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Under review as a conference paper at ICLR 2027

Aggregation Scale Shapes Anomaly-Duration Bias: Bounds, Readout Effects, and a Nonparametric Detector

Abstract

Anomaly duration can change which time-series anomaly detectors perform best, yet aggregate benchmark scores obscure this variation. Across 40 published detectors on TSB-AD, relative performance varies with duration even after controlling for file fixed effects, and all three pretrained forecaster families favour short anomalies. Under stationary normal increments, a shift-invariant statistic reading w consecutive increments has expected coverage at most min1, 2w/L + α on a flat level shift of length L at false-alarm rate α: detecting an anomaly's presence is distinct from covering its interior. Short-anomaly sweeps reveal empirical dilution under the tested aggregations. Controlled interventions on two frozen pretrained forecasters separate conditioning context, forecast horizon, and score aggregation. Over the tested grid, widening aggregation from 1 to 64 samples at a fixed one-step horizon extends the post-peak half-maximum duration by roughly an order of magnitude in matched configurations with nonzero peak coverage; context has smaller effects. Increasing horizon yields a similar extension. The combined effect is sub-additive on the log-duration scale, and wider readouts reduce peak coverage. On TSB-AD-U, the same aggregation substantially reduces the relative short-anomaly bias of both frozen forecasters. These findings motivate a nonparametric multiscale detector that combines calibrated short- and wide-scale evidence by a maximum. Without gradient training, it achieves competitive offline performance against tuned deep models on TSB-AD-U and TSB-AD-M under the reported development protocol. The results identify aggregation and readout as practical controls on duration bias and support duration-aware evaluation.

Primary area:
learning on time series and dynamical systems
Keywords:
time-series anomaly detection, anomaly duration, aggregation scale, time-series foundation models, multiscale anomaly detection, statistical detection theory

Reviews

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1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_zWe2OpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
1
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2
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Paper summary

The authors emphasize the importance of varying the window size in existing time-series anomaly detection studies and propose an anomaly detection method that utilizes increments and various window sizes. As the background of the method, they present five propositions, showing that in anomaly cases where only the mean changes, anomaly models operating on increments exhibit limitations with a fixed window.

To compute the anomaly score at time t, the method combines point-based and window-based anomaly scores. The point-based anomaly score is the score obtained by converting the time point into two dimensions, increment and actual value, and then performing kNN (k=3) against normal (increment, actual value) points. For the window-based anomaly score, the ranges of the increment and the actual value are first divided into 5 on a window basis, and then a grid is generated. For the windows extracted with various window sizes, if they belong to one of the 16 cells formed by the 25 grid points, the grid values of that cell are set to 1, so that each window is formed into a 25-dimensional binary vector. For each window, kNN is performed on the binary vector, and the results are calibrated and then averaged. The max of the point-based and window-based scores is used as the final anomaly score.

As of the most recent point (2026-09), the method shows excellent performance, ranking within the top 3 on both TSB-AD-U and TSB-AD-M.

Critical strengths
  • It shows high performance among all models, even among statistics-based methods.

  • It appears to be a good method built around the point that various window sizes should be utilized.

  • It is good that it achieves high performance on the current benchmark and for anomaly detection by using the actual error and increments together.

  • Although the strong performance of increment-based models in anomaly detection has already been demonstrated (Zhu et al.), proposed increment-based model achieves high performance.

  • It uses TSB-AD, a benchmark widely used in time-series anomaly detection.

Critical weaknesses
  • Overall, the paper is difficult to read.

    • Starting from the abstract, the descriptions, such as the expected coverage of the statistic and peak coverage, are not reader-friendly.
    • The appendix is also referenced repeatedly in the main text, which somewhat diminishes the purpose of the 9-page limit.
    • The font sizes of the tables are not consistent.
  • The theoretical background is weak.

    • Props 2, 3, and 4 all make claims about a limited anomaly type, namely level shift. The assumption of exact adaptation in Props 3 and 4 also does not seem obvious.
    • Prop 5 states the obvious point that a detector that considers a finite number of channel relationships cannot detect anomalies that appear only in the relationships between channels.
  • The final method is heuristic.

    • It seems to be a proof only to the extent that one should not use increments alone. Since the actual method is not forecasting-based, it seems unrelated to Props 3 and 4.
    • The mean and standard deviation used in TSB-AD-U and TSB-AD-M are also different.
    • The authors put forward the intuition that ‘when combined without calibration, the heavy-tailed score dominates the max,’ but did not verify this intuition.
Questions for authors
  • Is it possible to provide the code?

