acceptodds
Under review as a conference paper at ICLR 2027

KRAFT: Koopman-Referenced Adaptive Flow for Time-Series Anomaly Detection under Latent Domain Shifts

Abstract

Time-series anomaly detection (TSAD) in real-world systems is challenged by evolving normal behavior, where distribution shifts can be misidentified as anomalies. Existing drift-aware, domain adaptation, and test-time adaptation methods often require explicit domain information or risk anomaly contamination during adaptation. We study TSAD under latent domain shifts, where anomaly labels, domain labels, and shift boundaries are unavailable during deployment. We propose KRAFT, a Koopman-Referenced Adaptive Flow framework that models predictable normal evolution through Koopman latent propagation and constructs a dynamics-conditioned normal reference via conditional flow matching. A Koopman-pushed maximum mean discrepancy (KP-MMD) identifies residual mismatch beyond modeled evolution, while validation-guided restricted adapter updates accommodate latent shifts without absorbing anomalies. Theoretical analysis establishes conditions for residual shift detection and preservation of anomaly separability during adaptation. Experiments on diverse TSAD benchmarks, drift datasets, and multi-domain scenarios demonstrate that KRAFT effectively adapts to evolving normal behavior while maintaining anomaly detection capability.

Primary area:
learning on time series and dynamical systems
Keywords:
Time-Series Anomaly Detection, Latent Domain Shift, Koopman Operator, Flow Matching

Reviews

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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_cSedOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper proposes KRAFT for time-series anomaly detection (TSAD) under latent domain shifts, where neither domain identities nor shift boundaries are known. KRAFT leverages Koopman-predicted latent dynamics to condition a flow-matching model that generates an evolving normal reference. A Koopman-compensated maximum mean discrepancy (MMD) statistic detects persistent unexplained changes and triggers restricted adapter updates, which are accepted according to a held-out capped-risk criterion. Buffered observations are then rescored using the selected adapter. The paper provides conditional theoretical guarantees and evaluates the approach on public TSAD benchmarks, synthetic domain-shift datasets, and real-world case studies.

Critical strengths
  1. The paper addresses an important and practically relevant problem. Distinguishing shifts in normal behavior from genuine anomalies, without access to domain labels or shift boundaries, is a meaningful challenge. The proposed separation between predictable evolution and unexplained distributional changes offers a coherent approach to this problem.

  2. The empirical investigation is broad and includes informative component analyses. The evaluation spans 16 public TSAD datasets and four domain-drift datasets, employs complementary metrics and incorporates ablations and mechanism-level diagnostics. These results provide encouraging evidence that the complete framework is effective across diverse settings.

Critical weaknesses
  1. The evaluation does not sufficiently control for deferred decisions and retrospective adaptation. Appendix A.4 explicitly states that the adapter used to rescore a buffered observation may depend on that observation as well as on later observations within the episode. While this constitutes a legitimate deferred-detection setting, Appendix C.3 preserves each baseline’s original inference regime; consequently, identical chronological splits do not guarantee equivalent information access or decision delays. The paper does not report initial-versus-final detection performance, finalization-delay distributions, or comparisons under matched buffering and information constraints. As a result, it is difficult to determine how much of the reported advantage stems from the proposed method versus from the opportunity to adapt before retrospectively finalizing predictions. This substantially limits confidence in the comparative performance claims.

  2. The specific methodological advance is not sufficiently established relative to the closest alternatives. Conditional flow matching has already been applied to TSAD (e.g., SGFM), yet this line of work is neither discussed nor evaluated. Furthermore, CANDI, which is cited and directly relevant to selective adaptation under distribution shift, is absent from the comparisons. The existing ablations support the usefulness of the components, but they do not establish whether Koopman propagation confers a distinctive advantage over an alternative learned dynamics predictor within the complete detection pipeline. The TCN comparison in the battery study is informative, but it evaluates representations rather than end-to-end anomaly detection. While the combination may be novel, stronger positioning and controlled comparisons are needed to establish its substantive contribution.

Questions for authors
  1. Are the main results computed using the deferred final scores? How much of the improvement remains when only the retained initial scores are used? Please report the distribution of finalization delays and clarify whether the advantage persists when adaptive baselines receive equivalent access to buffered observations and comparable decision-delay budgets.

  2. How does KRAFT compare with CANDI under compatible data assumptions and evaluation protocols? Can the authors provide a controlled comparison in which Koopman propagation is replaced by a learned nonlinear latent predictor within the full detection pipeline, while retaining the flow model and adaptation procedure? Such a comparison would help distinguish the benefit of the proposed Koopman reference from that of predictive conditioning more generally.

  3. The validation ablation and Appendix D.2 diagnostics are helpful. However, capped validation can still favor an update that pushes a persistent anomaly below the detection threshold, and Theorem 1 provides only a conditional bound on recall loss. What evidence indicates that accepted updates preserve anomaly recall when persistent or recurring anomalies enter both the adaptation and validation buffers? Reporting recall before and after refinement in such cases would materially strengthen the central contamination-resistance claim.

