acceptodds
Under review as a conference paper at ICLR 2027

MoSiLa: Moment–Signature Landmarks for Multivariate Time Series Classification

Abstract

Regional compression reduces the cost of time series attention, but the resulting tokens determine which amplitude and order information remains available. We introduce MoSiLa (Moment–Signature Landmarks), a classifier that represents a learned feature field through multiscale means, temporal moments, and low-rank path coordinates. Two relation-aware attention blocks operate on at most 85 landmarks. An independent random-kernel expert provides an alternative representation, with training out-of-fold predictions selecting a single route or a mixture. Across all 30 UEA datasets, the complete MoSiLa system achieves 78.739% macro-average accuracy, the highest among 18 measured baselines under heterogeneous, TEST-selected training recipes. Every listed fixed-recipe ablation has a lower macro-average, with numerical reductions of 0.330–2.248 percentage points. A separate TRAIN-loss-selected evaluation yields 76.570% ± 0.439% across three seeds, exceeding the three-seed averages of MultiRocket, HYDRA, and their combination under the recorded preprocessing recipes. External results show numerical gains over the additional measured comparators but remain below the strongest included literature reports. These findings distinguish the performance of a complete classifier from the empirical utility of its representation choices.

Primary area:
learning on time series and dynamical systems
Keywords:
multivariate time-series classification, temporal landmarks, path signatures, moment representations, relation transformers

Reviews

Among:
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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_Ycj8OpenReview ↗
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2
Confidence
4
Informativeness
2
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2
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2
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Paper summary

The paper proposes MoSiLa, a multivariate time series classifier with two independent routes. The neural route uses an Inception-style convolutional encoder and compresses the feature field into at most 85 landmark tokens. Each token carries a regional mean, a signed temporal moment, a low-rank path displacement and signed area, and geometry. Two relation-aware attention blocks process the tokens, and the q = 1 token is the readout. The pattern route is a HYDRA-inspired random-filter expert with a ridge readout. A fixed rule, chosen from 5-fold out-of-fold training predictions, picks neural-only, pattern-only, or one of three mixtures per dataset. On all 30 UEA datasets the paper reports 78.739% macro-accuracy, the highest among 18 re-run baselines. It also reports ablations, a TRAIN-loss-selected evaluation (76.570 ± 0.439, 3 seeds), and two external datasets.

Critical strengths

The paper reports primary TEST-selected results alongside a TRAIN-loss-selected supplement. It also reports measured versus published baseline scores, all per-dataset results, retuned ablations, and a depth study. This is what makes the evaluation issues below identifiable at all.

Adding a fixed-feature route that is chosen from training predictions helps substantially on some datasets. The neural-only variant A07 loses 22.9 points on EigenWorms and 22.1 on EthanolConcentration. If properly controlled, the finding that learned and random-kernel routes are complementary per dataset would be useful to practitioners.

Critical weaknesses

MoSiLa's checkpoint is chosen by the combined predictor's TEST correct count, with ties updating the checkpoint. Table 7 illustrates the effect: selected epochs are 3 (FD), 3 (AF), and 4 (UW). When selection uses TRAIN loss, the score falls from 78.739 to 76.570 ± 0.439, a 2.17-point drop. The authors also state that earlier TEST access remains part of the development history. So even the 76.57 figure is not an untouched-test estimate.

Table 11 shows all 16 baselines with full-UEA30 references scoring 1.3–6.7 points below their published values (e.g., TimeMixer++ −6.7, MambaSL −6.2, Crossformer −6.0, TimesNet −5.8, HYDRA −5.8). The two baselines with partial reference coverage (Non-stationary Transformer, TimeFilter) are also lower in raw terms, though coverage differs. Published scores for MambaSL (79.819) and ConvTran(79.207) are above MoSiLa's 78.739. Some measured cells look like run failures rather than method weakness. Examples are TSCMamba on SAD(70.987 vs. 95.816 reported) and FEDformer on CT(68.593 vs. 97.284), each worth roughly 0.8–1 pp of that model's average. Measured HYDRA gets 64.885 on EigenWorms, while MoSiLa, which selects its HYDRA-inspired pattern route on this dataset, reaches 97.710, and the MambaSL-table reference for HYDRA is 98.473. Much of the margin over the classical baselines therefore looks like baseline measurement and not architecture.

MoSiLa uses five extra 100-epoch neural fits plus a 500-epoch final fit with patience 50. Most deep baselines use at most 100 epochs with patience 10, reuse recovered configurations without the original hyperparameter searches, and normalize TRAIN and TEST separately. No compute or runtime is reported. The paper states that its comparison is not an equal-budget attribution, but the abstract and conclusion still lead with highest among 18.