  • Can you show, based on data, that ‘when combined without calibration, the heavy-tailed score dominates the max’?

  • It would be good to additionally conduct a sensitivity analysis on the k of kNN and the 5x5 setting.

4 comments
AuthorsOpenReview ↗

Presentation, Theory, and Standardisation

Response overview: Thank you for identifying the presentation and design issues. We now state the fixed-prediction contribution first, supported by four forecasters and four metrics (§3.4; Table 21; Appendix C.5). We separate the theory from empirical choices and report added U/M calibration and sensitivity analyses. We also provide the Table 4 scoring code. U and M denote TSB-AD-U and TSB-AD-M; reported intervals are 95% paired file-bootstrap intervals. All section, appendix and table references refer to the revised manuscript.

Critical Weaknesses

W1. Readability and presentation

The revised exposition states the result before the technical definitions: The abstract and introduction explain that wider error averaging improves long-anomaly performance at a short-anomaly cost while predictions remain fixed. Section 3 defines coverage as the fraction of anomalous samples flagged and distinguishes peak coverage from a duration range measured against each configuration's own peak. Section 5 explains the components, calibration and combination before referring to implementation details.

We clarified the representation and presentation: Each increment/value pair distributes weight to neighbouring grid nodes; a node is marked occupied if its accumulated weight is positive. A 5×5 grid therefore produces 25 binary node indicators, not 16 cell indicators (§5; Appendix B.2). The five main-text tables use a consistent font size; the main text remains 10 pages and the complete PDF 44 pages. The September ranks were 3rd of 41 on U and 2nd of 31 on M; October ranks are 7th of 45 and 5th of 33. We date these comparisons rather than claim a current top-three position (Table 28).

W2. Scope and role of the theory

The theory links window width to a specific coverage limit: Proposition 2 shows why detecting a level shift's boundaries does not ensure interior coverage, and gives a necessary window-width condition for a target coverage. This conditional result requires a flat level shift, increment-only statistics and stationary normal increment-window distributions. WidthLadder uses both increments and signal values, so Proposition 2’s coverage bound for increment-only statistics does not directly apply to it (§3; Appendix A). Low bound-exceedance rates in §4 do not verify stationarity.

Adaptation is a condition for extending the argument to forecast residuals: Propositions 3–4 assume normal-like joint residual-block distributions after a shift; decreasing individual residuals does not establish this. Adaptation concerns the response to inputs, not weight updates. Section 3.4 tests aggregation empirically; these propositions do not derive the representation or fusion rule of the separate, non-forecasting WidthLadder detector.

Proposition 5 offers limited motivation for joint-channel tests: If only the joint distribution changes while every smaller channel subset remains normal, a statistic reading such a subset cannot distinguish the change. This elementary observation neither rules out jointly combining per-channel scores nor proves our joint-channel features beneficial. Their benefits require empirical testing, and failed design predictions remain reported (§6; Appendix C.13).

W3. Heuristic choices and different U/M standardisation

The U/M standardisation difference arose during development, rather than from track-specific tuning: Ablations provide empirical evidence for the grid, neighbour count k and fusion rule; the theory does not establish their optimality (Q3; Tables 23–26 and 31). U uses whole-series mean/standard deviation, whereas M uses the reference prefix. Both retain whole-series grid ranges and therefore offline information.

The added control finds small mean change but large individual effects: Applying M's standardisation to 347 U files, excluding three constant-prefix files, changes mean VUS-PR by −0.0028 [−0.0105, 0.0037]. This does not establish equivalence: 20 files change by more than 0.01, including one from about 0.99 to 0.02 (Table 32; Appendix C.13).

Calibration does not remove this limitation: Input standardisation rescales observations; score calibration uses their reference-score distribution. A fixed stabilising constant for scores above the prefix maximum prevents exact scale invariance. Tables 4 and 17 report stricter prefix-based controls.

AuthorsOpenReview ↗

Code, Calibration Diagnostics, and Sensitivity

Q1. Code availability

Yes, the Table 4 WidthLadder U/M scoring code is provided: The anonymous supplementary_code.zip includes the implementations and execution instructions for generating per-sample anomaly scores. The complete benchmark-evaluation pipeline, remaining experimental and analysis code, and supporting materials will be released upon acceptance (Appendix B.6).

Q2. Do heavier-tailed scores determine the maximum more often?

The diagnostics do not support the heavy-tail explanation; the observed calibration gain remains: The short-scale component has the larger finite-sample tail proxy in 94.9% of files, yet the multiscale component usually supplies the larger scores near the top of the fused-score distribution (Table 30; Appendix C.13).

