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Under review as a conference paper at ICLR 2027

Normal Support Imbalance: Correcting Support-Dependent Score Bias in Multivariate Time-Series Anomaly Detection

Abstract

Normal-only multivariate time-series anomaly detectors learn from nominally normal data, yet the resulting models may cover legitimate normal behaviors unevenly. We study this Normal Support Imbalance and find that weakly supported normal observations tend to receive higher raw anomaly scores, creating the potential for false-positive disparities under a shared threshold. We introduce RestoreAD, which uses Row-Uniform regularization to discourage concentrated normal-to-normal relations, retrieves normal references for both anomaly scoring and support estimation, and applies Cross-Support Normality Calibration (CSNC). CSNC aligns training-score medians across support bins while exactly preserving within-bin rankings. On the official TSB-AD-M Eval split, RestoreAD achieves the highest mean on each reported metric among the compared baselines. Diagnostic analyses show that CSNC weakens the dependence of normal anomaly scores on estimated support difficulty and narrows cross-support false-positive-rate gaps. A controlled study further shows that unequal training support can produce score and false-positive disparities even between normal regimes with symmetric representation geometry. These findings highlight normal-reference coverage as an important consideration for reliable anomaly detection.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
Anomaly Detection, Multivariate Time Series, Representation Learning

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_RRjwOpenReview ↗
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3
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Informativeness
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Paper summary

This paper addresses the problem of imbalanced support in the distribution of normal training data for anomaly detection. The authors propose RestoreAD, which uses uniform regularization to prevent concentration on a single candidate, retrieves normal references for anomaly scoring and support-difficulty estimation, and applies CSNC to align the scores. Experiments on TSB-AD-M examine detection performance and support-dependent false-positive disparities. A controlled experiment varies training support while keeping the representation geometry symmetric.

Critical strengths
  1. Considering support imbalance: Anomaly detection performance can be significantly affected by how well different regions of the normal-data distribution are represented in the training data. Explicitly considering this imbalance when calculating anomaly scores is a strength of this paper.
  2. Theoretical analysis of CSNC: The authors provide theoretical bounds for both population and empirical medians, which strengthen the theoretical support for the proposed approach.
Critical weaknesses
  1. Implications of reduced disparity: Proposition 1 provides a theoretical interpretation of cross-support comparability, and Figure 3 shows a smaller false-positive rate (FPR) gap together with a slight increase in the mean anomaly true-positive rate (TPR). However, the practical implications of reduced disparity are not sufficiently clear. Reporting the overall held-out FPR and TPRs across support bins at the existing training-Q95 thresholds would help clarify where the improvements occur.
  2. Temporal-overlap exclusion: Temporal-overlap exclusions are specified for relation regularization and reference-isolation estimation, but it is not clear whether the same exclusion applies to query-to-reference retrieval in Equation (6).
Questions for authors
  1. Can the authors explain more clearly the practical implications of reduced disparity, including how the improvements are distributed across different support regimes?
  2. Temporal-overlap exclusion is specified for VjV_j in Equation (5). Does the same exclusion apply when constructing NK(c)(i)\mathcal{N}_K^{(c)}(i) in Equation (6), particularly when training windows are scored for calibration? Please clarify how identical and overlapping query–reference pairs are handled, since these scores determine the CSNC medians and Q95 thresholds.
6 comments
AuthorsOpenReview ↗

Response to Reviewer RRjw (Part 1/2; Q1)

Response to Reviewer RRjw (Part 1/2; Q1)

Dear Reviewer RRjw,

Thank you for your careful review and constructive suggestions. We appreciate your recognition of the importance of normal support imbalance and the theoretical support for CSNC. Your questions have helped us strengthen the decision-level evaluation and clarify the retrieval and calibration protocol. We address your comments below.


Q1. Practical benefits across support groups

Thank you for highlighting the need to connect reduced disparity to decision-level outcomes. The practical benefit is lower mean worst-bin FPR at the same overall false-positive budget. We added analyses on all 180 M180 series and three seeds, comparing the same RU detector before and after CSNC with identical estimated support-group membership. We report support-wise training-Q95 results, followed by a matched-budget comparison.

