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Under review as a conference paper at ICLR 2027

Generalist Representation, Specialist Detection: TS-Router for Time-Series Anomaly Detection

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Abstract

Time-series anomaly detection (TSAD) is difficult to generalize across datasets because heterogeneous temporal dynamics imply different notions of normality and favor different detection criteria. While time-series foundation models provide transferable representations, coupling them with a fixed anomaly-scoring mechanism can overlook this variation. This motivates a different perspective on foundation-model-based TSAD: using foundation models to coordinate specialized anomaly criteria rather than directly imposing a universal one. Based on this view, we propose TS-Router, a generalist-representation, specialist-detection framework that estimates the relative competence of heterogeneous anomaly detectors from pretrained temporal representations and selects suitable specialists for each target series. Since real routing labels are unavailable, we derive soft competence supervision from specialists' relative performance on labeled simulated tasks. At deployment, routing requires no target anomaly labels, and only the selected specialists are fitted unsupervisedly on the target series. Across 16 real-world benchmarks and four complementary evaluation metrics, TSRouter achieves the strongest overall ranking, supporting competence routing as an effective alternative to directly using foundation models as universal anomaly detectors. The code is available at https://anonymous.4open.science/r/TS-Router-D8FF.

Primary area:
learning on time series and dynamical systems
Keywords:
Time-Series Anomaly Detection, Time-Series Foundation Models, Algorithm Selection, Model Routing, Synthetic Data

Reviews

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1234this paper, Top 30%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_YofCOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

Motivated by the observation that different time series may favor different detection criteria, this paper proposes TS-Router, a framework that uses TSFM to extract representation and uses a trained router to select top-k best anomaly detector and perform detection. The router is trained by minimizing the KL divergence between its predicted competence distribution and soft targets derived from detector performance on synthetic data. Experiments on 16 TSB-AD benchmarks show the best average rank across four metrics.

Critical strengths
  1. The design is practical. “route-before-fit”(rbf) avoids running the whole pool on every target, needs no target labels, and the router is a simple MLP on a frozen encoder.

  2. Solid and comprehensive experimental evaluation. Tab 1 shows results across 16 benchmarks and 4 metrics, with comparisons against both FM based and unsupervised anomaly detection methods. The ablations in tab 2 are also fairly thorough, comparing adaptive routing with fix selection, different fusion, as well as different TSFM and handcrafted features. The appendix provides further analyses of detector complementarity, top-k selection, detector pool size, and routing supervision. The comparisons with classical selectors under three different transfer settings are also a nice addition.

Critical weaknesses
  1. There is limited modeling of cross-variable dependencies. The method handles multivariate time series through variable-wise routing and score aggregation, but it does not explicitly model interactions between variables, which may limit its ability to detect anomalies that arise from abnormal relationships across variables.

  2. The results on multivariate benchmarks in Tab 7 also somewhat lacks consistency.

Questions for authors
  1. There is a potential confounder in the encoder comparison. TimeRCD is pretrained using RCD synthetic data generation framework, which is also used to construct the router competence supervision. Its stronger routing performance in tab 2 may therefore partly come from this alignment, rather than better transferable temporal representations in general.

  2. Could you provide an end-to-end runtime comparison between TS-Router and full ensembling? Since TS-Router only fits three detectors instead of eleven, it would be better to see how much runtime is actually saved by the rbf strategy.

4 comments
AuthorsOpenReview ↗

Response to Reviewer YofC (Part 1 of 2)

Thank you for your thoughtful review. We appreciate your recognition of the practical value of our route-before-fit design and your positive assessment of the experiments and ablations. Your suggestions helped us clarify what the encoder comparison supports and quantify the time saved by routing before fitting. We have highlighted the changes in the revised PDF. We first respond to your two questions.