We measured tail shape and actual score dominance separately: The proxy compares the reference-prefix 99.9th and 99th percentiles relative to the median; it does not establish asymptotic tail ordering. Among fused scores at or above the 99th percentile, including ties, the multiscale score strictly exceeds the short-scale score on over 90% of samples in 82.6% of files before calibration and 82.3% afterwards. Thus the larger proxy does not predict which component supplies most high scores.

Calibration's measured benefit remains valid without that explanation: Across all post-prefix samples, the median multiscale-win fraction falls from 0.70 to 0.49; VUS-PR increases by +0.009 [0.001, 0.019] with an unadjusted paired interval. This is an empirical gain, not validation of the heavy-tail mechanism. The pre-calibration comparison still uses robust z-scaling, and ties mean the selected upper-score set need not contain exactly 1% of samples (Tables 23 and 30).

Q3. Sensitivity to k and the grid

The analyses support k=3 over larger k and 5×5 over 3×3, but do not show that 5×5 is the best grid: On both U and M, k=3 gives higher mean VUS-PR than larger tested k values, and 5×5 improves over 3×3. The 5×5 grid has the highest tested mean on U, whereas 7×7 has higher means on M. Our central fixed-prediction aggregation finding does not depend on WidthLadder’s k or grid.

U sensitivity: Increasing k from 3 to 10 reduces mean VUS-PR from 0.5390 to 0.5148. Grid sizes 3×3, 5×5, 7×7 and 9×9 score 0.3930, 0.5390, 0.5319 and 0.5184. Paired intervals support losses for the coarse grid and larger k; finer-grid intervals include zero, establishing neither a difference nor equivalence. At k=1, self-matching makes prefix short-scale scores zero on 199 files, so its higher mean is not evidence of robustness (Tables 24 and 31).

The added M sweep covers all 180 files: Increasing k from 3 to 10 lowers VUS-PR from 0.4145 to 0.3991, a change of −0.015 [−0.027, −0.005]. The 3×3, 7×7 and 9×9 grids score 0.3768, 0.4222 and 0.4058. The 7×7 grid improves all four metric means on M: its VUS-PR gain of +0.008 has an unadjusted paired file-bootstrap interval [−0.0001, +0.0151] including zero, while the paired Wilcoxon test gives BH q=0.004 (q≤0.03 under each metric). The 9×9 grid lowers VUS-PR while improving ROC metrics. Appendix C.13 gives the full sweep, including intermediate k values. We retain the 5×5 setting selected on U; both U and M informed development, so these are sensitivity checks, not independent validation.

Thank you for the detailed response. The readability has improved compared with the previous version. The claims regarding the role of the theory, the heuristic design choices, and the heavy-tail explanation are now appropriately scoped, and the sensitivity analysis on k looks adequate.

However, while I appreciate that the paper investigates and experimentally tests a cause of the previously reported finding that detector rankings vary with the anomaly-duration distribution, I am not sure that this alone is sufficient for publication at ICLR. The experimental design also feels somewhat rough, as illustrated by the different standardisation used for TSB-AD-U and TSB-AD-M, and the proposed method still feels largely heuristic. My view is not negative, but I do not recommend acceptance of this paper.

AuthorsOpenReview ↗

Follow-up on Contribution and Experimental Scope

Thank you for taking the time to review the revised manuscript and share your further assessment. We would like to explain the evidence behind the design and why we believe the findings matter for detector evaluation.

The controlled experiments separate the effect of scoring from that of forecasting. With the model, forecast horizon and predictions fixed, changing only the aggregation width raises Chronos-Bolt's overall VUS-PR from 0.290 to 0.408 on the 350 TSB-AD-U files. Its rank moves from 26th to 9th against the same 40 benchmark methods (Table 3). This gain comes at a cost on short anomalies. We observe this trade-off across four forecasters and four metrics, with alignment controls on the original two models retaining the same direction (§3.4; Tables 3, 20–21; Appendices C.5 and C.13). The readout therefore matters when interpreting which anomaly durations a model handles well.

The analysis motivates combining scales with complementary duration profiles, and the ablations provide evidence for this choice. On TSB-AD-U, the multiscale component reaches 0.532 VUS-PR compared with 0.433 for width 100 alone (Remark 3; Table 16). We also test the fusion rule directly: replacing the reported maximum with a product reduces VUS-PR by 0.081, with a 95% paired file-bootstrap interval of [0.053, 0.109] (Tables 5 and 16). This supports the reported rule over the tested product on VUS-PR; it does not establish superiority over averaging. Table 5 distinguishes the design motivations from empirically selected choices and summarises the evidence for each. TSB-AD-U informed development, so these comparisons are not independent validation.