Support-wise results at training-Q95 thresholds. Raw and CSNC each use the 95th percentile of their respective training-score distributions. The table reports mean anomaly TPR (%) ↑ for the ten-bin evaluation subset (392/540 series–seed cases; 141 distinct series). Bins increase in estimated support difficulty; n denotes valid paired series with anomalies in each bin.

Support bin12345678910
Raw66.3664.0969.9673.6978.4182.2386.6988.5890.9997.12
CSNC81.1373.8976.6978.4181.7283.5787.1788.6791.1397.37
n486372848899115121118115

Across all 180 series, training-Q95 mean overall anomaly TPR is 85.73% → 86.45% (Raw → CSNC). Mean TPR gains are largest in the lower-difficulty bins, with the lowest-difficulty bin increasing from 66.36% to 81.13% (+14.77 pp). At the highest-difficulty end, mean TPR remains around 97%, while FPR decreases from 89.78% to 88.76% (135 valid series). These results describe how sensitivity and false positives change across support groups under training-Q95 thresholding. Since Raw and CSNC yield different overall test FPRs at these thresholds, we additionally compare them at the same overall false-positive budget below.

Comparison at the same overall false-positive budget. At an offline matched expected overall test FPR of 5%, we obtain:

MeasureRawCSNC
Mean worst-bin FPR ↓30.83%29.13%
Mean cross-bin FPR gap ↓30.74 pp29.00 pp
Mean overall anomaly TPR ↑47.72%47.91%

Using unrounded paired results, the mean worst-bin FPR reduction is 1.71 pp, with a descriptive 95% paired series-bootstrap interval of [1.33, 2.11] pp. Worst-bin FPR and FPR gaps are computed within each series–seed pair, then averaged over seeds within each series and equally across series. The gap has 179 valid series; other measures have 180. Matched working points use test-normal labels only for offline evaluation, not CSNC fitting or deployment threshold selection.

At the same overall false-positive budget, CSNC lowers mean worst-bin FPR and cross-bin disparity, with similar mean overall anomaly TPR. These results support its practical benefit in reducing the concentration of false positives across estimated support groups. We will include additional bin-wise analyses and sample counts in the revision.

AuthorsOpenReview ↗

Response to Reviewer RRjw (Part 2/2; Q2)

Response to Reviewer RRjw (Part 2/2; Q2)

Q2. Temporal exclusion in query-to-reference retrieval

In the submitted implementation, the temporal exclusion used for reference-isolation estimation in Eq. (5) is not applied to query-to-reference retrieval in Eq. (6). Retrieval uses the full reference bank, including during training-window scoring. Identical source windows and temporally overlapping references can therefore enter the scores used to fit CSNC medians and Q95 thresholds.

To assess this sensitivity, we froze the encoder and reference bank and compared three query-retrieval policies: unmasked retrieval, exclusion of identical source windows, and exclusion of all temporally overlapping windows. Under the supplemental strict non-overlap policy, admissible reference slots satisfy

A(i)={j:∣ti−tj∣≥L},L=96.\mathcal{A}(i)=\{j:\lvert t_i-t_j\rvert\ge L\},\qquad L=96.

where tit_i and tjt_j are source-window start indices within the same series. This excludes every overlapping reference slot, including duplicate slots representing the query window. We retain K=3K=3 without relaxing the mask.

For each policy, we recompute query scores and support estimates, then refit CSNC bin boundaries, medians and score-version-specific Q95 thresholds using only training-prefix scores. For comparable group-wise reporting, evaluation support-group membership remains fixed to the original unmasked setting, independently of the refitted CSNC calibration bins.

Across all 180 M180 series and three seeds, strict non-overlap retrieval gives the following results at the separately refitted training-Q95 thresholds:

MeasureRawCSNC
Overall FPR ↓20.37%18.87%
Worst-bin FPR ↓49.23%41.49%
Cross-bin FPR gap ↓43.82 pp35.08 pp

Metrics are computed within each series–seed pair, then averaged over valid paired seeds within each series and equally across series. The gap has 179 valid series; other measures have 180. Mean worst-bin FPR decreases by 7.74 pp, with a descriptive 95% paired series-bootstrap interval of [6.30, 9.28] pp. The reductions also persist after excluding the first 95 test points to remove boundary-crossing input windows.