Response to Q1. Thank you for raising this point. We agree that the shared simulation framework is relevant when interpreting TimeRCD’s performance. In the default run reported in Table 2 (seed 42), all three pretrained encoders achieve higher NDCG@3 and downstream VUS-PR than any of the conventional representations. Across the 11 univariate benchmarks, Chronos, MOMENT, and TimeRCD achieve NDCG@3 scores of 0.698, 0.721, and 0.782, respectively, compared with 0.674 for the strongest conventional representation on this metric (Catch22). Their VUS-PR scores are 53.27, 53.89, and 56.36, compared with 51.31 for the strongest conventional result (MiniRocket). As you suggest, pretraining on data from the same simulation framework may partly explain TimeRCD’s lead over the other encoders; Table 2 does not isolate that effect. Chronos and MOMENT, however, were not pretrained with the RCD simulator. Their encoders remained frozen, and only their routing heads were trained on Syn-RCD competence targets, under the same protocol as the TimeRCD router. Notably, MOMENT even slightly exceeds TimeRCD on downstream Affiliation-F1 (88.50 vs. 88.11) and event-level F1 (49.74 vs. 49.62) in Table 2 despite having no exposure to RCD during pretraining. Their results support our broader conclusion: pretrained temporal representations can guide specialist selection even when the encoder was not pretrained with the simulator used to supervise the router.

Response to Q2. Thank you for suggesting an end-to-end comparison. We added a timing breakdown in Appendix B.2.8 (Table 14). Across the 11 univariate benchmarks, selecting three specialists before fitting them reduces mean runtime from 16.19 to 3.55 seconds per series, a 4.56× speedup over running all eleven specialists. Both measurements use the same hardware and include specialist fitting, scoring, normalization, and fusion. Of the 3.55 seconds for TS-Router, 3.52 seconds are spent fitting and scoring the selected specialists; all other steps, including encoding and routing, take about 0.03 seconds. On series with at least 100,000 observations, mean runtime falls from 138.16 to 29.10 seconds. TS-Router thus uses about 22% of the full ensemble’s runtime while improving mean VUS-PR from 49.54 to 56.36 on the same benchmarks (Tables 2 and 14). For comparisons with other detectors, including runtime, trainable parameter counts, and memory use, please see Table 15 and our response to Reviewer Jf2E’s Critical Weakness 5.

AuthorsOpenReview ↗

Response to Reviewer YofC (Part 2 of 2)

We now address the two concerns raised under Critical Weaknesses.

Response to Critical Weakness 1. We agree that channel-wise routing can miss anomalies that arise solely from changes in the relationships between variables, as noted in Section 6. For example, two sensors may fall out of sync while each still exhibits its usual temporal pattern. Our focus is on selecting specialists for the temporal behavior of each channel. A natural extension would be to use a joint representation of several channels to select specialists that model their interactions. For a fuller discussion, please see our response to Reviewer Jf2E’s Critical Weakness 4. There we discuss when channel-wise detection can be effective, examine the evidence across all five multivariate benchmarks, and explain how the routing framework could be extended to detect changes in cross-channel relationships.

Response to Critical Weakness 2. We appreciate your observation that TS-Router’s advantage varies across the multivariate benchmarks in Table 7. On VUS-PR, it ranks first on SMAP, second on PSM and SMD, and fourth on MSL and SWaT. It thus places among the top four on each dataset and achieves the highest mean VUS-PR (34.70) among the 15 methods when the five datasets are weighted equally. Its mean scores on the other metrics are also competitive: third on Standard-F1 and fourth on both Affiliation-F1 and event-level F1. For example, TS-Router ranks second on VUS-PR but eighth on event-level F1 on PSM, whereas on SWaT it ranks fourth on VUS-PR and first on Affiliation-F1. An independent analysis by Pinet et al., which included all five benchmark collections, found that changes in cross-channel correlation were often accompanied by a detectable deviation in at least one channel. This offers one reason why channel-wise routing can be useful on multivariate targets, even though its gains vary by dataset and metric. Your observation also points to a question we would like to study more directly: when does a multivariate system benefit from selecting specialists that model channels jointly? We plan to extend TS-Router to make that choice and evaluate it on faults that are detectable only through changes in cross-channel relationships.

