acceptodds
Under review as a conference paper at ICLR 2027

Detecting Time Series Anomalies Like an Expert: A Multi-Agent LLM Framework with Specialized Analyzers

Abstract

Time-series anomaly detection often returns scores or intervals, while analysts need to understand the abnormal behavior and the evidence supporting it. We introduce SAGE (Specialized Analyzer Group for Expert-like Detection), a multi-agent framework for evidence-grounded diagnosis of univariate time series. Four specialized Analyzers examine point, structural, seasonal, and pattern anomalies using numerical tools and diagnostic visualizations. A Detector integrates their evidence into intervals, candidate types, and evidence-strength confidence scores; a Supervisor translates these records into analyst-facing reports. Synthetic in-context references are constructed from normal-reference training segments, reducing dependence on real anomalous demonstrations. Across Yahoo S5, KPI, and WSD, SAGE achieves an average Point-F1 of 66.26, the highest among the evaluated methods. Controlled synthetic evaluation examines localization and type diagnosis, while component ablations support the detection contribution of specialized evidence generation. In a method-blind human study, evaluators rate SAGE's diagnostic outputs as more useful than those of the compared methods.

Primary area:
learning on time series and dynamical systems
Keywords:
Time-Series Anomaly Detection, Large Language Models, Multi-Agent Systems, Anomaly Diagnosis, Tool-Augmented Reasoning

Reviews

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

The paper proposes SAGE, a training-free team of prompted LLM agents for univariate time series anomaly detection. Four Analyzers (point, structural, seasonal, pattern) call numerical tools such as STL, CUSUM, FFT and SAX. A Detector combines their outputs, and a Supervisor writes a report. The Detector also sees synthetic contrast pairs, built by injecting nine rule-based anomaly types into normal training segments.

Critical strengths
  1. The paper is honest about many of its limits (5% test portions, unequal budgets, uncalibrated confidence).
  2. Sensible split of labour: tools compute, the LLM judges.
  3. The output (interval, type, explanation) is closer to what an operator needs than a bare score.
  4. Broad set of studies: ablations, backbones, zero-shot runs, a human study.
  5. Prompts are given in full.
Critical weaknesses
  1. The test portion of KPI and WSD is only 5% of each series (the rest is dropped for API cost). For WSD that is about two 400-point windows per series. Many windows will have no anomaly and per-series F1 will be unstable. The main claim is therefore weakly supported. Please evaluate on the full test splits or at least a much larger fixed sample.

  2. It is not stated how the scores of the eight ML/DL baselines were turned into binary labels for Point-F1 (oracle threshold, percentile, or something else). This choice decides all of Table 1 and needs to be documented.

  3. The baselines look weak. Plain STL residuals (Table 8, 53.2 average Point-F1) beat every baseline in Table 1 (best is 46.08). Matrix Profile scores only 10.2. TAMA gets 3.82 on Yahoo but 65.69 on the synthetic set, which suggests a failed reproduction.

  4. The gains come from the specific LLM more than from the design. Point-F1 goes from 66.26 (Sonnet 4.6) to 48.20 (GPT-5.1) and 10.57 (Qwen3.5-9B). With GPT-5.1, SAGE is barely above LSTM-VAE (46.08). No open-weight model comes close, so the results cannot be reproduced without a proprietary model, and no code is released.

  5. The ablation is mixed. Specialization helps on Yahoo, but on KPI and WSD removing it raises three of four metrics (e.g. WSD PA-F1 98.87 vs 95.68), and the paper says it cannot fully describe that condition (Appendix E.3). Why would the specialized design hurt on two of three datasets?

  6. The "diagnosis" claim is not backed by real data. Type diagnosis is tested on 156 synthetic cases made with the same injection rules that shaped the Analyzer prompts (somewhat circular), and on a single-author annotation of 300 intervals, of which 251 are point anomalies. There are no real labels for structural, seasonal or pattern types. Also, the "recall" in Table 2a only measures whether the Analyzer returned some overlapping interval, not final detection.

  7. All decision logic sits in hand-written prompts (the cut at 50, the spike-cluster bonus, "typically less than 5% of points are anomalous"). It is not said how these were chosen or whether test series were looked at. The Detector may also report intervals that no Analyzer proposed, and nothing checks them against tool evidence. How often does this happen?

