acceptodds
Under review as a conference paper at ICLR 2027

Operation-Guided Progressive Human-to-AI Text Transformation Benchmark for Multi-Granularity AI-Text Detection

Abstract

As AI writing assistants become increasingly integrated into real-world drafting and revision workflows, many documents are no longer purely human-written or AI-generated, but instead result from progressive human–AI co-editing. However, existing AI-text detection benchmarks largely focus on final outputs and provide limited understanding of how AI authorship signals emerge, accumulate, or disappear throughout the revision process. We introduce OpAI-Bench, an operation-guided benchmark for studying progressive human-to-AI text transformation across document, sentence, token, and span granularities. Starting from human-written documents, OpAI-Bench constructs nine sequentially revised versions for each sample under predefined AI coverage levels and five representative AI edit operations, covering four domains while preserving complete authorship provenance at multiple granularities. The benchmark supports comprehensive evaluation with 8 document-level detectors, 7 sentence-level detectors, and 2 fine-grained token/span-level detectors. Experiments reveal that AI-text detectability is governed not only by the proportion of AI-edited content, but also by edit operation, domain, and cumulative revision history. Interestingly, we notice that mixed-authorship intermediate versions are often harder to detect than both fully human and heavily AI-edited endpoints, exposing non-monotonic detection patterns missed by existing benchmarks. OpAI-Bench provides a controlled testbed for analyzing whether, when, and how AI-assisted writing becomes detectable under realistic progressive editing scenarios.

Primary area:
datasets and benchmarks
Keywords:
AI-generated text detection, human-AI co-writing, benchmarking

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_e5tROpenReview ↗
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3(+1)
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3
Informativeness
2
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2
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Paper summary

The paper introduces OpAI-Bench, a benchmark for AI-text detection under progressive human-to-AI revision. Starting from 15,722 human-written documents across four domains (student essays, news, government reports, scientific abstracts), the authors build nine-version trajectories (v0 to v8) in which a fixed, document-seeded sentence ordering determines which sentences are rewritten. Sentence-level AI coverage rises from 0% to 100% under a fixed operation schedule (polish, paraphrase, style, compress, expand, style, paraphrase, polish), and each version is produced by editing the previous one, so earlier-selected sentences are re-edited at every later step. Provenance labels are released at the document, sentence, and token/span levels, with token labels projected from rewritten sentence regions. The authors evaluate 8 document-level detectors, 7 sentence-level detectors, and 2 token/span-level localizers, in zero-shot and fine-tuned settings, with Qwen3-8B held out as an unseen generator. The main empirical claim is that detectability is non-monotonic in AI coverage, with a pronounced dip around v4 where compression is applied at 50% coverage. Three ablations are offered to separate the contributions of coverage, operation, and revision history, and these are repeated with a second editing model.