Thank you again for your thoughtful review and constructive suggestions. We hope the additional experiments, analyses, and revisions address your concerns, and we would welcome any further questions or feedback.

As the discussion period is approaching its deadline, we would sincerely appreciate the opportunity to hear your thoughts on our response. We hope that the additional experiments and clarifications have addressed your concerns. Please feel free to raise any further questions or concerns, and we would be happy to address them while there is still time during the discussion period. We also welcome you to review our discussions with the other reviewers, where we provide additional explanations and results. Thank you again for your time and consideration.

Reviewer_YofCOpenReview ↗

Reply

Thanks for addressing my questions, and the clarifications did help. I would retain my positive rating.

Reviewer_Jf2EOpenReview ↗
Rating
2
Confidence
3
Informativeness
1
Presentation
3
Soundness
3
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Paper summary

The study proposes a new model for time-series anomaly detection, named TS-Router, which is based on pretrained time-series foundation models. Specifically, the authors use a pretrained foundation model to extract representations of time series and introduce a router model that learns to select the most suitable anomaly detectors based on these representations. The router is trained on synthetic time series with known anomalies, where the performance of different anomaly detectors is evaluated using VUS-PR to construct the training targets. During inference, the pretrained foundation model extracts representations from an unlabeled target time series, and the router uses these representations to select the three most suitable anomaly detectors. The selected detectors are then fitted independently on the unlabeled training data, and their normalized anomaly scores are averaged to produce the final anomaly score. The proposed method is primarily designed for univariate time series and is extended to multivariate settings by applying the same procedure independently to each series and averaging the resulting anomaly scores.

Critical strengths
  • (1) The idea of learning the relative competence of different anomaly detectors and using this information to select the most suitable detectors for each series is interesting.

  • (2) The experimental evaluation is comprehensive, covering multiple datasets and using several appropriate anomaly detection metrics.

  • (3) The paper is well organized and easy to follow.

  • (4) I appreciate the theoretical results provided, which address, to some extent, some of the main concerns arising from the proposed model design.

Critical weaknesses
  • (1) A central methodological concern is the reliance on synthetic datasets to learn which anomaly detectors are most suitable for real-world time series. Although the authors provide theoretical regret bounds under assumptions about representation coverage and the stability of detector competence between synthetic and real data, it is unclear to what extent these assumptions hold in practice. Real-world anomalies can exhibit patterns and characteristics that are not represented in the synthetic training data. As a result, detectors that perform well on synthetic time series with certain temporal characteristics may not necessarily perform well on real-world time series with similar characteristics but different anomaly patterns.

  • (2) The proposed method operates offline, as both the router and anomaly-score normalization use information from the test dataset. This limits its applicability to real-world scenarios requiring real-time anomaly detection. It also raises concerns about the fairness of comparisons with causal methods, which do not have access to future observations and may therefore be at a disadvantage. I encourage the authors to discuss these limitations and clarify the evaluation settings under which each baseline method is assessed.

  • (3) The paper does not specify how many independent runs were performed, and the reported results do not include standard deviations.

  • (4) For multivariate time series, the proposed method applies the routing and anomaly detection procedures independently to each variable and then aggregates the resulting anomaly scores. This may be limiting for real-world multivariate systems, where anomalies can arise from complex cross-variable dynamics and abnormal relationships between channels that cannot be captured by independent univariate modeling. Additionally, the synthetic datasets used to train the router are univariate, which raises concerns about generalization to multivariate settings. Univariate anomaly detection is generally a simpler task, while the main challenge lies in multivariate time series, which better reflect the behavior of complex real-world systems. I encourage the authors to discuss this limitation.

  • (5) Although the authors argue that the proposed approach reduces computational cost by fitting only the selected detectors, no quantitative analysis is provided to support this claim. Additionally, I would like to see more comparisons with recent non-foundation-model-based anomaly detection methods, as these approaches have also demonstrated strong performance. I encourage the authors to report training and inference times, the number of learnable parameters for non-foundation-model-based methods, and the memory requirements of foundation-model-based approaches to provide a more comprehensive comparison of computational efficiency.