We will explicitly document the stage-specific exclusion rules and include complete FPR/TPR results for all three retrieval policies in the revised appendix. CSNC’s reductions in mean worst-bin FPR and cross-bin disparity persist under strict non-overlap retrieval.


Thank you again for your thoughtful feedback. We will incorporate these additional analyses and clarifications into the revised manuscript to strengthen the empirical evidence and clarify the implementation details.

Best regards,

Authors.

Thank you for the clarification and additional analyses. The matched-FPR comparison and the strict non-overlap results substantially address my concerns. Please incorporate these results and the retrieval exclusion rules into the revised manuscript. Please also report the overall held-out FPR at the original training-Q95 thresholds and the complete FPR/TPR comparisons across the three retrieval policies.

Reviewer_KeN9OpenReview ↗
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3(+1)
Confidence
3
Informativeness
2(+1)
Presentation
2(+1)
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2(+1)
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Paper summary

The authors investigate the effect of low sample sizes for anomaly detection on multivariate data with normal distributions. At the center of the proposed approach is a bias towards more false positives in the anomaly detection when small sample sizes are used. In experiments on standard benchmarks the proposed method appears to outperform other methods. After reading the manuscript several times, I still have significant concerns as to the motivation and the soundness of the proposed approach.

Critical strengths

The authors use terminology and notation that makes the formalisation of the problem easy to understand.

The experiments use standard benchmarks

The baseline methods include many other recent competitor methods.

Recent and relevant scientific literature is included

Critical weaknesses

First and foremost I have to admit: I don’t understand what the authors propose and why. It seems there are many problems merged into the present paper, including covariate shift literature, anomaly detection, bias correction techniques from classical statistics. But even after reading the manuscript multiple times, it’s not clear what problem exactly the authors are trying to solve. If it’s the problem with under sampling: there’s other corrections that should be compared against. If it’s covariate / data shift: there’s other methods that could be compared against.

The experimental design is sensible, but it feels there should be synthetic data experiments to account for the two factors highlighted in the generative model in eq 1.

It seems like an important feature of the proposed approach is the calibration of the anomaly detector. So rather than comparing different models (which is great and should be part of the experiments), it would be helpful to compare different calibration methods. And there should be measures of calibratedness, such as Expected Calibration Error, Brier Scores, …

Questions for authors

Sorry if I missed that, but: why were no calibration measures included in the experiments? Did you check other calibration measures? Did you investigate standard k-fold cross-validation rather than just a single pre-defined split?

5 comments
AuthorsOpenReview ↗

Response to Reviewer KeN9 (Part 1/3; Q1–Q2)

Response to Reviewer KeN9 (Part 1/3; Q1–Q2)

Dear Reviewer KeN9,

Thank you for your careful review and constructive feedback. We appreciate your positive assessment of our experimental design and our use of standard benchmarks and recent baselines. Your suggestions have helped us clarify RestoreAD’s motivation and calibration target and strengthen its empirical validation. We address your concerns point by point below.


Q1. Problem definition and motivation

Reviewer comment: “I don’t understand what the authors propose and why.”

We study the task of multivariate time-series anomaly detection under normal-only training. We follow the established setting used by prior work such as PaAno [2] and evaluate on TSB-AD-M [1,2]. Training uses nominally normal observations without anomaly labels; “normal” means non-anomalous, with no Gaussian assumption.

Within this task, we identify a specific problem: support-dependent score bias among legitimate normal observations. Normal patterns with fewer or more distant relevant references can receive higher mismatch scores and incur more false alarms under a shared threshold. This bias can arise at a fixed total training size without normal train–test distribution shift.

RestoreAD addresses this problem through a connected pipeline: RU discourages concentrated normal-to-normal relations; retrieval estimates anomaly scores and support from the same reference bank; CSNC aligns normal-score medians across support bins.


Q2. Controlled synthetic validation

Reviewer comment: “synthetic data experiments to account for the two factors highlighted in the generative model in eq 1.”

