acceptodds
Under review as a conference paper at ICLR 2027

When Normal-Only Updates Are Not Enough: Test-Time Adaptation in Reconstruction-Based Time-Series Anomaly Detection

Abstract

Normal operating conditions can evolve after deployment, motivating test-time adaptation (TTA) of time-series anomaly detectors using incoming data. Yet the same stream may contain anomalies, so TTA with online updates must decide which test samples should be used for adaptation. This leaves a more basic question: even if updates are restricted to samples labeled as normal in the benchmark, does TTA reliably improve anomaly detection? We study this question with a controlled intervention that replaces the practical update selector with a rule that uses only samples labeled as normal in the benchmark, while keeping the rest of the online adaptation procedure unchanged. Across nine benchmark families, four optimizer configurations, and five random seeds, we obtain three main findings: (1) using only samples labeled as normal in the benchmark does not reliably improve detection; (2) practical TTA failures exhibit two distinct responses to this intervention, with 63 of 180 settings recovering a clear detection gain while 90 still show no clear detection gain; and (3) the updates reduce their immediate reconstruction objective across the evaluated settings, yet these reductions do not consistently lead to better anomaly ranking. Both failure patterns persist across alternative practical adaptation variants and modest perturbations of the benchmark labels. Together, these findings show that improving sample selection alone is not a complete solution to reconstruction-based TSAD TTA.

Primary area:
learning on time series and dynamical systems
Keywords:
time-series anomaly detection, test-time adaptation, reconstruction-based anomaly detection

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_5mXqOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
3
Read review
Paper summary

The paper analyses and benchmarks various methods of Test-Time Adaptation. The main idea of the paper, is to benchmark these methods under oracle access. Even in this unrealistic setting, they find that most datasets see no positive improvement from Test-Time Adaptation.

Critical strengths
  1. The resulting limitation of TTAs is very interesting.
  2. Ablations validate the findings under different conditions.
  3. Visualizing the results over different attributes in Fig 1 and Fig 2 increases trust into the paper.
Critical weaknesses

The biggest weakness I see is in the interpretation of the results. I don't see why having access to Oracle-level information wouldn't improve the results, and you don't provide any satisfactory reason for this.

My best explanation for this is a limitation of the datasets (if the dataset does not contain any shift, why should the oracle improve performance). This would substantially reduce the value of your paper: Instead of finding that TTA is often useless, the conclusion would be that TTA is only useful under a significant enough distribution shift. This seems obvious and is partially supported by Fig. 1: The situations with a very significant distribution shift (top right corner) are easily found by both oracle and practical algorithms and the interesting part of your paper only appears with less significant differences.

Could you please clarify if you have a better explanation?

Questions for authors

See my main Weakness. If you can refute my concern, I will recommend either a weak or a clear acceptance.

Could you maybe create a table/figure comparing the contamination rate of various datasets (during testing) against Oracle minus Practical performance? Depending on the result, this could validate my hypothesis or refute it directly.

I would also like to know why the authors rely on AUCPR instead of more modern TSAD methods like VUS-PR or Affiliation-F.

3 comments

R3-W1/Q1. Why Can Oracle Normal-Only Adaptation Still Fail?

Oracle normal-only selection does not guarantee better detection because normal-sample updates can also make anomalies easier to reconstruct. The update objective reduces normal reconstruction error but does not constrain how anomalous scores change relative to normal scores. We demonstrate this mechanism in a controlled Linear-AE experiment and show a corresponding local effect in an actual nonlinear AE.

1. Controlled explanation under a shift that harms detection

We use a two-dimensional rank-one Linear-AE. Rotating test-time normals by 30°, while keeping the source model fixed, reduces Frozen AUPRC from 1.0000 to 0.9356, demonstrating that the shift harms detection.

Favorable and Harmful conditions share the same shifted normals, source model, normal update samples, and 128-step angular-SGD trajectory. Only anomaly geometry differs; their Frozen anomaly-score distributions are identical, and anomalies never enter updates. Across five seeds, normal update-set loss decreases from 0.2599 to 0.0103 in both conditions. Yet on independent held-out sets (512 normals and 512 anomalies per condition), adapted AUPRC reaches 1.0000 (Favorable) versus 0.3410 (Harmful). In the Harmful condition, mean anomaly error falls from 0.4939 to 0.0014, below the adapted normal mean (0.0104).

