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Under review as a conference paper at ICLR 2027

PARC: Learning Historical References for Online Change-Point Detection

Abstract

Online change-point detection is challenging when no part of the observed sequence is known to follow the pre-change distribution. Waiting for a long reference can delay detection, while limited history may poorly characterize normal distributional variation. A large learned contrast need not exceed historical fluctuations in the same direction. We propose PARC, a rolling detector that estimates proposal-conditioned historical response distributions. Each proposal is defined by a recent-versus-earlier contrast at a particular time and scale, describing how the distribution may be changing. Conditioned on that proposal, PARC estimates the corresponding historical response distribution and learns how much that type of variation has occurred before. Different candidate changes are therefore evaluated against different historical variability. New proposals update the collection of references, while each comparison is fixed before later observations are tested. We analyze score sensitivity, the effect of startup on later thresholds, and a separate finite-horizon false-alarm guarantee under exchangeable normal sequences. Across two complete archives, PARC achieves higher detection coverage and lower capped detection loss than twelve evaluated baselines, with fewer early alarms than the strongest detection comparator on each archive under a matched protocol.

Primary area:
learning on time series and dynamical systems
Keywords:
online change-point detection, sequential detection, adaptive reference distributions, distribution shift, time-series analysis, statistical learning

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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.
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Paper summary

The paper proposes PARC, an online change-point detector that does not require a designated unchanged prefix. Past recent-versus-earlier feature contrasts define candidate change directions. For each direction, PARC constructs an empirical historical response distribution and scores subsequent blocks by their positive excess over its maximum, normalized by historical variability. Frozen short-window neural features support startup and are replaced by native long-window features. The analysis covers historical separation, score stability, startup threshold costs, and a separate finite-horizon false-alarm guarantee under exchangeable normal sequences. Evaluation on TSSB and TCPD reports improved detection coverage and capped delay loss over twelve baselines, supported by component studies and numerical theory checks.

Critical strengths
  1. A well-motivated and interpretable comparison mechanism. PARC evaluates each proposed change against historical variability measured in the same direction. This directly addresses why a large recent contrast need not constitute unusual behavior. Freezing each comparison before testing later raw observations makes the construction causally coherent. These properties give the method a clear rationale beyond simply combining multiple window discrepancies.

  2. Promising improvements in detection coverage under a reasonably careful evaluation protocol. PARC reports detection rates of 60.0% on TSSB and 51.0% on TCPD, compared with 48.4% and 39.5% for the strongest coverage comparators, respectively, while also reducing capped loss. Family-separated nested selection, retention of early changes in evaluation, and explicit accounting for missed and early alarms strengthen this evidence. The paper appropriately acknowledges that the gains primarily concern coverage rather than faster detection on jointly detected cases.

Critical weaknesses
  1. The submitted artifacts do not support independent verification of the central comparison. Appendix C.2 states that the complete per-method configuration grids are included with the artifact. However, the released reproducibility documentation explicitly states that baseline implementations, baseline configuration grids, and baseline-specific tests are absent. Several component and statistical analyses also lack complete reproduction workflows, and the nine recovered TCPD records lack a pinned acquisition/recovery recipe. This discrepancy is consequential because the main empirical claim depends on the correctness and fairness of these baseline implementations and operating points.

  2. The evidence does not yet sufficiently isolate the contribution of the central mechanism or establish generalization beyond the development archives. Both archives informed architecture development, so nested family splits do not eliminate prior design-selection effects. Moreover, the reported paired-family interval for the historical-maximum versus historical-mean comparison on TSSB includes zero, and a dedicated mature-gate ablation is missing. The neural startup advantage is primarily supported by TCPD, since all TSSB changes occur after the mature transition. Together, these limitations leave uncertainty about which components account for the gains and how reliably those gains transfer.

Questions for authors
  1. Can you reconcile Appendix C.2’s statement that the complete baseline configuration grids are included with the release documentation stating that they are absent? Can you provide the exact baseline implementations or pinned upstream versions, the selected configurations and thresholds for each outer fold, and the per-record first alarms underlying Table 1, together with the provenance and recovery procedure for the nine recovered TCPD records?

