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Under review as a conference paper at ICLR 2027

SM: Spectral State Space Models for Structured Multivariate Time Series

Abstract

Multivariate streams exhibit temporal memory and structured interactions among variables. Standard selective state space models capture the former but rely on channel-separable transitions, whereas graph neural networks capture the latter without a recurrent state-space interpretation. We propose the spectral state space model (SM) for structured multivariate time series, a graph-structured state space model in which the latent state is a graph signal and the linear state transport is a learned mixture of graph-spectral filters. A dynamic observation graph captures context-dependent relations, a compact B-spline filter bank provides frequency-selective transport, and a top-s router selects a sparse spectral subspace at every time step. Availability-aware pooling prevents unobserved entries from receiving readout weight. We establish exact graph-Fourier diagonalization of the linear transport, characterize when it produces cross-variable mixing in measurement coordinates, prove optimality of the implemented top- simplex rule, and bound the state of the gated, layer-normalized recurrence. Evaluated on the large-scale benchmark PhysioNet 2019, our method outperforms the state-of-the-art (SOTA) baselines on the standard primary metric and shows effectiveness. Controlled interventions quantify the contributions of spectral filtering, recurrent memory, graph coupling, and availability-aware readout.

Primary area:
learning on time series and dynamical systems
Keywords:
Spectral state space model, structured multivariate time series

Reviews

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1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_Xr5WOpenReview ↗
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2
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4
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2
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Paper summary

The paper introduces S^3M, a multivariate time-series architecture that integrates graph-spectral operators into recurrent state-space transitions. Its key components include dynamic graph construction, B-spline spectral filtering, input-dependent top-(s) routing, and availability-aware pooling. The theoretical analysis establishes diagonalization of the linear transport operator in the graph Fourier basis, conditions for cross-variable mixing, top-(s) support optimality, and a uniform state bound induced by LayerNorm. On PhysioNet 2019 sepsis data, with approximately 89.86% missingness, S^3M achieves an AUROC of (0.9239 \pm 0.0048) across three seeds, outperforming 15 baselines under the authors' controlled evaluation protocol. However, the evaluation is limited to a single clinical dataset, the temporal relationship between trajectory-level labels and input observations remains unclear, and per-step eigendecomposition incurs O(D^3) computational cost, potentially limiting scalability.

Critical strengths

S^3M introduces a mathematically interpretable recurrence by embedding a graph-spectral operator directly into the linear state transport, accompanied by clear theoretical characterizations of both its Graph-Fourier diagonalization and measurement-coordinate cross-variable mixing. Additionally, the empirical protocol is transparent and well-controlled: it maintains a fixed 70/15/15 split under native missingness across three seeds, and candidly reports computational bottlenecks, including the ~60.3-hour RTX A6000 training time and per-step eigendecomposition costs.

Critical weaknesses
  1. The clinical prediction task rests on an insufficiently specified temporal setup, making it unverified as a prospective early-warning system. The model uses full 72-hour patient trajectories to predict an endpoint label, but the manuscript does not adequately specify the temporal relationship between the input observations and sepsis onset. This formulation differs materially from the original PhysioNet 2019 challenge, which evaluates hourly pre-onset predictions using a timing-sensitive clinical utility function. Without establishing whether post-onset measurements can enter the input trajectories, the reported AUROC cannot be reliably interpreted as evidence of prospective early-warning performance.
  2. The empirical evidence exhibits limited generalizability and does not establish a rigorously comparable state-of-the-art advantage. The evaluation is confined to a single clinical dataset under one fixed patient-level split, lacking validation on independent datasets, multi-center cohorts, or non-clinical multivariate domains, while component ablations rely on only a single training seed. Furthermore, Table 3 juxtaposes results obtained under conflicting evaluation protocols; although these protocol differences are disclosed, the comparison does not establish a directly comparable state-of-the-art claim across structured time series.
  3. The theoretical derivations largely restate standard algebraic properties of the chosen design: Lemmas 1–3 and Theorem 1 follow directly from shared-basis eigendecomposition, simplex entropy regularization, and LayerNorm bounds. And, the manuscript does not adequately contrast its core mechanism with existing graph state-space models and dynamic spectral filters, leaving it unproven what concrete capabilities or advantages it provides beyond prior methods.
Questions for authors
  1. Does the fixed 72-hour input window include observations recorded after sepsis onset, and given the manuscript's explicit acknowledgment that verified onset timestamps are unavailable, how do the authors establish that the evaluation measures prospective early-warning performance rather than retrospective outcome classification using potentially post-onset data?
  2. In the all-missing boundary case of Eq. (6), finite logits cause the softmax to assign strictly positive weights to missing positions; how is this behavior reconciled with the claimed zero-weight guarantee, particularly given the method section's explicit statement that no separate all-missing fallback is implemented?
  3. What specific architectural capability or theoretical guarantee does S^3M establish beyond the closest existing graph state-space models and dynamic spectral-filtering approaches, and which aspect of the proposed method cannot be obtained through a straightforward extension of the closest prior approach?
  4. Filter responses are constructed via dense operations and the ablation shows only a marginal AUROC gain over dense routing; does top-ss routing provide measurable runtime or memory savings, or a consistent generalization advantage beyond qualitative sparsity?
11 comments
AuthorsOpenReview ↗