The contrast arises because updating the reconstruction subspace toward shifted normals can simultaneously make certain anomalies easier to reconstruct. Depending on anomaly geometry, successful normal fitting can therefore worsen normal–anomaly score separation, even when the distribution shift has already degraded Frozen detection.

2. Supporting evidence from a real AE update

We examined 20 predetermined checkpoints per trajectory across 60 Oracle trajectories. As an illustrative example, Daphnet window 726 (zero-indexed; seed 42, AdamW 1e−4) contains 12 benchmark-labeled normal points. Scoring the same fixed future normal and anomalous samples immediately before and after this update isolates its local effect.

Current normal-window loss decreases by 0.0045, while mean future anomaly scores decrease by 0.0093 and mean future normal scores increase by 0.00081. The mean anomaly-minus-normal gap narrows by 0.0101, and the correctly ordered pair fraction declines from 0.4651 to 0.4634. This illustrates an actual local objective–ranking conflict, not a complete explanation of Daphnet's online degradation.

3. Interpretation of Fig. 1 and remaining scope

Fig. 1 plots Oracle−Frozen and Practical−Frozen AUPRC changes, not distribution-shift severity; its upper-right region therefore cannot establish that larger shifts yield larger gains. Some of the 90 Neither-Improves (NI) settings may indeed have little exploitable adaptation demand, and our experiments do not explain every NI case. Nevertheless, they establish a concrete reason Oracle adaptation can fail beyond insufficient shift: normal-only selection does not ensure that parameter updates preserve anomaly ranking.

Q2. Test Anomaly Prevalence vs. Oracle–Practical Performance

The requested comparison reveals substantial variation in Oracle–Practical detection gains across datasets with similar test anomaly rates. We compare the test anomaly ratios reported in Appendix Table A.1 with the paired Oracle-minus-Practical AUPRC differences across all nine benchmarks.

DatasetTest anomaly ratio (%)Oracle − Practical AUPRC (pp)
Daphnet7.93−7.13
GECCO1.41+15.07
Genesis0.41+0.02
MSL10.48+0.00
PSM27.76+33.91
PUMP9.40+40.39
SMAP12.83+0.01
SMD4.16+1.08
SWAT12.14+8.93

For example, PUMP and SMAP have broadly comparable anomaly ratios (9.40% vs. 12.83%) but markedly different Oracle–Practical gaps (+40.39 vs. +0.01 pp). GECCO also shows a substantial Oracle advantage (+15.07 pp) despite its low anomaly ratio (1.41%). The dataset-level Spearman correlation is ρ = 0.117. Test anomaly prevalence does not directly measure normal-distribution shift.

Q3. Robustness Across Evaluation Metrics

The coexistence of oracle-only-gain (OOG) and neither-improves (NI) outcomes is not specific to AUPRC. We use unadjusted AUPRC as the primary metric to evaluate point-wise anomaly ranking without threshold selection or point adjustment. To assess metric robustness, we additionally evaluate VUS-PR and Affiliation-F on the same 180 configurations.

MetricBIOOGNIPOG
AUPRC (primary)2763900
VUS-PR3555900
Affiliation-F (P95)34321140
Affiliation-F (P99)41369211

Under VUS-PR, all 90 original NI cases persist, with 172/180 (95.6%) outcome classifications unchanged. For Affiliation-F, P95 and P99 refer to Frozen source-validation thresholds applied identically to all three arms. Both OOG and NI remain substantial across the alternative metrics, although individual classifications depend on the metric and, for Affiliation-F, the threshold.

I appreciate the authors efforts, and my reservations are partially resolved. I have adjusted my score.

Reviewer_rQ36OpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper presents a controlled diagnostic study examining whether test-time adaptation (TTA) reliably improves reconstruction-based time-series anomaly detection (TSAD) when updates are strictly limited to benchmark-labeled normal samples. The method fixes source initialization, architecture, optimizer, learning rate, and streaming evaluation protocol fixed while evaluating an oracle normal-only intervention across 9 benchmark datasets, 4 optimizer configurations, and 5 seeds. The paper conveys several interesting insights. First, normal-only updates fail to reliably boost detection. Second, pratice TTA failures bifurcate as 63 cells show oracle-only gains (OOG), whereas 90 cells show persistent failure under both practical and oracle updates (NI). Third, immediate reconstruction-loss reductions on normal samples occur across all 180 cells but correlate poorly with anomaly ranking improvements within individual datasets.

