acceptodds
Under review as a conference paper at ICLR 2027

Where Does Detection Fail? A Residual-Evidence Diagnostic Workflow for Industrial Control Systems

Abstract

Residual-based anomaly detectors for industrial control systems (ICS) convert model residuals into anomaly scores and alarms, but final detection metrics give little guidance on which component to examine when detection performance is poor. We present a retrospective diagnostic workflow built around covariance-normalized residual energy (CNRE), a measurement based on the squared Mahalanobis distance. The workflow asks whether the normal reference still describes the evaluation recording, whether attacks separate from normal operation under a stated reference, and how scoring and alarm rules use fixed residuals. Across fifteen detector-dataset pairs (five detectors on SWaT, WADI, and HAI), reference updates improve separation in some pairs but degrade it in others, and a retrospective policy that updates only where a label-free screen recommends it raises mean AUC from 0.751 (never updating) and 0.759 (always updating) to 0.809; on the twelve non-GDN pairs, which did not inform its boundaries, it gives 0.805 versus 0.759 and 0.747. Rescoring CNRE computed with a fixed reference reproduces most of the AUC gain of a reference update on WADI but not on SWaT. A detailed GDN case study connects the diagnostics: normal-only adaptation reduces normal prediction error by 27.3%, but the direction of its effect on attack separation depends on the reference protocol. With residuals fixed, stronger score ranking does not ensure that normal-calibrated alarms preserve their nominal false-positive rate. These results support choosing intervention stages and interpreting their outcomes through separate measurements of reference fit, attack evidence, and alarm calibration.

Primary area:
learning on time series and dynamical systems
Keywords:
Industrial control systems, Anomaly detection, Cyber-physical systems, Time series, Distribution shift, Diagnostic evaluation

Reviews

Among:
Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 4 reviews, above 27% of the others.
Reviewer_jvZqOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper points out that in industrial control systems, the metrics of anomaly detectors cannot tell which component of the pipeline leads to poor performance. For this, the authors decompose the anomaly detector to three stages and propose a workflow based on covariance-normalized residual energy to do the controlled comparisons of the normal reference, the residual-producing model, and the scoring and alarm rules. Experiments on 5 detectors and 3 datasets show that the effects of reference updates and rescoring vary across detector–dataset pairs. A GDN case study further shows that the effect of a model change depends on how the reference is fitted.

Critical strengths
  1. This paper clearly separates the interventions by the pipeline stages, and designs targeted controlled experiments to evaluate the effects of these interventions.
  2. The GDN case study compares the results of the same intervention under different reference protocols, indicating that the measured effect can reverse. This highlights that a model change cannot be interpreted without specifying how the normal reference is fitted.
Critical weaknesses
  1. The related work is not comprehensive. Only 3 of 23 references are from the latest 3 years (2024 ~ 2026). Some representative work are not discussed. For example, [1] proposes to determine which sensor or actuator has been manipulated by applying attribution methods to anomaly detectors. [2] has already used the methodology that keeps the trained model unchanged and separately studies the downstream decision rules. Besides, it has discussed the normal training-test distribution differences of SWaT and WADI.

  2. The difference from some related work is not stated clearly. Although the authors cites Garg et al.(2022)[3], they have not convincingly established the additional diagnostic value of the proposed workflow. [3] decomposes the detector to a model, a scoring function and a thresholding function, and varies the model and the scoring function independently on a grid of 10 models and 4 scoring functions. The "evidence extraction" and the "controlled comparison" principle in this paper are basically extensions of it. Besides, it also deploys a sliding-window update and observes that such scoring functions "can also adapt to anomalies in the test set". The authors should state what is new precisely.

  3. The policy comparison is retrospective and can be contaminated by attacks. The D_ref is computed based on the whole evaluation recording, and then the policy is evaluated on the same recording. The included "attack periods" can increase the statistics. A prospective screen computed on a trailing window is necessary for the practical value, not just an optional extension.

[1] Fung C, Zeng E, Bauer L. Attributions for ML-based ICS Anomaly Detection: From Theory to Practice[C]//NDSS. 2024.

[2] Fung C, Srinarasi S, Lucas K, et al. Perspectives from a comprehensive evaluation of reconstruction-based anomaly detection in industrial control systems[C]//European Symposium on Research in Computer Security. Cham: Springer Nature Switzerland, 2022: 493-513.