Critical strengths
  • The released data is a useful resource for the community. Each source document comes with all intermediate versions, stable sentence identifiers, and aligned document-, sentence-, and token-level provenance, across four domains and roughly 280K samples. Even though the current paper makes limited use of the trajectory structure, other researchers can build version-aware tasks on top of it, such as change detection between consecutive versions or estimating the extent of AI editing.
  • The evaluation is broad and carefully controlled at the data level. The paper covers detectors from several families at three granularities, in both zero-shot and fine-tuned settings, with a held-out generator and splits made at the source-document level to prevent leakage across versions. The fixed-coverage ablation also yields a concrete and actionable finding: at matched coverage, compression is consistently harder to detect than paraphrasing or expansion. This gives detector developers a specific failure mode to target.
Critical weaknesses
  • Limited novelty. Controlled AI involvement (APT-Eval, EditLens), word- and sentence-level attribution (HACo-Det, DAMASHA), and operation taxonomies (CUDRT, which covers closely related create, update, delete, and rewrite operations) are all established. The cumulative trajectory is therefore the only distinctive element, yet the paper tests its value only through a single ablation, which in fact shows a similar v4 drop under independent editing. No task makes use of the trajectory itself, such as detecting changes between consecutive versions or identifying the version at which AI involvement begins. The token- and span-level labels are also projected from whole rewritten sentences, so they add little beyond sentence-level provenance.
  • Insufficiently justified core design. The entire benchmark rests on a fixed nine-version schedule, but the paper offers only a brief rationale for it. The number of versions, the order of operations, and the position of each operation in the schedule are never ablated. This matters because the headline “critical v4 region” coincides with the only compression step. The paper’s own fixed-coverage ablation suggests that this is an operation effect, possibly confounded by the shorter length of compressed sentences, and not a property of intermediate coverage. The claim that intermediate versions are “harder than both endpoints” also requires a prevalence-independent metric. AUROC is reported only at the document level with v1 to v8 pooled, and F1-AI is undefined at v0, so per-version AUROC or balanced accuracy is needed to support this comparison.
Questions for authors
  • Could you clarify how OpAI-Bench differs from prior work on controlled AI involvement and edit operations, such as CUDRT, APT-Eval, and other similar benchmarks, which already cover closely related edit operations and show that detection does not scale consistently with the degree of AI editing? It would also be helpful to know what the cumulative trajectory enables beyond per-version evaluation, given that the independent-editing ablation shows a similar drop at v4. If possible, a task that directly uses the trajectory, such as detecting changes between consecutive versions or identifying the version at which AI involvement begins, would make this contribution much clearer.
  • Since compression appears only at v4, would it be possible to run a small ablation that changes the order or position of operations in the schedule, for example placing compression at a lower or higher coverage level?
  • The current token- and span-level labels are projected from whole rewritten sentences, so a lightly polished sentence and a sentence rewritten several times receive the same label. Have you considered graded labels based on edit magnitude or the number of rewrites, and how would the fine-grained localization results change under such labels? Similarly, would it be feasible to include a subset with real human edits interleaved with AI edits, so that the benchmark more closely reflects realistic human–AI co-editing?

If the authors can address the weaknesses and questions above, I would be happy to raise my score.

8 comments
AuthorsOpenReview ↗

Response to Reviewer e5tR [1/7]

We thank the reviewer for the constructive and detailed comments, and for recognizing the value of OpAI-Bench as a research resource and its comprehensive evaluation. We have uploaded a revised version of our paper to accommodate all your suggestions. Below, we further provide detailed clarifications for each of your questions, including new experiments and analyses.

W1.1: Limited novelty. Controlled AI involvement (APT-Eval, EditLens), word- and sentence-level attribution (HACo-Det, DAMASHA), and operation taxonomies (CUDRT, which covers closely related create, update, delete, and rewrite operations) are all established.

Thanks for this comment. We clarify that, while controlled AI involvement, fine-grained attribution, and edit-operation taxonomies have been studied in prior work, OpAI-Bench tracks AI-text detection across cumulative revision trajectories of the same human-written document. Each source document has nine aligned versions (v0–v8), where each version builds on the previous one and earlier AI-edited sentences can be rewritten again, with the editing operation, AI coverage, and provenance known at every step. APT-Eval, EditLens, HACo-Det, DAMASHA, and CUDRT address important aspects of AI editing and attribution, but none of them provides successive versions of the same document as part of the benchmark (Table 1). APT-Eval generates each polished variant independently from the original human text, HACo-Det revises a document over multiple turns but evaluates only the final coauthored text, EditLens focuses on documents edited in a single pass, and CUDRT constructs a separate dataset for each operation. We have added CUDRT to the Related Work (Section 2), and we show below how the trajectories are used in our analyses (W1.2 and W1.3).

W1.2: The cumulative trajectory is therefore the only distinctive element, yet the paper tests its value only through a single ablation, which in fact shows a similar v4 drop under independent editing.

Thanks for the comment. We would like to clarify that the cumulative trajectory is not a separate element of OpAI-Bench, but the setting that links its other components. Unlike the benchmarks compared in Table 1, OpAI-Bench provides successive versions of the same document, each building on the previous one, and combines controlled AI coverage, cumulative editing, diverse edit operations, and multi-granularity annotations. Each version records its AI coverage, editing operation, and provenance, so the effects of these factors on detection can be followed along one revision history rather than measured on isolated edits. The value of this design is examined in three ways: the cumulative-versus-independent ablation, the edit-magnitude analysis, and two new trajectory-level analyses (W1.3).