Critical strengths
  • The diagnostic setup in the paper sounds technical. By keeping source checkpoints, optimizer states, online sequencing, and parameter scopes identical while varying only the update mask, the setup cleanly isolates sample selection from other TTA factors.
  • The paper comprehensively evaluates 9 benchmark datasets, 3 model architectures (AE, USAD, LSTMED), multiple parameter scopes (full model vs. decoder-only), update cadences (B∈{1,2,4,8}B \in \{1, 2, 4, 8\}), and label perturbation checks, resulting in a full picture on the weakness of TTA.
  • The evaluation uses unadjusted point-level AUPRC and computes anomaly scores strictly prior to current-window parameter updates, avoiding common benchmarking pitfalls like information leakage and point-adjustment inflation.
Critical weaknesses
  • The paper lacks of theoretical analysis explaining why gradient descent on normal samples reduces anomaly reconstruction error. The reviewer believes that even a toy experiment that analyzes linear autoencoder subspace drift under SGD can enhance the paper’s contribution.
  • The evaluation metrics seem to mismatch. Online updates shift the baseline scale of reconstruction error over time, causing temporal non-stationarity. Evaluating these drifting scores with a single global AUPRC can rank early anomalies below late normal points even if instantaneous separability improves. Without evaluating streaming or window-standardized metrics, it remains unproven whether the observed degradation stems from representation collapse or metric artifacts.
  • The primary backbone is a flattened MLP autoencoder operating on a fixed window size of w=12 and stride 12. Flattening temporal sequences into an unconstrained MLP autoencoder makes the model vulnerable to representation collapse (reconstructing anomalies as easily as normal points) while discarding temporal dynamics.
  • While documenting negative results has utility, the paper stops at categorizing failure modes. It does not validate a constructive regularizer, objective modification, or score-calibration method to prevent normal updates from compressing anomaly scores.
Questions for authors
  • Did the authors test any online score standardization (e.g., streaming z-score normalization over a sliding historical window) before computing global AUPRC? How much of the degradation in Daphnet or other NI settings is driven by non-stationary score thresholds rather than degraded sample separability?
  • Why was a uniform window size of w=12w = 12 selected across datasets with vastly different physical sampling rates (from 1 Hz to 64 Hz)? Does Oracle TTA behavior stabilize when ww is chosen based on the underlying periodicity of each system?
4 comments

R2-W1: Why Can Normal-Only Updates Reduce Anomaly Scores and Harm Ranking?

Normal-only updates can reduce anomalous reconstruction errors because changes to shared model parameters affect both normal and anomalous scores. Reducing normal reconstruction loss does not guarantee improved normal–anomaly score separation. We explain this through a first-order SGD analysis, a controlled Linear-AE experiment, and a local observation in a nonlinear AE.

1. First-order gradient explanation. Let LN(θ)L_N(\theta) denote the reconstruction loss on selected normal samples and sθ(x)s_\theta(x) the reconstruction score of a sample. For one SGD step, θ′=θ−η∇θLN(θ)\theta'=\theta-\eta\nabla_\theta L_N(\theta), the first-order change in an anomalous score is

Δs(a)≈−η∇θsθ(a)⊤∇θLN(θ).\Delta s(a)\approx-\eta\nabla_\theta s_\theta(a)^\top\nabla_\theta L_N(\theta).

Thus, the anomalous score can decrease when its gradient aligns with the normal-loss gradient, even though anomalies are excluded from the update objective. For a normal–anomaly pair (n,a)(n,a), the score-margin change is

Δ[s(a)−s(n)]≈−η[∇θsθ(a)−∇θsθ(n)]⊤∇θLN(θ).\Delta[s(a)-s(n)]\approx-\eta[\nabla_\theta s_\theta(a)-\nabla_\theta s_\theta(n)]^\top\nabla_\theta L_N(\theta).

The normal-only objective does not constrain the sign of this margin change.

