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Paper summary
TimeSpur reframes cross-variable dependency modeling in multivariate time-series forecasting as a predictive-utility routing problem rather than a correlation-discovery problem. It has four parts: (i) an independent per-variable forecasting branch (instance normalization, moving-average decomposition, low-rank variable-specific modulation) that produces a base forecast P0 and a state encoding H; (ii) an offline directed candidate graph built once from the training split via Top-K one-step lagged correlation; (iii) paired stochastic masking, where one sampled source variable per instance is removed and the resulting error increase (measured against the observed future) yields edge-level utility supervision u*; and (iv) a state-conditioned utility router that scores candidate edges from observed history only, binary-gates positive-utility edges, and aggregates their states into a sparse residual Δs. At inference only history is used (no masking, no future). Experiments on 8 benchmarks report "best in 11/16" dataset-metric comparisons, an efficiency study (0.17M params), ablations, routing case studies, and a 3-seed robustness check.
Critical strengths
- Novel, well-motivated framing. Separating dependency discovery (cheap correlation candidates) from dependency validation (outcome-grounded utility) is conceptually clean, and the paired-masking trick obtains supervision of one source against all targets from a single extra forward pass, avoiding O(C) masking. This is the paper's most consequential idea and the basis for its appeal.
- Strong efficiency with honest analysis. 0.17M parameters, lowest-class latency/memory, a controlled accuracy-vs-sparsity trade-off, and candid limitations/appendix diagnostics (including acknowledging noisy utility labels). This raises confidence and broadens practical applicability.
Critical weaknesses
- Marginal, weakly-established empirical gains. Improvements over the strongest baseline are tiny and close to seed variance: ETTm2 Avg MSE 0.258 vs XLinear 0.259 (effectively a tie), ETTh2 0.342 vs 0.349, Weather 0.222 vs 0.225; TimeSpur actually loses on Traffic and ETTm1. Main Table 1 reports no seed variance, and the significance test (Appendix I) is only against XLinear on 4 of 8 datasets. The ablation margins are similarly small (ETTm1 full 0.291 vs Independent 0.297), and notably "Dynamic w/o Utility" (0.298) is no better than no routing at all — undercutting the claim that the mechanism is essential.
- The central premise is not convincingly evidenced. Utility labels are noisy single-window counterfactuals: Appendix Table 6 shows active edges have positive measured utility only 52.3% of the time, with ~1e-4 magnitude. Since the router is trained on exactly this signal, the claim that it "activates only edges with positive predictive gain" is not demonstrated at the edge level. Combined with the one-step linear candidate graph, fidelity to the stated goal is uncertain.
Questions for authors
- Protocol: were all ten baselines retrained under the same L=320 look-back, splits, and tuning, or copied from their original papers? This directly affects fairness of all comparisons.
- Please reconcile the Table 1 vs Table 4 discrepancies (ETTm1 MSE avg; Weather MAE avg).
- Can you report seed standard deviations for the main Table 1 results, and a significance test against all baselines (not only XLinear)?
- Given Table 6 (52.3% precision, near-zero magnitudes), in what sense is the gate better than chance per edge, as opposed to only at the group level?
- Why is "Dynamic w/o Utility" worse than "Independent" on ETTm1? Does the router destabilize when masking supervision is removed?
5 comments
Response to Q1: We sincerely thank the reviewer for raising this important concern regarding experimental fairness. We would like to clarify that all baseline comparisons follow consistent experimental settings, including the same input sequence length (L = 320), dataset splits, and data preprocessing procedures, to ensure the comparability of the reported results. Regarding the sources of the baseline results: XLinear and EMAformer: We retrained and evaluated these two models using their official implementations under the same experimental settings, with the input sequence length fixed at L = 320. Other baseline models: Their results were adopted from the baseline comparisons reported in TimeMosaic, rather than directly copied from their respective original papers. These results also correspond to an input length of L = 320 and follow consistent dataset splits and preprocessing settings. Furthermore, to improve experimental transparency and reproducibility, we have explicitly clarified the sources of the baseline results and their corresponding experimental settings in Appendix D of the revised manuscript, allowing readers to verify and reproduce the comparisons. We sincerely appreciate the reviewer's valuable suggestion regarding experimental rigor.