[3] Garg A, Zhang W, Samaran J, et al. An evaluation of anomaly detection and diagnosis in multivariate time series[J]. IEEE Transactions on Neural Networks and Learning Systems, 2022, 33(6): 2508-2517.

Questions for authors
  1. Could you elaborate on the related work and explain clearly the differences between this paper and the related work?
  2. Could you add the experiment for the prospective screen on the same recording?
  3. In Appendix A, it is stated that TranAD uses the v3 residual archive. Could you explain what "version" means and why it is v3? Does the choice affect the results?
2 comments

Thank you for the review and for the references.

W1 and Q1, related work. We added both papers to Section 2. Fung et al. (2022) keep the trained model fixed while they study the detection rule, and they observe that some benign test data in SWaT and WADI differs from the benign training data and remove features with a Kolmogorov-Smirnov test. Fung et al. (2024) attribute detected attacks to manipulated sensors. Our revision relates to both. We locate the difference between training and test in time and in specific channels, we test it by intervention, and our attribution targets the elevation of normal residual energy, not the attacked component.

W2, what is new relative to Garg et al. We agree that evidence extraction and controlled comparison follow their decomposition, and that they already observed that adaptive scoring can absorb anomalies. We state three differences. First, they vary the model and the scoring function. We treat the normal reference as a third component that is controlled separately. Second, we test the reference diagnosis by an intervention on the detector's inputs (Section 5.6). Third, we measure what the reference changes in comparisons between detectors. Across four label-free reference protocols, 36 of 540 comparisons between two detectors reverse with intervals that exclude zero (Appendix M). We also compared with their Gauss-D scoring directly (Appendix I).

W3 and Q2, prospective screen and contamination by attacks. We agree that this is necessary and ran it on the same recordings (Appendix H). A trailing median over 24 hourly blocks makes the same seven update decisions with no false trigger. It reacts about 12 hours late, and its mean AUC of 0.756 is no better than always updating at 0.759. Shorter windows react sooner but trigger on the ten-hour SWaT attack. Boundaries calibrated on training data alone were too tight and triggered falsely on most retained pairs. The revised abstract and Section 5.2 report that the causal version only matches always updating.

On contamination, we recomputed the screen without the attack timestamps and without the longest run. All fifteen decisions are unchanged (Appendix G). The statistic itself does move. For TranAD on SWaT it doubles when attacks are removed, but it stays far above the boundary.

Q3, TranAD v3. The version refers to our residual archive, not to the method. The SWaT model in our original archive had collapsed to a constant output, with a training error of 0.139 against 0.0068 after the rebuild, and no checkpoint had been kept. Version 3 rebuilds all three datasets with the same preprocessing and recipe and keeps the checkpoints. On SWaT it uses a learning rate of 0.001 instead of 0.008 and the seed with the lowest training loss, and no test labels enter this choice. On WADI and HAI the original archives were valid, and the choice does not affect the results. Fixed-reference AUC is 0.611 against 0.612 on WADI and 0.917 against 0.909 on HAI (Appendix P).

Thank you for the response and experiments. The revised version addresses my questions. Weakness 1 has been resolved, and Weaknesses 2 and 3 have been explained and supplemented with experiments. However, I maintain my rating because the paper's contributions as a method and as an analysis are still limited. As a method, the causal trailing-window screen only matches always updating, and Section 5.2 also states that the reference screen does not improve on simpler drift checks. As an analysis, the revision validates the reference diagnosis by intervening on specific input channels, but the more general conclusions, such as benign test data differing from benign training data and adaptive scoring absorbing sustained attacks, are close to the existing findings of Fung et al. (2022) and Garg et al. (2022).

Reviewer_sC27OpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

Residual-based anomaly detectors for industrial control systems convert prediction or reconstruction errors into scores and alarms. Final detection metrics provide limited guidance on whether failures arise from reference mismatch, weak attack separation, or downstream scoring and calibration. This paper proposes a retrospective diagnostic workflow using covariance-normalized residual energy to organize controlled comparisons across these stages. Experiments across 15 detector–dataset pairs show that selective reference updating raises mean AUC from 0.751 to 0.809, while a GDN case study demonstrates reference-dependent adaptation effects and alarm miscalibration.