2. Controlled Linear-AE experiment. We use a two-dimensional rank-one Linear-AE represented by an orthogonal projector and optimized with angular SGD. For a point with magnitude rr and direction ϕ\phi, its reconstruction error under projection direction α\alpha is sα(x)=r2sin⁡2(ϕ−α)s_\alpha(x)=r^2\sin^2(\phi-\alpha). Updating the projection direction toward shifted normals can therefore increase or decrease anomalous reconstruction error depending on anomaly geometry.

Rotating test-time normals by 30° while keeping the source model fixed reduces Frozen AUPRC from 1.0000 to 0.9356. Favorable and Harmful conditions share identical shifted normals, source initialization, normal update samples, and 128-step update trajectories. Only anomaly geometry differs, and their Frozen anomalous-score distributions are identical. No anomalies enter the updates.

Across five seeds, both conditions reduce normal update-set loss from 0.2599 to 0.0103. Yet on independent held-out samples, AUPRC increases to 1.0000 (Favorable) but decreases to 0.3410 (Harmful). Mean anomalous reconstruction error changes from 0.4939 to 1.4578 in the Favorable condition, versus 0.4939 to 0.0014 in the Harmful condition, below the adapted normal mean of 0.0104.

The same normal-only update trajectory can therefore improve normal reconstruction while producing opposite anomaly-ranking outcomes, depending solely on anomaly geometry.

3. Supporting evidence from a nonlinear AE. We examined 20 predetermined checkpoints per trajectory across 60 Oracle trajectories. As an illustrative example, Daphnet window 726 (zero-indexed; seed 42, AdamW 1e−4) contains 12 benchmark-labeled normal points.

Scoring the same fixed future normal and anomalous samples immediately before and after this update, current-window normal loss decreases by 0.0045. Meanwhile, mean future anomaly scores decrease by 0.0093 and mean future normal scores increase by 0.00081. The anomaly-minus-normal gap narrows by 0.0101, and the correctly ordered pair fraction declines from 0.4651 to 0.4634.

The controlled experiment provides a geometric explanation for harmful normal-only updates, while the Daphnet probe demonstrates a corresponding local objective–ranking conflict in a nonlinear AE.

R2-W2/Q1: Temporal Score Non-Stationarity and Global AUPRC

Causal score standardization substantially changes the measured AUPRC effects, but oracle-only-gain (OOG) and neither-improves (NI) outcomes remain under all tested calibration rules. Global AUPRC ranks scores emitted throughout the online stream, so comparability across time matters.

1. Causal score-standardization test. We evaluated rolling standardization with H = 128, 512, 2048 preceding windows, using only past scores and source-validation initialization. Frozen, Practical, and Oracle maintain separate score histories. Calibration affects evaluation only: model updates, trajectories, and sample selection are unchanged. Each adaptive arm is compared with Frozen under the same calibration rule.

Scoring ruleBI / OOG / NI / POGOriginal 75 negative Oracle effects still negative
Raw scores27 / 63 / 90 / 075 / 75
H = 12825 / 63 / 92 / 014 / 75
H = 51225 / 50 / 95 / 1033 / 75
H = 204828 / 56 / 86 / 1035 / 75

Calibration changes the signs of many originally negative Oracle effects and alters outcome classifications. Nevertheless, OOG and NI remain substantial at all three history lengths.

2. Relative improvement versus absolute detection. On Daphnet, the median paired Oracle-minus-Frozen effect changes from −7.16 pp (raw) to −0.16 pp (H = 512). Yet median absolute AUPRC drops from 0.2842 to 0.1329 for Oracle and from 0.3557 to 0.1352 for Frozen. (Paired-effect medians are not obtained by subtracting separate arm medians.) Hence, a smaller relative deficit does not imply better absolute detection.

Causal calibration reveals score-comparability sensitivity, but does not isolate how much degradation is due to temporal scale drift. Separately, the fixed-held-out-set Linear-AE experiment and fixed-future-sample Daphnet probe in W1 show that normal-only parameter updates can harm ranking without mixing scores recorded at different times.

R2-W3/Q2: Robustness Across Backbones and Window Lengths

Both oracle-only-gain (OOG) and neither-improves (NI) regimes persist with a recurrent backbone and across a nine-family window-length sweep; they are not specific to the original flattened AE at w = 12.