10 comments

Thank you for your thoughtful feedback. We first address the weaknesses you identified and then respond to each of your questions in more detail. We will provide the revised manuscript as soon as possible.

Response to the Critical Weaknesses

W1. Deferred decisions and access to later observations. Though our manuscript describes retrospective buffer rescoring as part of the overall procedure, we have to clarify that our Table 1 uses the initial arrival-time scores (siinits_i^{\mathrm{init}}), retained separately as described in Appendix A.4, rather than the deferred final scores (sifinals_i^{\mathrm{final}}). Each initial score is computed from the arriving observation, its preceding history, and the adapter accepted before the current block. In other words, the initial scores used in Table 1 are never replaced by scores computed with later observations or subsequently updated adapters. Thus, Table 1 evaluates online adaptation without retrospective changes to the evaluated scores. Under this protocol, KRAFT leads Sub-PCA by 7.38 percentage points on Aff-F (85.35 vs. 77.97) and 1.01 points on VUS-PR (33.24 vs. 32.23). Allowing deferred rescoring in KRAFT-R adds a further 2.11 and 1.06 points, respectively. We report this incremental gain together with its delay: across the 16 datasets, median release delays ranged from 16 to 19 observations, and on 10 datasets the 95th percentile was at most 31 observations. Q1 clarifies the information available to KRAFT at scoring time and distinguishes the two protocols. NgPM Q5 gives all four performance metrics, and RHFw Q1 gives the delay distribution for each dataset.

W2. Methodological contribution and comparison with the closest alternatives. SGFM established conditional flow matching as a generator for TSAD. KRAFT’s contribution is to use the same learned dynamics to generate a normal reference and to decide when that reference needs updating. Koopman propagation conditions the generator through a bidirectional Gaussian bridge and advances the historical window used by KP-MMD. A persistent mismatch then triggers a candidate update subject to held-out validation. We tested this design in the complete detector: with the flow architecture and adaptation rule fixed, Koopman led all three learned propagators on all four metrics across the 16 public datasets in our single-seed comparison. A complementary test on five CDS streams shows how the propagator affected adaptation timing. Koopman and the latent Neural ODE each initiated adaptation ten times; all ten Koopman starts matched distinct true domain boundaries, compared with eight for the Neural ODE. We also evaluated CANDI on the same training and test data using its official defaults. Across the five multivariate datasets, arrival-time KRAFT led on all four means, including 86.08 vs. 74.32 on Aff-F. Q2 details the end-to-end replacements, the CANDI comparison, and KRAFT’s relationship to SGFM.

Q1. Initial scores, deferred scores, and decision delays

Do the main results use deferred scores? How much of the advantage remains with initial scores, and does it persist when adaptive baselines receive the same buffering and delay budget?

Table 1 reports arrival-time scores with online adaptation enabled and no retrospective rescoring. Under this protocol, KRAFT achieves 85.35 Aff-F and 33.24 VUS-PR, versus 77.97 and 32.23 for Sub-PCA. Our response to NgPM Q5 compares initial and rescored results on all four metrics. RHFw Q1 reports the release-delay distribution for each dataset. We apologize for the ambiguity and will label the scoring protocol in Table 1 and Appendix A.4.

However, it is worth noting that later observations can also inform earlier scores in TimeRCD (Lan et al., 2026) and Anomaly Transformer (Xu et al., 2022) through full-window attention, and in TSB-AD's Sub-PCA (Liu and Paparrizos, 2024) through center-aligned subsequence scores. In this sense, KRAFT-R can also be viewed as using information from future observations to score the current observation at time tt.

Q2. CANDI, learned propagation alternatives, and SGFM

How does KRAFT compare with CANDI under compatible protocols? Does Koopman propagation improve end-to-end detection over a learned nonlinear predictor when the flow model and adaptation procedure are retained?

CANDI. We used the authors’ TSB-AD implementation of CANDI with the same chronological training prefixes and test segments as KRAFT. Under its default online configuration, CANDI reserves the final 20% of each training prefix to construct its validation reference set and uses the 95th percentile of scores on the training portion to help select adaptation samples. CANDI records each test batch’s scores before updating on that batch. We compared these continuous scores with KRAFT’s arrival-time scores. Both methods were evaluated using the same TSB-AD protocol: Aff-F, F1-T, and point F1 each use their metric-specific threshold search on the labeled test series, VUS-PR integrates over thresholds, and each dataset receives equal weight. NgPM Q5 gives the full 16-dataset comparison. For the five multivariate datasets, which match CANDI's intended setting, the means are:

MethodAff-FF1-TPoint F1VUS-PR
KRAFT, initial scores86.0840.0634.1525.28
CANDI74.3237.2233.3523.33

The mean point-F1 gap is 0.80 points here, and CANDI leads on point F1 and VUS-PR on SWaT.