We agree that the different standardisation rules on TSB-AD-U and TSB-AD-M limit the consistency of the WidthLadder evaluation. Applying the TSB-AD-M rule to the TSB-AD-U files yields a small mean change but substantial changes on some files (Table 32), so we do not claim equivalence. The aggregation experiments do not use WidthLadder; they compare alternative readouts of the same saved predictions within each forecaster.

We believe that identifying how aggregation changes duration bias, and testing a design that combines complementary scales, provides useful guidance for both detector development and evaluation.

Reviewer_ZrUxOpenReview ↗
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1
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3
Informativeness
2
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Paper summary

This paper examines how anomaly duration and aggregation scale affect time-series anomaly detection. It analyzes 40 published detectors on TSB-AD and derives a conditional coverage bound for shift-invariant local statistics, distinguishing anomaly presence detection from interior coverage. Experiments on two frozen pretrained forecasters separate context, forecast horizon, and residual aggregation, showing that aggregation alone changes short- versus long-anomaly performance while predictions remain fixed. These findings motivate WidthLadder, a nonparametric multiscale nearest-neighbor detector. Validation combines controlled anomaly injections, real-anomaly width sweeps, and TSB-AD-U/M evaluations. The method achieves competitive offline performance without gradient training, although the reported benchmarks also informed its development rather than providing an independent final evaluation.

Critical strengths

S1. Separating prediction from score aggregation. By holding predictions fixed and varying only residual aggregation, the paper isolates the scoring rule’s effect on duration-dependent performance. This demonstrates why forecasting-based anomaly detectors should be compared with attention to both the underlying model and how prediction errors are converted into anomaly scores.

S2. Theoretical characterization of coverage limits. Under stationary increments in the normal process, Proposition 2 establishes an upper bound of min⁡1,2w/L+α\min {1, 2w/ L+\alpha} on coverage for shift-invariant local statistics applied to flat level shifts. The bound explicitly connects window width to anomaly duration and shows why increasing model capacity or shift amplitude cannot overcome interior indistinguishability within this class. This provides a principled account of a specific detection failure mode and a theoretical basis for distinguishing anomaly presence detection from interior coverage.

Critical weaknesses

W1. The mechanistic analysis insufficiently supports the proposed design and its benefits. The theory motivates using multiple scales but does not sufficiently explain the benefits of the specific representation and fusion rule. The final maximum-based fusion shows no statistically significant advantage over simple averaging and performs worse than the short-scale component alone on the shortest anomalies. Together with the failed design predictions reported in Section 6, these results leave unclear which validated design principles follow from the analysis, weakening confidence in the algorithmic contribution.

W2. The aggregation effects are insufficiently validated across metrics and implementation choices. Tables 3, 4 focus on VUS-PR, while the residual-aggregation experiments average errors within fixed blocks and assign the resulting score to every point in each block. It remains unclear whether the main effects persist under standard point-wise metrics or alternative block alignments and overlapping windows. This limits confidence that the observed performance changes generalize beyond the particular evaluation and score-assignment procedures.

W3. Independent evaluation of the final detector is lacking. TSB-AD-U informed the design choices, and the final TSB-AD-M result was obtained through sequential evaluations rather than an independent held-out test of the final detector. Although this is transparently disclosed, the reported rankings provide limited evidence that the empirically selected design generalizes to previously unseen data.

Questions for authors
  • Q1. Given the mixed design outcomes in Section 6, which theory-motivated design choices are empirically supported by the existing ablations? Please distinguish gains in overall performance from improvements in duration-specific weaknesses, particularly relative to the wide-scale component alone and simple averaging.

  • Q2. Using the same scores, labels, and duration groups as Table 3, which duration-dependent performance trends persist under point-wise AUROC and AUPRC without point adjustment, as well as VUS-ROC? Please also assess whether the main conclusions about WidthLadder and its ablations hold under these metrics using the available scores.

  • Q3. With predictions and residuals held fixed, do the aggregation effects persist when shifting block boundaries or using overlapping moving averages of the same width? Please compare absolute coverage and achieved FPR alongside the relative frontier L1/2L_{1/2}, using the same calibration procedure.

  • Q4. Does the relationship between optimal width and anomaly duration in Figure 1 persist on a common eligible event subset over a feasible range of widths, with reference-set sizes controlled? Separately, how sensitive is this relationship to values of kk other than 3?