The margins over TSLANet and ConvTran do not survive Holm adjustment (adjusted p = 0.074). MoSiLa is top-1 on 11 of 30 datasets. The only TRAIN-based comparison (Table 1) includes only the three classical methods. None of the neural baselines (TSLANet, ConvTran, MambaSL) are re-run under TRAIN-based selection.

The primary results and ablations are single-seed(42). The three-seed SD of the full model is 0.439 pp (SD measured under TRAIN-loss selection, so only indicative), while the drops for removing path, moment, and relation bias are 0.330, 0.460, and 0.551. Their unadjusted paired p-values are 0.369, 0.452, and 0.160. Only A07 (removing the pattern expert) reaches p = 0.020 unadjusted, and that is the route component, not the landmark interface that the paper's contributions emphasize.

A few datasets drive the differences. On SRS1, A00 scores 91.468 while A02–A06 all score 85.666, which alone accounts for ≈0.19 pp (5.80/30) of their drops. FM (63.0 vs. 58–59) adds ≈0.15 pp.

For datasets where A00 selects the pattern-only route (Table 7), the neural ablations should be identical to A00. They are for EW, EP, ER, and SWJ, but not for EC(56.274 vs. 55.133 vs. 57.034), SRS1,or HB. This suggests the gate is re-selected for each variant, so the ablations mix architectural effects with route-selection variance.

There is no pattern-only variant, no fixed 50/50 mixture, and no comparison of OOF-gated selection against always-averaging, although the introduction motivates the gate by claiming that unconditional averaging can dilute the stronger predictor.There is also no ablation of the five candidates or of the fold-variation rule, which the paper itself calls a heuristic.

The retuned ablations (18–35 configurations per variant, search counts unequal) do not say which data the search selected on. If it was TEST, they are optimistically biased. Depth(1/2/3 blocks) also shows large single-dataset swings (PEMS 80.3/89.0/86.7; SRS1 85.7/91.5/85.7) with p = 0.140 and 0.057.

Questions for authors

Which data split did the retuned ablations (Table 9) select on? How were the search spaces and search counts chosen?

What do the A01–A06 variants do with the gate? Is the route re-selected per variant? Why do EC, SRS1, and HB differ across variants when A00 selects the pattern route, while EW, EP, ER, and SWJ do not? What is the selected route for each variant?

What are the seed means and standard deviations (at least three seeds) for A00 and A01–A07 under TRAIN-loss selection, with paired tests, so the landmark-component effects can be compared with seed noise?

Please report a pattern-only variant, a fixed equal-mixture variant and the neural-only variant under the same selection protocol. Does the out-of-fold gate outperform always-averaging?

Please re-run the main deep baselines(TSLANet, ConvTran, MambaSL, TSCMamba) under a TRAIN- or validation-based checkpoint rule with a matched epoch budget, or explain why this is infeasible. Can the anomalous cells(TSCMamba on SAD, FEDformer on CT, TSLANet on IW, where the measured 55.860 contrasts with a reported 10.012 that looks like chance level) be audited?

What is the training and inference cost(wall-clock time or FLOPs) for the full system compared with the baselines? The bounded-token argument covers only part of the cost.

A direct comparison with Rough Transformers is acknowledged as missing. Can you add one, or a signature-only ablation using the same encoder?

On the external datasets, ADFTD seeds range from 44.955 to 57.660(standard deviation 4.59), so the 1.755-point margin over Crossformer is below one standard deviation. FLAAP uses a window-level random split. Do these results support any claim beyond comparable?

What is the route-selection stability across seeds, per-dataset variation in selected routes, and uncertainty in the performance differences?This would help determine whether the learned gate captures repeatable dataset characteristics or responds to small-sample variation.

4 comments
AuthorsOpenReview ↗

Response to Reviewer Ycj8 (1/2): Selection and ablations

We appreciate the reviewer’s careful examination of the selection procedure, ablations, and experimental comparisons. The revision includes a common training-side selection protocol, complete three-seed TRAIN-loss ablations, additional routing controls, and subject-disjoint external evaluation. We describe the corresponding evidence below.

Q1. Selection split and search budgets for the retuned ablations

We have withdrawn the original retuning table and its component-ordering claim. That study used 18–35 trials per variant, while the selection split and the reason for the unequal trial counts were undocumented.

In the replacement study, every variant uses the same four learning-rate/weight-decay configurations, batch size 16, and a 200-epoch cap. Candidates are fitted on partition FF of official TRAIN. Partition VV selects by validation accuracy, followed by negative log-likelihood and fixed tie rules. Appendix B.2 specifies the search and checkpoint procedure, and Appendix I distinguishes this protocol from the historical study.