Response to Q2: We sincerely thank the reviewer for identifying the inconsistencies between Tables 1 and 4, specifically regarding the average MSE on ETTm1 and the average MAE on Weather. Table 4 contains the latest experimental results, and we inadvertently overlooked updating the corresponding values in Table 1. We have now corrected these values in Table 1 to ensure consistency between the two tables. We apologize for this oversight and greatly appreciate the reviewer's careful examination of our manuscript.
Response to Q3: We sincerely thank the reviewer for this valuable suggestion. We agree that reporting standard deviations across random seeds and extending statistical comparisons beyond XLinear would provide a more comprehensive evaluation of the reliability of our experimental results. To address this concern, considering the limited time available, we selected five representative and competitive baselines: XLinear, EMAformer, PatchMLP, iTransformer, and TimeMixer, for additional multi-seed experiments. We repeated the experiments using three random seeds (2024, 2025, and 2026) across eight benchmark datasets and four prediction horizons (H ∈ {96, 192, 336, 720}), with the input length fixed at L = 320. We report the mean and standard deviation (Mean ± Std) of MSE and MAE for each experimental setting. The complete results are provided in Appendix I (Robustness across Random Seeds) of the revised manuscript. Furthermore, we extended the statistical analysis to all five selected baselines using two-sided paired t-tests, with Holm correction for multiple comparisons. The results demonstrate statistically significant improvements over PatchMLP, iTransformer, and TimeMixer in both MSE and MAE (adjusted p < 0.05). Although the differences compared with EMAformer and XLinear do not reach statistical significance, TimeSpur still achieves lower overall average MSE and MAE than both EMAformer and XLinear. These findings, together with the consistently small standard deviations across random seeds, further support the robustness and effectiveness of TimeSpur. The detailed experimental results and statistical analysis are provided in Appendix I. Overall, the additional experiments demonstrate that TimeSpur maintains low variability across different random seeds while achieving competitive forecasting accuracy. We sincerely appreciate the reviewer's constructive suggestion, which has helped us strengthen the experimental evaluation and improve the transparency of our manuscript.
Response to Q4: We sincerely thank the reviewer for raising this important question. We acknowledge that the 52.33% positive-utility precision indicates that the model does not achieve highly accurate edge-level utility prediction. Nevertheless, compared with random selection, the learned gate exhibits a modest discriminative advantage, achieving a balanced accuracy of approximately 54.47%. Furthermore, the positive-utility rates of activated and suppressed edges differ by 25.80 percentage points. We would like to clarify that utility-based routing aims to favor relationships with higher expected predictive utility, rather than guaranteeing positive realized utility for every activated edge. For further discussion of the utility supervision mechanism and the interpretation of Table 6, please refer to our Response to W2.
Response to Q5: We sincerely thank the reviewer for raising this important question. We would like to clarify that the inferior performance of Dynamic w/o Utility does not necessarily indicate training instability. Instead, it highlights the difficulty of identifying beneficial cross-variable dependencies without explicit utility supervision. The Independent variant relies exclusively on each variable's historical information, thereby avoiding potentially redundant or misleading information from other variables. In contrast, Dynamic w/o Utility introduces additional cross-variable interactions, but its routing decisions are learned only through the final forecasting loss. This indirect supervision makes it more difficult to determine whether an individual dependency actually contributes to improving prediction accuracy. Consequently, the router may activate relationships that introduce redundant information or estimation noise, causing the additional modeling flexibility to yield limited benefits or even slightly worse forecasting performance. Importantly, suboptimal routing decisions should be distinguished from training instability. Removing masking-based utility supervision does not eliminate the training signal, as the router continues to be optimized through the final forecasting loss. To further investigate this concern, we conducted additional training diagnostics across three random seeds. None of the runs exhibited NaN/Inf losses or gradients, and the final-epoch gate-flipping rates of the Dynamic w/o Utility variant ranged from 0.33% to 1.15%. We also observed no evidence of gradient explosion or loss divergence. These results suggest that removing masking supervision does not lead to apparent numerical instability or persistent gate oscillations in our evaluated runs. Therefore, the primary role of masking-based utility supervision is not to guarantee training convergence, but to provide a more direct signal for evaluating the predictive contribution of individual dependencies. By comparing forecasting errors with and without a candidate relationship, it helps the router distinguish beneficial interactions from redundant or potentially harmful ones.