  • Q5. Which design choices were fixed before the first TSB-AD-M evaluation, and which, if any, were changed after inspecting its results? Is there an evaluation of the finalized detector on data that did not inform these choices? If not, please clarify the resulting scope of the generalization claims.

5 comments
AuthorsOpenReview ↗

Design Rationale and Validation

Response overview: Thank you for recognising the fixed-prediction comparison. We added metric, alignment and component controls, and evaluated the frozen detector on SKAB. These results distinguish support for combining scales from evidence about particular design choices. U and M denote TSB-AD-U and TSB-AD-M. Duration groups use mean anomaly length in samples. Reported intervals are 95% paired file-bootstrap intervals; multiplicity adjustment is stated where applied. All section, appendix and table references refer to the revised manuscript.

Critical Weaknesses

W1. Mechanistic support for the detector design

Combining scales is supported; the representation and fusion rule remain empirical: On U, the multiscale component achieves 0.532 VUS-PR versus 0.433 for width 100 alone (Table 16). Adding the short-scale score gives a smaller gain, +0.007, which does not survive multiplicity adjustment and does not repair the shortest-anomaly weakness. Q1 reports these trade-offs.

The revised method explains what is combined: The short-scale score reads a value and its increment; the multiscale score averages calibrated block scores from several widths. Maximum fusion takes the larger score, while M also uses joint-channel scores. Section 5 and Appendix B.2 explain the construction; the theory does not determine these choices.

W2. Dependence on metrics and score assignment

Long-anomaly gains and short-anomaly losses persist under the added metrics and alignments. Four forecasters show long-anomaly gains and short-anomaly losses under four metrics. For the original two, shifting block boundaries and using overlapping averages preserves this direction with predictions fixed. Effect sizes vary and peak coverage falls. Q2–Q3 report the numerical checks (Appendices C.5 and C.13).

W3. Independent evaluation

SKAB provides an unused-source evaluation of the frozen detector: The detector and protocol were fixed before scoring all 34 files. U and M informed development. SKAB's files share one apparatus and three recording days, so they are not 34 independent replicates. Q5 gives the results and scope (§5.2; Appendix C.13).

AuthorsOpenReview ↗

Ablations and Additional Metrics

Q1. Which design choices are empirically supported?

Multiple widths help overall, but maximum fusion does not resolve the shortest-anomaly weakness: The multiscale component improves U VUS-PR from 0.433 at width 100 alone to 0.532. Adding the short-scale score through maximum fusion gains +0.007 [0.001, 0.015], but only before Benjamini–Hochberg (BH) adjustment. Adjusted gains occur in the two longest-duration groups (+0.022 and +0.028), not the weak 4–30 group (Tables 16 and 25–26).

The shortest-duration losses remain: The full detector outperforms the short-scale component overall, but the difference in the 1–3 group is −0.184 [−0.295, −0.082]. Against averaging the same two scores, maximum fusion has no established overall VUS-PR advantage and loses 0.046 in that shortest group. Averaging is also better under the three additional metrics (Q2).

M does not establish a preferred fusion rule: Holding joint-channel scores fixed, maximum-minus-average comparisons have intervals including zero under all four metrics. This leaves the differences unresolved, rather than demonstrating equivalence. The ablations support the tested scale combination, not an optimal representation, scale set or fusion rule (Appendix C.13).

Q2. Results under VUS-ROC, AUROC and AUPRC

The forecaster trade-off persists; maximum fusion is not consistently better than averaging: The three additional metrics also retain WidthLadder's overall advantage over short-scale-only. We use the same saved predictions, labels and duration groups, without point adjustment. A64 averages 64 residuals; A1 scores one. The slope measures metric change with log duration: a positive A64-minus-A1 change favours longer anomalies, not every duration.

All four forecasters show positive slope changes: The A64-minus-A1 changes are:

ForecasterVUS-ROCAUROCAUPRC
Chronos-Bolt+0.020+0.020+0.122
TimesFM 2.0+0.020+0.022+0.138
Time-MoE+0.039+0.035+0.093
Moirai+0.020+0.021+0.134

Scope of these comparisons: All nominal 95% paired intervals exclude zero. These slopes are not relative to the 40-detector mean. The original two models' ROC slopes remain negative; their shortest-group AUPRC falls to about 0.05. The added-model metric analyses are post-hoc, and the intervals are not multiplicity-adjusted (Table 21; Appendix C.5).