Backbone architecture. Our primary MLP-AE backbone is directly relevant to recent TSAD-TTA research, as both M2N2 and CANDI use MLP-based autoencoders in their evaluations. Although the flattened MLP lacks an explicit recurrent temporal inductive bias, submitted Table 2 also evaluates recurrent LSTMED (28 OOG and 140 NI cases) and USAD (52 OOG and 99 NI cases), each across 180 matched configurations. Thus, the coexistence of both regimes is not limited to the primary MLP-AE.

Window-length robustness. We evaluated w ∈ {12, 24, 48} across all nine benchmark families, four optimizer configurations, and five seeds (180 planned cells per length), using a common evaluation prefix for comparison, including the w = 12 reference.

Window lengthBIOOGNIPOGValid cells
122763900180/180
242655990180/180
4831441000175/180

At w = 48, five SMD configurations are undefined due to numerical failures and are excluded rather than counted as NI. All 90 original NI cases remain NI at both longer window lengths. Window length affects the exact classifications, but both OOG and NI remain substantial. These fixed-length comparisons do not test per-system periodicity-based window selection.

R2-W4: Constructive Guidance and Tests of Candidate Mitigations

The matched comparison distinguishes selection-sensitive cases from failures that persist after replacing practical selection with benchmark-labeled normal selection. This distinction points to different aspects of TTA that warrant attention.

1. Diagnostic guidance. In the 180-cell AE grid, 63 OOG cases gain more than 0.5 pp under Oracle while Practical TTA does not achieve a clear gain, motivating investigation of practical sample selection and normal-sample coverage. In 90 NI cases, neither arm achieves a clear gain; replacing the selector alone is insufficient under the evaluated updater. These cases motivate examining the update objective, optimization dynamics, model constraints, and scoring procedure, without assigning a unique cause.

2. Candidate interventions. We tested decoder-only and SANA-style restricted adaptation, selected-count loss normalization, and evaluation-only causal score calibration. Substantial NI populations persist under these changes. None establishes a generally reliable safeguard; in particular, calibration changes score evaluation rather than the underlying parameter updates.

The practical implication is to evaluate proposed remedies by downstream anomaly ranking, rather than treating cleaner update masks or lower normal reconstruction loss as sufficient evidence of successful TTA.

The reviewer appreciates the authors’ extra explanation and experiments. This new information has partly eased the concerns, so the rating is adjusted.

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

This paper investigates whether restricting test-time adaptation (TTA) to benchmark-labeled normal samples is sufficient to improve reconstruction-based time-series anomaly detection. The authors introduce a matched experimental framework comparing a frozen detector, practical TTA based on predicted-normal sample selection, and an oracle TTA variant that uses ground-truth normal labels for update selection while keeping the remaining adaptation procedure unchanged. Experiments across nine benchmark datasets, four optimizer configurations, and five random seeds reveal that normal-only adaptation does not consistently improve detection performance. Among the 180 experimental settings, 63 show a clear detection gain only under oracle normal-only TTA, while 90 show no clear gain under either practical or oracle adaptation. Furthermore, although oracle updates consistently reduce the immediate reconstruction objective, these reductions do not reliably translate into improved anomaly ranking. Additional analyses across model architectures, adaptation variants, and label perturbations support these observations. The paper concludes that improving update-sample selection alone is insufficient to guarantee successful TTA, highlighting the mismatch between reconstruction optimization and downstream anomaly detection performance.

Critical strengths
  1. Clear and well-motivated research question. The paper investigates an important assumption in test-time adaptation for time-series anomaly detection: whether selecting only normal samples for model updates is sufficient to improve detection performance. This question is relevant to existing TTA methods that emphasize reliable sample selection.

  2. Well-structured experimental design. The matched comparison among Frozen, Practical, and Oracle TTA provides a useful framework for examining the role of update-sample selection. By keeping the model initialization, optimizer, learning rate, and update protocol consistent, the study reduces several potential confounding factors and enables a more focused comparison.

  3. Extensive empirical evaluation and robustness analysis. The experiments cover nine benchmark datasets, four optimizer configurations, and five random seeds. The authors further examine different reconstruction-based backbones (AE, USAD, and LSTMED), update scopes, adaptation variants, and label perturbations. These evaluations provide supporting evidence that the observed failure patterns are not limited to a single model or experimental configuration.

  4. Useful insights into TTA failure patterns. The distinction between oracle-only-gain and neither-improves cases provides a more informative characterization of TTA failures than aggregate detection performance alone. Furthermore, the analysis of reconstruction-loss reduction and anomaly-score ordering highlights the mismatch between optimizing the reconstruction objective and improving downstream anomaly detection performance.