Controlled propagation replacement. Each alternative supplied a predicted latent state to both the flow model and the MMD reference window. We kept the flow architecture, training budget, adaptation rule, and arrival-time scoring fixed. Across 16 datasets (one seed), replacing Koopman with the strongest alternative, a latent Neural ODE, reduced mean Aff-F, F1-T, point F1, and VUS-PR by 1.80, 2.55, 2.16, and 2.73 percentage points, respectively. The Aff-F drops were larger for the residual MLP (3.98) and the unconstrained linear generator (7.56). Thus, the choice of propagator affected end-to-end detection even when every variant retained predictive conditioning (NgPM Q2).

Positioning relative to SGFM. KRAFT's main contribution is to use the same learned Koopman dynamics to generate a normal reference and to detect departures from its predicted evolution. Persistent departures trigger candidate adapter updates, which are accepted only after held-out validation. Conditional flow matching serves as our generator and has precedent in TSAD, including SGFM (He et al., 2024). Within this component, we introduce a Koopman-informed bidirectional Gaussian bridge (Eq. 4) that combines forward and backward predictions from the two training endpoints to supervise intermediate velocities. To our knowledge, this specific bridge construction has received limited attention in flow-matching TSAD. We will discuss SGFM and related work and clarify these contributions in the revision.

Q3. Recall when a persistent anomaly contaminates both buffers

When persistent or recurring anomalies enter both the adaptation and validation buffers, how much anomaly recall is retained after an accepted update?

An update can reduce capped validation loss by pushing an anomaly score below the detection threshold. To test this failure mode, we selected candidates for which anomalous points in both buffers came from the same labeled event lasting at least 256 observations. The gate accepted 13 of 14 such candidates on PSM and 18 of 20 on SWaT. We counted each distinct event once and rescored it offline with the pre-update and end-of-episode adapters, holding the observations, scoring statistics, and threshold fixed.

DatasetAccepted candidates / eventsAnomaly pointsRecall beforeRecall afterInitial true positives retainedDetections lost / gained
PSM13 / 921,38032.00%32.33%6,445 / 6,842 (94.20%)397 / 468
SWaT18 / 839,80838.51%38.63%14,659 / 15,331 (95.62%)672 / 719

Refinement retained 94.20% of previously detected anomaly points on PSM and 95.62% on SWaT. Newly detected points slightly outnumbered lost detections, so pooled recall changed little. Recall nevertheless fell in 4 of 9 PSM events and 3 of 8 SWaT events, with maximum drops of 1.30 and 0.73 percentage points, respectively. The longest SWaT attack accounted for 90.2% of anomaly points in this subset. Excluding it, the remaining seven events still retained 95.15% of initial detections. These results quantify the masking observed within persistent events. RHFw Q6 reports the complementary online comparison with and without validation.

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

The paper looks at TSAD when the "normal" distribution drifts over time and neither the domain labels nor the change points are known. The proposed method, KRAFT, has three pieces. (i) A normal reference generator: a TCN encoder maps the history to a latent zz, a stable linear Koopman generator K=(A−A⊤)−diag(softplus(bK))K=(A-A^\top)-\mathrm{diag}(\mathrm{softplus}(b_K)) propagates it, and a conditional flow-matching velocity field, trained on a bidirectional Gaussian bridge, produces a one-step-ahead prediction x^t\hat x_t conditioned on the propagated latent. (ii) A shift detector, KP-MMD, which compares the current latent window with the previous window pushed forward by exp⁡(KΔ)\exp(K\Delta). The idea is that only the shift the Koopman model cannot explain ("exogenous") should trigger adaptation. (iii) When the smoothed and hysteresis-filtered KP-MMD evidence persists for pp blocks, rank-4 adapters in the velocity network get one SGD step per block. A candidate is accepted only if it lowers a threshold-capped residual risk on the most recent part of the buffer by at least γ\gamma. Scores in the pending buffer are then recomputed with the accepted adapter, so final decisions come with a delay.

On the theory side there is a concentration-type bound on KP-MMD (Prop. 1), a separation condition (Cor. 1), and Theorem 1, which says accepted updates reduce the normal capped risk and that recall loss is bounded by the near-threshold anomaly mass plus db2/t2d_b^2/t^2. Experiments cover 16 TSB-AD datasets, INSECTS, three synthetic multi-domain suites (BDS/MDS/CDS, 5 sequences each), a NASA battery probe study and an industrial pump case. KRAFT ranks first on average on all four metrics, and the ablations show adaptation is the most important component.

Critical strengths
  1. The comparison with baselines may not be on equal footing, and most of the gain seems to come from the adaptation + deferred rescoring path.