Finally, we would like to once again express our sincere gratitude to the reviewer for the time and effort devoted to evaluating our manuscript, as well as for the valuable comments and constructive suggestions. We have carefully considered each of your concerns and further improved the manuscript through additional theoretical analysis, experimental results, and clarifications. We sincerely hope that our responses have adequately addressed your concerns and that you will reconsider your evaluation of our work. We greatly appreciate your time and thoughtful feedback.
Response to W1: We sincerely thank the reviewer for these valuable comments. To address the concerns regarding limited performance improvements and variability across random seeds, we conducted additional experiments using three random seeds and five competitive baselines. The complete results, including the mean, standard deviation, and statistical analysis, are provided in Appendix I (Robustness across Random Seeds) of the revised manuscript. Regarding the ablation results, we have further clarified why Dynamic w/o Utility may underperform Independent. Please refer to our detailed responses to Q3 and Q5 for the additional experimental evidence and explanations.
Response to W2: We sincerely thank the reviewer for this important and insightful comment. We agree that the results in Table 6 require a more careful interpretation, particularly regarding the relationship between masking-based utility supervision and the actual predictive contributions of activated edges.
We would like to clarify the objective of utility-based routing. The utility estimator is designed to learn the expected predictive contribution of candidate relationships from historical observations, rather than perfectly predict the sign of the realized utility for every individual test window. Since utility targets are obtained through paired masking on individual windows, they may be affected by sample-specific fluctuations. Consequently, even when a relationship has positive estimated utility, its realized contribution may still be negative on certain unseen windows. Table 6 provides evidence of group-level utility discrimination, although it does not establish perfect edge-level selection. Specifically, 52.33% of activated edge instances exhibit positive measured utility, compared with only 26.53% of suppressed instances, representing a difference of 25.80 percentage points. Furthermore, the mean measured utility of activated edges is +1.43 × 10⁻⁴, whereas that of suppressed edges is −4.08 × 10⁻⁴. These results suggest that the learned routing decisions are associated with differences in measured predictive utility, although individual decisions do not always agree with the signs of their realized utilities. We acknowledge that 52.33% positive-utility precision is insufficient to support the stronger claim that every activated relationship provides a positive forecasting gain. We have therefore refined the corresponding discussion to distinguish selection based on expected utility from guaranteed positive realized utility at the individual-edge level. Regarding the candidate graph**, lagged correlation is employed as an efficient prior for identifying potentially informative temporal relationships, rather than as a direct estimate of predictive utility. The subsequent utility-based routing mechanism evaluates these candidates according to the current historical state. Therefore, candidate construction and dynamic activation serve different purposes:
In summary, we acknowledge that the current diagnostic results support a more limited conclusion than perfect edge-level utility identification. The results demonstrate a directional association between routing decisions and measured utility at the group level, while the effectiveness of the overall mechanism is evaluated through forecasting performance and ablation experiments. We have clarified this distinction and revised the corresponding statements to avoid overstating the precision of individual routing decisions. We sincerely appreciate the reviewer's constructive criticism, which has helped us present the motivation, empirical evidence, and limitations of the proposed mechanism more accurately.