Questions for authors
  • (1) I encourage the authors to include comparisons with more recent non-foundation-model-based anomaly detection methods, as the most recent baseline is from 2024. In particular, I would expect to see comparisons with relevant methods published at ICLR 2026, NeurIPS 2025, and ICML 2026. I also encourage the authors to discuss these recent approaches in the related work section, highlighting their differences from the proposed method.

  • (2) The router is trained using specialist competence measured exclusively by VUS-PR, while the final evaluation considers four different metrics. How sensitive is the router to the choice of competence metric? I encourage the authors to explain why VUS-PR was selected over other metrics and provide a sensitivity analysis examining how alternative competence metrics, such as Affiliation-F1 or F1T, affect specialist selection and anomaly detection performance.

7 comments
AuthorsOpenReview ↗

Response to Reviewer Jf2E (Part 1 of 4)

Thank you for your thoughtful review. We appreciate your interest in learning which detectors suit a given series and your positive assessment of the experiments and theoretical analysis. Your questions prompted us to test synthetic-to-real transfer more directly and to clarify the settings in which the results apply. We have revised the manuscript in response to your comments and highlighted the changes in the updated PDF so that you can easily locate the revisions discussed below. We first respond to your two questions.

Response to Q1. Following your suggestion, we added three recent non-foundation detectors and evaluated them on all 16 benchmarks: KAN-AD (ICML 2025), which uses a Fourier-based predictor to model temporal patterns; CATCH (ICLR 2025), which learns relationships between channels within frequency bands; and CrossAD (NeurIPS 2025), which models dependencies across temporal scales and windows. We discuss these methods in Section 2 and report their results in Tables 1 and 7. Each learns a scoring rule from the target data, whereas TS-Router uses supervision from simulated tasks to select specialists for each target and then fits those specialists on its unlabeled prefix. KAN-AD, CATCH, and CrossAD achieve mean VUS-PR scores of 31.93, 35.37, and 35.67, respectively, compared with 49.59 for TS-Router. With these baselines included, TS-Router retains the highest mean score on each of the four detection metrics.

Response to Q2. We chose VUS-PR as our default primarily because it is an established metric in time-series anomaly detection benchmarks such as TSB-AD and provides a common, threshold-independent basis for comparing specialists. It evaluates each detector’s continuous scores without requiring a separate alarm threshold for each detector or task. Its emphasis on precision and recall is also useful when anomalies are rare. To examine how much this choice matters, we changed only the metric used to construct the competence labels, keeping the frozen encoder, eleven specialists, Top-3 budget, fusion rule, and eleven evaluation benchmarks fixed (Appendix B.2.6, Table 10).

Competence supervisionVUS-PRAffiliation-F1Event-level F1Standard-F1
VUS-PR56.3688.1149.6247.73
Affiliation-F156.2788.4949.1746.83
Event-level F1 (F1T)58.2489.1753.0349.96
Standard-F155.2887.8350.0047.77

The advantage of adaptive selection is consistent across all four supervision choices: whichever metric supplies the competence labels, TS-Router outperforms both the hindsight-best fixed Top-3 and full-pool ensembling on all four primary detection metrics shown above (Tables 2 and 10). With specialist scores and the fusion rule held fixed, the differences reflect changes in the selected sets. Table 10 measures the effect of these changes on detection; it does not report how often the sets change. F1T supervision gives the highest scores in this ablation. We retain VUS-PR as the default because it lets us compare specialist competence without choosing an operating threshold.

AuthorsOpenReview ↗

Response to Reviewer Jf2E (Part 2 of 4)

We now address the concerns raised under Critical Weaknesses.