Cumulative-versus-independent ablation. The independent setting preserves the same version schedule while removing accumulated re-editing (Section 5.2 and Appendix F.3). Since compression is applied at v4 in both settings, a drop around v4 is expected in both. The drop remains under independent editing, with magnitude varying across detectors and generators, which shows that the non-monotonic pattern does not depend on accumulated re-editing alone. Revision history matters elsewhere: previously AI-edited sentences are detected more often than newly edited ones (Q1.3), and cumulative editing raises sentence-level balanced accuracy for all three LLM detectors (+2.9 to +5.1 pp, source-paired and adjusted for length and AI-word coverage, 95% CIs excluding zero). The trajectory-level analyses in W1.3 further show the v4 drop within individual documents.

Edit-magnitude analysis. Each version is compared with both its preceding version and the original human source (Section 5.1 and Appendix E.4). The final version (v8) has the smallest stepwise change but the highest sentence-level recall, indicating that detectability depends on accumulated revision history and not only on the change introduced at a single step.

W1.3: No task makes use of the trajectory itself, such as detecting changes between consecutive versions or identifying the version at which AI involvement begins.

Following the reviewer's suggestions, we have added two analyses that use the trajectory itself (Section 5.2 and Appendix E.6).

For detection delay, we track when each document is first flagged as AI-edited along its revision trajectory. Although AI editing begins at v1, Table R1 shows that only 1.4–3.8% of trajectories are flagged at this version. Detection increases across subsequent revisions, but even by v8, only 19.9–74.9% have been flagged at least once, depending on the detector. For example, DeskLib detects 2.5% by v1, 22.2% by v4, and 58.0% by v8. This analysis shows how long AI involvement can remain undetected across successive revisions of the same document, rather than only measuring detection performance at individual stages.

AuthorsOpenReview ↗

Response to Reviewer e5tR [2/7]

Table R1. Cumulative detection rates (%) across revisions. Each value is the percentage of trajectories detected at least once by that version, among trajectories not flagged at v0. Results cover four domains and the three primary generators, using 5%-FPR thresholds calibrated per detector, domain, and generator.

DetectorBy v1By v2By v3By v4By v5By v6By v7By v8
DeskLib2.58.819.822.238.248.453.858.0
GigaCheck2.813.635.141.956.969.072.774.9
E5-Small1.42.95.66.815.619.623.526.3
OOD-LLM-Detect3.88.517.821.128.232.135.137.8
RADAR1.94.27.18.313.216.118.519.9

We further analyze score changes between consecutive versions of the same document. As shown in Table R2, all five detectors fall below 0.5 (0.24–0.48) at v3→v4, even though the average share of AI-edited sentences increases from 42% to 51%. This is the only transition where all five detectors fall below 0.5. At every other transition, most detectors score the later version higher. Within the same document, more AI editing therefore does not always lead to a higher detector score.

Table R2. Consecutive-version ordering of detector AI scores. Each value measures how often the later version receives a higher AI score than the preceding version, with ties counted as half. Results cover four domains and four generators.

Detectorv0→v1v1→v2v2→v3v3→v4v4→v5v5→v6v6→v7v7→v8
DeskLib0.780.650.750.280.870.730.560.83
GigaCheck0.580.630.710.480.710.760.480.59
E5-Small0.730.550.660.260.800.580.560.74
OOD-LLM-Detect0.630.550.640.350.810.610.620.63
RADAR0.630.510.630.240.740.440.460.54

Together with the existing ablation, these analyses demonstrate the value of OpAI-Bench's cumulative trajectories for studying detection delay and score changes between consecutive revisions, beyond evaluating individual document versions.

W1.4: The token- and span-level labels are also projected from whole rewritten sentences, so they add little beyond sentence-level provenance.

We clarify that OpAI-Bench's token- and span-level annotations capture AI editing provenance rather than the exact words or characters changed during rewriting (Appendix B.3). This lets us evaluate whether detectors can identify AI-edited text, including small revisions that leave much of the original human writing unchanged, which prior work has shown to be difficult to detect (Saha and Feizi, 2025). Although these annotations are derived from sentence-level editing decisions, they support evaluation at the output granularity of token- and span-level detectors, without first aggregating their predictions to sentences, allowing us to examine how accurately these models localize AI-edited regions within documents.