    • In KRAFT, the final score of a sample in the pending buffer is computed after adaptation on data that includes that sample and later ones (App. A.4 states this explicitly: "it does not make the refined score an arrival-time prediction"). As far as I can tell, all offline baselines score at arrival time with a fixed model. Only M2N2 adapts at all.
    • Table 2 shows that w/o adaptation, KRAFT drops to 71.19 Aff-F and 28.00 VUS-PR on the public benchmarks. Both are below Sub-PCA (77.97 / 32.23), and the Aff-F is also below TranAD and OmniAnomaly. So the reference generator itself (Koopman + flow matching, which is most of the technical contribution) does not outperform Sub-PCA on these benchmarks. The headline numbers come almost entirely from the test-time machinery.
    • On top of that, the threshold-free metric tells a much weaker story than the thresholded ones. On VUS-PR, KRAFT vs. Sub-PCA is 33.24 vs. 32.23, and Sub-PCA or TranAD/USAD clearly win on NAB, NEK and SWaT. The big margins are on Aff-F / F1 / F1-T. There KRAFT uses its own calibrated 0.99-quantile threshold, but the thresholding protocol for baselines is never stated: App. C.3 promises "result sources" but does not give them. IForest getting exactly 0.00 Aff-F on Power and SWaT also suggests that something may have gone wrong with the baseline thresholding.

    Together, I am not convinced the reported gap reflects better detection rather than a more favorable protocol. This is the main reason for my rating.

  2. The "anti-contamination" mechanism and the theory don't really give the protection claimed.

    • The capped risk min⁡si,u\min{s_i,u} only ignores anomalies that stay above uu. An update that pushes an anomaly from above uu to below uu reduces the capped risk, so it is rewarded. In other words, the criterion can actually favor the masking failure it is meant to prevent. The authors acknowledge this in A.3 ("capping ... does not alone ensure that anomalous patterns cannot be fitted").
    • Long anomalous segments (PSM and SWaT have 11–13% anomaly ratio) will produce persistent KP-MMD mismatch. They therefore open an episode whose validation set is the later part of the same anomaly.
    • Theorem 1 doesn't close this gap. The recall bound q+≥q−−ωb(t)−db2/t2q^+\ge q^- - \omega_b(t) - d_b^2/t^2 follows from Markov's inequality on the prediction displacement and holds for any bounded update, validated or not. The validation step never enters it. Assumption 3 (uniform validation accuracy over temporally dependent, data-selected buffers) is where most of the difficulty lies, and it is assumed rather than shown.
    • Similarly, Cor. 1 is only informative when the propagation mismatch aba_b is small relative to Δexo\Delta_{\text{exo}}. But whether the Koopman model correctly captures "normal continuation" is exactly the point in question.
    • Assumption 1 is a definition rather than an assumption: endo vs. exo is defined relative to the model's own continuation, so the split is not identifiable from data.

    I'd suggest toning down "theoretical guarantees for preserving anomaly separability".

Critical weaknesses
  1. Protocol fairness. Please report KRAFT with arrival-time scores siinits^{\text{init}}_i only (adaptation on, no buffer rescoring), together with the release delay LiL_i per dataset. Please also state how baseline thresholds were chosen and whether baselines were rerun or taken from TSB-AD. If the gain largely survives under a shared threshold rule and no rescoring, my main concern goes away.
  2. KP-MMD at Δ=nr=100\Delta=n_r=100. With a contractive KK, ∣exp⁡(100K)∣op≤e−100λ∗|\exp(100K)|{op}\le e^{-100\lambda*}. If the spectra are similar to the battery study (ρ(exp⁡K)≈0.91\rho(\exp K)\approx 0.91–0.960.96), the pushed-forward reference could collapse towards the origin. KP-MMD would then mostly measure the norm of the current latents rather than residual shift. Can you report ∣exp⁡(Knr)∣|\exp(K n_r)| and the propagated-vs-current latent norm ratio on the TSAD benchmarks?
  3. Contamination on long anomalies. What happens to recall on long anomalous segments (e.g. PSM/SWaT), with and without validation? Relatedly, given the per-observation adapter displacement of about 10−510^{-5} in Table 8, how does adaptation produce a 38-point Aff-F gain on the drift datasets?
  4. Hyperparameter selection. The defaults (nr=100n_r=100, p=3p=3, γ=0.02\gamma=0.02) are best on all four averaged metrics for all three parameters. Since the sensitivity study is run on the evaluation streams, how were the defaults selected? If they were selected using these same results, the reported numbers would be somewhat optimistic.

Post-rebuttal update: The authors clarified that Table 1 reports arrival-time scores without rescoring and that all methods share the TSB-AD threshold rule. They also corrected the IForest baseline. This resolves my main concern about protocol fairness, and I have raised my rating from 2 to 3. My comment below the rebuttal discusses the remaining issues: the VUS-PR gain over Sub-PCA is not significant, the hyperparameters were chosen on the evaluation data, the interpretation of KP-MMD at n_r = 100 is not supported, and the introduction and conclusion still overstate the theoretical guarantees.