  2. Can you provide paired effect estimates and uncertainty intervals for the historical-maximum versus historical-mean controls on both archives? How sensitive is the 16-block historical reference to increasing history length, outliers, or previous changes, and are comparisons with a robust quantile reference available at comparable empirical false-alarm levels? Separately, is there an existing ablation that removes the mature coordinate gate while keeping the other components and fitting protocol unchanged?

  3. Please clarify which architectural choices were informed by results on TSSB or TCPD, and whether any evaluation families or collections were entirely excluded from architecture development. If independent or cross-archive transfer results already exist, can you provide them to help assess generalization beyond the development archives?

  4. The mature representation concatenates per-channel spectral and moment features without explicitly encoding cross-channel dependence. To what extent can it detect changes that preserve individual-channel statistics but alter cross-channel correlation or relative phase? If controlled results for such changes are available, can you provide them and clarify whether detection relies mainly on transient effects near the change boundary?

3 comments

Thank you for your review. We updated the code package, added controls, and evaluated PARC on one additional dataset, WEAR. We updated the paper with revisions highlighted.

Reproducibility. Thank you for pointing out the missing grids. The updated ZIP now includes reproducibility details such as the detector, baseline grids, fitted configurations, recovery scripts, simulations, ablations and results.

Historical endpoint (New comparison). We expanded the ablation using the same proposals, preprocessing, and budget, with separate thresholds. D and E are detection and early-alarm percentages. N is no-change alarms and L is capped loss.

EndpointTSSB D / E / N / LTCPD D / E / N / L
Maximum60.0 / 2.9 / 1.0 / .59051.0 / 4.0 / 0.0 / .653
Mean53.6 / 4.3 / 0.0 / .62746.5 / 5.5 / 1.2 / .676
95th percentile58.0 / 3.5 / 1.0 / .61851.5 / 4.0 / 0.0 / .647

N averages five splits, with six TSSB and two TCPD no-change records. The maximum detects more changes with fewer early alarms than the mean. The mean has fewer no-change alarms on TSSB, and the 95th percentile is slightly better on TCPD. See Section 6.4 and Appendix F.

In addition, we added an ablation for the variability term based on your feedback.

Variability scalingTSSB detection / earlyTCPD detection / early
Direction-specific (PARC)60.0% / 2.9%51.0% / 4.0%
Equal-trace isotropic46.1% / 9.3%48.0% / 6.0%
Diagonal54.5% / 8.1%43.0% / 7.0%
Floor only38.6% / 3.2%46.0% / 8.0%

PARC detects more changes with fewer early alarms than these controls. Each variant fits its own threshold, so the alarm rates differ.

History (new sensitivity experiment). Thank you for this point. We tested different numbers of historical blocks:

Historical blocksTSSB detectionTCPD detection
827.8%49.0%
1660.0%51.0%
3253.0%52.0%
6453.6%52.0%

TCPD series are shorter and have earlier changes than TSSB. The 8- and 16-block variants detect mostly the same TCPD records, although their thresholds are fitted separately.

Cross-channel sensitivity (New simulations). Thank you for this point. We added a simulation study to include two-channel time series change in both correlation and either mean or scale. Each setting contains 100 time series (length 512). Delay is the median among detected changes.

Marginal change + correlationPARC detected / delayCorrelation diagnostic detected / delay
Mean +0.511 / 25442 / 126
Mean +1.041 / 25445 / 126
Mean +1.567 / 19552 / 126
Mean +2.083 / 16459 / 126
Scale ×1.258 / 25445 / 142
Scale ×1.518 / 25447 / 128
Scale ×2.034 / 16160 / 132.5

PARC detects more changes as the mean shift increases, although many alarms are late. The diagnostic detects more of the smaller mean and scale changes.