Our controlled study using synthetic data in Fig. 4 (Appendix C.5) varies training support between two geometrically symmetric normal regimes while holding the representation mapping fixed. The results show that unequal support can induce normal-score and FPR disparities, and that CSNC reduces these disparities. Following your suggestion, we extend this study by independently varying normal support and anomaly strength to probe the two influences motivating Eq. (1).

We report the 5:1 and 10:1 imbalanced conditions (2,000 training windows; three seeds). Within each condition, Raw and CSNC share the same retrained Base+RU detector and reference bank, with separate Q95 thresholds fitted on the same independent normal calibration pool. Normal training, calibration and testing use matched generators and regime proportions.

Values are mean ± SD across three seeds. The gap is the absolute FPR difference between the two known normal regimes.

Training ratioMeasure ↓RawCSNC
5:1Overall FPR (%)5.32 ± 0.545.18 ± 0.86
5:1Worst-regime FPR (%)16.32 ± 2.8911.21 ± 0.46
5:1Regime FPR gap (pp)13.20 ± 3.707.23 ± 1.37
10:1Overall FPR (%)5.40 ± 0.965.28 ± 0.60
10:1Worst-regime FPR (%)22.89 ± 4.0515.75 ± 3.12
10:1Regime FPR gap (pp)19.25 ± 4.7411.52 ± 3.36

CSNC reduces the mean FPR gap by 45.2% and 40.2%, and mean worst-regime FPR by 31.3% and 31.2%, respectively, while observed overall FPR remains close to 5%.

To examine the anomaly-strength factor, we sweep seven standardized perturbation strengths for local pulses and oscillatory bursts, including a zero-strength control. The encoder, reference bank and calibration statistics remain fixed across strengths within each support condition. At 10:1, increasing pulse strength from 0.025 to 0.10 raises Raw AUROC from 0.5140 to 0.7093, illustrating strength-dependent detectability.

Under the tested imbalanced conditions, CSNC reduces mean worst-regime FPR and cross-regime disparity without normal train–test distribution shift.

References are listed in Part 3.

AuthorsOpenReview ↗

Response to Reviewer KeN9 (Part 2/3; Q3–Q4)

Response to Reviewer KeN9 (Part 2/3; Q3–Q4)


Q3. Comparison with alternative calibration methods

Reviewer comment: “it would be helpful to compare different calibration methods.”

Following your suggestion, we constructed four normal-only calibration controls from established tools: global and support-conditioned ECDF mapping [3], support-conditioned median/MAD normalization (robust Z) [4], and conditional median-spline regression [5]. All methods share the frozen detector, reference bank, and available nominally normal calibration pool. Support-conditioned methods use the same support estimates; fitting uses no anomaly labels.

The time-held-out calibration evaluation covers all 180 TSB-AD-M series and three seeds. We average seeds within each series, then weight series equally.

Calibration methodAUROC ↑AP ↑VUS-PR ↑
Global ECDF0.69660.22920.2989
Support-conditioned robust Z0.73220.36250.4070
Support-conditioned ECDF0.70750.20330.2724
Median-spline regression0.73280.40840.4453
CSNC0.74330.41580.4543

CSNC achieves the highest mean on all three detection metrics among the compared calibration methods. Its VUS-PR gain over median-spline regression, the strongest alternative, is 0.0089 (descriptive 95% paired series-bootstrap interval: [0.0024, 0.0175]).

With the detector and available calibration pool held fixed, these results support CSNC’s advantage over the tested distribution-based, location-scale, and continuous median-correction alternatives.


Q4. Calibration target and evaluation measures

Reviewer comment: “why were no calibration measures included in the experiments? Did you check other calibration measures?”

Thank you for highlighting the need to clarify the calibration target and its evaluation. CSNC targets cross-support comparability of normal anomaly scores by aligning support-bin medians. Figure 3 evaluates this target through support–score dependence and cross-bin FPR disparity.