Response to Critical Weakness 1. We understand your concern and agree that, as with other approaches that learn from simulated time series, such as CauKer, ForecastPFN, and TimeRCD, our simulator may not cover all patterns encountered in practice. Simulation remains valuable in time-series research, where large real-world datasets with reliable annotations are often scarce. In our setting, varying the temporal background and anomaly mechanism lets us compare the same specialists across tasks and learn when one detector tends to outperform another. Your example illustrates the concern well: a synthetic series and a real series may exhibit similar temporal patterns yet contain different anomalies and favor different detectors. Theorem 1 allows for this possibility. It assumes that the synthetic distribution covers the relevant real representations and that, conditional on a given representation, each specialist’s mean competence is sufficiently similar across the two domains. An unseen anomaly pattern does not by itself rule out transfer: what matters is whether specialists that perform well in simulation also tend to perform well on real targets with similar representations. Representation similarity alone does not guarantee this correspondence. Table 2 provides evidence about specialist selection before score fusion. Across all 11 univariate benchmarks included under the criterion in Appendix B.1.1, the router trained solely on synthetic tasks achieves a Hit@3 of 0.632, compared with 0.532 for Best Fixed Top-3. With the same budget of three specialists, adapting the selection to each target thus increases the chance of including a best-performing detector by 10 percentage points. The downstream benefit varies across datasets: as discussed in our response to Reviewer s7yn, SR alone achieves 99.65 VUS-PR on Stock, compared with 73.18 for the fused TS-Router output (Table 9). Table 1 puts this example in perspective. Across all 16 benchmarks, TS-Router achieves the highest mean detection score and the best average rank on each of the four metrics, even though the router is not told which anomaly mechanisms occur in a target series or whether they are represented in simulation. Together, these results provide evidence that synthetic supervision can guide specialist selection on unseen targets and that this transfer has practical value for detection.

Motivated by your comment, we added a direct test of whether specialists that perform well on a target’s nearest synthetic neighbors also perform well on the target itself. For each target series, we retrieved its 32 nearest synthetic tasks in the frozen representation space and selected the three specialists with the highest mean VUS-PR on those neighbors. As a control, we kept the neighbors fixed but randomly permuted the complete competence profiles across synthetic tasks. This preserves each specialist’s overall performance distribution while breaking the link between a task’s representation and its competence profile. Target anomaly labels were used only to evaluate the selections. Alongside Hit@3, we report Top-3 selection loss: the difference between the mean individual VUS-PR of the target’s three best specialists and that of the three selected specialists. Both metrics evaluate selection before fusion. We averaged the control over 100 permutations and gave each benchmark equal weight. We also report results for the nine benchmarks remaining after excluding MGAB and TODS.

Keeping the original pairings increased Hit@3 from 0.4840 to 0.5058 and reduced selection loss from 0.2097 to 0.1481 across all 11 benchmarks. After excluding MGAB and TODS, Hit@3 increased from 0.4118 to 0.4478, and selection loss fell from 0.2314 to 0.1659, a 28.3% reduction. The observed loss of 0.1659 was also below the 2.5th–97.5th percentile range across the 100 shuffled controls (0.2060–0.2637). Thus, knowing which specialists performed well on similar synthetic tasks helped identify stronger specialists on the target benchmarks, beyond what could be inferred from the specialists’ overall performance distributions alone. This supports local transfer of specialist preferences on average, while allowing individual series with similar representations to favor different detectors, as in your example.

AuthorsOpenReview ↗

Response to Reviewer Jf2E (Part 3 of 4)

Synthetic evidence used for selectionAll 11: Hit@3 ↑All 11: Top-3 selection loss ↓9 excl. MGAB/TODS: Hit@3 ↑9 excl. MGAB/TODS: Top-3 selection loss ↓
Neighbors with shuffled competence profiles0.48400.20970.41180.2314
Neighbors with their original competence profiles0.50580.14810.44780.1659