For 16 channels, feature extraction takes 6.78 ms for PARC and 19.81 ms with pairwise correlations. These are feature-extraction times, not full-detector times. PARC’s channel-wise features are simpler to compute, but may miss changes that affect only relationships between channels. The full analysis is in Appendix H. Channel-wise extraction is also used by WEASEL+MUSE (Schäfer and Leser, 2018) in the related field of time-series classification.

Nonetheless, extending PARC to model cross-channel relationships is an important direction for future work, and we must address the computational cost as well. Thank you again for your suggestion.

Transfer to WEAR (The new dataset added for revision). We found and evaluated the frozen detector on a new dataset, WEAR, which is a separate wearable-sensor dataset. We used 14 participants to fit thresholds and 8 other participants for evaluation. We set a target threshold level of 10%. The results are:

MethodDetected changes (%) ↑Early alarms (%) ↓Control alarms (%) ↓
PARC26.30.09.1
Online RFF-MMD20.01.39.1
RBF-MMD6.30.06.8
Hahn CUSUM5.00.04.5
MdFOCuS5.01.34.5
PM-CuSum (M)3.82.50.0
NEWMA2.50.04.5
Energy2.50.04.5

In the above table, PARC has the highest detection rate and fewest early alarms. Some methods have fewer control alarms, but PARC is still the best when considering all three aspects. We selected 64-second windows to obtain enough shifts and same-activity control windows. The eight test participants were not used to fit thresholds. The detection difference remains uncertain across participants. We include the full protocol and results in Appendix G in the revised paper.

Thank you again for your valuable time, and we hope this can address most of your concerns.

Thank you for addressing my comments, but I still have a few questions.

The mean has fewer no-change alarms on TSSB, and the 95th percentile is slightly better on TCPD.

Given these mixed results, could you report paired uncertainty intervals for maximum versus percentile and compare their detection rates and delays after a large past fluctuation?

We added a simulation study to include two-channel time series change in both correlation and either mean or scale.

Could you test a correlation-only change while keeping each channel’s marginal distribution unchanged, so we can see whether PARC detects the dependence change itself?

We found and evaluated the frozen detector on a new dataset, WEAR, which is a separate wearable-sensor dataset.

Given that WEAR only evaluates startup and the advantage over Online RFF-MMD disappears at the 5% target, could you clarify how far these results support generalization of the full method?

Thank you so much for your quick reply and very helpful suggestions. There were some insufficient explanations from the previous revision. We have revised the paper again, with the changes highlighted.

Maximum versus percentile. We added paired 95% family-bootstrap intervals for maximum minus 95th percentile. We first average the predictions for each record across five splits. The results are:

ArchiveDetection difference (percentage points)Capped-loss difference
TSSB+2.03 [0.00, 4.69]-0.028 [-0.056, -0.008]
TCPD-0.50 [-1.67, 0.00]+0.007 [-0.003, 0.019]

In the above table, the maximum gives lower capped loss on TSSB, and the percentile performs similarly on TCPD. These intervals use saved predictions. We do not repeat model fitting.

We also added a simulation of mean/scale changes to include 200 time series for each case in the below table. Both versions use the same features and change directions to ensure a fair comparison. The results are:

Past fluctuationMaximum: detected / median delayPercentile: detected / median delay
None64 / 206.579 / 221
Spike53 / 21971 / 254
Brief excursion52 / 25463 / 254

We can see past fluctuations reduce detection, but percentile detects more changes. For changes detected by both, the median paired delay difference is zero. Therefore, overall they are similar and percentile a reasonable alternative (Appendix F, Tables 11–12).

Correlation-only change. Thank you so much for this suggestion. Our earlier simulation changed both correlation and mean or scale, so it did not answer your question. We added a test that changes only Gaussian innovation correlation from +0.8 to -0.8. Each channel's marginal distribution and temporal dependence remain unchanged. PARC detects 19/200 changes versus 198/200 for a targeted correlation diagnostic, with 14/200 versus 10/200 normal alarms.

Thank you for this helpful suggestion. This test shows a limitation of PARC’s channel-wise features. We now state it clearly in the revised paper and identify efficient cross-channel features as future work, and this future work must overcome detection delay and computational cost as well. The discussion is in the main paper and Appendix I.