CSNC outputs anomaly scores rather than estimates of P(Y=1∣X)P(Y=1\mid X). ECE assesses probability calibration, while Brier is a proper scoring rule for probabilistic predictions [6]; applying them here would require an additional score-to-probability mapping. Following your suggestion, we now add normal-score KS distance and matched-budget false-positive analyses under the time-held-out protocol (180 series, three seeds):

MeasureRawCSNCValid series
Absolute normal support–score Spearman ρ ↓0.54860.2724180
Maximum bin-to-pooled normal-score KS distance ↓0.50190.3807180
Worst-bin FPR at matched 5% overall FPR (%) ↓17.5814.87180
Cross-bin FPR gap at matched 5% overall FPR (pp) ↓19.2815.98155

Metrics are computed per series–seed pair, then averaged over valid paired seeds within each series and equally across series. The FPR gap is the maximum minus minimum bin FPR and requires at least two bins containing normal test observations. Matched-budget rows use test-normal labels to match an expected overall FPR of 5% for offline analysis; they do not estimate deployment thresholds or establish nominal false-alarm control.

At the same overall false-positive budget, CSNC reduces mean worst-bin FPR by 15.4% relative. The descriptive 95% paired series-bootstrap interval for the absolute FPR reduction is [1.54, 3.92] percentage points. All four diagnostics show lower mean values, supporting improved cross-support score comparability and a less concentrated false-positive burden across support groups.

We will clarify this calibration target and include these additional diagnostics in the revision.

References are listed in Part 3.

AuthorsOpenReview ↗

Response to Reviewer KeN9 (Part 3/3; Q5)

Response to Reviewer KeN9 (Part 3/3; Q5)


Q5. Temporal validation and split sensitivity

Reviewer comment: “Did you investigate standard k-fold cross-validation rather than just a single pre-defined split?”

Predefined training/test splits are common practice in time-series anomaly detection, as in Anomaly Transformer [8], DCdetector [9], and PaAno [2]. We follow the prescribed TSB-AD-M split [1] for benchmark comparability. This also preserves our intended setting: learning from historical normal observations and evaluating subsequent data. Applying standard K-fold directly to overlapping windows can share input observations across fitting and evaluation folds and use later observations for fitting when evaluating earlier ones [7]. We therefore retain chronological separation.

To address your concern about reliance on a single split, we additionally conducted a chronological split-sensitivity study. We use the first 30%, 50%, or 70% of each training prefix for encoder and reference-bank fitting, reserving the subsequent portion for calibration. With window length 96, a 95-point fitting–calibration gap and exclusion of the first 95 test points prevent cross-block input-window overlap. Hyperparameters and the remaining test suffix are fixed across settings.

Prespecified length requirements retain 147 of 180 series. Each setting uses three seeds; worst-bin FPR is evaluated at a matched expected overall FPR of 5%.

Fitting fractionAUROC ↑ (Raw / CSNC)Worst-bin FPR (%) ↓ (Raw / CSNC)
30%0.7572 / 0.764020.45 / 17.75
50%0.7562 / 0.768320.10 / 16.71
70%0.7598 / 0.767020.10 / 17.79

For comparable worst-bin reporting, evaluation support-group membership is fixed using the 50% setting. Metrics are computed per series–seed pair, then averaged over seeds within each series and equally across series. Matched-FPR working points use test-normal labels only for offline evaluation.

CSNC achieves higher mean AUROC and lower mean worst-bin FPR across all three tested boundaries, with relative worst-bin FPR reductions of 11.5%–16.9%. These results show that its benefits in anomaly ranking and support-wise false-positive allocation persist across the tested fitting/calibration boundaries.


References

[1] The Elephant in the Room: Towards A Reliable Time-Series Anomaly Detection Benchmark. NeurIPS, 2024.

[2] PaAno: Patch-Based Representation Learning for Time-Series Anomaly Detection. ICLR, 2026.

[3] Computer Age Statistical Inference: Algorithms, Evidence, and Data Science. 2021.

[4] Robust Statistics: Theory and Methods (with R). 2019.

[5] Handbook of Quantile Regression. 2018.

[6] Classifier calibration: a survey on how to assess and improve predicted class probabilities. Machine Learning, 2023.

[7] Evaluating time series forecasting models: an empirical study on performance estimation methods. Machine Learning, 2020.

[8] Anomaly Transformer: Time Series Anomaly Detection with Association Discrepancy. ICLR, 2022.