WidthLadder gains do not imply maximum fusion is best: On U, averaging exceeds maximum by approximately 0.002 VUS-ROC, 0.002 AUROC and 0.033 AUPRC, with unadjusted paired intervals excluding zero. Maximum still exceeds the short-scale component overall under all four metrics; its AUPRC difference from product fusion is unresolved (Table 23).

The added M analysis separates component removal from fusion: Rescoring all 180 files reproduces archived VUS-PR/VUS-ROC within 1.2e-16. Short-scale-only changes VUS-PR by −0.088 [−0.118, −0.060] and lowers the other metrics by 0.055–0.090, all surviving BH adjustment. Multiscale-only differs by −0.002 VUS-PR [−0.023, +0.020] overall; its 4–30 group difference is −0.074, with only seven files and an interval including zero. Both variants also omit joint-channel scores, so these are not isolated scale effects.

Changing only M fusion leaves the advantage unresolved: With identical joint-channel scores, average-minus-maximum is −0.002 [−0.007, +0.003], with intervals including zero for all four metrics. Removing joint-channel scores gives −0.017 [−0.032, −0.005], but the paired Wilcoxon test gives BH q=0.11. Appendix C.13 details the M comparisons; M informed design, so these post-hoc checks are not independent validation.

AuthorsOpenReview ↗

Alignment, Width Controls, and Evaluation History

Q3. Alignment, absolute coverage and achieved FPR

Yes, changing alignment preserves the trade-off with predictions and residuals fixed: For Chronos-Bolt and TimesFM, we shifted block boundaries and tested centred and trailing moving averages. At anomaly duration 64, A64 raises coverage—the fraction of anomalous samples flagged—from about 0.08 to 0.18–0.29. At duration 1, it lowers coverage from 0.73–0.81 to 0.03–0.19 (Table 20).

The longer relative range does not imply uniformly better detection: The duration reaching half of each configuration's own peak increases by factors of 19–22 for shifted blocks, 12–13 for centred averages and 26–31 for trailing averages. These pooled summaries differ from Table 2's matched-configuration summaries, and peak coverage falls across the tested alignments (Table 20). In the original horizon/aggregation sweeps, some wide configurations never reach absolute coverage 0.25, so the registered absolute-frontier claim remains unconfirmed (§3.4; Appendix C.5).

Calibration controls the measured FPR, not an unseen-data guarantee: The same rule achieves empirical FPR ≤1% in every tested calibration condition, though rates are not identical across variants. Calibration uses normal-labelled samples from the evaluated series, so the result does not guarantee the same FPR on unseen normal data.

Q4. Common event cohort, reference counts and k

Yes, the width–duration relationship persists under these controls: On 1,456 events eligible at every width up to 128, the best widths across successive duration groups are 2, 8, 16, 64, 64, 128 and 128. They are unchanged at k=1 and 5; at k=10 only the longest group changes. Here k is the number of nearest reference neighbours. Fixing exactly 100 reference windows per width retains the pattern on 938 eligible events (Table 22; Appendix C.13).

The result concerns group averages within the tested range: The longest groups select the maximum tested width, so behaviour beyond 128 and per-event optimality remain unresolved. The k=3 result was known before expectations for the other controls were recorded and is post-hoc. Queries occur after the reference prefix, avoiding the k=1 self-match issue in detector calibration.

Q5. Development history and evaluation on unused data

The initial scale and fusion choices were fixed before M, but M is not an independent test of the finalized detector: Fusion, block widths and maximum across channels preceded the first M run. Calibration was selected on U before the second M run; joint-channel scores were introduced after earlier M evaluations. A fourth run did not adopt a Šidák correction (Appendix B.4).

The frozen SKAB evaluation adds unused-source evidence; U/M remain development benchmarks: All 34 labelled SKAB experiments were evaluated without outcome-based selection. After accounting for overlapping records and weighting the three days equally, maximum fusion scores 0.8145 VUS-PR versus 0.7386 for averaging with identical joint-channel scores; maximum is higher on each day (Appendix C.13).

SKAB supports a limited comparison: It covers one apparatus, three days and mean anomaly durations of 188–586. Maximum does not beat the better individual component on any day, and joint-channel scores change no final test score. We report descriptive differences without independent-file significance or short-anomaly generalisation. The offline protocol uses a separate 1,200-sample normal reference and whole-series grid ranges; it differs from the SKAB leaderboard protocol. The reference/test boundary increment sets a range extreme in 153 of 272 channel/file pairs and can affect the grid. Appendix C.13 gives the protocol.

The additional U files do not provide a clean independent test: The 34 additional U files also remain exploratory because of a duplicate pair, contaminated reference prefixes and shared UCR segments, including three matches to evaluation files up to their anomalies (§5.2; Table 33).