Response to Critical Weaknesses 1

Critical Weaknesses 1. The clinical prediction task rests on an insufficiently specified temporal setup, making it unverified as a prospective early-warning system. The model uses full 72-hour patient trajectories to predict an endpoint label, but the manuscript does not adequately specify the temporal relationship between the input observations and sepsis onset. This formulation differs materially from the original PhysioNet 2019 challenge, which evaluates hourly pre-onset predictions using a timing-sensitive clinical utility function. Without establishing whether post-onset measurements can enter the input trajectories, the reported AUROC cannot be reliably interpreted as evidence of prospective early-warning performance. Response. We thank the reviewer for identifying this important limitation. We agree that the original manuscript did not state the temporal scope precisely enough. Following your suggestion, we added a new Appendix F, “Temporal Protocol, Onset Censoring, and Scope of the Clinical Benchmark,” and revised the Results and Reproducibility Statement in the main paper.

The revised text now defines the evaluated task explicitly as

y^endpoint=fθ(X1:72,M1:72,Δ1:72),\widehat y_{\mathrm{endpoint}}=f_\theta(X_{1:72},M_{1:72},\Delta_{1:72}),

where the first 72 retained rows are mapped to one trajectory-level endpoint label. The model does not emit an hourly sequence of pre-onset risks, the retained files do not provide an adjudicated hourly sepsis-onset timestamp, and the experiment does not compute the original PhysioNet 2019 timing-sensitive clinical utility function. We therefore narrow the claim: the reported AUROC is a retrospective endpoint-classification benchmark under the fixed P19 protocol, not evidence of prospective early-warning performance or bedside clinical utility.

To quantify the temporal sensitivity rather than leave the issue qualitative, we added an inference-only onset-censoring audit using the locked validation-selected seed-7 checkpoint and the same 6,051-example test split. The uncensored score is AUROC 0.9187. Masking observations strictly after the first positive SepsisLabel proxy gives AUROC 0.8905 (absolute change -0.0282), and masking the proxy hour and all later hours gives AUROC 0.8917 (absolute change -0.0271). The corresponding AUPRC values are 0.6456, 0.5625, and 0.5571. This shows that the benchmark score is sensitive to observations after the proxy. Because the first positive label is only a proxy and not a verified clinical onset timestamp, we describe this as temporal or post-proxy sensitivity evidence, not as prospective validation or an estimate of challenge utility.

We retain the retrospective benchmark value: the same fixed window, missingness channels, endpoint definition, split, and locked test partition are supplied to every compared model, so the protocol still supports controlled endpoint-discrimination and mechanism comparisons. We also state the limitation explicitly and list the requirements for a future prospective evaluation: adjudicated onset times, a declared pre-onset prediction origin, removal of all post-onset observations, hourly risk outputs, a challenge-compatible timing-sensitive utility function, and temporal or prospective external validation.

See:

  • Main-paper Results revision: the routing-case paragraph now states: “Because the retained protocol uses a fixed 72-hour trajectory and does not provide an adjudicated onset time or an hourly timing-sensitive utility score, we interpret this experiment as a retrospective endpoint-classification benchmark rather than as evidence of prospective early-warning or clinical utility; the temporal sensitivity audit is reported in Appendix F.”
  • Main-paper Reproducibility revision: the protocol description now states that the fixed 72-hour input is evaluated against a trajectory-level endpoint label and that, because no adjudicated hourly onset timestamp or hourly utility score is available, the experiment is not presented as prospective early-warning validation.
  • Appendix F.1, “Task actually evaluated”: gives the fixed-window equation, identifies the value/availability/elapsed-time channels, explains that one endpoint score is emitted rather than hourly scores, and distinguishes the benchmark from the original hourly utility protocol.
AuthorsOpenReview ↗

Response to Critical Weaknesses 1 (continued)

  • Appendix F.2, “Relation between the 72-hour window and onset”: explains why the absence of a verified onset timestamp prevents us from asserting that every input row is pre-onset. Table 9 reports the audit counts: among 6,051 test trajectories, 440 have a positive endpoint label, 334 have the first-positive proxy within the first 72 rows, 106 have it after the window, and 5,611 have no positive proxy in the available record. The appendix explicitly says that this proxy is an analysis device, not a clinical gold standard.
  • Appendix F.3, “Onset-censoring sensitivity audit”: reports Table 10 with the locked-checkpoint results: original AUROC 0.9187; post-onset-censored AUROC 0.8905; from-onset-censored AUROC 0.8917. The strict and inclusive masks change 21,582 and 23,631 test observations in 329 and 334 trajectories, respectively. The appendix explains that the score changes quantify temporal sensitivity but do not establish prospective lead time or challenge utility.
  • Appendix F.4, “Retrospective benchmark interpretation”: states exactly what the AUROC and controlled interventions support under the common fixed-window protocol and withdraws the prospective/clinical-utility interpretation.
  • Appendix F.5, “Prospective early-warning limitation and required follow-up protocol”: states that prospective early-warning performance cannot be established with the retained data and lists the protocol needed to establish it in future work.
AuthorsOpenReview ↗

Response to Critical Weaknesses 2

Critical Weaknesses 2. The empirical evidence exhibits limited generalizability and does not establish a rigorously comparable state-of-the-art advantage. The evaluation is confined to a single clinical dataset under one fixed patient-level split, lacking validation on independent datasets, multi-center cohorts, or non-clinical multivariate domains, while component ablations rely on only a single training seed. Furthermore, Table 3 juxtaposes results obtained under conflicting evaluation protocols; although these protocol differences are disclosed, the comparison does not establish a directly comparable state-of-the-art claim across structured time series.