Q2. Gate reselection for A01–A06 and differences when A00 selects the pattern expert

Yes. Each full-system variant reselects its route using training-side out-of-fold predictions. Consequently, an ablation can select a different route even when A00 selects the pattern expert alone.

For example, on EC at seed 44, A00 selects pattern-only, whereas A05 selects equal mixing. Their reselected-system predictions can therefore differ. With A00’s pattern-only route frozen, both instead use the same pattern predictions and obtain identical results.

Table 10 reports the selected routes, and Figure 3 separates full-system reselection from neural-only and frozen-gate evaluation. For a frozen conditional gate, the fitted parameters remain fixed, while its inputs and resulting mixture weights are recomputed from each variant’s neural predictions. This distinguishes route reselection from changes in the neural branch under a fixed gate function.

Q3. Complete three-seed TRAIN-loss ablations and paired tests

We have added all eight variants on 30 datasets with seeds 42–44 in Tables 18–19. This experiment changes the neural checkpoint criterion to minimum mean TRAIN cross-entropy; hyperparameter selection continues to use TRAIN-internal validation.

VariantTRAIN-loss accuracy (%)A00 minus variant (pp)pHp_H
A00 — Full model78.153 ± 1.166——
A01 — Remove path term77.543 ± 0.4310.6091.000
A02 — Remove temporal moment77.743 ± 1.0130.4101.000
A03 — Remove relation bias77.008 ± 0.7571.1440.415
A04 — Mean readout77.338 ± 1.1170.8140.535
A05 — Maximum readout78.055 ± 0.4960.0971.000
A06 — Last-token readout77.357 ± 1.1590.7960.917
A07 — Neural branch only77.443 ± 0.4620.7090.535

The SD summarizes the three seed-specific macro-averages. Tests use 30 paired dataset differences after averaging over seeds, with Holm correction across seven contrasts. None of the TRAIN-loss contrasts passes correction.

Under validation-based checkpoint selection, relation-bias removal is the only full-system component contrast that passes the seven-comparison correction: 1.342 pp, pH=0.020p_H=0.020. Separately, Table 15 reports descriptive dataset-exclusion sensitivity for this validation-selected component study: excluding SRS1, excluding SRS1 and FM together, and leaving out each dataset in turn. We have restricted the component conclusions to the conditions in which they are supported.

Q4. Individual experts, equal mixing, candidate selection, and the fold penalty

Using the same calibrated expert pair, Table 8 reports:

Routing policyAccuracy (%)
Full selector78.733
Neural expert only77.894
Pattern expert only75.915
Fixed equal mixture77.752

The selected system improves over pattern-only by 2.818 pp and equal mixing by 0.980 pp, both with pH=0.026p_H=0.026. Its 0.839-pp difference from neural-only remains inconclusive (pH=0.105p_H=0.105). These values use Holm correction across the three routing contrasts.

We also report two controls for the selector itself. Restricting the candidates to the two single experts and equal mixing gives 78.667%, a descriptive difference of 0.066 pp from the full selector. Removing the fold-variation penalty gives 78.714 ± 0.941%, a descriptive difference of 0.019 pp.

The penalty is a selection heuristic, not a confidence bound. These controls do not establish a statistically significant benefit from the penalty or the two additional mixture candidates. The principal supported routing result is the improvement over fixed equal averaging.

AuthorsOpenReview ↗

Response to Reviewer Ycj8 (2/2): Baselines, costs and external evaluation

Q5. Strong baselines and the specifically questioned dataset results

The four primary deep baselines now use the same training-side selection protocol as MoSiLa. The paired comparisons favor MoSiLa over ConvTran, MambaSL, and TSCMamba after Holm correction; the TSLANet comparison remains inconclusive (pH=0.057p_H=0.057, Tables 1 and 5).

For the questioned dataset results, Table 20 reports 96.771 ± 0.984% for TSCMamba on SAD, 96.309 ± 0.000% for FEDformer on CT, and 58.435 ± 0.916% for TSLANet on IW.

We also clarified the source of 10.012%: it is TSLANet’s InsectWingbeat accuracy in the MambaSL authors’ re-evaluation, reported in Appendix C.1, Table 5(b), p. 21 of their conference paper. It represents a separate evaluation condition.

For EW, the added comparison gives 94.402 ± 1.166% for HYDRA, above 82.697 ± 4.473% for MoSiLa’s pattern expert. These targeted comparisons are reported alongside the primary results.

Q6. Full training and inference costs

For the five-method primary comparison, median end-to-end time is 2,280.2 s for MoSiLa, compared with 1,974.9–1,984.3 s for the four primary baselines.