  8. The human study has 10 raters and 25 samples, with ground truth shown next to the predictions, so "Accuracy" mostly re-measures detection. Only SAGE writes a structured report, so blinding is doubtful, and the Wilcoxon test treats 250 dependent pairs as independent.

  9. The novelty is limited: an orchestration of standard tools around a hosted LLM, which the paper itself says is "not a new numerical detector". Multi-agent and retrieval-based LLM detectors (TSAD-Agents [1], LLMAD [2]) already exist.

  10. The cost is high: about 80 s per 400-point window and about 27K tokens per window. The total cost of the main run, and of each LLM baseline, is not given.

References: [1] Xu, X., Wang, H., Liang, Y., Yu, P. S., Zhao, Y. and Shu, K. (2026). Can Multimodal LLMs Perform Time Series Anomaly Detection? (TSAD-Agents). The ACM Web Conference 2026 (WWW '26). arXiv:2502.17812.

[2] Liu, J., Zhang, C., Qian, J., Ma, M., Qin, S., Bansal, C., Lin, Q., Rajmohan, S. and Zhang, D. (2024). Large Language Models can Deliver Accurate and Interpretable Time Series Anomaly Detection (LLMAD). arXiv:2405.15370.

Questions for authors
  1. How were baseline scores thresholded in Table 1?

  2. How many test windows per dataset contain at least one anomaly? What are the results on the full test splits?

  3. Which runs produced Table 1 and which Table 13? Why do only Point-F1 values match?

  4. How were the Detector rubric and the Global Rules chosen? Did anyone inspect test series?

  5. How does SAGE perform with an open-weight backbone of reasonable size?

  6. What is the total token and dollar cost of the full benchmark, for SAGE and for each LLM baseline?

2 comments
AuthorsOpenReview ↗

Response to Reviewer hqsh

Thank you for the careful review. We address the concerns in order.

1. Test scope (W1, Q2).

We used the final 5% of KPI/WSD for testing following LLMAD's setting (Sec. 4.1) and to limit API time and cost on long series. SAGE uses the first 70% for normal references and excludes the middle 25%; splits and file selection differ. The Sonnet runs cover 19 KPI and 18 WSD series, with 318 and 52 non-overlapping 400-point windows; 54 and 20 contain anomalies. Series with no labeled anomaly in the final 5% were excluded. We will disclose these rules and counts and limit conclusions to the evaluated portions. We do not have full-partition results.

2. Thresholds (W2, Q1).

SAGE uses training data for normal references but no separate anomaly-labeled validation set for cutoff selection. The Detector scores selected intervals, not every time point, so point-score calibration procedures do not transfer directly. For offline evaluation, SAGE selects a cutoff per test series on a 0.01 confidence grid to maximize raw Point-F1 using test labels. The ML/DL evaluations maximize the same objective over 100 thresholds between the 50th and 99.9th percentiles of each series' test scores. One binary prediction supplies all four metrics; only Point-F1 is optimized. This is a post-hoc oracle comparison, not deployment performance. Users can use types and evidence to set a domain-specific cutoff; its performance is untested. The grids differ, and direct-output LLM/VLM methods retain method-specific post-processing. We will document each rule.

3. Baselines and TAMA (W3).

STL residuals reach 53.2 mean Point-F1, above every ML/DL row in Table 1 (best 46.08). SAGE is about 66.3 in that comparison, which does not isolate the LLM's contribution or establish superiority over every lightweight method. On 355 Yahoo series, TAMA's saved outputs have 2.23% mean point precision and 63.80% recall: many false positives explain its low Point-F1. The synthetic task differs from Yahoo. We will describe the evaluated TAMA adaptation without generalizing this result to the method as a whole.

4. Backbones, ablation, and contribution (W4, W5, W9, Q5).

Mean Point-F1 is 66.26 with Sonnet 4.6, 48.20 with GPT-5.1, 42.84 with Qwen3.5-27B, and 10.57 with Qwen3.5-9B. The best result relies on a proprietary backbone. Removing specialization changes Point-F1 from 79.69 to 41.08 on Yahoo, 60.97 to 59.22 on KPI, and 58.12 to 55.54 on WSD, but raises the other three metrics on KPI/WSD. We will discuss this mixed result. Our contribution is the procedure for aggregating family-specific numerical/visual evidence, normal-derived contrasts, and support/conflict-aware diagnostic records. We do not claim novel tools or model architecture; the ablation does not isolate compute or backbone effects.