WEAR and the full method (new experiments). The earlier inputs tested only startup. Sorry for this confusion. We now added the fair experiments to evaluate all 22 people at 5, 10, 15, and native 50 Hz. Each person's thresholds are fitted from the other 21 people. We keep other settings all fixed.

D/E/C are detection / early-alarm / control-alarm percentages over 211 transitions and 128 controls.

RateTargetPARC: D / E / C (%)RFF-MMD: D / E / C (%)
5 Hz5%23.7 / 0.5 / 5.516.6 / 2.4 / 5.5
5 Hz10%27.0 / 0.9 / 10.922.7 / 3.8 / 10.9
10 Hz5%27.5 / 0.0 / 5.511.8 / 1.9 / 6.3
10 Hz10%28.4 / 0.5 / 10.222.3 / 3.3 / 10.2
15 Hz5%22.3 / 0.5 / 5.510.4 / 1.4 / 3.1
15 Hz10%23.7 / 2.8 / 11.717.1 / 3.8 / 10.2
Native 50 Hz5%11.4 / 0.5 / 5.515.2 / 2.4 / 5.5
Native 50 Hz10%18.5 / 1.9 / 13.318.0 / 4.3 / 9.4

We can conclude the following lessons:

  • External transfer: At 5–15 Hz, PARC has the highest detection rate among all eight methods at both targets, with fewer early alarms than RFF-MMD. At 10 Hz, it also achieves lower capped loss with the same or fewer control alarms.
  • Mature-stage detection: Almost all detections at 10 Hz and all detections at native 50 Hz occur in the mature stage. These new results show that PARC transfers effectively.
  • Sampling resolution: The same frozen model detects changes at all four rates. At native 50 Hz, PARC raises fewer early alarms at both targets and achieves similar detection to RFF-MMD at the 10% target.

Therefore, overall PARC show postive transfer and beats other sota methods on this separate dataset.

Archive ablations (existing Table 2):

VariantTSSB detection / early (%)TCPD detection / early (%)
PARC60.0 / 2.951.0 / 4.0
Native short features59.1 / 3.543.0 / 7.0
Fixed 64-point context59.1 / 3.540.0 / 5.5
No startup retirement25.5 / 7.052.0 / 7.5

The TCPD results show why we use learned startup comparisons. The TSSB results show why we retire them after startup. WEAR adds mature-stage transfer without retraining. These tests use the same recordings and are not an untouched confirmation. We describe the design in Sections 4.5 and 6.3. The new results are in Section 6.4, Table 4, and Appendix G, Tables 13–14.

Thank you again for helping us clarify these results. We truly appreciate the time you have spent reviewing our work!!

Reviewer_645HOpenReview ↗
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Paper summary

PARC proposes candidate change directions from past observations, measures historical variation along those directions, and scores later observations against frozen historical references. It combines short-window startup features with a longer-window detector.

Critical strengths

Detection without a declared unchanged segment is a relevant problem. The evaluation includes missed detections and separates proposal construction from later testing, which makes the reported results more informative.

Critical weaknesses
  1. It is not yet clear how much the defining reference mechanism contributes. Appendix C.7 includes the right kinds of controls, but the interval for the TSSB improvement over a historical-mean reference includes zero. The strongest-coordinate control also matches the reported TCPD capped loss at that operating point. The full system performs well, but these results leave uncertainty about whether the proposed historical endpoint is the main reason. Both archives also informed architecture development, so an untouched evaluation would be particularly informative.

  2. False-alarm reliability in the intended setting remains weakly established. The theorem requires separate exchangeable normal sequences and a fixed monitoring horizon. It does not justify the benchmark thresholds fitted using labeled training families. The authors acknowledge this, but the archives contain only six and two null records, so the empirical evaluation cannot fill that gap. The conditional separation results also do not establish how reliably the learned proposals achieve the required alignment and historical coverage.

Overall, I lean toward weak rejection. The overall benchmark results are encouraging, but the evidence for the specific mechanism and deployment reliability is less conclusive.