Response to Critical Weakness 2. We agree that TS-Router, as evaluated here, operates offline. Table 1 evaluates retrospective detection: the task is to locate anomalies in an already observed series. As clarified in Section 4.3, the frozen router selects specialists from the complete unlabeled series. The selected specialists are fitted only on the training prefix, but we standardize their scores over the full evaluation suffix before fusion and rescale the fused scores over that same suffix. A score at time t can therefore depend on later observations, even though no target labels are used for routing, fitting, or scoring. All methods in Table 1 use the same target splits and retain their respective scoring procedures. TimeRCD, DADA, Chronos, MOMENT, TimesFM, and Time-MoE use pretrained inference without target fitting. OmniAnomaly, USAD, TranAD, TFMAE, DCdetector, KAN-AD, CATCH, and CrossAD are fitted on the unlabeled prefix and score the evaluation suffix using their respective implementations (Appendices B.1.2 and B.1.5). A common split does not imply equal access to future observations: a causal method uses only observations available by time t, whereas TS-Router can use the completed series. Table 1 thus supports a comparison on the retrospective task, not a ranking under matched real-time constraints.

For practical monitoring, a system could select specialists from historical data and reuse them as new observations arrive. For example, it could select and fit three specialists before a monitoring window begins, keep that set fixed throughout the window, and use the accumulated history to update the selection before the next window. This avoids rerunning the router at every timestamp. To issue alarms in real time, the specialists would also need to score each observation as it arrives, with normalization based only on past data. We have not evaluated this streaming variant. Under the offline protocol we did evaluate, Table 2 isolates the contribution of target-specific selection: the adaptive and fixed strategies use the same specialist scores, the same budget of three, and the same fusion rule. Adaptive selection achieves a mean VUS-PR of 56.36, compared with 47.44 for the hindsight-best fixed trio.

Response to Critical Weakness 3. We now report results across five independent router-training seeds (42–46). Table 2 retains the default single-run scores (seed 42) and reports the five-seed standard deviations in parentheses; Figures 3 and 4 show the five-seed means with bands of ±1 standard deviation. For the default Top-3 router, the results (mean ± SD) are 56.46 ± 1.26 for VUS-PR, 88.41 ± 0.80 for Affiliation-F1, 50.00 ± 1.12 for event-level F1, and 47.52 ± 1.31 for Standard-F1. Averaged across the five runs, selective routing retains a 6.92-point VUS-PR advantage over full-pool ensembling (56.46 vs. 49.54).

Reviewer_s7ynOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

Different anomaly detection methods are suitable for different time series. This paper proposes TS-Router, which first extracts data features using a pretrained model, then selects three of 11 detection methods, trains them separately, and combines their detection results. The selection policy is learned from labeled synthetic data, while anomaly labels are not used when selecting and training detectors on the target data. Experiments cover 16 benchmark datasets, with overall performance exceeding that of the compared methods.

Critical strengths
  1. The method has practical value, and its effectiveness is supported by experiments. Selecting detection methods based on data characteristics can reduce the need for manual selection. Across 11 univariate benchmarks, combining the three selected methods outperforms directly combining all methods, improving VUS-PR from 49.54 to 56.36.

  2. The comparisons and ablations are reasonably comprehensive. The paper compares foundation models, traditional detectors, and automated selection methods, and evaluates features extracted by three pretrained models.

Critical weaknesses
  1. The conditions under which a detector-selection policy learned from synthetic data transfers to real data remain unclear. The existing experiments do not specifically examine these conditions, and cases of poor performance receive insufficient explanation. For example, on Stock, TS-Router achieves a VUS-PR of 73.18, compared with 99.65 for SR alone.

  2. The stability and consistency of the results require further verification. The main experiments report results for only one random seed, without reporting variability across repeated runs. In addition, the results in Figure 4 for selecting three detectors from the full pool of 11 appear inconsistent with the default results in Table 2. The authors should clarify whether the configurations differ and explain the validation-set split and the basis for parameter selection.

Questions for authors
  1. What primarily causes the performance degradation on datasets such as Stock: selecting unsuitable detectors or combining their outputs? How do anomaly types unseen during training affect detector selection?

  2. Why do the results in Figure 4 and Table 2 differ under the default settings? Could the authors clarify the validation-set construction and parameter-selection procedure, and report the mean performance and variability across multiple runs?