5. Diagnosis and human study (W6, W8).

The 156 injected cases share the Analyzers' type definitions, although synthetic ICL was disabled. Table 2's “recall” measures overlap with the relevant Analyzer evidence interval, not final Detector recall or independent accuracy on natural anomaly types. The 300-interval annotation is single-author and point-dominated; we will clarify aggregation and scope. Ten raters assessed 25 cases with method names hidden and order randomized, but reference and predicted intervals visible. Ratings reflect combined detection/report quality, not verification of every explanation. The Wilcoxon test treats repeated rater/case observations as independent; we will emphasize descriptive rater-level results.

6. Detector rules (W7, Q4).

The prompt's 50-point minimum evidence score determines what the Detector reports and differs from the evaluation cutoff. Spike-cluster guidance addresses dilution of individual z-scores in rolling statistics; “typically <5%” is a sparsity prior. The authors did not inspect benchmark test series or labels when choosing these rules, and we do not claim the constants are optimal. The Detector may report a visually supported interval outside Analyzer candidates. We will clarify this behavior; its frequency has not been measured, so we will not say every output was proposed by an Analyzer.

7. Tables and cost (W10, Q3, Q6).

Table 13 retained full-metric backbone values from an earlier analysis. Its Sonnet Point-F1 matches Table 1 after rounding, but some PA-F1, Affiliation-F1, and Delayed-F1 entries differ. Table 1 is our current main comparison; we will remove Table 13 and retain the Point-F1 backbone comparison. Recorded Sonnet latency is about 80 s per 400-point Yahoo window. One Yahoo A1 run used about 22.4K input and 4.9K output tokens per window; these are not whole-study averages or total costs. Total costs require usage logs. We make no cost-efficiency claim.

Thanks to the authors for the detailed reply. I could only check it against the submitted PDF, so I have not verified the changes promised for the revision.

  • Test scope: The new counts are useful, but they show that the KPI and WSD results are based on a handful of series. Were all the baselines evaluated on exactly the same series? It would also help to see some spread across series, since one series can move the average quite a bit.

  • Thresholds: The answer to Q1 changes how Table 1 should be read. If only SAGE gets a cutoff tuned on the test labels while the LLM baselines do not, the comparison with them is not on equal terms. Please add SAGE with a fixed cutoff next to Table 1 and state clearly in the paper how the cutoff is chosen for each method.

  • TAMA and STL: The explanation for the low TAMA score is plausible, and I withdraw my remark about a failed reproduction. STL is a strong baseline and should appear in Table 1 under the same protocol as the others.

  • Backbones: I missed that Table 12 already has Qwen3.5-27B, so Q5 is answered. Still, the gains seem to depend on the hosted model, and the benefit of specialization is clear only on Yahoo. The claims should be worded accordingly.

  • Diagnosis and human study: The reply agrees with my reading but adds no new evidence. The abstract should say only what was measured (a combined rating on a small number of cases), and diagnosis on real non-point anomalies is still untested.

Overall, the rebuttal improves the documentation but does not add new experiments. The test-label cutoff for SAGE and the small number of series behind the KPI and WSD results still weaken the main claim, so I keep my rating at weak reject. A fixed-cutoff comparison on the same series, with some spread, would change my view.

Reviewer_yUjLOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper introduces a multiagent framework for evidence-grounded diagnosis of univariate time series. It consists of four specialized Analyzers and an evidence grounded Detector using synthetic in-context learning.

Critical strengths
  • This paper introduces a multi-agent workflow that combines specialized Analyzers, numerical and visual tools based on structured evidence generation and aggregation, linking family-specific analysis to explicit records of anomaly intervals, candidate types, and supporting evidence.

  • This paper evaluates anomaly-type diagnosis based on human ratings of report quality in terms of accuracy, validity, clarity, and usefulness.

  • The authors openly acknowledge limitations such as evidence on variable contributions in multivariate data, as discussed in the Conclusion.