**Response:**Thank you for this important comment. We agree that the previous draft did not make the scope of the evidence sufficiently clear. The three baselines in Table 4—TimeCHEAT, iTimER, and NCDE—were run under the same settings as our algorithm, and their results are reported in the original Table 3. We have added the fixed-split results for Raindrop and a paper-based SPECTRA reimplementation to the rightmost column of Table 3, added a new Appendix K synthesizing the evidence and its limits, and expanded the Reproducibility Statement with the NATOPS retraining protocol and fixed-split baseline settings. Appendix J already reports the four added nonclinical datasets, while Appendix H reports the independently retrained NATOPS ablations across seeds 7, 8, and 9. We revised the Discussion and Conclusion to avoid presenting the results as a broad state-of-the-art claim.

See:

“Appendix J reports held-out results for FingerMovements, NATOPS, AtrialFibrillation, and CharacterTrajectories, with one seed-7 evaluation for each dataset. S$^3$M is competitive on accuracy in these supplied comparisons, but the leading method varies by metric and dataset; it does not consistently lead in AUROC, AUPRC, or Macro-F1. These experiments address the absence of nonclinical domains, but their single-seed design does not quantify run-to-run uncertainty. They also do not add an independent clinical cohort or a multicenter validation. The P19 results therefore remain evidence on one retrospective benchmark and one fixed patient-level split, not evidence of clinical transportability.”

“The P19 Table 4 remains a seed-7 study of one unchanged Full forward pass plus six frozen-checkpoint interventions. To add a multi-seed check of independently retrained variants, Appendix H.3 reports fresh training of the Full model and the same six variants on NATOPS for seeds 7, 8, and 9. Their AUROCs (mean ± sample SD) are: Full S$^3$M, 0.729840 ± 0.229729; identity graph, 0.461284 ± 0.079221; no spectral filter, 0.561679 ± 0.140948; dense routing, 0.517975 ± 0.077934; no Laplacian diffusion, 0.537556 ± 0.104235; no state recurrence, 0.692914 ± 0.031617; and unmasked readout, 0.604957 ± 0.136592. The large seed variation, including for Full S$^3$M, warrants a cautious interpretation. These are genuinely retrained multi-seed component results on a separate nonclinical dataset; they do not convert the P19 frozen-intervention study into a P19 multi-seed retraining experiment.”

“The rightmost column of Table 3 now supplies a common-protocol P19 comparison for Raindrop and a paper-based SPECTRA reimplementation, in addition to the already available matched-split results for TimeCHEAT, iTimER, and NCDE. Under the fixed neighbor_v1 70/15/15 split (split seed 7) and training seeds 7, 8, and 9, the mean ± sample-SD AUROCs are 92.39 ± 0.48% for S$^3$M, 91.8418 ± 0.2704% for Raindrop, 87.69 ± 7.63% for SPECTRA, 88.10 ± 3.51% for TimeCHEAT, 83.71 ± 0.27% for iTimER, and 90.84 ± 0.51% for NCDE. The published-source column is retained as context but reflects different splits and evaluation protocols. For S$^3$M, seed 7 is the original run and seeds 8 and 9 are validation-selected warm-start continuations from its EMA checkpoint; its reported SD is descriptive, not an independent-seed uncertainty estimate.”

“The matched column permits a more direct comparison among the listed P19 runs than the source-protocol values alone, but it still represents a single dataset and a single fixed split. The four nonclinical results are single-seed, and the multi-seed ablation check is on NATOPS rather than P19. The S$^3$M seed-8 and seed-9 runs are warm-start continuations, so the reported dispersion is descriptive rather than an independent-replication estimate; the small difference from Raindrop is not a significance test. SPECTRA is a paper-based reimplementation and not an evaluation of the authors’ official implementation. Accordingly, we limit the empirical claim to comparative performance under the stated P19 protocol and report the nonclinical and NATOPS findings as supplementary evidence; we do not claim a robust state-of-the-art advantage across structured time series, clinical sites, or datasets.”

Reviewer_SmbCOpenReview ↗
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Paper summary

This paper proposes S3M, a graph-structured recurrent model for multivariate time series. S3M combines dynamic graphs, learnable spectral filters, sparse routing, and availability-aware pooling within a recurrent model for multivariate time series. The model represents hidden states as graph signals and combines dynamic graph construction, learnable B-spline spectral filters, sparse input-dependent routing, and availability-aware pooling. The approach is promising and achieves the highest mean AUROC among the baselines on the authors’ fixed PhysioNet2019 split.

Critical strengths
  • The paper addresses a relevant problem by jointly modeling temporal dependencies, cross-variable interactions, and missing observations.