Critical weaknesses
  1. Incomplete isolation of anomalous information in the Oracle setting. Although Oracle TTA excludes benchmark-labeled anomalous points from the reconstruction loss, the entire input window is still fed into the model. Since the AE backbone processes flattened windows, anomalous observations may influence the representations and gradients associated with normal points. Consequently, the Oracle setting does not completely isolate adaptation from anomalous information. An additional experiment using anomaly-free input windows would help clarify whether this factor contributes to the observed failures.

  2. Potential confounding factors in the matched intervention. While Practical and Oracle TTA share the same optimization settings, they may select different numbers of samples for each update. Since the masked reconstruction loss is normalized by the full window length rather than the number of selected samples, differences in update performance may reflect both sample-selection quality and effective gradient magnitude. Additional controls matching the number of selected samples or normalizing the loss by the selected sample count would help disentangle these factors.

  3. Limited explanation of the underlying failure mechanisms. The paper demonstrates that reducing reconstruction loss on normal samples does not necessarily improve anomaly detection. However, the analysis remains largely observational and does not sufficiently explain why normal-only updates degrade anomaly ranking in certain settings. Although selective compression and net pair gain provide useful insights, their within-dataset associations with detection improvement are relatively weak. Further analysis of parameter drift, anomalous-score changes, or optimization dynamics could provide a deeper understanding of these failures.

  4. Limited representativeness of the evaluated TTA methods and backbones. The main experiments rely on a relatively simple threshold-based Practical TTA strategy and an AE backbone. Although the authors include USAD, LSTMED, and M2N2-/CANDI-style adaptation variants, the alternative adaptation strategies are evaluated on smaller experimental grids, and the evaluated backbones do not cover more recent reconstruction architectures. Broader evaluations would strengthen the generalizability of the findings.

  5. Insufficient analysis of dataset characteristics and distribution shifts. The effectiveness of Oracle TTA varies substantially across datasets, with large improvements on some benchmarks and degradation or negligible changes on others. However, the paper does not systematically investigate which dataset characteristics or types of distribution shift explain these differences. Analyzing shift severity, normal-pattern variability, or the similarity between normal and anomalous observations could help identify the conditions under which normal-only adaptation is beneficial or harmful.

  6. It is recommended to provide anonymized code during the review stage to enhance reproducibility and credibility.

Questions for authors
  1. Oracle adaptation: Since anomalous observations remain in the input windows despite being excluded from the reconstruction loss, could they still influence model updates? Would using anomaly-free input windows change the results?

  2. Confounding factors: Practical and Oracle TTA may select different numbers of samples, resulting in different effective update magnitudes. Would the findings remain consistent when controlling for sample counts or normalizing the loss by the number of selected samples?

  3. Failure mechanisms: Why do normal-only updates sometimes degrade anomaly detection despite reducing reconstruction loss? Could the authors provide further analysis of anomalous-score changes or parameter drift?

  4. Dataset heterogeneity: What dataset characteristics or distribution-shift patterns explain the substantial differences in Oracle TTA performance across datasets?

3 comments

W1/Q1 — Do Anomalous Inputs Explain Oracle Failures?

The two central failure patterns observed in our primary AE experiments persist under stricter controls on anomalous inputs. We acknowledge that masking anomalous positions in the reconstruction loss does not prevent their values from influencing gradients in the flattened-window AE. We therefore conducted two additional controls: (1) strict clean-window, which skips updates on windows containing anomalies, and (2) sanitized-input, which replaces anomalous input values with source-training means. Both controls preserve all 180 original outcome classifications (BI/OOG/NI/POG = 27/63/90/0), including all 90 neither-improves cases. Substantial Oracle degradation also persists on Daphnet (median Oracle-minus-Frozen ΔAUPRC: −7.16 pp originally, versus −7.32 and −6.55 pp under the two controls, respectively).

W2/Q2 — Does Loss Normalization Explain the Failure Regimes?

Both oracle-only-gain and neither-improves regimes persist under selected-count loss normalization. To address the concern that averaging the masked reconstruction loss over the full window may affect effective gradient magnitudes, we repeated the full 180-cell AE experiment with the loss normalized by the number of selected points, keeping the original selection rules and online optimization protocol unchanged. Only 5/180 outcome classifications changed (BI/OOG/NI/POG: 27/63/90/0 → 30/60/90/0), and all 90 original neither-improves cases persisted.

