a change in the number of channels is handled. The channel ID is the position index: channel cc receives ece_c.

  • More channels: new channels have no learned row. One can fill these rows approximately (for example with the mean of the learned rows), or train the model without channel IDs from the start. Without channel IDs, channels are distinguished only by their values and neighbours, and no parameter is tied to CC.
  • Graph: the top-kk neighbours are recomputed at every patch among the channels present at that time. When channels are added, there are simply more candidates. Because there is no learned fixed adjacency matrix, a change in CC does not break the model.

Readout: how a change in history length is handled.

  • Mamba backbone: the scan is recurrent, so when LL grows and the number of patches P=L/PsP = L/P_s grows with it, the same weights simply run for more steps. There is no positional embedding.
  • Readout: the concatenation head reads only the last κ\kappa patches, so Linear(κD→H)\mathrm{Linear}(\kappa D \to H) is used unchanged. Earlier history is compressed into the Mamba state and passed on to the last κ\kappa patch states.
  • Difference from the baselines: in PatchTST, iTransformer and DLinear the head or the embedding is a linear layer that reads the whole length LL at once, so its shape no longer matches when LL changes.

Thank you again for the constructive feedback. We would be happy to discuss any remaining concerns.

AuthorsOpenReview ↗

Kind reminder – Follow-up on our response

Dear Reviewer XZH9,

As the ICLR rebuttal period is drawing to a close, we would like to send a kind reminder regarding our response.

Thank you again for your constructive review and the concrete suggestions on the graph ablations and same-checkpoint evaluation.

We have posted a detailed response addressing both of your main points and your question. The key changes are:

  • We added the fixed-graph and dense-attention variants to Table 5, keeping the backbone, losses, and hyperparameters identical to the full model. We also included the channel-independent (w/o graph) and w/o graph-stream ablations.
  • We clarified the role of the graph stream: within-patch mixing is performed only by the top-k graph, while the graph stream provides a shared patch-level temporal context. The ablation without the graph stream is now reported.
  • We confirmed that STREAM can be evaluated with additional channels or a longer lookback using the same checkpoint without retraining. We explained how channel embeddings (or the no-ID variant) and the readout handle these changes, and provided a comparison table showing which baselines can or cannot do the same.

All changes are highlighted in blue in the revised PDF. We would be grateful if you could take a look at the response and the revised manuscript when convenient. Please let us know if any further clarification would be helpful.

Comments on the paper

2 comments
AuthorsOpenReview ↗

General Response and Summary

We thank all reviewers for their careful and constructive reviews. We are glad that the reviewers found the fixed-core channel-expansion protocol a useful way to study when additional channels help forecasting (XZH9, Eoiy, c5BV), the separation of within-patch channel mixing from across-patch recurrence practically motivated, with a clear speed benefit from state caching (XZH9, Eoiy, c5BV), and the per-fraction appendix tables useful for inspecting the claims (Eoiy).

The reviews identified three kinds of problems: inconsistencies in reported numbers, missing ablations of the graph, and claims that were broader than the evidence. We address each below. All changes are highlighted in blue in the revised PDF.

G1. Corrected reporting errors (Eoiy W1/Q1/Q2, c5BV W2). Reviewer Eoiy is right that several reported numbers were inconsistent with the stated protocol. We traced them to reporting errors, corrected the values and revised every affected table.

  • (a) Scenarios A and B at f=1/8f = 1/8. At this fraction the two scenarios are the same condition, so the differences in the submitted tables could not come from the intervention. Tables 10 and 11 are revised with the correct values, and the slopes in Table 1 are recomputed from them. The re-run baseline entries also change scenario C, so Table 12 and the slopes in Table 2 are recomputed as well. Small differences between A and B remain for some baselines even at a fixed seed, because GPU training is not fully deterministic (the selective-scan kernel of Mamba, cuDNN algorithm selection with cudnn.benchmark = True, and non-deterministic floating-point accumulation); they are at most about 3%.
  • (b) Lookback axis. Two errors affected the lookback results. First, we found that Table 13 mixed entries scored on the core with entries scored on all channels. Every entry of Table 13 is now obtained on all channels, and the summary in Table 3 is recomputed. Second, the lookback axis is scored on all channels, whereas the channel axis is scored on the core, so the full-channel entries of Table 10 and the L=96L = 96 entries of Table 13 use different scoring masks. Section 3.2 no longer states that the two axes share an anchor, and every table now states its scoring mask.
  • (c) Rollout table. The STREAM rows of Table 4 were recomputed after correcting the normalisation rule used during rollout (see Eoiy, Part 4). In the submitted version the lookback normalisation statistics were kept fixed during cached rollout; in the revision they are recomputed over the last LL steps (observed and generated values) each time a block (a patch in fine-grained rollout) is generated. This rule is now stated in Appendix B.