  • Incorporating graph-spectral transport directly into recurrent state updates is a coherent and interesting design.

  • The reported AUROC is encouraging. The evaluation uses a common patient-level split, training-only normalization, and validation-based checkpoint selection.

Critical weaknesses
  • Frozen interventions measure a trained model’s dependence on a component, but degradation may reflect representation mismatch rather than the inferiority of an ablated architecture after retraining. The manuscript also mentions seven interventions, while the table lists six variants.

  • The motivation emphasizes limitations of channel-separable SSMs, but the experiments lack matched comparisons against the same model backbone, such as Graph-Mamba and recurrent state space modeling.

  • The compression of dynamic graphs with learned static graphs is missing. The results do not clearly establish whether the benefit comes from placing graph-spectral propagation inside recurrence.

  • Evidence for sparse routing and robust superiority is limited. Sparse and dense routing achieve nearly identical single-seed AUROC values, 0.9187 and 0.9176, while the implementation retains the dominant dense computations.

Questions for authors
  • Are the Table 4 variants independently retrained or evaluated through frozen-checkpoint interventions? Please reconcile the protocol descriptions and the number of interventions.

  • Can matched controls compare graph-spectral recurrence with channel-separable recurrence, external graph encoding, and a learned static graph?

  • Does the sparse and dense routing difference persist across seeds? What measurable benefit does sparsity provide in the current implementation?

  • Does the severe degradation from unmasked readout still happen after retraining, or does it mainly reflect a frozen-intervention mismatch?

  • Can the authors quantify uncertainty in the AUROC difference from TiDE and explain the lower AUPRC?

12 comments
AuthorsOpenReview ↗

Response to Critical Weaknesses 1.

Critical Weaknesses 1.Frozen interventions measure a trained model’s dependence on a component, but degradation may reflect representation mismatch rather than the inferiority of an ablated architecture after retraining. The manuscript also mentions seven interventions, while the table lists six variants.

Response:

Thank you for pointing out both issues. We agree that the earlier wording conflated table rows with component interventions and did not state strongly enough that a frozen intervention can include representation mismatch.

The corrected P19 accounting is one unchanged Full S^3M forward pass plus six frozen-checkpoint interventions, one for each component variant. Thus Table 4 has seven rows and six interventions. The phrase "seven interventions" has been removed. The earlier cost wording has also been replaced: approximately 60.3 hours refers to training the Full model once; the six variants are forward-only edits of its frozen checkpoint.

We now interpret a P19 decrease narrowly. It means that the trained checkpoint's representation and readout depend on the targeted computation under the fixed intervention. It does not prove that an independently retrained ablated architecture would have the same AUROC or that the component is universally necessary. Since the downstream layers remain fixed, removing a component can produce a state distribution mismatched to the learned readout. Appendix H.2 states this caveat, and Section 4 repeats it next to the reported differences.

We added independently retrained NATOPS checks to expose the distinction. Appendix H.3 reports fresh Full and variant checkpoints for seeds 7/8/9; the Full AUROC is 0.729840 ± 0.229729 and the six controls are 0.461284 ± 0.079221, 0.561679 ± 0.140948, 0.517975 ± 0.077934, 0.537556 ± 0.104235, 0.692914 ± 0.031617, and 0.604957 ± 0.136592, respectively. Appendix H.4 reports a separate seed-7 NATOPS retraining audit with Full 0.811296 and controls 0.391519, 0.497778, 0.472407, 0.504111, 0.667222, and 0.745815. The difference between these independently retrained checks and the locked P19 intervention is why we do not equate frozen degradation with retrained architecture inferiority.

See: complete location and content

  • Table 4: the caption distinguishes the unchanged Full row from six frozen interventions and says that seven rows are seven test-time evaluations, not seven training runs.
  • Section 4: the revised text says "seven rows but six interventions" and states that checkpoint parameters are frozen.
  • Section 4: the next paragraph says that frozen results support checkpoint dependence but do not establish that a retrained ablated architecture would necessarily perform worse.
  • Reproducibility Statement, label sec:reproducibility: the single Full-model training cost and six forward-only interventions are explicitly separated.
  • Appendix H opening and H.1: the corrected one-plus-six count and Table 13 override inventory are given.
  • Appendix H.2: the representation-mismatch limitation is stated explicitly.
  • Appendix H.3: fresh independently retrained NATOPS rows for Full plus the six Table 4 variants are reported across seeds 7/8/9 with mean ± sample standard deviation.
  • Appendix H.4: the separate seed-7 NATOPS rows are reported with their seven test metrics.
  • Appendix H.5: limits the scope to P19 checkpoint dependence plus the two NATOPS retraining audits.
AuthorsOpenReview ↗

Response to Critical Weaknesses 2.

Critical Weaknesses 2. The motivation emphasizes limitations of channel-separable SSMs, but the experiments lack matched comparisons against the same model backbone, such as Graph-Mamba and recurrent state space modeling.