Questions for authors

How much of the improvement remains at matched measured false-alarm rates? Is there an evaluation on data not used during architecture development, with enough null sequences to assess this reliably?

4 comments

Thank you for your time and valuable review. We updated the paper, added new analysis and especially a new dataset WEAR. We also updated the paper with highlighted changes and the code ZIP.

Effect of historical variability (New ablations). In the revision, we added new experiments to evaluate the variability term in the submitted PARC score. The variants use the same proposal construction and historical maximum, but different variability terms. Each variant selects its own parameter settings and fits its threshold on training families. The proposed feature weights are used to measure historical variation and score later observations. The new results are:

Variability scalingTSSB detection / earlyTCPD detection / early
Direction-specific, PARC60.0% / 2.9%51.0% / 4.0%
Equal-trace isotropic46.1% / 9.3%48.0% / 6.0%
Diagonal54.5% / 8.1%43.0% / 7.0%
Floor only38.6% / 3.2%46.0% / 8.0%

In the above table, PARC detects more changes with fewer early alarms. This explains the reason for using direction-specific scaling.

Historical maximum and alarm rates (New comparisons). Additionally, we also compare the historical maximum with the mean and the 95th percentile. The maximum detects 60.0% of changes on TSSB and 51.0% on TCPD, compared with 53.6% and 46.5% for the mean. It performs comparably to the 95th percentile, which detects 58.0% and 51.5%. We fit a separate threshold for each choice.

We have to control the alarm limits in order to compare the detections, so we set an upper limit of 5% early alarms and no alarms on the archive no-change records for each method. PARC detects 56.5% versus 44.6% for online RFF-MMD on TSSB, and 49.5% versus 19.5% for Hahn CUSUM on TCPD. These thresholds use evaluation labels to compare methods under the same alarm limits. They are not deployment thresholds.

Transfer to WEAR (new evaluation). We now evaluate the frozen detector on all 22 WEAR participants at 5, 10, 15, and native 50 Hz. Each person's thresholds are fitted using controls from the other 21 people. The architecture, weights, and baseline configurations remain unchanged. At 10 Hz, the results are:

D/E/C are detection / early-alarm / control-alarm percentages over 211 transitions and 128 controls.

Method5% target: D / E / C (%)10% target: D / E / C (%)
PARC27.5 / 0.0 / 5.528.4 / 0.5 / 10.2
Online RFF-MMD11.8 / 1.9 / 6.322.3 / 3.3 / 10.2
RBF-MMD3.8 / 2.8 / 5.54.3 / 4.3 / 8.6
Hahn CUSUM3.3 / 1.9 / 4.72.8 / 2.4 / 8.6
MdFOCuS3.3 / 0.5 / 4.73.8 / 3.3 / 9.4
PM-CuSum (M)4.3 / 0.9 / 4.75.2 / 2.4 / 7.8
NEWMA0.5 / 4.3 / 6.30.9 / 10.0 / 12.5
Energy1.4 / 1.9 / 6.31.9 / 2.8 / 10.2

We also compare PARC with RFF-MMD across the four rates:

RateTargetPARC: D / E / C (%)RFF-MMD: D / E / C (%)
5 Hz5%23.7 / 0.5 / 5.516.6 / 2.4 / 5.5
5 Hz10%27.0 / 0.9 / 10.922.7 / 3.8 / 10.9
10 Hz5%27.5 / 0.0 / 5.511.8 / 1.9 / 6.3
10 Hz10%28.4 / 0.5 / 10.222.3 / 3.3 / 10.2
15 Hz5%22.3 / 0.5 / 5.510.4 / 1.4 / 3.1
15 Hz10%23.7 / 2.8 / 11.717.1 / 3.8 / 10.2
Native 50 Hz5%11.4 / 0.5 / 5.515.2 / 2.4 / 5.5
Native 50 Hz10%18.5 / 1.9 / 13.318.0 / 4.3 / 9.4

These results show that PARC transfers without retraining and detects changes beyond startup. It detects more changes with fewer early alarms than the leading baseline at several sampling rates. Full results are in Section 6.4 and Appendix G.