The accounting includes preprocessing, hyperparameter search, out-of-fold fitting, final fitting, pattern and gate computation where applicable, and evaluation. Tables 11–12 provide the stage breakdown, latency, and memory. MoSiLa’s median inference time is 0.625 ms per sample, with both experts computed.

The 85-token bound limits attention interactions, while MoSiLa’s median end-to-end runtime is higher than those of the four primary baselines under this protocol. Appendix F specifies the accounting scope; independent runtimes for the auxiliary controls are not separately reported.

Q7. Rough Transformers and a same-encoder signature-only comparison

We have included both comparisons. Rough Transformers achieves 76.282 ± 0.802% and is reported descriptively.

The controlled neural-branch comparison gives 77.894 ± 0.450% for the full landmark representation and 76.414 ± 0.684% for signature-only. The paired advantage is 1.479 pp, with a pointwise 95% CI of [0.652, 2.307] and pH=0.001p_H=0.001.

Appendix M and Table 21 specify the full 90-coordinate signature, matched encoder architecture and paired initialization, retained attention and readout, and independent end-to-end training. This comparison evaluates the two complete representation constructions; the corresponding results and tests are in Tables 2 and 5.

Q8. External evaluation with subject separation and uncertainty

We have replaced the earlier external comparison with subject-disjoint evaluation against ConvTran. ADFTD uses 54/16/18 training, validation, and TEST subjects; FLAAP uses 4/2/2. All windows from a subject remain together, including in the inner checkpoint and out-of-fold splits. Five fitting seeds repeat training on each fixed partition (Appendix G).

On ADFTD, the paired subject-average accuracy difference is +4.844 pp, with a 95% CI of [0.757, 9.119] and pH=0.033p_H=0.033. On FLAAP, the difference is −1.816 pp, favoring ConvTran, with only two held-out subjects.

Inference uses held-out subjects as the paired units after averaging fitting seeds; the five seeds do not increase the number of independent subjects. The evidence supports an advantage on the ADFTD split, while FLAAP provides an unfavorable estimate with limited inferential resolution. Tables 5 and 13 and Figure 5 report these results.

Q9. Stability of route selection across seeds

Under validation-based checkpoint selection, 8 of 30 datasets select the same route for all three seeds. Across the 90 selections, neural-only is selected 48 times, pattern-only 15 times, equal mixing 13 times, conditional mixing 12 times, and constant mixing twice.

Figure 4 displays the three selections for each dataset, and Table 10 provides the detailed routes. We report this variation explicitly because it limits interpreting the selected route as a repeatable characteristic of a dataset.

Thank you to the authors for their rebuttal. However, I still have several concerns:

The headline result (78.739%) remains TEST-selected , while the TRAIN-loss supplement (76.570%) is only reported as a secondary result. The new three-seed TRAIN-loss ablations show no component contrast passing Holm correction, so the landmark interface's contribution is not statistically isolated from noise. The full selectors improvement over equal mixing is only 0.980 pp, and the neural-only comparison is inconclusive.

These unresolved concerns keep the paper below the acceptance bar. I will maintain my score (Rating : 2)

AuthorsOpenReview ↗

Follow-up on checkpoint selection and component comparisons

Thank you for raising the checkpoint issue. The abstract and Table 1 of the 18 November revision report 78.733 ± 0.854% as the primary result across 30 UEA datasets and three seeds. Hyperparameters and training duration were selected within official TRAIN, and calibration and routing were fixed before TEST scoring. The 78.739% TEST-selected result and the 76.570% TRAIN-loss result are both historical results retained in Appendix I, Table 16. Appendix I also discloses that the UEA TEST sets informed earlier development. Under the revised protocol, switching the checkpoint criterion to TRAIN loss while retaining validation-based hyperparameter selection gives 78.153 ± 1.166% (Table 18). Revised manuscript, Table 1, p. 6

We agree that none of the seven TRAIN-loss ablations passes Holm correction. The most direct evidence for the landmark representation comes from a separate validation-selected comparison in which both models use the neural branch alone. With matched encoder architectures and independent training, the complete landmark representation exceeds signature-only by 1.479 percentage points (pointwise 95% CI [0.652, 2.307], Holm-adjusted p=0.001p=0.001, Tables 2 and 5). This comparison tests the two complete representations. Table 17 also reports exploratory neural-only effects for removing the path coordinates and the temporal moment under validation selection. Whether those individual effects persist under TRAIN-loss checkpointing remains unresolved.