[9] DCdetector: Dual Attention Contrastive Representation Learning for Time Series Anomaly Detection. KDD, 2023.


Thank you again for your time and constructive suggestions. We will incorporate these clarifications and additional analyses into the revised manuscript.

Best regards,

Authors.

Reviewer_ttv4OpenReview ↗
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3
Confidence
3
Informativeness
2
Presentation
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2
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Paper summary

This paper studies Normal Support Imbalance in normal-only multivariate time-series anomaly detection: legitimate normal patterns may receive unequal coverage from learned references, resulting in support-dependent anomaly-score shifts and false-positive disparities. The proposed RestoreAD framework combines channel-wise representation learning with Row-Uniform (RU) regularization, reference-based anomaly scoring and support estimation, and Cross-Support Normality Calibration (CSNC).

Critical strengths

The paper addresses a practically relevant problem. Distinguishing poorly supported normal behavior from anomalous behavior is important for systems with heterogeneous operating regimes. Examining false-positive disparities provides useful insight beyond aggregate detection metrics.

Critical weaknesses
  • Channel-independent scoring creates a potential blind spot for joint anomalies, which may manifest solely as violations of cross-channel relationships. Because each channel independently retrieves its nearest references, an observation whose individual channels resemble normal patterns but whose joint configuration is abnormal may receive a low anomaly score.
  • The evaluation is limited to multivariate time series, leaving the applicability and effectiveness of the proposed framework in univariate settings untested.
Questions for authors
  • Could the authors compare Base and Base+RU in terms of normal-regime coverage, support distributions, normal-score distributions, and group-wise false-positive rates? A controlled experiment with known regimes and a retrained encoder would help establish whether RU improves coverage of weakly supported normal patterns.
  • The raw and CSNC scores use thresholds set to the 95th percentile of their respective training-score distributions, but they may yield different overall false-positive rates on the test data. Could the authors report the overall FPR, worst-support-bin FPR, and anomaly recall within each support bin for both raw and calibrated scores?
  • How does RestoreAD handle anomalies that arise solely from violations of cross-channel relationships? An analysis of failure cases would help clarify the limitations of channel-independent scoring.
  • The core scoring and calibration mechanisms appear applicable when the number of channels is one. Could the authors explain the restriction to multivariate evaluation and assess whether the proposed support-imbalance diagnosis and correction also hold on a univariate benchmark?
5 comments
AuthorsOpenReview ↗

Response to Reviewer ttv4 (Part 1/3; Q1)

Response to Reviewer ttv4 (Part 1/3; Q1)

Dear Reviewer ttv4,

We sincerely thank you for your careful review and for recognizing the practical relevance of normal support imbalance. Your constructive suggestions have helped us strengthen the empirical evaluation and clarify RestoreAD’s scope and limitations. We address Q1 below; Q2 follows in Part 2, and Q3–Q4 in Part 3.


Q1. Base vs. Base+RU: coverage, support, scores and FPR

  1. Controlled retraining and regime-wise diagnostics.

Complementing Appendix C.5’s fixed-representation study, we retrained Base and Base+RU in pairs on two sign-symmetric normal regimes of equal population complexity (2,000 windows; three seeds), with matched data, initialization and other training settings; CSNC was disabled. The table illustrates the 5:1 condition with 500 references, using model-specific banks and Q95 thresholds fitted on the same independent, balanced normal calibration pool. Statistics are computed per seed before averaging.

DiagnosticBaseBase+RU
Training relation KL ↓0.04460.0231
Distinct weak-regime references ↑113.3113.7
Dense-regime normal score: P50/P95 ↓0.01438/0.019970.01120/0.01537
Weak-regime normal score: P50/P95 ↓0.01716/0.022990.01355/0.01819
Dense-regime FPR at calibration Q95 (%) ↓2.221.94
Weak-regime FPR at calibration Q95 (%) ↓8.178.11
Overall FPR at calibration Q95 (%) ↓5.195.03

In this illustrative condition, Base+RU reduces relation KL, increases distinct weak-regime references, and yields lower normal-score quantiles and slightly lower mean FPRs. Under the same 5:1 ratio, a separate 1,000-slot sensitivity check also gives a lower mean within-regime nearest-reference cosine distance for weak-regime normal windows in the fixed standardized input space (0.021818 → 0.021744).