Response: Thank you for pointing out that the original experiments did not isolate the limitation of channel-separable recurrence from the proposed graph-spectral transition. Following your suggestion, we added Appendix I with independently retrained NATOPS controls using the same S$^3$M implementation, data protocol, training budget, model width, and validation-based checkpoint selection. The controls compare Full S$^3$M with channel-separable recurrence, graph encoding outside recurrence, graph propagation after recurrence, and a learned sample-static graph. We report both seeds 7/8/9 and a separate seed-7 audit. The results show that Full S$^3$M exceeds the channel-separable, post-recurrence, and static-graph controls in the three-seed mean, while the external-encoding control has a higher mean AUROC. We therefore do not claim robust superiority over every alternative. These are same-codebase mechanism controls, not an official Graph-Mamba reimplementation; we state this limitation explicitly. See (new Appendix I text and results):

“The channel-separable control disables the graph and spectral paths. The external-encoding control applies graph-spectral encoding to the current-input branch before a channel-separable recurrent update. The post-recurrence control first performs a channel-separable recurrent update and then applies the spectral graph filter and Laplacian diffusion to that updated state. The learned static-graph control forms one observation-conditioned graph from sequence-averaged inputs and hidden representations and reuses it at all time steps; the Full model instead recomputes the observation graph at each step.”

“These are matched mechanism controls within the released S$^3$M implementation: they share the dataset protocol, training budget, model width, and checkpoint-selection rule. They are not an independent reimplementation of Graph-Mamba, and we do not use them to claim a benchmark-level ranking against that model family.”

Three-seed NATOPS test AUROC, mean ± sample SD: Full S$^3$M, 0.729840 ± 0.229729; channel-separable recurrence, 0.569364 ± 0.160674; external graph encoding, 0.812457 ± 0.019204; graph propagation after recurrence, 0.615691 ± 0.178495; learned sample-static graph, 0.503926 ± 0.066401. Separate seed-7 AUROC: 0.811296, 0.742574, 0.796519, 0.550444, and 0.459519, respectively.

“These small-sample comparisons are descriptive; they do not establish statistical significance or a robust ranking.”

AuthorsOpenReview ↗

Response to Critical Weaknesses 3.

Critical Weaknesses 3. The compression of dynamic graphs with learned static graphs is missing. The results do not clearly establish whether the benefit comes from placing graph-spectral propagation inside recurrence.

Response: Thank you for identifying the missing dynamic-versus-static comparison and the need to isolate graph placement. We have followed your suggestion to add Appendix I to solve this problem. Appendix I now includes a learned sample-static graph that is independently retrained under the same NATOPS protocol, as well as a graph-after-recurrence control. The static graph is constructed from sequence-averaged inputs and hidden representations and reused at every time step; the Full model recomputes its observation graph at each step. In the three-seed study, Full S$^3$M has AUROC 0.729840 ± 0.229729, compared with 0.503926 ± 0.066401 for the static-graph control and 0.615691 ± 0.178495 for graph propagation after recurrence. The separate seed-7 values are 0.811296, 0.459519, and 0.550444. Since seed 9 yields nearly identical AUROC for Full and the static control, and the three-seed Full result has substantial variability, we describe this as suggestive controlled evidence rather than a definitive or universal benefit.

See (new Appendix I text and results):

“The learned static-graph control forms one observation-conditioned graph from sequence-averaged inputs and hidden representations and reuses it at all time steps; the Full model instead recomputes the observation graph at each step.”

“The per-seed AUROCs clarify the variability: Full S$^3$M obtains 0.811296, 0.907741, and 0.470481; graph propagation after recurrence obtains 0.550444, 0.817630, and 0.479000; and the learned static-graph control obtains 0.459519, 0.580259, and 0.472000, for seeds 7, 8, and 9, respectively.”

“We also audited graph variation on the validation-selected seed-7 Full checkpoint. Across 180 test sequences, 9,180 sequence-time points, and 24 variables, the relative Frobenius discrepancy between the time-varying graph and the sequence-static graph averaged 0.0934 (SD 0.0283); the dynamic graph’s temporal variation relative to its sequence mean averaged 0.0837 (SD 0.0258). Mean dynamic-graph density was 0.4811 (SD 0.0757). This forward-pass diagnostic establishes that the learned graph changes over time in this checkpoint, but it is descriptive rather than causal.”

Reviewer_VPyROpenReview ↗
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Paper summary

This paper proposes S³M, a spectral state space model for structured multivariate time series. The method integrates a dynamic observation graph, graph-spectral filtering, sparse spectral routing, and recurrent state updates to model temporal dependencies and interactions among variables. The authors also provide several theoretical results characterizing the spectral transition, sparse routing, cross-variable mixing, and boundedness of the recurrent state.

The proposed method is evaluated on the PhysioNet 2019 sepsis prediction benchmark, where it achieves the highest reported AUROC among the compared methods.

Critical strengths

The idea of incorporating graph-spectral propagation directly into recurrent state transitions is interesting. The proposed framework attempts to jointly model temporal memory and interactions among variables, which is relevant to structured multivariate time-series learning. However, it seems a bit overcomplicated.

Critical weaknesses
  1. Despite the paper proposing a general framework for structured multivariate time series, evaluation is limited to a single dataset. Moreover, although S³M achieves the highest AUROC, it does not consistently outperform the baselines on the other reported metrics, including AUPRC, accuracy, and Macro-F1. The paper would benefit from a more balanced discussion of these results, particularly given the class imbalance of the clinical prediction task.