We also agree that the routing gain is modest. With the same calibrated experts, selection improves on fixed equal mixing by 0.980 percentage points (Holm-adjusted p=0.026p=0.026). Against the neural expert alone, the difference is 0.839 points (p=0.105p=0.105, Table 8). The evidence supports selecting a route over always assigning equal weights. An average benefit from adding the pattern route to the neural classifier remains uncertain.

Reviewer_c6cgOpenReview ↗
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1
Confidence
2
Informativeness
2
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1
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Paper summary

MoSiLa proposes a multivariate time-series classifier that compresses learned features into multiscale landmarks containing means, temporal moments, and low-rank path coordinates. Two relation-aware attention blocks process at most 85 landmarks. A separate random-kernel expert offers an alternative prediction route, and out-of-fold training predictions choose the neural route, the pattern route, or a mixture. The paper evaluates all 30 UEA datasets against 18 measured baselines, reports structural ablations and external datasets, and separately studies TRAIN-loss checkpoint selection. The complete system reaches 78.739% macro-average accuracy in its primary, TEST-selected condition. A three-seed TRAIN-loss-selected evaluation reaches 76.570% ± 0.439% and is compared directly with three classical baselines under the recorded preprocessing recipes.

Critical strengths

S1. The proposed interface combines multiscale amplitude summaries and path-order information in a bounded landmark set. This is a coherent way to study what regional compression preserves, beyond simply reducing the number of attention tokens.

S2. The paper is unusually explicit about evaluation limitations. It separates measured and literature scores, reports ablations and a TRAIN-loss-selected condition, and acknowledges that the main condition is TEST-selection-biased. These disclosures make the results easier to interpret and re-evaluate.

Critical weaknesses

W1. The primary evaluation selects the neural checkpoint according to the combined predictor's TEST correct count, with training permitted for up to 500 epochs. Although model parameters are optimized using training data, test labels directly influence checkpoint selection. This introduces selection bias and prevents the reported 78.739% average accuracy from serving as an unbiased estimate of generalization performance. The TRAIN-loss-selected evaluation decreases to 76.570% ± 0.439%, illustrating the sensitivity of the reported results to checkpoint selection. Furthermore, this supplementary evaluation compares MoSiLa against only three classical baselines rather than the strongest deep learning competitors. Consequently, the paper does not establish its central performance advantage under a consistently test-independent evaluation protocol. This is a major concern affecting the main empirical conclusion.

W2. The full system combines a neural landmark model with a strong independent random-kernel expert. Removing the pattern expert decreases average accuracy by 2.248 percentage points, whereas removing path coordinates or temporal moments produces smaller reductions of 0.330 and 0.460 points, respectively. Moreover, the final predictor selects the pattern expert alone on seven datasets. These observations suggest that a substantial portion of the system-level improvement may arise from expert complementarity rather than the proposed landmark representation. The absence of a direct comparison with closely related signature-attention methods, particularly Rough Transformers, further limits the evidence for the distinctiveness and effectiveness of the central representation contribution.

Questions for authors

Q1. Can the authors provide a fully test-independent comparison against the strongest deep learning baselines? The primary results use TEST-selected checkpoints, whereas the TRAIN-loss-selected experiments include only MultiRocket, HYDRA, and MR+Hydra. A matched evaluation against TSLANet, ConvTran, and MambaSL using validation-based checkpoint selection and comparable training budgets would materially affect my assessment of the paper's main empirical claim.

Q2. How much of the improvement is attributable specifically to Moment--Signature Landmarks rather than the random-kernel expert and route-selection mechanism? Can the authors provide a comparison of the neural-only MoSiLa branch against similarly sized convolution-attention models, as well as a comparison using the same pattern expert and gate with alternative neural backbones? This would help isolate the value of the proposed landmark representation.

Q3. How do the authors explain the substantial discrepancy between reproduced baseline performance and published results? For example, the measured MambaSL accuracy is 73.587%, compared with the cited published result of 79.819%. Can the authors clarify whether differences in preprocessing, hyperparameter search, checkpoint selection, or implementation are primarily responsible, and whether the main conclusions remain valid under a more closely matched protocol?

2 comments
AuthorsOpenReview ↗

Response to Reviewer c6cg (1/2): Evaluation protocol

We thank the reviewer for the detailed assessment and the suggestions on evaluation and component attribution. We have revised the primary comparison, added controlled representation and backbone comparisons, and clarified the relationship between the revised protocol and the earlier experiments. We address these points below.

Q1. Comparison with strong deep baselines under TEST-independent selection and comparable budgets

We have replaced the TEST-selected primary comparison with a protocol that selects hyperparameters and checkpoints using only official TRAIN. The UEA TEST sets informed earlier development, as disclosed in Appendix I; the revised selection procedure therefore does not make these benchmarks previously unseen.