Critical strengths
  1. The workflow carefully distinguishes reference, model, scoring, and threshold interventions through comparisons on matched residuals and timestamps.
  2. Evaluation spans five detector families and three primary datasets, includes uncertainty estimates, and transparently reports unsuccessful interventions and transfer failures.
  3. The reference-sensitive adapter experiments and alarm-calibration analysis provide useful evidence that better normal prediction or score ranking need not improve detection.
Critical weaknesses
  1. The workflow’s incremental benefit over existing model–scoring–threshold analysis is not established through direct comparisons of diagnostic accuracy or intervention efficiency.
  2. The twelve non-GDN validation pairs share the boundary-development datasets, while updates improve only 5 of 17 update-recommended NoBOOM recordings, leaving cross-dataset reliability weakly supported.
  3. Reference-versus-scoring attribution remains incomplete because the cross-detector analysis tests only one rescoring rule and does not separately isolate mean, variance, and cross-variable covariance updates.
  4. The model-intervention findings rely on one GDN checkpoint per dataset with incompletely documented original validation provenance, so adapter seeds do not establish robustness across independently trained detectors.
Questions for authors
  1. What measurable diagnostic advantage does the workflow provide over simpler residual-drift screening and established modular evaluation?
  2. Which observable properties distinguish beneficial reference updates from the unsuccessful recommendations on NoBOOM?
  3. Are WADI’s extremely elevated CNRE values robust to verified preprocessing consistency and independently trained checkpoints?
  4. How much of the reference-update gain comes from recentering versus covariance reweighting?
  5. Do the selective-update gains persist for low-FPR alarm recall and event-level detection delay, rather than pooled timestamp AUC alone?
1 comment

Thank you for the careful review and for the specific questions.

W1 and Q1, advantage over drift screening and modular evaluation. In selecting which pairs to update, the screen has no advantage over simpler drift checks. Appendix G shows that they reach the same decisions, and Section 5.2 now says so. The advantage we can measure comes from the step that existing modular evaluation does not include, an intervention that tests the diagnosis. Holding one WADI sensor returns the screen to retain and raises the fixed-reference AUC by 0.31 to 0.41. After this repair the fixed reference detects 7 and 9 of 13 attack runs at 1% FPR, against 3 and 5 for the guarded update on unmodified input (Section 5.6, Appendix K).

W2 and Q2, cross-dataset support and NoBOOM. This limitation stands and remains in Section 6. On your question, we split the 17 update-recommended NoBOOM recordings by fault share. Four of the five improvements fall in the middle third, and both the lowest and the highest third mostly get worse. We found no observable property that separates the successful recommendations from the unsuccessful ones, and we report this as a negative result.

W3 and Q4, recentering against covariance. Appendix I refits the mean, the variances, and the correlation structure separately. On WADI the mean alone gives nothing and mean plus variance matches the full update. On SWaT the full covariance adds 0.05 to 0.08 AUC. A split of the AUC into pairs within the same hour and pairs across hours explains the difference. On WADI the stale reference already ranks attacks above normal points of the same hour, so the update gain is an alignment of levels across hours, which rescoring reproduces. On SWaT the stale reference mis-orders attacks within the hour, at 0.475 for GDN, and only a refitted covariance restores the order, at 0.823. Four further rescoring rules give the same split.

W4, one checkpoint. We retrained GDN on the fitting split with three seeds and repeated the adapter study. The reversal between reference protocols replicates on all three bases. The size of the loss under held-out references does not, and its sign follows the base (Section 5.5, Appendix L).

Q3, robustness of the WADI values. Inference with the archived checkpoints reproduces the archived residuals to within 1.5×10−51.5 \times 10^{-5}. Three models trained independently with the released GDN code give a screen statistic between 10710^7 and 101110^{11}. In all of them the cause is the single sensor, and holding it returns the statistic to between 0.4 and 0.6 (Appendices J and K).

Q5, low FPR and event-level delay. The AUC gain of the selective policy does not carry over to AP, at 0.498 against 0.499 for never updating, or to recall at 1% FPR, at 0.427 against 0.460. At the event level, at a matched 1% FPR, it detects 62.2% of attack runs against 57.3% and 58.2%. This gain comes from SWaT. On the three WADI update pairs the update does not detect more runs. Delay does not separate the policies. Of all detections, 86% occur within one minute of the start of the run (Appendix N).