False-alarm guarantee (New simulations). Thank you for this point. We added simulations of autoregressive and oscillatory normal time series. In each of 1,000 trials per type, we draw 19 normal reference sequences and one normal test sequence. At 512 observations, they produce 59 and 63 alarms. The intervals for both rates include the 5% target.

We also tested PARC on 128 same-activity windows from WEAR. At 10 Hz, we observed seven alarms at the 5% target and 13 at the 10% target. We used simulation to test the false-alarm rule because we can generate exchangeable normal reference and test sequences.

Thank you again for your valuable suggestions and time for our paper.

Reviewer_645HOpenReview ↗

Response to the rebuttal

Thank you for the new WEAR experiments and ablations, which partially address my concerns. I remain uncertain about the specific benefit of the historical maximum over a percentile reference and the reliability of calibration beyond the evaluated settings.

Thank you for your time and response. Sorry for the unclear enough responses.

For Q1, Maximum versus percentile. The two choices give us similar detection rates on both archives. In our simulation, the 95th percentile detected more changes after a past spike or brief fluctuation, with no additional early or control alarms. We therefore consider it a reasonable alternative to the maximum. This is reflected on Appendix F, Tables 11–12 in the revised paper.

For Q2, Calibration beyond the tested settings. The 5% bound applies to any fixed detector and horizon when the 19 normal reference sequences and the next normal sequence are exchangeable, even with temporal dependence within sequences. For the independent WEAR dataset, which we included for revision during the response phase, we used participant-held-out thresholds for all 22 participants. With a 5% target, PARC triggered 7 alarms in 128 same-activity windows (5.5%) at 10 Hz, and this rate stayed the same at 5, 15, and 50 Hz. When we have goal for a 10% target, observed rates ranged from 10.2% to 13.3%. These results closely match the intended target rates, and this adds more support that the calibration stays consistent across different sampling rates on this independent, real-world dataset, all without needing to retrain.

I hope this explanation is more clear. If you have more concerns, please let us know. Thank you so much for your time!

As a brief follow-up, we found few real datasets with both annotated changes and enough no-change recordings to evaluate false alarms. TSSB and TCPD contain only six and two no-change records, respectively. Both archives informed our design.

To give the best effort and compare methods fairly, we (1) used the same five cross-validation splits for every method. In each split, we fitted thresholds on one set of time-series families and tested on different families. We (2) also added simulations to evaluate the false-alarm rule on fresh normal sequences and (3) used WEAR to test transfer without retraining PARC. On WEAR, we used 22 leave-one-participant-out folds. Each participant was tested once, with thresholds fitted on the other 21.

Thank you again for your valuable feedback and time!!

Reviewer_5U6vOpenReview ↗
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Paper summary

The paper introduces a novel idea in the field of CPM: setting up a CPM without an initial subset that is defined as "normal". The basis is to compare windows of recent data to identify directions of chances. In this way the paper introduces the idea of having multiple historical references.

Critical strengths
  • the definition of the temporal protocol is well detailed
  • well positioned w.r.t. history contamination, temporal dependencies and exchangeability
  • comparison with several baselines and good structure of the experimental section
  • the paper is well presented and figures are very nice
Critical weaknesses
  • It seems to this reviewer that the nested CV selected configurations and thresholds but does not protect from architectural decisions coming from archives. Please clarify this point
  • Partitions are not independent each other. The paper clarifies this point but the problem remains. How would you solve it?
  • In the experimental section there are very few null cases. Hence, experimental results suffer from this limitation. How can be this issue managed?
  • Some relevant baselines are cited but not used in the experimental results. Why?
Questions for authors

See previous box

1 comment

Thank you for your valuable and thoughtful review on our paper PARC. We have revised the paper, the supplementary materials, and added one additional dataset. I hope they can address most of your concerns.