  1. Fixed-reference control isolates the representation benefit.

We fixed the indices of 500 Base-selected reference windows and re-encoded the same source windows with each encoder. The table reports three-seed means for local pulses and oscillatory bursts at strength 0.25 on balanced test pools. Entries are Base → Base+RU.

Training ratioProbeAUROC ↑AP ↑
1:1Local pulse0.6813 → 0.69660.6807 → 0.6955
1:1Oscillatory burst0.6646 → 0.67340.6518 → 0.6600
5:1Local pulse0.6650 → 0.67260.6780 → 0.6887
5:1Oscillatory burst0.6462 → 0.65100.6414 → 0.6458
10:1Local pulse0.6460 → 0.65180.6636 → 0.6723
10:1Oscillatory burst0.6415 → 0.64430.6389 → 0.6407

Base+RU achieves higher mean AUROC and AP in all six displayed probe conditions with reference-window indices held fixed. Together with the Base+RU gains in manuscript Table 2, these controls support RU’s independent representation benefit beyond changes in reference-window selection.

We will incorporate these additional analyses and clarifications into the revised manuscript.

AuthorsOpenReview ↗

Response to Reviewer ttv4 (Part 2/3; Q2)

Response to Reviewer ttv4 (Part 2/3; Q2)


Q2. Test FPR and recall across support bins

We compared Raw (the RU detector before CSNC) and CSNC on M180 test suffixes (180 series, three seeds), sharing the encoder, reference bank and training-fitted evaluation groups. Metrics are computed per series–seed pair, averaged over valid paired seeds within each series, then equally across series. Worst-bin FPR and max–min gaps are computed before averaging.

  1. Comparison at matched overall FPR.

Results use the default calibration setting, B=10. Entries are Raw → CSNC; rates are percentages and gaps are percentage points (pp). There are 180 valid series, except 179 for gaps.

Expected overall FPRWorst-bin FPR ↓FPR gap ↓Overall recall ↑
1%11.69 → 11.3211.75 → 11.3637.45 → 37.66
5%30.83 → 29.1330.74 → 29.0047.72 → 47.91
10%45.77 → 42.9145.23 → 42.1452.62 → 52.82

At 5%, the paired change in worst-bin FPR is −1.71 pp (descriptive paired-series bootstrap 95% CI [−2.11, −1.33]); overall recall changes by +0.19 pp (CI [−0.08, 0.45]). Changes and confidence intervals use unrounded data. Matched working points use test-normal labels and fractional boundary-tie acceptance for offline evaluation only; they are not deployment thresholds. CSNC fitting uses no test labels.

  1. Results under training-Q95 thresholding.

Raw and CSNC each use the 95th percentile of their respective training-score distributions. Under the default B=10 setting, worst-bin FPR is 87.84 → 87.25%, and overall recall is 85.73 → 86.45%. The table below reports mean anomaly recall (%) at training Q95 for the ten-bin evaluation subset (392/540 series–seed cases; 141 distinct series). Bins increase in estimated support difficulty; n counts valid paired series with anomalies in each bin. Higher values are bolded.

Support bin12345678910
Raw66.3664.0969.9673.6978.4182.2386.6988.5890.9997.12
CSNC81.1373.8976.6978.4181.7283.5787.1788.6791.1397.37
n486372848899115121118115

Mean recall is higher in all ten displayed bins. These recall results use method-specific training-Q95 thresholds and complement the matched-budget comparison above.

At matched overall FPR, CSNC lowers mean worst-bin FPR and cross-bin disparity across all three tested budgets, with similar mean overall recall. These results support its practical benefit in reducing the concentration of false positives across estimated support groups. We will incorporate these analyses and clarifications into the revised manuscript.

AuthorsOpenReview ↗

Response to Reviewer ttv4 (Part 3/3; Q3-Q4)

Response to Reviewer ttv4 (Part 3/3; Q3-Q4)


Q3. Anomalies arising solely from cross-channel relationships

RestoreAD retrieves normal references independently across channels and may therefore have limited sensitivity to anomalies whose individual channels match normal patterns but whose joint configuration is incompatible. CSNC adjusts support-dependent score offsets without explicitly enforcing joint consistency.