Reviewer_A6CTOpenReview ↗
Rating
2
Confidence
2
Informativeness
1
Presentation
1
Soundness
2
Read review
Paper summary

In this paper, the authors propose a diagnostic workflow for anomaly detection in industrial control systems, based on model residual measurements (performed with covariance-normalized residual energy, i.e., half the squared Mahalanobis distance between detector residuals and the reference). The objectives are to check drifts relative to reference data, detection capabilities, and the effectiveness of scoring/alarm rules. The workflow is evaluated on 5 detectors and 3 datasets.

Critical strengths
  • The experiment design and reporting are thoroughly described, and the authors provide the code to replicate the results, supporting reproducibility.
Critical weaknesses
  • The technical contribution appears weak, and most of the provided findings are already known and have been shown in previous studies (e.g., Garg et al. (2022) for adaptive scoring absorbing attacks, and Siffer et al. (2017) for adaptive thresholds). The only new result is the sign flip of the adapter effect, but it should be better validated, as the adapter’s reference is fitted on the same normal data used to train the adapter, and it cannot be generalized, as it was mainly reported for a single detector/checkpoint/dataset. Finally, it is difficult to see practical gains relative to standard baselines (e.g., simple drift checks) when using the workflow in real-world scenarios, given its stated purposes and limitations. For instance, the empirical evaluation shows that label-free screening identifies some cases where updating the reference helps, but these are related to high-drift cases that any simpler method would likely spot (as happens in SWaT when thresholding at the 99th training percentile).

  • The paper is difficult to follow, defers definitions of key terms, and is often confusing when making claims and limiting/weakening them right after. Fig. 2 is very hard to read.

Questions for authors
  • Could you please report each detector’s native anomaly score for the 15 pairs, next to CNRE?
  • Could you please compare DrefD_{ref} with simpler baseline screens (e.g., fraction of the points above the training 99th percentile, or ratio of test to training prediction error)?
  • Could you please fit the adapter reference on a separate normal split and check whether the sign flip remains?
2 comments

Thank you for the direct review. We address each point.

Known findings. We agree that the absorption of attacks by adaptive scoring is known from Garg et al. and that the same trade-off appears in SPOT. We cite both for these points. The new material is in Section 5.6. A stale reference is traced to a few input channels and confirmed by intervention, and this accounts for a difference of 0.46 AUC between two ways of normalizing the released GDN score on WADI.

The sign flip of the adapter, and Q3. You asked for a reference fitted on a separate normal split and noted that the result rested on one checkpoint. We did both.

With the archived checkpoint and references fitted on normal data that the adapter never saw, the adapter's loss shrinks to 0.053 to 0.075 AP on HAI and vanishes on SWaT.

We then retrained GDN on the fitting split only, with three seeds, and trained the adapter on each. Under each model's own fitting-split reference the adapter loses AP on all three bases, by 0.02 to 0.10. Under the adapter's reference it gains on all three, by 0.04 to 0.14. So the reversal between reference protocols replicates. With held-out references the difference is 0.007 with a standard deviation of 0.053, and its sign follows the base. So a loss under an independent split does not hold in general, and the revised Section 5.5 says so. The study still uses one detector on one dataset, which Section 6 states.

Practical gain over simple drift checks, and Q2. We agree, and the revision no longer claims otherwise. Appendix G compares the screen with six simpler label-free screens. Three of them reach the same policy AUC, and the fraction of energies above the training 99th percentile gives the same fifteen decisions. Section 5.2 now says that the screen does not improve on simpler drift checks. What the workflow adds comes after the flag. The intervention shows which channels are responsible and what follows. On WADI, the fixed reference on repaired input detects 7 and 9 of 13 attack runs at 1% FPR for GDN and TranAD, against 3 and 5 for the guarded update on unmodified input.

Q1, native scores. Appendix J reports the GDN-style score next to CNRE for all fifteen pairs, with its normalization statistics taken from the test set, as released, and from the training residuals. The two versions differ by 0.17 to 0.42 AUC in four update-diagnosed pairs and by at most 0.07 elsewhere. TranAD's own score, the mean squared residual, is reported there as well. We do not have the NSIBF and GeCo models, so their own scoring rules could not be recomputed.

Presentation. Figure 2 is redrawn with every point labelled. In the new text each result comes first, and its limits are collected at the end of the subsection instead of following each claim.