Critical weaknesses
  1. Given the growing research activity in LLM-based explanation, I believe it is difficult to establish technical novelty and reliability based on subjective human ratings alone. Clearly define the criteria for good explanations and the limitations of existing methods, propose a new algorithm to overcome these limitations, and demonstrate its superiority using independent, objective metrics.

  2. The evaluation covers only a limited set of benchmark datasets and baseline methods. An accuracy comparison with NORMA and MP, examples of leading methods, on dataset TSB-UAD [X], widely used in the time-series anomaly detection community, would strengthen the evaluation. Table 3 of [X] provides a performance comparison across 18 datasets. Showing higher average accuracy would be ideal, but identifying the types of data for which the method works best would also be valuable. 

[X] J. Paparrizos et al., TSB-UAD: an end-to-end benchmark suite for univariate time series anomaly detection, VLDB 2022.

For more recent datasets and evaluation metrics, see [Y].

[Y] J. Paparrizos et al., Advances in Time-Series Anomaly Detection: Algorithms, Benchmarks, and Evaluation Measures, ACM SIGKDD, 2025.

  1. The choice of the four Analyzers and nine Injection Rules could be better motivated. Please clarify why they are necessary and sufficient.
Questions for authors

I have listed the weaknesses in order of priority. I would appreciate it if the authors could address some of the suggestions, even if not all.

3 comments
AuthorsOpenReview ↗

Response to Reviewer yUjL

Thank you for the constructive review. We address your three concerns in order.

1. Explanation quality and technical contribution.

Subjective ratings alone do not establish factual reliability. A useful diagnosis localizes an interval, links a plausible type to inspectable evidence, and guides follow-up. Appendix Table 17 defines the 1–5 anchors for Accuracy, Validity, Clarity, and Usefulness. Evaluators saw ground-truth and predicted intervals, so their ratings of 25 cases do not independently verify each type or explanatory statement.

Our contribution is the procedure in Section 3: family-specific Analyzers generate numerical and visual evidence; a Detector weighs supporting and conflicting evidence in a shared candidate representation, alongside normal-derived contrasts; and its record retains intervals, types, and evidence for the Supervisor. LLMAD, TAMA, and TSAD-Agents can also explain findings and/or use tools. We do not claim novelty for individual tools or a new model architecture. Four detection metrics (Table 1), type-level evaluation on 156 injected cases with synthetic ICL disabled (Table 2), and ablations (Figure 3) support distinct aspects of SAGE. They do not establish factual explanation accuracy for natural anomalies, and we will keep the diagnostic claim within that scope.

2. Benchmark coverage and MP/NormA comparisons.

The original evaluation already overlaps the suggested benchmark families: Yahoo S5 and KPI/IOPS appear in TSB-UAD [X], while WSD appears in the later TSB-AD collection. Our selected files and test portions do not reproduce either full benchmark protocol. Applying multi-agent API inference to all 18 public TSB-UAD datasets (1,980 series), let alone the entire suite, exceeds the rebuttal-period time and inference budget. We therefore restrict the conclusion to the evaluated series and test portions.

Within that scope, we additionally ran Matrix Profile (MP) and SAND on the same test files and indices as SAGE (Yahoo 355, KPI 19, WSD 18). MP uses a STUMPY self-join and TSB-UAD's ACF window selector. SAND is a related publicly available method, not a direct NormA evaluation. Both offline baselines score each full contiguous series without labels; on KPI/WSD this gives them access to the intervening unlabeled 25% excluded from SAGE's normal-reference construction. For each series, we select the operating point maximizing raw Point-F1; all distinct score thresholds were checked for MP/SAND.

DatasetMP Point-F1SAND Point-F1SAGE Point-F1
Yahoo15.5843.5479.69
KPI4.296.5760.97
WSD6.7327.8058.12

We also used the official TSB-UAD implementation to compute VUS-ROC/PR from continuous MP/SAND scores and SAGE interval-confidence scores, with the same file-specific ACF buffer for all methods. The VUS analysis uses a separate Sonnet 4.6 inference run from the F1 comparison; it is reported separately for that reason. SAGE's interval confidence is assigned to covered points (maximum on overlaps; zero elsewhere).