To examine this boundary, we reused three frozen RU models from Q1’s balanced 1:1 condition. Complementary swaps of complete channel windows between two legitimate regimes exactly preserve each channel’s empirical window distribution and within-window temporal structure. Across all 31 unique nontrivial partitions of the six channels, Full RestoreAD achieved AUROC 0.5011 ± 0.0010. We average partitions within each seed, then report mean ± SD across three seeds. The same models achieved AUROC ≈ 1 on all four tested within-channel pulse controls, distinguishing sensitivity to these local deviations from sensitivity to joint configuration.

We additionally tested shared-reference kNN, which requires common reference-window indices across channels. With the same frozen encoders and reference banks and CSNC disabled for both retrieval rules, AUROC increased from 0.5029 ± 0.0021 for independent retrieval to 0.6868 ± 0.0373. This partial recovery identifies a concrete way to incorporate joint consistency without encoder retraining. This diagnostic extension is not part of the submitted RestoreAD. We will include these controlled failure cases and diagnostic results in the appendix and expand Appendix F’s scope and limitations discussion.


Q4. Evaluation scope and applicability to univariate time series

Our initial multivariate evaluation followed the paper’s application focus on industrial and cyber-physical monitoring, where multiple sensor streams are observed over time. We therefore adopted the official TSB-AD-M split as our primary benchmark. RestoreAD itself does not require C>1C>1: at C=1C=1, channel averaging becomes the identity, RU still regularizes relations among candidate windows, and reference scoring, support estimation, and CSNC retain their definitions. In multivariate streams, normal-reference support can additionally differ across channels within the same context. RestoreAD retains channel-wise mismatch and support evidence before aggregation, making its channel-preserving design particularly well suited to this setting.

To directly assess whether the support-imbalance diagnosis and correction extend to univariate data, we evaluated the official TSB-AD-U evaluation list (350 series) with frozen settings, three seeds, and a 2×2 ablation of RU and CSNC. We report mean ± SD across seed-level macro-averages on the test suffixes; ranking metrics cover 349 series because one test suffix contains no anomalies.

VariantAUC-ROC ↑AUC-PR ↑VUS-PR ↑
Base0.7513 ± 0.00270.3128 ± 0.01080.3804 ± 0.0133
Base+CSNC0.7570 ± 0.00250.3157 ± 0.00920.3851 ± 0.0139
Base+RU0.8386 ± 0.00260.4379 ± 0.00520.5164 ± 0.0047
Full0.8411 ± 0.00340.4391 ± 0.00540.5186 ± 0.0044

RU accounts for most of the detection gains. To assess the support-imbalance diagnosis and CSNC separately, we compare scores before and after CSNC using the same RU encoder and reference bank:

DiagnosticWithout CSNCWith CSNCValid series
Normal-score/support-difficulty Spearman ρ ↓0.62970.5188347
Worst-bin FPR at matched 5% overall FPR (%) ↓36.7834.24350
Overall recall at matched 5% overall FPR (%) ↑57.9558.44349

CSNC reduces the association between support difficulty and normal test scores. At an offline matched 5% expected overall FPR, the paired change in worst-bin FPR is −2.54 percentage points (CSNC−Raw; descriptive paired-bootstrap 95% CI [−3.28, −1.86]), with similar overall recall. Highest-difficulty-bin recall decreases from 72.59% to 71.61% (305 valid series), identifying a group-wise trade-off. Matched working points use test-normal labels for evaluation only, not calibration fitting or deployment threshold selection.

On the posthoc subset of 315 series with anomaly-free training prefixes, the Base → Full VUS-PR gain persists (0.3584 → 0.5088) without retraining. These results support the applicability of the support-imbalance diagnosis and correction to univariate data and complement our primary multivariate evaluation. We will add these results and clarify the benefits and decision-level limitations of support-conditioned calibration.


Thank you again for your careful and constructive feedback. We will incorporate these analyses into the revision.

Best regards,

Authors.

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

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