I thank the authors for their rebuttal and additional experiments, but I keep my rating as my main concerns still stand (and some of them were confirmed by the new results).

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

This paper presents a retrospective diagnostic workflow for residual-based anomaly detectors in industrial control systems. It uses covariance-normalized residual energy (CNRE), essentially a Mahalanobis residual score, to examine three possible limitations: mismatch between the training reference and evaluation data, weak attack–normal separation in the residuals, and ineffective downstream scoring or alarm calibration. The workflow is evaluated on five detectors across SWaT, WADI, and HAI. The authors compare fixed and adaptive references, alternative scoring and thresholding rules, and a GDN adapter under different reference-fitting protocols. The main empirical finding is that selectively updating the reference based on a label-free screening rule performs better on average than always or never updating it, while model, reference, scoring, and threshold choices can lead to substantially different interpretations of the same detector.

Critical strengths
  1. The component-wise diagnostic perspective addresses a meaningful evaluation problem. By separately varying the reference, residual producer, scoring rule, and alarm threshold, the paper demonstrates that poor final detection performance cannot always be attributed to the underlying model.
  2. The evaluation covers heterogeneous detector families under controlled comparisons. Applying a common residual-based analysis to five detectors across three ICS benchmarks provides useful empirical evidence that reference adaptation is not uniformly beneficial.
Critical weaknesses
  1. The methodological and theoretical novelty is limited. CNRE is a standard Mahalanobis residual statistic, while the remaining workflow mainly combines blockwise medians, rolling reference estimation, percentile-based rescoring, and component-wise ablations. As a result, the contribution appears closer to an evaluation protocol assembled from established techniques than a technically substantive new method.
  2. The core decisions depend heavily on manually specified empirical rules. The retain/update decision is determined by the thresholds 3 and 10, derived from only three GDN cases, while other central choices including block duration, rolling-window length, lag, winsorization range, guard threshold, and maximum freeze duration are also manually fixed.
  3. The experiments do not directly establish that the proposed workflow resolves the stated diagnostic challenges. The paper shows how different interventions change detection metrics, but it does not evaluate whether the workflow correctly identifies the actual source of failure, as no ground-truth failure causes or diagnostic-accuracy results are provided. The experiments therefore illustrate these challenges and provide useful case studies, but they do not directly demonstrate reliable failure localization.
Questions for authors
  1. What is the technical contribution beyond combining a standard Mahalanobis residual statistic with blockwise aggregation, empirical decision boundaries, rolling reference estimation, and controlled component comparisons?
  2. How were the thresholds 3 and 10 and the other core hyperparameters selected, and can the authors provide a systematic sensitivity analysis showing how diagnostic decisions and policy performance change across these settings?
  3. Can the authors provide direct experiments on independent industrial processes and datasets to demonstrate that the complete decision rule can reliably distinguish reference mismatch from sustained attacks and other causes of elevated residual energy, including cases in the inconclusive region, and that the resulting update decisions remain effective when made prospectively rather than retrospectively?
1 comment

Thank you for the detailed review.

W1 and Q1, technical contribution. We agree that CNRE is the standard Mahalanobis statistic and that the workflow is built from established parts. We say so in the paper. The contribution we defend is an empirical one. The normal reference is a component that can fail on its own. Its failure can be flagged without labels, and the flag can then be verified by holding a few input channels at training values. Once verified, it explains differences that earlier comparisons assigned to the model or the scoring rule. Section 5.6 and the general response give the evidence.

W2 and Q2, hand-set rules. The boundaries 3 and 10 came from the three GDN cases, as stated. Appendix F now varies every setting. Over 22 one-factor variations of window, lag, winsorization, guard rate, maximum freeze, and covariance estimator, the selective policy exceeds both alternatives in all 22, by 0.013 to 0.068 AUC. The fifteen screen decisions are the same for block lengths from ten minutes to four hours. Of 105 boundary combinations, 49 give exactly the result of 3 and 10. We also state the limit of this analysis. The plateau exists because no pair has a statistic between 1.94 and 62.5, so these datasets cannot tell boundaries apart inside that gap.

W3, no ground truth for the diagnosis. This was the most useful comment for us. Section 5.6 and Appendix K now test the reference diagnosis against a cause that we can manipulate. Channel sets and pass criteria were fixed before each run. On WADI all criteria hold, on the archived models and on three models trained with the released GDN code. On SWaT our primary channel set met three of four criteria and missed the AUC criterion, and a second pre-specified set met all four. We report both.