Reviewer_egddOpenReview ↗
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Paper summary

The paper claims that anomaly duration is a hidden axis of performance in time-series anomaly detection and that aggregate benchmark scores obscure it. Across 40 detectors on TSB-AD, relative performance varies with duration, and pretrained forecasters favour short anomalies. The authors prove a coverage bound showing that detecting an anomaly's presence differs from covering its interior, and show that widening score aggregation extends the detectable duration range at the cost of peak coverage. Based on this, they design widthladder, a training-free multiscale detector that is competitive with tuned deep models on TSB-AD-U and TSB-AD-M.

Critical strengths

The paper is easy to follow. The method to treat anomaly duration as an explicit evaluation axis is useful. Leaderboard rankings partly reflect a benchmark's duration composition, and the paper shows that this effect can be as large as the performance differences between top methods.

Critical weaknesses

The main concern is the novelty of the paper. The theory is thin and narrow in scope. Proposition 1 is the standard total-variation / Neyman–Pearson bound, as the authors acknowledge. Proposition 2 is a counting argument that requires a pure level shift, an increment-only statistic, and stationary increments, making it too restrictive. Proposition 3 holds only under exact or approximate adaptation. There is also substantial overlap with prior work. The horizon–duration trade-off, the max-over-horizons remedy, the strength of pretrained forecasters on short anomalies, and the use of duration as a regrouping axis on TSB-AD have all been proposed previously.

Questions for authors
  1. Does the duration-slope heterogeneity replicate on benchmarks outside TSB-AD, and with metrics other than VUS-PR?
  2. How do you separate duration effects from anomaly type and shape?
  3. Can the readout-intervention conclusions be extended to more forecasters (MOMENT, Time-MoE, Moirai)?
3 comments
AuthorsOpenReview ↗

Novelty and Theoretical Scope

Response overview: Thank you for recognising duration as a useful evaluation axis. Our contribution is to isolate how anomaly scoring changes performance with duration. We have clarified the prior-work distinction and theoretical assumptions, and added forecaster, metric and anomaly-type controls. All section, appendix and table references refer to the revised manuscript.

Critical Weaknesses

W1. Novelty and overlap with prior work

Our contribution isolates scoring from forecasting: We keep the model, forecast horizon and predictions fixed and change only residual averaging. On TSB-AD-U (U), averaging 64 residuals rather than one increases the relative duration slope by +0.078 [0.063, 0.091] for Chronos-Bolt and +0.083 [0.068, 0.099] for TimesFM 2.0 (95% paired file-bootstrap intervals). This slope measures performance against the 40-method file mean as log duration increases: the changes favour longer anomalies, with losses on short anomalies (§3.4; Table 3).

The distinction from prior work is explicit: Liu and Paparrizos (2024) established forecasters' strength on point anomalies; Zhu et al. (2026) studied the horizon–duration trade-off and maximum over horizons; Yeh (2026) compared short and long anomalies. Our fixed-prediction intervention tests a different effect. Our maxH baseline uses different residual and normalisation conventions from Zhu et al., rather than exactly reproducing it (Appendix D).

Coverage extends to longer anomalies at a cost: In matched configurations with nonzero peaks, averaging 64 rather than one residual increases the duration at half of each configuration's own peak coverage by factors of 11.3 and 13.0 for the two models. Coverage means the fraction of anomalous samples flagged. Peak coverage falls, so these factors are not proportional gains in the fraction detected (Table 2).

The broader analysis establishes observed heterogeneity: Thirteen of 40 detector slopes remain significant after within-source permutation tests and Benjamini–Hochberg (BH) correction: six negative and seven positive. File-level duration differences remain observational, not a duration-only causal experiment (§2; Table 1).

W2. Scope and strength of the theory

The theoretical contribution is a conditional width–duration limit on coverage: Proposition 1 is standard, and Proposition 2 uses a simple counting argument. It makes explicit why detecting a level shift's boundaries does not ensure interior coverage and gives a necessary window-width condition for a target coverage. This is not a sufficient detection guarantee. The bound requires a flat level shift, increment-only statistics and stationary normal increment-window distributions. WidthLadder uses both increments and signal values, so Proposition 2’s coverage bound for increment-only statistics does not directly apply to it (§3; Appendix A).

Controls support the mechanism within its scope: Coverage exceeds the bound in 0.8% of tested flat-shift conditions using centred, shift-invariant statistics, versus 64.5–94.1% when controls change the anomaly structure and/or permit amplitude information (§4). These are condition-exceedance rates, not false-positive rates; low exceedance does not verify stationarity of real prefixes.