G2. Ablations of the channel graph and the role of the graph stream (XZH9 W1/W2, Eoiy W3/W4/Q4, c5BV W1). Table 5 now isolates the graph. Each variant keeps the backbone, losses and hyperparameters of the full model. Entries are the relative MSE change (%) with respect to the full model (positive = worse) at L=H=96L = H = 96; ETTh1 and Solar use all channels, the others the core channels of scenario A.

VariantETTh1SolarPEMS04PEMS07ERA5-t2mAvg.
w/o graph (channel-independent)−3.9+7.9+103.9+85.5+1.9+39.1
w/o graph stream−1.8+0.2+14.2+1.60.0+2.8
Fixed graph−2.9−1.5+5.6+17.5+1.7+4.1
Dense (all channels)−2.8+7.7+10.9−5.0+1.5+2.5

The sparse graph accounts for most of the cross-channel benefit: removing it roughly doubles the error on the two road networks, whereas removing the global graph stream costs 2.8% on average. Re-estimating the graph at every patch matters on the road networks (+5.6% and +17.5% when the graph is frozen) and not on ETTh1 or Solar. On ETTh1 (C=7C = 7) no graph variant helps, which is consistent with our premise that small standard benchmarks do not reward channel mixing. Section 5.5 now reports and discusses these ablations.

Role of the graph stream. Channel mixing, that is, which channel exchanges information with which, is done only by the top-kk graph within a patch. Across patches, Mamba processes each channel independently, so a channel on its own cannot see how the graph as a whole is changing. The graph stream passes this overall state to every channel: it summarises the channel average of each patch into a patch-level temporal context that is identical for every channel. The ablation above reports the model without it. The contributions and the caption of Figure 3 now state this distinction instead of saying that channels interact only through the top-kk graph.

AuthorsOpenReview ↗

General Response and Summary

Continued from last general response:

G3. Claims narrowed to what the evidence supports.

  • Channel axis (Eoiy W2/W4). Section 3.1 no longer says that added channels act only as context. Section 5.2 no longer says that channel-independent models stay flat for lack of a path, or that STREAM does not degrade under noisy channels. The slope, the absolute error and the additional error caused by an intervention are reported separately.
  • Top-kk selection (XZH9 W2, Eoiy W3). Section 4.1 no longer states that uninformative channels are out-competed by construction; Appendix E (Figures 9 and 10) shows where this holds.
  • NBP (Eoiy W5). Section 4.3 describes NBP as an auxiliary objective under whole-lookback normalisation.
  • Rollout (c5BV W3/Q2, Eoiy W7). Section 5.4 and the conclusion present the H=720H = 720 study as a comparison of autoregressive decoding capability and no longer state "four of five datasets"; Table 4 and Section 5.4 report both decoding modes for every model.

G4. Additional results.

  • Autoregressive baselines. Zero-shot Toto 2, Timestral and TimesFM 1.0/2.0 are added to Table 4 (c5BV W3/Q2, Eoiy W7).
  • Visualisation. Figures 8–11 in Appendix E show the neighbours of one channel across the four channel fractions with informative (Figure 8), noisy (Figure 9) and failing channels (Figure 10), and through a 720-step rollout (Figure 11) (Eoiy W2/W3, c5BV W1/Q1).
  • Efficiency. We report the peak memory of the top-kk construction up to C=16,384C = 16{,}384, the latency split into a one-time prefill and a per-step cost, and the scaling with CC and LL (tables in our response to Reviewer Eoiy, Part 4) (Eoiy W6/Q6).
  • Same-checkpoint evaluation. We checked, for every model, whether a trained checkpoint can be evaluated with more channels or a longer lookback without retraining (XZH9 Q1).

We respond to each reviewer in detail below, and thank the reviewers again for the time they put into this submission.

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

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