Additional experiments on different multivariate time-series datasets would be necessary to demonstrate that the proposed architecture is broadly effective rather than specialized to the evaluated benchmark.

  1. Section 3.1 introduces several components, including the spectral filter bank, sparse router, recurrent transition, and availability-aware prediction mechanism. But the presentation is heavily equation-driven, with limited explanation. The formatting of Sections 3.1 and 3.2 should be carefully redone.

I suggest reorganizing Section 3.1 around the main computational pipeline, beginning with an intuitive explanation of the spectral recurrent transition before presenting the implementation details.

  1. Section 3.2 contains several lemmas and a theorem concerning graph-Fourier diagonalization, sparse routing, cross-variable mixing, and state boundedness. However, several of these results follow relatively directly from the model's construction or standard mathematical properties.

For example, the graph-Fourier diagonalization results follow from constructing the transition as a function of the graph Laplacian, while the uniform state bound largely follows from the application of LayerNorm. The theoretical results do not sufficiently explain why the proposed architecture should achieve better predictive performance, more effective temporal modeling, or improved computational efficiency.

I suggest retaining the most relevant theoretical statements in the main paper and moving the detailed proofs to the Appendix. The additional space could be used to better motivate the architecture and analyze the experimental findings.

  1. There appears to be an inconsistency between the description of Table 4 and the experimental procedure explained in Section 4. The caption of Table 4 discusses the computational cost of running the full model and six ablated variants, whereas Section 4 describes frozen-checkpoint forward interventions applied to an already trained model.

These two procedures support different conclusions. Removing components from a trained model can demonstrate its dependence on those components, but it does not necessarily establish how well the corresponding simplified architectures would perform if trained independently.

Since the paper relies on these results to demonstrate the contributions of its architectural components, the authors should clarify the exact experimental protocol and distinguish intervention-based sensitivity from conventional retraining ablations.

  1. The paper would benefit from a clearer presentation and more thorough experimental analysis.
Questions for authors
  1. Can the authors clarify whether the component studies in Table 4 involve independently retrained ablated models or frozen-checkpoint interventions? How should these results be interpreted when assessing the necessity of each component?

  2. Why is the proposed general multivariate time-series framework evaluated on only one dataset? Can the authors provide additional evidence of generalization to other structured time-series tasks?

  3. What is the practical advantage of sparse spectral routing over dense filter selection? Table 4 reports only a small AUROC difference, and the implementation does not appear to reduce the dominant computational complexity.

  4. Can the authors explain how the theoretical results in Section 3.2 support the claimed practical advantages of the proposed model beyond establishing properties that follow from its mathematical construction?

13 comments
AuthorsOpenReview ↗

Response to Critical Weaknesses 1

Critical Weaknesses 1. Despite the paper proposing a general framework for structured multivariate time series, evaluation is limited to a single dataset. Moreover, although S³M achieves the highest AUROC, it does not consistently outperform the baselines on the other reported metrics, including AUPRC, accuracy, and Macro-F1. The paper would benefit from a more balanced discussion of these results, particularly given the class imbalance of the clinical prediction task. Additional experiments on different multivariate time-series datasets would be necessary to demonstrate that the proposed architecture is broadly effective rather than specialized to the evaluated benchmark.

Response: Thank you for this constructive comment. We followed your recommendation in two ways. First, we added a main-paper Discussion that reports the metric trade-offs directly and explains how class imbalance changes the interpretation of AUROC, AUPRC, Accuracy, and Macro-F1. In clinical datasets such as P19, AUROC is generally valued because doctors primarily care about the missed diagnosis rate. Second, we added Appendix J with one complete result table for each of four nonclinical multivariate time-series classification datasets: FingerMovements, NATOPS, AtrialFibrillation, and CharacterTrajectories. These additional comparisons extend the evaluation beyond the clinical P19 benchmark, while we explicitly identify them as single seed-7 evaluations and avoid claiming uniform superiority.

For P19, the revised discussion states that S³M has the highest mean AUROC among the controlled baselines (0.9239 ± 0.0048), but does not lead on every metric: TiDE has higher mean AUPRC (0.6784 ± 0.0142 versus 0.6669 ± 0.0189), and TimeCHEAT has higher Accuracy (0.9154 ± 0.0152 versus 0.8431 ± 0.0305) and Macro-F1 (0.7492 ± 0.0143 versus 0.6791 ± 0.0308). The P19 test split contains 440 positive endpoint labels among 6,051 trajectories (7.27% prevalence). We retain AUROC as the primary P19 comparison metric because the clinical task emphasizes ranking patients by risk and avoiding missed positive cases, but we now state explicitly that AUROC alone does not establish sensitivity, calibration, or clinical utility at a chosen operating threshold. AUPRC is prevalence-sensitive, while Accuracy and Macro-F1 depend on the threshold and class distribution, so all four metrics are reported and discussed. See: Main-paper Discussion (the complete added text):

“On P19, S³M achieves the highest mean AUROC among the controlled baselines (0.9239 ± 0.0048), but it does not dominate every metric. TiDE has higher mean AUPRC (0.6784 ± 0.0142 versus 0.6669 ± 0.0189), while TimeCHEAT has higher accuracy (0.9154 ± 0.0152 versus 0.8431 ± 0.0305) and Macro-F1 (0.7492 ± 0.0143 versus 0.6791 ± 0.0308). We therefore interpret the P19 results as strongest on ranking discrimination under the benchmark protocol, not as uniform superiority.”

