- Rating
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- Confidence
- 3
- Informativeness
- 2
- Presentation
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- Soundness
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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
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It shows high performance among all models, even among statistics-based methods.
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It appears to be a good method built around the point that various window sizes should be utilized.
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It is good that it achieves high performance on the current benchmark and for anomaly detection by using the actual error and increments together.
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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.
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It uses TSB-AD, a benchmark widely used in time-series anomaly detection.
Critical weaknesses
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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.
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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.
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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
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Is it possible to provide the code?
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Can you show, based on data, that ‘when combined without calibration, the heavy-tailed score dominates the max’?
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It would be good to additionally conduct a sensitivity analysis on the k of kNN and the 5x5 setting.
4 comments
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.
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.
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.