Questions for authors
  1. Protocol fairness. Please report KRAFT using the arrival-time scores siinits^{\text{init}}_i only, i.e. adaptation still happens but no buffer rescoring. Also report the distribution of the release delay LiL_i on each dataset. If most of the gain survives without rescoring, my main concern largely goes away.
  2. Baseline thresholds. How were thresholds chosen for the baselines on Aff-F / F1 / F1-T? Were their numbers rerun in your own pipeline or taken from TSB-AD? Could you report results where all methods, including KRAFT, use the same threshold rule, e.g. the same 0.99 quantile on the same calibration split?
  3. KP-MMD at Δ=nr=100\Delta=n_r=100. With a contractive KK, ∣exp⁡(100K)∣op≤e−100λ∗|\exp(100K)|{op}\le e^{-100\lambda*}. The battery study gives ρ(exp⁡K)≈0.91\rho(\exp K)\approx 0.91–0.960.96. If the spectra on the TSAD benchmarks are similar, the pushed-forward reference could be shrunk by a factor of roughly 10−210^{-2} or more, i.e. collapsed towards the origin. In that regime KP-MMD mostly measures how far the current latents are from zero, not "residual shift after compensation". Can you report ∣exp⁡(Knr)∣|\exp(K n_r)| and the norm ratio of propagated vs. current latents on the TSAD benchmarks? And explain why the result is still meaningful?
  4. Ablation magnitudes. At deployment H=1H=1, so zi,τ=exp⁡(Kτ)ziz_{i,\tau}=\exp(K\tau)z_i is close to ziz_i. Yet replacing it with ziz_i drops Aff-F by 11 points on public data (e.g. SMD 92.69 → 66.77). Why is the effect so large? How many seeds are the ablation numbers averaged over, and what is the variance?
  5. Hyperparameter selection. The default (nr=100n_r=100, p=3p=3, γ=0.02\gamma=0.02) is the best of five settings for all four metrics averaged over all 20 datasets, for all three hyperparameters. Since the sensitivity study is run on the evaluation streams themselves, could you clarify how the defaults were selected? If they were picked based on these results, the reported numbers would be somewhat optimistic.
  6. Contamination diagnostic. Table 8 shows adapter displacement per observation of about 10−510^{-5}. With displacement that small, how does adaptation produce a 38-point Aff-F gain on the drift datasets (Table 2)? I'd also like to see what happens to recall on long anomalous segments, specifically on PSM/SWaT, with and without validation.
  7. Statistics. The Wilcoxon tests treat 4 metrics on the same dataset as independent observations, at α = 0.10. Can you redo them per metric at the dataset (or sequence) level? With 5 sequences per synthetic suite and std of ±20–30, I'm not sure the drift-benchmark conclusions are robust.
8 comments

Thank you for your thoughtful feedback. We first address the weaknesses you identified and then respond to each of your questions in more detail. We will provide the revised manuscript as soon as possible.

Response to the Critical Weaknesses

W1. Protocol fairness and the source of the performance gain. Though our manuscript describes retrospective buffer rescoring as part of the overall procedure, we have to clarify that our Table 1 uses the initial arrival-time scores (siinits_i^{\mathrm{init}}), retained separately as described in Appendix A.4, rather than the deferred final scores (sifinals_i^{\mathrm{final}}). Each initial score is computed from the arriving observation, its preceding history, and the adapter accepted before the current block. In other words, the initial scores used in Table 1 are never replaced by scores computed with later observations or subsequently updated adapters. Thus, Table 1 evaluates online adaptation without retrospective changes to the evaluated scores. With historical rescoring disabled in both runs, enabling online adaptation raised mean Aff-F from 71.19 to 85.35 and VUS-PR from 28.00 to 33.24 across the 16 public datasets. Under this arrival-time protocol, KRAFT exceeded Sub-PCA by 7.38 Aff-F points (13 wins in 16 datasets, paired p=0.00098p=0.00098). The reference generator also contributed under a fixed adaptation protocol: on SMD, removing Koopman conditioning lowered Aff-F in each of three paired runs, with a mean drop of 25.92 points. Q1 distinguishes arrival-time scoring from optional rescoring and reports release delays. Q4 gives the seed-level ablation, and Q7 reports the paired comparisons.

W1, continued. Thresholds and baseline results. We verified that Table 1 uses the same TSB-AD rule for KRAFT and the baselines: each F-score is optimized separately on each labeled test series. The historical 99th-percentile threshold governs KRAFT’s online decisions and capped validation. We also reran IForest on all 768 series, obtaining 78.05 Aff-F on Power and 78.58 on SWaT. With the corrected IForest results, arrival-time KRAFT significantly outperformed 7 of 11 baselines on threshold-independent VUS-PR and 11 of 11 on Aff-F in separate dataset-paired tests at α=0.10\alpha=0.10. Q2 documents the threshold rules, baseline sources, and corrected results. Q7 reports the tests by metric.