DatasetMethodVUS-ROCVUS-PR
YahooMP87.0641.99
SAND89.9661.78
SAGE88.5360.72
KPIMP23.445.94
SAND54.005.83
SAGE84.4531.84
WSDMP28.043.17
SAND54.3925.83
SAGE72.2250.09

SAGE leads the Point-F1 comparisons and both VUS metrics on KPI/WSD; SAND narrowly leads Yahoo VUS-ROC/PR. Within Yahoo, SAGE leads VUS-PR on A1/A2 and SAND on A3/A4. This variation is informative, but the experiment is neither a full TSB-UAD evaluation nor a direct NormA comparison.

3. Four Analyzers and nine injection rules.

The four families organize distinct evidence: local statistics for point anomalies; persistent level, trend, or variance changes for structural anomalies; periodicity and amplitude for seasonal anomalies; and motifs/waveform shape for pattern anomalies. They are not mutually exclusive gates, and several Analyzers may support one interval. The nine injection rules create contrastive ICL references and controlled synthetic evaluation cases for the nine defined types; they are not applied as detection rules at inference. We do not claim that four Analyzers or nine rules are necessary, sufficient, or optimal for every anomaly. Removing specialization lowers Yahoo Point-F1 from 79.69 to 41.08, with smaller effects on KPI/WSD (Figure 3). This supports specialization in the evaluated setting, without establishing complete anomaly coverage or an optimal taxonomy.

Thank you for the response. I appreciate the authors' detailed response.

My main concern remains whether these results offer meaningful advantages over existing methods. The response does not yet provide sufficient evidence of such advantages in terms of (1) novelty in LLM-based explanations, (2) performance improvements over pre-LLM anomaly detection methods, and (3) modeling of the anomaly detection task.

I will therefore keep my rating unchanged.

Thank you for clarifying your remaining concerns. We may not have made the evidence for SAGE’s advantages sufficiently clear. Its diagnostic procedure connects each reported interval and candidate type to family-specific numerical and visual evidence, weighs supporting and conflicting findings, and reports the relevant time-series characteristics and rationale. This evidence-to-diagnosis procedure is our methodological contribution.

The assessment is not based on human ratings alone. In Table 1, SAGE achieves the highest average across all four detection metrics among the evaluated methods, including 66.26 Point-F1 versus 46.08 for the strongest pre-LLM ML/DL baseline. Our earlier response also provides MP and SAND comparisons on the evaluated test portions. The controlled type study and component ablations examine complementary aspects of the diagnostic workflow.

Finally, SAGE models detection and diagnosis jointly through records containing an interval, candidate types, evidence strength, and supporting evidence. The four Analyzers organize complementary time-series evidence; the nine injection rules construct contrastive references. Our claims concern the evaluated settings, without asserting that this taxonomy is necessary or sufficient for every anomaly.

Comments on the paper

3 comments
AuthorsOpenReview ↗

Response to Reviewer QQoz

Thank you for the careful review and for proposing controls that would clarify what drives SAGE's results. We address each question below.

1. Same-evidence and compute-matched controls.

SAGE's methodological contribution is the procedure for generating family-specific numerical and visual evidence, passing it through a shared candidate representation, and using a Detector to weigh supporting and conflicting observations before producing interval, type, and diagnostic records. Removing specialization lowers Point-F1 from 79.69 to 41.08 on Yahoo, 60.97 to 59.22 on KPI, and 58.12 to 55.54 on WSD. However, this ablation also changes the agent configuration and compute; three other metrics improve without specialization on KPI/WSD. It therefore does not isolate a benefit from multi-agent collaboration at a matched budget. The lightweight detector comparison likewise does not give a non-LLM fusion module the same Analyzer outputs. We have not run the requested same-evidence fusion or compute-matched single-agent controls, and will not claim that LLM aggregation independently outperforms either alternative. Such controls are valuable follow-up experiments.

2. KPI/WSD test scope.

LLMAD (Sec. 4.1) also evaluates the final 5% of KPI and WSD. We followed that test proportion while limiting the time and API cost of multi-agent inference on long series. In our comparison, SAGE and the reimplemented LLMAD baseline use the same evaluation files and final test portions. SAGE uses the first 70% of each series to construct normal references and does not use the intervening 25% for inference; both methods are evaluated on the final 5%.