W3/Q3 — Why Can Normal-Only Updates Harm Anomaly Ranking?

Normal-only updates can harm anomaly ranking because reducing reconstruction error on normal samples does not constrain how anomalous scores change relative to normal scores. We examine this with a controlled Linear-AE experiment and a local probe of an actual nonlinear AE update.

  1. Controlled geometric explanation

We use a rank-one Linear-AE represented as a one-dimensional orthogonal projector and optimized with angular SGD. Rotating test-time normals by 30° while keeping the source model fixed reduces Frozen AUPRC from 1.0000 to 0.9356. Favorable and Harmful conditions share the shifted normals, source model, normal update samples, and 128-step update trajectory; only anomaly geometry differs, with identical Frozen anomalous-score distributions. Across five seeds, both reduce normal update-set loss from 0.2599 to 0.0103, yet adapted AUPRC reaches 1.0000 (Favorable) versus 0.3410 (Harmful). Aligning the reconstruction subspace with shifted normals can also make certain anomalies easier to reconstruct, thereby damaging normal–anomaly score separation.

  1. Supporting evidence from an actual AE update

We examined 20 predetermined checkpoints per trajectory across 60 Oracle trajectories. As one illustrative case, a Daphnet update at zero-indexed window 726 (AE, seed 42, AdamW 1e−4) uses 12 benchmark-labeled normal observations. We score the same fixed future normal and anomalous samples immediately before and after this step. Current-window normal loss decreases by 0.00454, while mean future anomalous scores decrease by 0.00933 and mean future normal scores increase by 0.00081. The mean anomaly-minus-normal gap narrows by 0.01015, and the correctly ordered pair fraction falls from 0.46509 to 0.46338.

These experiments demonstrate a concrete way in which normal-only updates can worsen anomaly ranking despite reducing normal reconstruction loss. The Linear-AE experiment provides a controlled geometric explanation, while the Daphnet probe shows a corresponding harmful local effect in a nonlinear AE.

W4 — Representativeness of Backbones and TTA Methods

Our primary MLP-AE backbone is directly relevant to recent TSAD-TTA research, as both M2N2 and CANDI use MLP-based autoencoders in their evaluations. Beyond this backbone, we evaluate USAD and recurrent LSTMED under full-model and decoder-only adaptation (Table 2), together with M2N2- and CANDI-style adaptation variants (Appendix Table B.2). Both oracle-only-gain (OOG) and neither-improves (NI) regimes persist across these evaluated configurations.

W5/Q4 — What Explains Heterogeneous Oracle Outcomes Across Datasets?

Normal-distribution shift is associated with Oracle detection gains, but shift magnitude alone does not determine adaptation outcomes.

1. Dataset-level shift analysis. We measured the marginal Wasserstein-1 distance between source and benchmark-labeled test-normal distributions. Across nine benchmark families, measured shift shows a positive Spearman association with Oracle-minus-Frozen AUPRC gains (ρ = 0.60). This is a descriptive association, and marginal Wasserstein-1 does not capture temporal dependencies, multivariate interactions, or normal–anomaly geometry.

2. Evidence beyond shift magnitude. The controlled Linear-AE experiment in W3 shows that identical shifted normal distributions and normal-only update trajectories can produce opposite detection outcomes depending solely on anomaly geometry. This demonstrates that normal-distribution shift alone is insufficient to determine whether adaptation improves anomaly ranking.

I thank the authors for their patient explanations and additional experiments, which have substantially addressed my questions. However, I believe the empirical evidence supporting the proposed failure mechanism remains insufficient. The authors examined 1,200 checkpoints across 60 Oracle trajectories, but have not reported what proportion of these updates reduce the score gap between normal and anomalous samples, or whether this phenomenon is systematically associated with the experimental results for NI, OOG, and other settings.

The paper currently promises to release the implementation code, experimental configurations, and result-processing scripts after publication, but an accessible anonymous code repository or complete implementation has not been provided during review. Although the authors added extensive experiments during the rebuttal period, I still find it difficult to independently verify their implementation and results. I therefore maintain my original score.

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

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