Propositions 3–4 extend the argument only under forecaster adaptation: They require normal-like joint distributions of residual blocks after the shift. Adaptation means the response to inputs, not weight updates; decreasing individual residuals does not verify the condition. This gives a conditional link to forecaster scoring, while the fixed-forecast experiments test aggregation empirically. It does not derive WidthLadder's representation or fusion rule (Appendix A.8).

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Replication Scope and Anomaly-Type Controls

Q1. Replication outside TSB-AD and under other metrics

We have not replicated 40-detector heterogeneity on another benchmark or under other metrics: The common archive provides file-level VUS-PR values, not the per-sample scores needed for other metrics. Comparable results for all 40 detectors on another benchmark have also not been assembled. SKAB tests WidthLadder and its components, not the 40-detector comparison.

The separate aggregation result is supported across four forecasters and four metrics: With predictions fixed, averaging 64 residuals (A64) rather than one (A1) improves long-anomaly performance at a short-anomaly cost for Chronos-Bolt, TimesFM 2.0, Time-MoE and Moirai under VUS-PR, VUS-ROC, point-wise AUROC and AUPRC, without point adjustment. For the added Time-MoE and Moirai models, all six duration-slope changes under the three additional metrics are positive, with nominal 95% paired intervals excluding zero. Positive changes indicate a shift toward longer anomalies, not gains at every duration. These metric analyses are post-hoc and not multiplicity-adjusted (Tables 3 and 21; Appendix C.5).

Q2. Separating duration from anomaly type and shape

Duration-dependent differences persist within fixed shapes, with remaining prevalence and source limitations: We combine fixed-shape injections with type-adjusted benchmark analyses. The added injections fix the host, four onset positions, event count, amplitude coefficient and shape across nine durations (1–256), removing the original experiment's onset and event-count changes (Appendix C.13; §4 describes the original injections).

The controlled comparison shifts from POINT to SUBSEQ as duration increases: On 39 hosts from seven sources, the best observed POINT score minus the best SUBSEQ score has negative median host correlations with duration in all eight shape × metric conditions. Under VUS-PR, the correlations are −0.57 for shifts and −0.30 for noise; 36–39 hosts have negative correlations across the conditions (host-level Holm-adjusted p < 10⁻⁶). For shifts, the mean score difference changes from +0.13 at duration 1 to −0.12 at 256. This is an oracle comparison using each group's best observed result, not a deployable selector. POINT includes a width-100 hybrid; longer events increase anomaly prevalence, realised noise statistics vary, and hosts share sources.

Exclusion and covariate adjustment provide separate checks: Excluding 49 point-flagged files leaves significant 40-detector heterogeneity (within-source permutation p=0.0002). Separately, adjustment on all 350 files for the point-anomaly flag and the fraction of anomaly increments within the reference prefix's range gives forecaster slopes of −0.018, −0.013 and −0.014. Source-bootstrap intervals include zero for two models (Table 27). Restricting mean duration to above 30 also gives intervals spanning zero. We therefore do not establish a further relative forecaster trend in that range (Table 29).

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Additional Forecasters

Q3. Extension to MOMENT, Time-MoE and Moirai

Time-MoE and Moirai reproduce the long-anomaly gain and short-anomaly cost: We added Time-MoE 200M and Moirai 2.0-R small on all 350 U files at context 64. A64 averages the same predictions' residuals over 64 samples; A1 scores them individually.

Both satisfy the locally recorded pre-run criteria: Time-MoE's relative duration slope changes from −0.023 to +0.043, a gain of +0.066 [0.051, 0.080]; Moirai's changes from −0.073 to +0.015, a gain of +0.088 [0.071, 0.103]. These are nominal 95% paired file-bootstrap intervals. In the longest-duration group (1001+), VUS-PR rises from 0.401 to 0.566 and from 0.347 to 0.611, respectively; in the shortest (1–3), it falls from 0.574 to 0.270 and from 0.860 to 0.402. Both also meet the maxA criterion: combining normalised scores across widths without label-based selection scores no more than 0.01 below the better A1/A64 overall score. Appendix C.5 and Tables 3 and 12 give the criteria, checkpoints and full comparisons.

MOMENT remains untested because its comparison protocol is not yet fixed: We must first establish the reconstruction/forecasting setup and window-to-point scoring rule; changing these together with aggregation would mix their effects. Our conclusion therefore covers the four tested forecasters.

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