The recorded Sonnet runs cover 19 KPI and 18 WSD series and 318 and 52 non-overlapping 400-point test windows, respectively. Matching label copies show that 54 KPI and 20 WSD windows contain an anomaly. We will state the test portions and counts clearly. These experiments support conclusions about the evaluated final portions, not full-partition performance or stable gains on every series. We do not have results for a larger fixed test portion; per-series distributions would require the corresponding result records.

3. Type agreement and human evaluation.

Table 2's detection “recall” measures whether the Analyzer assigned to the injected family returned an evidence interval overlapping the injected anomaly; it is not final Detector recall. Reported type agreement compares the highest-confidence predicted type with the injected type on detected cases. The table does not give a sufficiently clear denominator and aggregation rule to reproduce every percentage from its displayed counts. We will check the case-level predictions and aggregation, provide a type-level confusion matrix and exact definition if recoverable, and correct any inconsistent numbers. Until then, we will not treat those rates as independent validation of type accuracy on natural anomalies. The 156 injected cases use the same taxonomy as the Analyzers, with synthetic ICL disabled; the auxiliary 300-interval annotation was made by one author and is dominated by point anomalies.

Ten raters evaluated 25 selected cases. Method names were hidden and presentation order randomized, but raters could see reference and predicted anomaly intervals. Their ratings therefore describe combined detection/report quality on those cases, not blinded verification of every diagnostic statement or operational impact. The reported Wilcoxon test also treats repeated rater/case observations as independent. We will emphasize descriptive rater-level results rather than a significance claim that ignores this dependence.

4. Budget, latency, backbones, and confidence.

The reported approximately 80 s is Sonnet 4.6 latency per 400-point Yahoo window; it does not establish suitability for second-scale real-time alerts. One representative Yahoo A1 run used about 22.4K input and 4.9K output tokens per window, not a whole-study average. We have not compared methods under matched budgets or strict latency limits. Backbone choice also matters: average Point-F1 is 66.26 with Sonnet 4.6, 42.84 with Qwen3.5-27B, and 10.57 with Qwen3.5-9B. We will describe this dependence rather than imply consistent transfer across models.

Detector confidence is an ordinal evidence-strength score, not a calibrated anomaly probability. It is assigned to selected candidate intervals, not every time point. The reported per-series Best-F1 cutoff uses test labels, so it measures an offline operating point rather than false-positive behavior at a deployment cutoff. An operator can inspect reported types and evidence to choose a domain-specific cutoff, but its false-positive rate and threshold sensitivity have not been established by the current experiments. We will make this distinction explicit.

Remaining Concerns

  1. Same-evidence fusion and compute-matched single-agent comparisons remain absent, making it difficult to establish the independent contribution of multi-agent reasoning.
  2. Excluding test series without labeled anomalies introduces potential selection bias and limits the assessment of false positives. Different data-selection protocols further weaken the comparison with LLMAD.
  3. Using test labels to select per-series Best-F1 thresholds raises concerns about the validity of the reported detection performance, particularly under realistic deployment conditions.
  4. Anomaly-type agreement remains insufficiently reproducible, while the human evaluation does not independently establish the reliability of the generated diagnoses.

I appreciate the authors' detailed response. However, most concerns have been acknowledged rather than resolved through additional evidence. Therefore, I prefer to maintain my original rating.

Thank you for the follow-up. We first need to correct our previous description of the KPI/WSD comparison. In our study, SAGE and the reimplemented LLMAD baseline used the same evaluation files and temporal test portions. Our statement implying that their test-file selection differed was incorrect. SAGE’s normal-reference construction and LLMAD’s retrieval procedure are method-specific, but they do not imply different test files. We apologize for the misleading wording.

We agree that a same-evidence fusion baseline and a compute-matched single-agent control would better isolate the contributions of LLM aggregation and agent collaboration. Our current ablations measure the effect of removing specialization within SAGE; we do not present them as matched-budget evidence for agent count alone.

The reported Best-F1 uses test labels for retrospective threshold selection, not for Analyzer or Detector inference. It characterizes detection at an oracle operating point and does not establish false-positive performance under a deployment threshold. We will also make the type-agreement denominator and aggregation procedure explicit before relying on those percentages, and describe the human ratings as assessments of report quality on the evaluated cases. Within these bounds, the detection results and ablations support the performance of the full SAGE framework on the evaluated test portions.

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

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