  3. All three F1 metrics use test labels to select the optimal threshold. What detection performance and false-positive rates would be obtained using thresholding rules that do not require test labels?

Comments on the paper

5 comments
AuthorsOpenReview ↗

Response to Reviewer s7yn (Part 1 of 2)

Thank you for your thoughtful review. We appreciate your recognition of the practical value of selecting detectors for each target series, particularly your observation that combining three selected specialists outperforms ensembling all eleven. We are also glad you found the comparisons and ablations reasonably comprehensive. We believe your suggestions have strengthened the paper. We have revised the manuscript in response to your comments and highlighted the changes in the updated PDF so that you can easily locate the revisions discussed below. We first respond to your three questions.

Response to Q1. In response to your question, we added an analysis of all 20 Stock series that separates the loss due to specialist selection from the loss due to score fusion and compares anomaly recurrence on Stock with 50,000 synthetic tasks (Appendix B.2.10, Figure 5). SR was the best individual detector on every Stock series, yet the router consistently ranked it between 7th and 11th. Even choosing the best of the three selected detectors in hindsight yields a mean VUS-PR of only 76.67, compared with 99.65 for SR; fusion reduces the score by a further 3.49 points to 73.18. Thus, 86.8% of the gap to SR (22.98 of 26.47 points) arose before fusion. The clearest mismatch we found was in anomaly frequency: 88.3% of labeled test episodes were isolated spikes, and every Stock series had more episodes per 1,000 observations (44.95–122.84) than any synthetic task we audited (maximum 7.04). This difference may help explain why the router overlooked SR. In addition, 3.8–16.2% of observations in the fitting prefixes were labeled anomalous, which can make it harder for detectors to estimate normal behavior from the prefix; SR requires no such fitting. As for anomaly types unseen during router training, a new mechanism may still produce a pattern, such as a sharp local deviation, that a selected specialist detects well. Selection can suffer when the new mechanism instead favors a detector that the router ranks outside its Top-3. On Stock, the new analysis identifies the missed detector and documents the frequency shift, but it does not establish that the anomaly type itself was absent from training. We appreciate the question because it helps put the aggregate results in perspective. Both evaluations include Stock: adaptive selection achieved a higher mean Hit@3 than the best fixed set of three specialists on the 11 eligible univariate benchmarks (0.632 vs. 0.532; Table 2), and TS-Router achieved the highest mean detection score on each of the four metrics across all 16 benchmarks (Table 1). These results suggest that specialist preferences learned in simulation can guide selection on real targets on average. For an anomaly type unseen during router training, a new mechanism may still favor the same specialists if it produces a familiar temporal pattern.

Response to Q2. Thank you for catching this discrepancy. You were right to expect the full-pool result in Figure 4 to agree with the default setting in Table 2. When we retrained the router for the original pool-size ablation, we inadvertently used a batch size of 256 instead of the 512 used for Table 2. The two results therefore came from different training configurations. We apologize for overlooking this mismatch. We reran the ablation with the default batch size of 512 across five seeds (42–46). At the shared setting of three selected specialists from a pool of eleven, Figures 3 and 4 now agree on all four metrics: 56.46 ± 1.26 VUS-PR, 88.41 ± 0.80 Affiliation-F1, 50.00 ± 1.12 event-level F1, and 47.52 ± 1.31 Standard-F1 (mean ± SD). Table 2 retains the original seed-42 scores and reports the five-seed SD in parentheses; its VUS-PR of 56.36 is the single-run score, while 56.46 is the five-run mean. We also clarified the validation protocol in Section 5.1 and Appendix B.1.5. For the default router, we split 850,000 synthetic tasks into 765,000 training and 85,000 validation tasks, stratifying by the specialist with the highest VUS-PR on each task. We used the validation set only to monitor KL loss and retained the final checkpoint after 30 epochs, without early stopping or validation-based checkpoint selection. The eleven specialists use hyperparameters selected on TSB-AD’s held-out tuning split. KAN-AD, CATCH, and CrossAD follow their original configurations and use validation within the training prefix for early stopping. No target test labels were used for hyperparameter or checkpoint selection.