Architecture and data splits. We used both TSSB and TCPD during the architecture design, but the network and gate weights were trained on synthetic data only. To give a relatively fair evaluations, we use family-separated splits that keep the families used for fitting separate from those used for evaluation. We also repeat model selection with different groups of families to check whether the results change.

Transfer to WEAR (The new dataset added for revision). We found and evaluated the frozen detector on new dataset WEAR, and this is a separate wearable-sensor dataset. We used 14 participants to fit thresholds and 8 other participants for evaluation. We set a target threshold level of 10%, the results are:

MethodDetected changes (%) ↑Early alarms (%) ↓Control alarms (%) ↓
PARC26.30.09.1
Online RFF-MMD20.01.39.1
RBF-MMD6.30.06.8
Hahn CUSUM5.00.04.5
MdFOCuS5.01.34.5
PM-CuSum (M)3.82.50.0
NEWMA2.50.04.5
Energy2.50.04.5

In the above table, PARC has the largest detection rate and smallest early alarms. Some methods have fewer control alarms, but PARC is still the best after considering all the three aspects. We selected 64-second windows to obtain enough shifts and same-activity control windows. The eight test participants were not used to fit thresholds. The detection difference remains uncertain across participants. We include the full protocol and results in Appendix G in the revised paper.

Limited no-change data and false alarms. Thank you for this question. TSSB and TCPD focus on annotated changes and contain six and two no-change records, respectively. In this revision, we found a new and recent dataset WEAR by evaluating PARC on 44 same-activity windows from eight WEAR participants and observed four alarms. We also tested false-alarm control on simulated normal time series with temporal dependence, and we can get many independent reference and test sequences. The WEAR windows provide a useful real-data evaluation, and the simulation directly tests the assumptions of the stated guarantee.

We provided additional analysis, and evaluated the stated rule on simulated normal time series with temporal dependence. Specifically, for a fixed detector and horizon, let Mi=max⁡t≤HSt(Xi)M_i=\max_{t\le H}S_t(X_i) be the maximum score on normal reference sequence ii. There are 19 reference sequences exchangeable with the normal test sequence in total, and the rank rule uses h=max⁡i≤19Mih=\max_{i\le19}M_i and gives

Pr⁡0(τh≤H∣D)≤120=0.05.\Pr_0(\tau_h\le H\mid\mathcal D)\le \frac{1}{20}=0.05.

This probability averages over the reference and test sequences, given that we have the fixed design D\mathcal D. The dependence within each sequence does not need to be known. We draw new reference and test sequences in 1,000 trials for each shift. At horizon 512, the autoregressive and oscillatory change point give 59 and 63 alarms.

We stated and explained the guarantee and its assumptions in Section 5. The original numerical details are included in Section 6.5 and Appendix D. The additional simulation and its limitations are included in Appendix H in the revised paper. These results show the stated guarantee under its assumptions, but not for label-fitted thresholds or every individual reference set.

Baselines and code. Thank you for pointing out this limitation. We prepared an updated supplementary ZIP with the frozen detector, baseline adapters and grids, selected configurations and thresholds, per-record alarms, TCPD recovery scripts and checksums, and the WEAR evaluation. It also includes the normal-sequence simulation and mechanism-ablation scripts. This updated ZIP file contains the most details needed to reproduce the work. We will also make the code public after the conference decision phase.

Some relevant baselines are cited but not used in the experimental results. Why? We have selected 12 baseline scores for our neural, kernel and classical sequential methods. The scores are from both established and recent approaches and cover a variety of detection mechanisms. All methods are evaluated using the same causal evaluation protocol.

Our related work section includes several other studies, some of which are not directly applicable to our task but are included for completeness. For example, some of the cited offline segmentation studies are included for completeness. Other cited online methods are relevant but not included in our comparison. Therefore, our comparison is representative but not exhaustive. In Section 2 we describe the evaluated methods in more detail.

Thank you again for your valuable time and suggestions.

Comments on the paper

1 comment

We thank all reviewers again for your time and helpful suggestions. As the discussion deadline approaches, please let us know if you have any remaining questions or concerns. We would be happy to clarify them.

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

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