W2. What KP-MMD measures after 100-step propagation. Even when the propagated reference is close to zero on the scale of the RBF kernel, KP-MMD depends on pairwise distances within the current window as well as distances to zero. Two windows with identical pointwise latent norms can therefore yield different drift evidence. We also checked whether propagation helps at the actual 100-step horizon. On 13,783 labeled-normal segments, decoding the propagated state gave lower prediction error than decoding the unchanged state on all 16 datasets (mean RMSE ratio 0.8936). Replacing the propagated MMD reference with the unchanged historical window reduced mean Aff-F by 11.19 points and VUS-PR by 4.22 points. Q3 gives the operator norms, observed window ratios, and prediction errors for each dataset.

W3. What the theory establishes about drift and contamination. Assumption 1 defines normal continuation relative to the learned dynamics. Corollary 1 then gives a quantitative separation condition: a shift is detectable when its discrepancy exceeds twice the combined propagation, contamination, and estimation error. Theorem 1 addresses a different decision. Under Assumption 3 on validation accuracy, an accepted update improves normal capped risk when its acceptance margin exceeds the validation-error and contamination terms. The recall bound depends separately on prediction displacement and the mass of anomalies near the threshold. We will make these roles explicit in the revision. Q3 tests propagation against observed normal trajectories, and Q6 directly measures the effect of validation on persistent anomalies.

W3, continued. Long anomalies and adapter displacement. The benefit of validation was largest while a fault persisted. After the first 128 observations of each long event, validation raised arrival-time recall from 22.08% to 28.23% on PSM and from 30.90% to 39.56% on SWaT. Table 8’s displacement statistic averages over all observations of the indicated class, including steps with no update, while an accepted update can affect many subsequent predictions. Figure 14 illustrates that distinction on one CDS stream: enabling adaptation reduced the false-positive rate in the first post-shift domain from 46.3% to 17.3%. Q6 reports the displacement definition, the four-benchmark Aff-F comparison, and the full early- and late-event recall results.

W4. Hyperparameter selection and sensitivity. We selected one global configuration, (nr,p,γ)=(100,3,0.02)(n_r,p,\gamma)=(100,3,0.02), using aggregate performance on the 20 evaluation datasets and applied it across all datasets. The sensitivity study shows how the comparison changes around that choice. When each parameter was moved in turn to either adjacent tested value, all six neighboring configurations exceeded the strongest baseline mean on each of the four metrics, yielding 24 of 24 favorable comparisons. Across the full sweep, the corresponding count was 33 of 48 non-default setting–metric comparisons. Q5 gives the selection procedure, parameter ranges, and metric-specific baseline values.

Response to the Questions

Q1. Arrival-time performance and release delays

Please report KRAFT using only arrival-time scores, with adaptation enabled and buffer rescoring disabled. What is the distribution of release delays on each dataset?

We apologize for the ambiguity. Table 1 reports KRAFT's arrival-time scores with online adaptation enabled and historical rescoring disabled. Our response to NgPM Q5 gives the 16-dataset means for both KRAFT and KRAFT-R, which is the optional variant that rescores buffered observations using the validated adapter before releasing their final scores. We will clarify the scoring protocol in Table 1 and Appendix A.4. It is worth noting that TSB-AD’s Sub-PCA assigns each sliding-window score to the center of the window, so observations after time tt can influence the score at tt (TSB-AD implementation). In this sense, KRAFT’s optional retrospective scoring mechanism (KRAFT-R) likewise uses later observations to reassess the anomaly score at time tt.

For KRAFT-R, release delay is the number of observation steps from arrival to final release, including the wait within the current 32-observation block. We report the median, 95th percentile (P95), and maximum over all valid test observations in each dataset. “Across blocks” is the percentage of observations still pending at the end of their own block.

DatasetAcross blocksMedian / P95 / MaxDatasetAcross blocksMedian / P95 / Max
IOPS2.67%16 / 31 / 255UCR1.95%16 / 31 / 511
MGAB0.79%16 / 30 / 223WSD4.59%16 / 31 / 255
NAB7.32%17 / 111 / 383YAHOO3.77%16 / 31 / 223
NEK18.62%19 / 148.2 / 191MSL8.22%17 / 107 / 255
Power4.45%16 / 31 / 639PSM12.10%18 / 157 / 287
SED8.16%17 / 110 / 255SMAP6.67%17 / 86 / 319
Stock2.66%16 / 31 / 223SMD2.20%16 / 31 / 255
TODS4.07%16 / 31 / 255SWaT3.53%16 / 31 / 895

On 10 of 16 datasets, P95 was at most 31 steps. SWaT had the longest observed delay (895 steps), but only 3.53% of observations were held across blocks. On PSM, cross-block waiting was more frequent (12.10%), although the maximum delay was shorter (287 steps).

Reviewer_NgPMOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

This paper proposes KRAFT for time series anomaly detection under latent domain shifts. It combines Koopman-conditioned flow matching, evolution-compensated MMD, and validation-guided adapter updates. Anomalies are detected through residuals relative to the generated normal reference.

Critical strengths

The problem is practically relevant, particularly the need to accommodate normal changes without absorbing anomalies. Compensating for predictable normal evolution before measuring distributional mismatch is a reasonable design. Experiments cover diverse datasets and include component ablations and theoretical analysis.