“The P19 test split contains 440 positive endpoint labels among 6,051 trajectories (7.27% prevalence). S³M’s mean AUPRC (0.6669 ± 0.0189) is well above the prevalence baseline but below TiDE (0.6784 ± 0.0142). AUROC summarizes ranking across thresholds and is less sensitive to prevalence; AUPRC is prevalence-sensitive and emphasizes precision among high-scoring cases. Accuracy depends on the operating threshold and class distribution, while Macro-F1 gives more balanced weight to classwise precision and recall but is also threshold-dependent. Because avoiding missed positive cases is clinically important, AUROC alone cannot establish that a model is safer or more useful: that requires an explicitly selected operating point, sensitivity and false-alarm reporting, calibration, and prospective or utility-based evaluation. We retain AUROC as the primary metric for comparison with the P19 benchmark while reporting and discussing all four metrics.”

“To address dataset breadth, Appendix. J adds separate held-out result tables for FingerMovements, NATOPS, AtrialFibrillation, and CharacterTrajectories. S³M’s performance is mixed across these tasks and metrics: it is competitive on accuracy in the supplied comparisons, but it does not lead consistently on AUROC, AUPRC, or Macro-F1. These are single-seed results, so they extend the evaluation beyond P19 but do not establish seed-robust generalization or a general advantage across structured time-series tasks.”

AuthorsOpenReview ↗

Response to Critical Weaknesses 1 (continued)

See: Appendix J, complete added tables and their values:

DatasetS³M AccuracyS³M Macro-F1S³M AUROCS³M AUPRCBest AccuracyBest Macro-F1Best AUROCBest AUPRC
FingerMovements0.50000.46370.45300.4788S³M, 0.5000FRETS, 0.4800TSMixer, 0.4714TSMixer, 0.4992
NATOPS0.53890.46450.87460.5851S³M/Pyraformer, 0.5389Pyraformer, 0.5038Pyraformer, 0.9137Pyraformer, 0.6398
AtrialFibrillation0.73510.58900.78320.6503S³M/PatchTST/TimesNet, 0.7351PatchTST, 0.6629PatchTST, 0.8492PatchTST, 0.7014
CharacterTrajectories0.70330.59910.87010.6856S³M, 0.7033S³M, 0.5991Autoformer, 0.9131S³M, 0.6856

The full method-by-method values are included in Appendix J as four separate tables, one dataset per table. The appendix closes with the following qualification:

“The four comparisons show why we report multiple metrics. In the supplied tables, S³M has the highest or tied-highest accuracy on these tasks, but its AUROC is not the highest on any of the four. Its Macro-F1 is highest only on CharacterTrajectories, and its AUPRC is highest only on CharacterTrajectories. In particular, the strongest comparator differs across datasets and metrics. This pattern supports reporting S³M as a potentially useful general architecture whose observed performance depends on the task and metric; it does not justify claiming that it consistently outperforms established time-series models. Because every added dataset is represented by one reported seed-7 evaluation, multi-seed replication is needed to characterize uncertainty and robustness.”

Complete method-level rows reproduced from the supplied experiment summary:

FingerMovements

MethodAccuracyMacro-F1AUROCAUPRC
S3M0.50000.46370.45300.4788
Autoformer0.42000.39580.39420.4804
DLinear0.46000.45800.45180.4845
FITS0.43000.42950.44140.4799
FRETS0.48000.48000.44860.4803
Koopa0.45000.44550.43180.4733
Pyraformer0.46000.46000.43620.4736
TimeMixer0.44000.43800.45700.4784
TimeXer0.44000.43800.43220.4676
TSMixer0.48000.47810.47140.4992

NATOPS

MethodAccuracyMacro-F1AUROCAUPRC
S3M0.53890.46450.87460.5851
Crossformer0.32780.19800.82400.4490
ETSformer0.45560.41630.84820.4718
FITS0.48890.39690.87090.5460
FRETS0.37220.25290.78920.4072
Pyraformer0.53890.50380.91370.6398
TimesNet0.43330.35830.85840.5110

AtrialFibrillation

MethodAccuracyMacro-F1AUROCAUPRC
S3M0.73510.58900.78320.6503
Autoformer0.64320.56770.76150.5838
DLinear0.59460.40880.62360.4268
ETSformer0.67030.65640.81770.6892
FEDformer0.72430.65270.79340.6344
FITS0.57300.43490.63390.4717
FRETS0.56760.46450.61440.4455
iTransformer0.63780.52560.70130.5176
Koopa0.62160.45850.64380.4720
Non-stationary Transformer0.63780.49970.70000.5188
PatchTST0.73510.66290.84920.7014
Pyraformer0.62160.39000.64570.4738
RLinear0.48110.35930.61610.4111
TiDE0.59460.42720.61670.4559
TimeMixer0.57300.42970.60300.4217
TimesNet0.73510.64880.81980.6652
TSMixer0.69730.62490.79710.6607