Q3, independent processes, sustained attacks, prospective decisions. We answer the three parts separately.

We did not add a new industrial dataset. BATADAL and the NoBOOM pilot remain scope checks, and the limitation stays in Section 6.

On telling a mismatch from a sustained attack, the new result is partly negative. A causal rule that reads only how long the residual level has been elevated cannot do it in time. Every trailing window of 18 hours or less triggers on the ten-hour SWaT attack, and every window of 20 hours or more reacts to a real shift eight or more hours late (Appendix H). What separates the two is the intervention. On WADI the elevation comes from one sensor at a time when no attack is active. None of our pairs falls in the inconclusive region, so we cannot evaluate that case.

On prospective decisions, the causal screen with 24 blocks makes the same seven update decisions with no false trigger, but its mean AUC of 0.756 is no better than always updating. The revised abstract and Section 5.2 say this.

Comments on the paper

2 comments

We thank all reviewers for their constructive feedback. We have substantially revised the manuscript with new experiments addressing the concerns about diagnostic validation, methodological contribution, experimental robustness, and practical relevance. The main changes are summarized below; new material is highlighted in blue in the revised PDF.

  • Direct validation of the reference diagnosis (new Section 5.6 and Table 4). We introduce targeted channel interventions to validate the causes of elevated residual energy. On WADI, we trace the reference mismatch to a single out-of-range sensor, 2B_AIT_002_PV. Holding this sensor at its pre-jump value reduces the reference-screen statistic from approximately 10710^7 to below 1 and improves fixed-reference AUC from 0.450 to 0.861 for GDN and from 0.583 to 0.893 for TranAD. The finding is further reproduced with three independently trained models using the released GDN code. On SWaT, intervening on four channels similarly reduces the screen statistic from 8711 to 1.89 for GDN and improves AUC from 0.814 to 0.901. These experiments provide direct evidence connecting reference mismatch to specific input channels.

  • Stronger validation of reference-dependent model evaluation (revised Section 5.5, Table 3, and Appendix L). We extend the GDN adapter case study with crossed model–reference comparisons, separate normal reference-fitting splits, and three independently retrained base models. On HAI, normal-only adaptation reduces prediction MSE by 27.3%, yet its measured effect on AP changes from a loss of 0.121 under individually refitted references to a gain of 0.020 under the shared frozen reference. Additional experiments separate the effects of reference mean, marginal scales, and correlations. The reference-dependent reversal is reproduced across retrained bases under fitting-split references, while its magnitude under held-out references varies across checkpoints.

  • Additional scoring and reference-mechanism analyses (revised Sections 5.4–5.6 and Appendices I–J). We isolate recentering, variance, and correlation effects and evaluate additional rescoring rules. We also compare CNRE with detector-specific scoring implementations and examine the impact of normalization-statistic provenance. On WADI, the released GDN scoring procedure achieves approximately 0.83 AUC with test-set normalization versus 0.37 with training statistics. The difference disappears after the identified sensor intervention, connecting the apparent scoring advantage to the reference mismatch.

  • Expanded robustness and practical evaluation (revised Section 5.2 and Appendices F–H and N). We add systematic sensitivity analyses, comparisons with simpler label-free drift screens, prospective screening, and low-FPR and event-level evaluations. The retrospective selective-update policy improves mean AUC from 0.751 to 0.809, and its main decisions are stable across broad parameter ranges. However, simpler screens produce the same decisions, and the causal version achieves 0.756 AUC, comparable to always updating (0.759). We therefore clarify that the screen supports diagnostic investigation rather than claiming a superior deployment policy.

Together, these additions strengthen the experimental basis of our three-stage residual-evidence diagnostic workflow, particularly by validating reference-diagnosis hypotheses through controlled interventions and demonstrating how reference and scoring choices affect the interpretation of detector performance. We address each reviewer's specific concerns and provide additional results in the individual responses below.

Dear reviewers, thank you again for your time. We posted our responses and the revised PDF on November 12. If any point is still unclear, or if a further analysis would help, we would be glad to provide it before the discussion closes. We would also appreciate hearing whether the intervention results in Section 5.6 change your assessment of the diagnostic validation.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.