The revised comparison covers MoSiLa, TSLANet, ConvTran, MambaSL, and TSCMamba on all 30 UEA datasets with seeds 42–44. All five methods use the same TRAIN-internal validation partitions, training-fitted preprocessing, four hyperparameter configurations, a 200-epoch cap, and a common dataset-specific total time allowance. Validation selects the configuration and final training duration. Calibration and routing are fixed before TEST scoring. The complete procedure is specified in Appendix B.2.

Tables 1 and 5 report:

MethodAccuracy (%)MoSiLa advantage (pp)Holm-adjusted pp
MoSiLa78.733 ± 0.854——
TSLANet76.843 ± 0.3371.8900.057
ConvTran76.219 ± 0.4192.5130.038
MambaSL75.711 ± 0.7923.0210.009
TSCMamba75.953 ± 0.7852.7790.009

Accuracy is the mean ± sample SD of the three seed-specific dataset macro-averages. Paired tests average seed differences within each dataset and apply Holm correction across the four baseline comparisons; differences are calculated before rounding.

Under this shared protocol, MoSiLa improves over ConvTran, MambaSL, and TSCMamba after correction. The comparison with TSLANet remains inconclusive. These results establish the comparison under the stated search space and resource budget, rather than each baseline’s best achievable performance.

AuthorsOpenReview ↗

Response to Reviewer c6cg (2/2): Attribution and MambaSL

Q2. Contribution of the landmark representation and comparison with an alternative backbone

To distinguish representation effects from the second expert, we added a comparison between the neural branches alone. The full landmark representation achieves 77.894 ± 0.450%, compared with 76.414 ± 0.684% for signature-only: a paired improvement of 1.479 pp, with a pointwise 95% CI of [0.652, 2.307] and pH=0.001p_H=0.001.

The two models use the same encoder architecture, paired initialization, regional partitions, attention blocks, and readout, and are trained independently. The signature control includes all 90 first- and second-level coordinates of a time-augmented nine-dimensional path. This comparison supports the complete landmark construction relative to that specified signature alternative (Tables 2, 5, and 21; Appendix M).

We also added an alternative neural branch comprising three temporal convolutions, up to 85 single-scale mean tokens, two four-head attention blocks, and a learned-query readout. Appendix E specifies the layers and parameter-counting convention. Including the classifier, this alternative has 8,216 fewer trainable parameters, corresponding to 1.08–1.63% across datasets and falling within the stated 5% matching tolerance.

ComparisonMoSiLa (%)Alternative (%)Paired difference (pp)pHp_H
Neural branch alone77.89476.9560.9380.107
Same pattern expert, calibration, and frozen gate78.73378.0710.6610.107

For the second comparison, we retain the pattern predictions, calibration, and fitted gate parameters, while recomputing neural-dependent gate inputs from the alternative branch. Both backbone comparisons remain inconclusive (Tables 2, 5, and 9).

Finally, the selected system improves over equal mixing by 0.980 pp (pH=0.026p_H=0.026); its 0.839-pp difference from the neural branch alone remains inconclusive (pH=0.105p_H=0.105, Table 8). Together, these controls provide evidence for the landmark representation relative to signature-only and for route selection relative to equal averaging. They do not identify an additive contribution from every component.

Q3. Discrepancy with the published MambaSL results

We agree that this discrepancy requires explicit accounting. Appendix I now distinguishes three results: 73.587% in our historical comparison, 75.711 ± 0.792% under the revised protocol, and 79.819% in the MambaSL reference paper.

The historical comparison used TEST-dependent checkpoint selection, different epoch and patience limits across methods, separate normalization of the splits, and recovered baseline configurations. The reference paper used seed 2021 and a 240-configuration search. The revised experiment instead applies the shared four-configuration search and resource budget described above.

The revised MambaSL result remains 4.108 pp below the reference. The available comparisons do not isolate the contributions of preprocessing, search, seed, and implementation to this gap. We have therefore limited the conclusion to the comparison directly supported by the revised experiment: under the declared common protocol and budget, MoSiLa exceeds MambaSL by 3.021 pp (pH=0.009p_H=0.009, Tables 1 and 5).

Reviewer_1NTsOpenReview ↗
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4
Informativeness
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Paper summary

This paper proposes MoSiLa for multivariate time-series classification. MoSiLa represents time series using landmarks that capture feature values and temporal order at multiple scales, and applies an attention mechanism to learn relationships between these landmarks. MoSiLa also employs a neural classifier and a random-kernel classifier, and selects either classifier or a mixture of them based on out-of-fold performance on the training data. Experimental results on 30 UEA datasets demonstrate that the proposed method achieves competitive classification performance compared to existing methods.