Critical weaknesses

1、The necessity of flow matching is insufficiently established. At deployment, it produces a single deterministic prediction scored through residuals. Its advantages over direct forecasting or conventional Neural ODE models remain unclear. 2、KP-MMD combines learned dynamics propagation with standard MMD. Existing ablations support evolution compensation but do not establish the distinctive value of Koopman propagation over alternative predictors. 3、The distinction between endogenous and exogenous shifts depends on the learned dynamics. Unexplained mismatch can also arise from persistent anomalies or prediction errors. Unlabeled validation may accept updates that learn persistent anomalies as normal. 4、The residual score does not explicitly account for conditional predictive uncertainty, potentially confusing normal stochastic or multimodal behavior with anomalies. 5、The experimental comparison omits directly relevant recent methods such as CANDI from 2026, despite citing it.

Questions for authors

1、What benefits does flow matching provide over capacity-matched forecasting and Neural ODE models under the same conditioning and adaptation protocol? 2、Does Koopman-based compensation outperform compensation using other learned predictors? 3、How do KP-MMD and unlabeled validation distinguish normal domain changes from persistent anomalies and dynamics-model errors? 4、How reliable is single-reference residual scoring under multimodal normal behavior or heteroscedastic noise? 5、Could the authors compare KRAFT with CANDI under matched conditions and report performance when historical buffer rescoring is disabled or decision delays are matched?

7 comments

Thank you for your thoughtful feedback. We first address the weaknesses you identified and then respond to each of your questions in more detail. We will provide the revised manuscript as soon as possible.

Response to the Critical Weaknesses

W1. Contribution of flow matching. KRAFT produces a deterministic prediction at deployment, but flow matching gives the predictor additional supervision during training. The Koopman-informed bridge supplies velocity targets at intermediate states along the prediction path. With the ODE architecture, conditioning, solver, and online adaptation objective held fixed, this supervision improved all four metrics on every one of the 16 public datasets in our controlled run, with mean gains of 0.96–1.22 percentage points. Q1 presents the matched ODE comparison, the capacity-matched GRU baseline, and the separate contribution of online flow matching.

W2. Value of Koopman propagation. The learned Koopman dynamics provide a common model of normal evolution for generating the reference and propagating the historical window used by KP-MMD. On five CDS streams with known domain boundaries, both Koopman and the latent Neural ODE initiated adaptation ten times. All ten Koopman starts matched true boundaries, compared with eight for the Neural ODE. Across the 16 public datasets, Koopman also achieved higher end-to-end scores than all three learned alternatives on all four metrics in the same-seed comparison. Q2 describes the controlled replacements and reports the results.

W3. Adaptation under persistent mismatch. KRAFT uses sustained KP-MMD evidence to propose an update and requires a reduction in capped risk on later, held-out observations before accepting it. Lowering an anomalous residual that remains above the cap contributes zero validation gain. On long anomalies, enabling validation improved arrival-time recall after the first 128 observations by 6.15 percentage points on PSM and 8.66 on SWaT. Even when the same anomaly entered both buffers, accepted updates retained 94.20% and 95.62% of previously detected anomaly points, respectively. Q3 reports both the online comparison and the paired before-and-after evaluation.

W4. Single-reference scoring across operating regimes. KRAFT generates its reference from the observed history and predicted latent evolution. When the history identifies the active operating mode, the model can generate a mode-specific reference. After a sustained change, a validated adapter update can move the reference toward the new normal behavior. KRAFT also centers and scales each channel’s residuals using its historical median and median absolute deviation, so each error is assessed relative to that channel’s typical variability. Q4 explains how history conditioning, adaptation, and robust calibration address these sources of normal variation.

W5. Comparison with CANDI. We evaluated CANDI with its official defaults on the same training and test data, using the same TSB-AD metrics and dataset weighting. With historical rescoring disabled, KRAFT exceeded CANDI on all four 16-dataset means, including 85.35 vs. 73.46 on Aff-F and 33.24 vs. 27.54 on VUS-PR. These gains are already present in the scores recorded at arrival. Q5 gives the full comparison and reports the additional results under deferred rescoring.

Response to the Questions

Q1. What does flow matching contribute?

What benefits does flow matching provide over capacity-matched forecasting and Neural ODE models under the same conditioning and adaptation protocol?

KRAFT itself uses an ODE predictor; the role of flow matching is to provide a different training signal. Endpoint-only training supervises the integrated prediction, whereas FM directly supervises velocities at sampled intermediate states along our learned Koopman-informed bridge. This introduces a dynamics-informed inductive bias beyond endpoint fitting. During online adaptation, retaining the FM term additionally constrains candidate updates through these pathwise targets alongside endpoint prediction loss. Our controlled ODE comparisons therefore assess the empirical contributions of offline velocity supervision and the online FM term separately.