CharacterTrajectories

MethodAccuracyMacro-F1AUROCAUPRC
S3M0.70330.59910.87010.6856
Autoformer0.69290.57020.91310.6774
DLinear0.63790.52240.89030.6514
ETSformer0.70190.59830.87070.6566
FITS0.58220.49960.83930.5738
FRETS0.58360.50080.83200.5144
Koopa0.61490.52380.84060.5688
Pyraformer0.58980.50000.84440.5681
TimeMixer0.61350.52290.83060.5713
AuthorsOpenReview ↗

Response to Critical Weaknesses 2

Critical Weaknesses 2. Section 3.1 introduces several components, including the spectral filter bank, sparse router, recurrent transition, and availability-aware prediction mechanism. But the presentation is heavily equation-driven, with limited explanation. The formatting of Sections 3.1 and 3.2 should be carefully redone. I suggest reorganizing Section 3.1 around the main computational pipeline, beginning with an intuitive explanation of the spectral recurrent transition before presenting the implementation details.

Response: Thank you for your helpful comment. We have followed your suggestion and reorganized Section 3.1 around the main computational pipeline, beginning with an intuitive explanation of the spectral recurrent transition before presenting the implementation details. We have also reorganized Section 3.2. Section 3.1 now starts with an intuitive explanation of the spectral recurrent transition, followed by a compact pipeline equation and four clearly separated implementation steps: input encoding and dynamic graph construction, spectral filtering and sparse routing, the recurrent spectral transition, and availability-aware prediction. We clarified the roles of the input channels, graph Fourier coordinates, sparse top-ss routing, graph diffusion, gated updating, layer normalization, and availability masking. We also added a short explanation of the regularization terms. Section 3.2 now begins with a theory roadmap and groups the results by their purpose: Fourier-coordinate interpretation, shared spectral basis and operator norm, sparse-routing optimality, basis dependence and cross-variable mixing, and the uniform layer-normalized state bound. We also explicitly distinguish the linear transport analysis from the full nonlinear recurrent update. The detailed revised text is shown in the blue-highlighted original manuscript text in Sections 3.1 and 3.2.

Section 3.1 — Spectral State Space Model

Computational pipeline and intuition. The hidden state Ht−1∈RD×hH_{t-1}\in\mathbb{R}^{D\times h} is a graph signal: its DD rows correspond to measured variables and its hh columns are latent features. At time tt, the dynamic observation graph supplies a Laplacian Lt=VtΛtVt⊤L_t=V_t\Lambda_tV_t^{\top}. Its eigenvectors provide graph-Fourier coordinates in which a spectral filter is a frequency-dependent gain. The router selects a small set of learned filters, mixes their gains with normalized nonnegative weights, and combines that result with explicit graph diffusion. After transforming back to measurement coordinates, the model adds the current input, applies the update gate and pointwise nonlinearity, and normalizes the state. Cross-variable propagation therefore occurs inside the recurrent transition itself.

The revised section now includes the following computational-pipeline equation:

Pt=(Gˉt−κℓLt)Ht−1+Win(ℓ)XtP_t = (\bar G_t - \kappa_\ell L_t)H_{t-1} + W_{\mathrm{in}}^{(\ell)}X_t

Ht=LN((1−u)Ht−1+utanh⁡(Pt))H_t = \mathrm{LN} ((1-u)H_{t-1} + u \tanh(P_t))

The first term is diagonal in graph-Fourier coordinates but generally dense in the canonical variable basis, so it can mix variables while retaining a frequency interpretation. The remainder of this subsection follows the same computation from graph construction through spectral routing, recurrent update, and availability-aware prediction.

The main computation is summarized as follows:

  1. Step 1: Encode the value, availability, and elapsed-time channels into XtX_t and construct the observation-conditioned graph.
  2. Step 2: Evaluate a compact graph-spectral filter bank and use the current input plus graph spectrum to select a sparse top-ss mixture.
  3. Step 3: Transport the previous recurrent state with the routed spectral operator, add the current-input projection, and apply the gated nonlinear update.
  4. Step 4: Pool only available state entries and combine the pooled representation with the average routing summary for prediction.

Step 1: Input encoding and dynamic observation graph

The graph branch is the first context-dependent component after encoding; it uses the current block input, availability, elapsed time, and a learned variable identifier.

Step 2: Spectral filter bank and sparse router

The graph spectrum turns the variable interaction pattern into graph frequencies, so each learned filter can assign a different gain to each frequency.

Step 3: Spectral recurrent transition

Once the sparse mixture has been formed, the previous state is transported across variables and graph frequencies, the current input is projected into the hidden width, and the two signals are combined by the gated nonlinear update.

Step 4: Availability-aware prediction

Unavailable positions are removed before the readout softmax, so missing entries cannot receive pooling weight.

Comments on the paper

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Response Letter Summary

Dear Chairs and Reviewers:

Thank you for taking time out of your busy schedule to review our manuscript and put forward valuable comments and suggestions on the paper. In response to each of your valuable comments, we have carefully considered one by one and revised accordingly. In the revised paper, all changes have been highlighted in blue in the manuscript and detailed in the response letter.

Thank you again for your help comments

Best Wishes

Authors

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

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