Critical strengths

None

Critical weaknesses
  1. Motivation is unclear.
  2. Although the authors raised two research questions, they do not address why such research questions are challenging and important.
  3. There is insufficient explanation regarding how the proposed method addresses the research questions.
  4. The paper is difficult to understand due to the frequent use of ambiguous terms such as "moment-signature landmark", "fixed-cardinality landmark interface", and "TEST-selected neural checkpoint".
  5. The Methods section only describes the computational processes without clearly explaining the necessity of each component.
  6. The contribution is unclear. The proposed method appears to be a combination of various techniques focusing on improving classification performance.
  7. The Experiments section lacks sufficient results to support the contributions of this paper.
  8. It is difficult to determine whether the experimental setups for the proposed method and the baselines are identical or whether the reported performance allows for a fair comparison.
Questions for authors
  1. Why are the research questions important, and what specific problems do the authors focus on?
  2. How does the proposed method address the research questions?
  3. What are the contributions of this study?
  4. Please specify the role and necessity of each of the four design choices in the Method section.
  5. How did the authors select the model for evaluation without a validation dataset?
  6. Were the proposed method and the baselines evaluated under the same experimental setup? Do the reported classification results allow a fair comparison?
  7. What are the "Common 10 datasets", and why are the results presented separately from those of the 30 datasets? What insights do these results provide?
  8. How do the results presented in Figure 3 have relevance to the contribution of this paper?
  9. Can you provide additional experimental results to support the method design and contributions of this paper?
4 comments
AuthorsOpenReview ↗

Response to Reviewer 1NTs (1/2): Motivation, design and selection

We thank the reviewer for the suggestions on the motivation, design rationale, and presentation of the experiments. We have revised the introduction and experimental organization to connect the research questions to the method and to the comparisons that evaluate its contributions. The main clarifications are as follows.

Q1. Problems motivating the study

Sections 1 and 3 now state two research questions.

First, how can temporal progression within an encoded region be retained in a bounded set of regional tokens? A regional mean is unchanged when the encoded feature vectors within that region are reordered. Features with the same mean can therefore differ in their temporal progression. This question concerns order within the encoded region: the convolutional encoder can already capture local order.

Second, how should a learned classifier be combined with a random-filter classifier when their relative performance varies across datasets? This motivates a selection procedure that can retain either expert alone as well as consider mixtures.

Q2. How MoSiLa addresses these problems

MoSiLa constructs at most 85 regional tokens across four temporal resolutions. Each token combines a regional mean, a signed temporal moment, low-dimensional displacement and signed-area coordinates, and region geometry. Two attention blocks exchange information across regions, and the updated whole-sequence token supplies the neural prediction.

A second expert uses independent random-filter features. Training-side out-of-fold predictions then select either expert or a mixture before TEST evaluation. Section 3 and Figure 1 describe the representation and selection stages.

Q3. Main contribution

The representation contribution is a bounded regional token construction that combines feature level with selected order-sensitive statistics. The classifier contribution is a training-based route selector that includes both experts as standalone candidates.

We now evaluate these contributions separately. The same-encoder signature comparison evaluates the regional representation (Table 2), while the single-expert and equal-mixture comparisons evaluate the routing procedure (Table 8). This organization makes the evidence for each contribution explicit.

Q4. Roles of D1–D4

We have clarified the four design roles:

  • D1: represents regional feature level and temporal order using means, signed moments, and path coordinates.
  • D2: uses relative location and scale to relate regional tokens and aggregate information into the whole-sequence readout.
  • D3: supplies a second prediction from independent random-filter features.
  • D4: selects among the experts and mixture candidates using out-of-fold predictions.

Tables 6–9 evaluate these roles. Under validation-based checkpoint selection, relation-bias removal is the only full-system component contrast that passes the seven-comparison correction. Table 17 separately reports exploratory effects for the neural-only and frozen-gate views. We distinguish these settings when interpreting the component results.

Q5. Model selection for evaluation

Algorithm 1 and Appendices A.4 and B.2 now specify the complete procedure.

Official TRAIN is divided into fitting partition FF and validation partition VV. Validation selects the configuration and final training duration. Each base out-of-fold fit reuses the selected configuration and chooses its checkpoint within its own training complement. Calibration and route selection use the resulting out-of-fold predictions from FF.

The meta stage reuses one such prediction matrix. Its scores guide candidate selection and are not unbiased estimates of the complete two-level learner. The final experts are refitted on F∪VF\cup V, with calibration and routing fixed before TEST scoring. The appendices also specify the small-sample fallback rules.