The FM-trained ODE removes the online FM term. The endpoint-trained ODE also replaces offline velocity supervision with endpoint loss. Both share the velocity network, Koopman conditioning, Heun solver, and online endpoint loss with proximal regularization. The direct GRU uses the same online objective and predicts from the 64-step history alone. Its prediction network is within 3% of the velocity network's parameter count.

16-dataset means, one seed. Variant rows show differences from KRAFT in percentage points.

ModelAff-FF1-TPoint F1VUS-PR
KRAFT85.3539.5736.1033.24
FM-trained ODE (no online FM)−0.69−0.99−0.84−1.03
Endpoint-trained ODE−1.65−2.19−2.06−2.25
Direct GRU−4.12−6.21−5.02−4.93

With online adaptation fixed, offline FM improved all four metrics on every dataset over endpoint-only training (0.96–1.22 points on average across datasets). Removing online FM lowered the four mean scores by 0.69–1.03 points.

Q2. Does Koopman compensation outperform other learned predictors?

Does Koopman-based compensation outperform compensation using other learned predictors?

Our constrained Koopman propagator provides a structured inductive bias for evolution compensation. The shared generator defines time-consistent propagation across horizons, while its negative-definite symmetric part explicitly prevents amplification of latent perturbations. Under the bounded modeling-error assumption of Proposition 2, this yields a propagation-error bound that also controls the propagation component of the KP-MMD error budget. These properties motivate using the propagator to represent normal continuation. Our following joint replacement experiments also provide empirical evidence for the constrained propagator within the complete KRAFT pipeline, rather than isolating its contribution to MMD compensation alone.

We replaced the propagator in both the flow conditioning input and the MMD reference window, keeping the flow architecture, latent dimension, training budget, and adaptation protocol fixed. Scores are arrival-time means across 16 equally weighted datasets (seed 42).

Latent propagatorAff-FF1-TPoint F1VUS-PR
Constrained Koopman (KRAFT)85.3539.5736.1033.24
Latent Neural ODE83.5537.0233.9430.52
Time-conditioned residual MLP81.3733.7530.8827.83
Unconstrained linear generator77.7828.9027.1223.68

Koopman led all three alternatives on all four metrics on each dataset in this run. This joint ablation measures the benefit of the propagator across its two roles in the full detector.

Q3. What can KRAFT distinguish without labels?

How do KP-MMD and unlabeled validation distinguish normal domain changes from persistent anomalies and dynamics-model errors?

KRAFT combines KP-MMD and held-out validation to detect unexplained distributional changes and assess candidate updates using unlabeled observations. KP-MMD detects departures from the modeled normal evolution, while validation requires a reduction in capped risk on later held-out observations. Under the stated assumptions, our analysis provides guarantees for shift detectability and recall-loss control during adaptation. We further evaluate protection against persistent-anomaly contamination through the experiments below.

Online detection with and without validation. For anomalies lasting at least 256 observations, enabling validation increased arrival-time recall after the first 128 observations from 22.08% to 28.23% on PSM and 30.90% to 39.56% on SWaT.

Detection retention after accepted updates. We selected events where the same anomaly entered both the training and validation buffers and an update was accepted. We rescored each event offline with the pre-update and end-of-episode adapters, holding the observations, scoring statistics, and threshold fixed. Of the anomaly points detected before the updates, 94.20% remained detected across nine PSM events and 95.62% across eight SWaT events. New detections offset the losses, bringing pooled recall from 32.00% to 32.33% and 38.51% to 38.63%, respectively.

Q4. How reliable is a single reference under conditional uncertainty?

How reliable is single-reference residual scoring under multimodal normal behavior or heteroscedastic noise?

KRAFT generates one reference per observation. Its reliability depends on how much normal variation the observed history explains and how well the historical residual scale represents current operating conditions. KRAFT addresses these factors through history-conditioned reference generation, validation-guided adaptation, and robust residual calibration.

Multimodal normal behavior. A system can exhibit several normal operating modes over time while its recent history identifies which mode is active. KRAFT conditions its reference on that history and its Koopman-predicted latent evolution, so it can generate different references for different modes. After a persistent regime change, KP-MMD can flag a mismatch between the current and propagated latent distributions. A candidate adapter update can then shift the reference toward the new behavior if it reduces capped risk on later, held-out observations. A limitation arises when the same history admits several well-separated normal outcomes. The single reference represents only one predicted trajectory, so a valid alternative outcome can receive a large residual.

Heteroscedastic noise. For each channel, KRAFT centers residuals using their historical calibration median and scales them using a scaled median absolute deviation (Eq. 47) before aggregating their squared values (Eq. 14). This measures each deviation relative to that channel’s typical historical prediction error and limits the influence of extreme calibration residuals on the estimated scale. It accounts for baseline variability across channels. If variability within a channel increases with operating conditions, however, the historical scale can be too small for the new regime. Even an accurate reference can then yield elevated scores on normal observations.

These mechanisms support tracking predictable changes in normal behavior. The deployed score measures a standardized deviation from the reference, and its false-alarm rate can vary across regimes.

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

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