AuthorsOpenReview ↗

Response to Reviewer s7yn (Part 2 of 2)

Response to Q3. Thank you for raising this question. The main tables use test labels to select the threshold that maximizes each F1 metric. To evaluate performance when labels are unavailable for threshold selection, we added an offline comparison of all 15 methods on the 11 univariate benchmarks (Appendix B.2.9, Table 16). For each method and series, we set the threshold to the 95th, 99th, or 99.5th percentile of that series’ unlabeled test scores and flag timestamps whose scores exceed it. We use labels only afterward to evaluate the alarms. At the 95th percentile, TS-Router achieves an event-level F1 of 23.75, a Standard-F1 of 23.68, and an Affiliation-F1 of 70.89, with a false-positive rate of 3.74%. Raising the threshold to the 99th and 99.5th percentiles reduces the false-positive rate to 0.65% and 0.29%, respectively, while Standard-F1 falls to 18.29 and 17.60. Absolute F1 scores are lower under fixed percentiles than under oracle thresholding. The anomaly rate ranges from 0.2% to 10.6% across benchmarks (Table 3), so the same alarm budget can be restrictive on some targets and generous on others. Although TS-Router’s Affiliation-F1 ranking declines under fixed thresholds, it ranks first in both event-level F1 and Standard-F1 and achieves the lowest false-positive rate at each of the three thresholds.

We now address the two concerns raised under Critical Weaknesses.

Response to Critical Weakness 1. We agree that aggregate results alone do not tell us when a selection policy learned in simulation will transfer. For an anomaly type unseen during router training, the key question is whether it changes which specialists are effective. A new mechanism may still produce a pattern that the selected specialists detect well, whereas selection can suffer if it favors a detector that the router ranks low. As discussed in our response to Q1, Stock illustrates the latter kind of ranking mismatch: the router missed SR on all 20 series. The shift we observed there was in how frequently anomalies recurred, rather than evidence that the anomaly type itself was absent from training. Our new analysis asks whether specialists that perform well on similar synthetic series also tend to perform well on a real target. Theorem 1 identifies two relevant conditions: synthetic tasks should cover the representations encountered on real targets, and each specialist’s mean competence at a given representation should remain sufficiently similar across domains. This does not require two similar series to share an anomaly type or a best detector. Across all 11 eligible univariate benchmarks, the trained router improves Hit@3 from 0.532 for the best fixed trio to 0.632 (Table 2). To examine transfer more directly, we held each target’s 32 nearest synthetic neighbors fixed and compared selections before and after shuffling competence profiles across synthetic tasks. On the nine benchmarks remaining after excluding MGAB and TODS, preserving the original pairings reduced mean Top-3 selection loss by 28.3%, from 0.2314 to 0.1659. In other words, knowing which specialists performed well on similar synthetic tasks helped us select specialists whose individual VUS-PR was closer, on average, to that of the target’s three best detectors. We report the full comparison in our response to Reviewer Jf2E, Critical Weakness 1.

Response to Critical Weakness 2. We agree that a single run gives limited evidence about stability. Across five training seeds (42–46), selecting three of the eleven specialists yielded a mean VUS-PR of 56.46 (SD 1.26), compared with 49.54 for full-pool ensembling. The advantage of selective fusion therefore persists when averaged across runs. Our response to Q2 explains the original discrepancy, reports the corrected results, and details the validation and parameter-selection protocols.

We hope these analyses and revisions address your concerns, and we would welcome any further questions or suggestions.

As the discussion period is approaching its deadline, we would sincerely appreciate the opportunity to hear your thoughts on our response. We hope that the additional experiments and clarifications have addressed your concerns. Please feel free to raise any further questions or concerns, and we would be happy to address them while there is still time during the discussion period. We also welcome you to review our discussions with the other reviewers, where we provide additional explanations and results. Thank you again for your time and consideration.

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

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