AuthorsOpenReview ↗

Response to Reviewer 1NTs (2/2): Comparisons and design evidence

Q6. Consistency of the comparison conditions

MoSiLa and the four primary baselines share the 30 UEA datasets, TRAIN-internal partitions, seeds, training-fitted preprocessing, four-configuration search, 200-epoch cap, and dataset-specific total time allowance. Tables 11–12 report the realized costs.

Under this protocol, MoSiLa achieves 78.733 ± 0.854%. Comparisons with ConvTran, MambaSL, and TSCMamba pass Holm correction, while the TSLANet comparison remains inconclusive (pH=0.057p_H=0.057, Tables 1 and 5). Appendix I separately documents the earlier use of TEST during development. We limit the primary comparison to the declared selection procedure and budget.

Q7. Definition and purpose of “Common 10”

The subset comprises EthanolConcentration, FaceDetection, Handwriting, Heartbeat, JapaneseVowels, PEMS-SF, SelfRegulationSCP1, SelfRegulationSCP2, SpokenArabicDigits, and UWaveGestureLibrary.

These are the ten datasets used in the MambaSL summary. Table 3 identifies this subset in its first ten rows, and Table 4 reports the corresponding per-dataset results alongside the remaining UEA datasets. All ten already belong to UEA30. Our primary ranking and statistical inference use the complete 30-dataset suite.

Q8. How the revised Figure 3 supports the contribution

We have replaced the accuracy-profile similarity plot with paired component effects under three evaluation conditions: the full system reselects its route, the neural branch is evaluated alone, or A00’s gate is frozen. The full-system panel includes uncertainty intervals.

In the frozen-gate view, A00’s selected candidate, calibration, and fitted gate parameters remain fixed. Conditional gate inputs and resulting mixture weights are recomputed from each variant’s neural predictions. Figure 3 therefore separates effects associated with route reselection from changes in the neural branch under the fixed gate function.

Q9. Additional evidence for the design

The revision adds complementary controls that clarify both the supported contributions and their limits.

The same-encoder comparison supports the complete landmark representation over signature-only by 1.479 pp (pH=0.001p_H=0.001). The alternative convolution–attention backbone falls within the stated 5% parameter-matching tolerance on every dataset, while both backbone comparisons remain inconclusive (pH=0.107p_H=0.107).

Under TRAIN-loss checkpoint selection, none of the seven component contrasts passes correction. The subject-disjoint external comparison favors MoSiLa on ADFTD and favors ConvTran on FLAAP, where only two TEST subjects are available.

Together, these experiments support a specific empirical conclusion: the proposed regional representation improves over the stated signature-only control, and the full procedure outperforms three primary baselines under the shared evaluation budget. The revision reports the inconclusive and adverse comparisons alongside these gains.

Thank you to the authors for their detailed response. However, I still have several concerns.

The authors explain what the proposed method does, but they do not sufficiently establish why these problems deserve attention or how addressing them contributes to multivariate time series classification. Similarly, the necessity of the proposed architecture (D1-D4) is still insufficiently justified.

In addition, I have substantial concerns regarding the presentation and soundness of the paper. I believe that addressing the feedback during the rebuttal could help improve the paper.

Considering these unresolved concerns, I will maintain my score.

AuthorsOpenReview ↗

Follow-up on the motivation for D1–D4

Thank you for asking why these design choices matter for classification. Consider a window in which two distinct multichannel activations occur in the order u,vu,v for one class and v,uv,u for another. At the level of the encoded features, both windows have the same regional mean and position. If the class depends on which response comes first, that mean loses the distinction. The signed temporal moment in Eq. 1 changes when the two activations exchange places. D1 thus makes both feature level and temporal progression available within the 85-token budget. D2 lets attention relate a brief event to a longer interval through their relative positions and durations. Table 2 supports the complete regional representation over the matched-encoder signature control. For D2 specifically, removing the relation bias lowered mean accuracy by 1.342 percentage points under validation-based checkpoint selection (Holm-adjusted p=0.020p=0.020, Table 5).

The motivation for D3 and D4 is visible in two of the submitted comparisons. Averaged over three seeds, the fixed-filter pattern expert leads the neural expert by 4.69 percentage points on EthanolConcentration. On FaceDetection, the neural expert leads by 7.02 points (supplement, data/backbone.csv). D3 makes the alternative pattern prediction available, and D4 uses out-of-fold training predictions to choose either expert or a mixture. Table 8 supports this choice over fixed equal averaging. Its advantage over the neural expert alone remains uncertain. We agree that the evidence supports specific design choices and leaves the individual necessity of all four components open.

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

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