To examine whether edit intensity changes these conclusions, we additionally evaluated token- and span-level detectors with graded labels based on edit magnitude and rewrite count (Q3.1 and Appendix E.8). Recall increases with rewrite count and generally with edit magnitude, revealing differences in localization difficulty among regions with the same binary label, while the trends across versions, including the drop at v4, remain consistent with the binary evaluation.

W2.1:Insufficiently justified core design. The entire benchmark rests on a fixed nine-version schedule, but the paper offers only a brief rationale for it.

Thanks for raising this concern. We clarify that the benchmark is designed to model progressive AI-assisted writing, where different parts of a document are revised over multiple rounds and previously edited content can be revisited. As described in Sections 3.1–3.2, our design combines gradually increasing AI coverage, diverse editing operations, and cumulative revisions, with each version building on the preceding one. Each intermediate version is a valid stopping point, so the benchmark evaluates detection at different levels of AI involvement without assuming that real workflows reach full AI editing, and the fixed schedule keeps comparisons consistent across documents, domains, and generators.

Each component of the schedule is also tested through controlled ablations of AI coverage, editing operations, and cumulative versus independent editing (Section 5.2 and Appendix F). We have further added an ablation on the position of compression (W2.2; Table 6 and Appendix F.5) and per-version AUROC (W2.4; Table 4 and Appendix E.7).

AuthorsOpenReview ↗

Response to Reviewer e5tR [3/7]

W2.2: The number of versions, the order of operations, and the position of each operation in the schedule are never ablated. This matters because the headline “critical v4 region” coincides with the only compression step.

As described in Section 3.1, nine versions balance coverage resolution with construction cost, with one human source (v0), seven intermediate mixed-authorship checkpoints (v1–v7), and one fully AI-edited endpoint (v8). Regarding the order of operations, the five operations represent different revision intents. Polishing, paraphrasing, and style rewriting are repeated at different coverage levels, while compression and expansion are placed in the intermediate region as contrasting deletion and addition operations (Section 3.1).

Following the reviewer's suggestion in Q2, we have added a compression-position ablation to test whether the drop at v4 moves with the compression step (Section 5.2, Table 6, and Appendix F.5). Compression is moved to v2 (Early) or v6 (Late) by swapping it with the operation originally applied at that version, while the coverage schedule, sentence selection, and cumulative construction remain unchanged. At every matched version, GPT-5.4 and DeskLib perform worst under the schedule that applies compression at that version (Table R5). For example, moving compression to v6 reduces the F1-AI of GPT-5.4 from 88.3% at v5 to 45.3% at v6, compared with 77.8% at v6 under the original schedule. The degradation therefore moves with the compression step, confirming that compression contributes to the drop at v4 in the main schedule. At the same time, performance also varies at versions without compression (Q2), consistent with our main finding that detectability depends on editing operations and cumulative revision history as well as AI coverage.

W2.3: The paper’s own fixed-coverage ablation suggests that this is an operation effect, possibly confounded by the shorter length of compressed sentences, and not a property of intermediate coverage.

Thanks for raising this point. Our results indicate that both factors play a role, in different ways. AI coverage determines the overall level of detectability, which remains low across the early and intermediate versions (e.g., per-version AUROC of 0.51–0.69 at v1–v3 for the five detectors with signal; Table 4). The specific drop at v4, however, follows the compression operation: when compression is moved to v2 or v6, the degradation appears at that version instead (W2.2; Table 6 and Appendix F.5). Accordingly, the revised paper describes the degradation around v4 as associated with compression at intermediate coverage rather than with coverage alone (Section 5). Regarding the possible length confound, the operation effect remains after controlling for length:

  1. Sentence length. In Ablation 1, comparing compressed sentences with paraphrased sentences of exactly the same word count (matches found for 99.8% of compressed sentences), the three LLM-based sentence detectors still detect compressed sentences 22–36 pp less often.
  2. Matched length and coverage. We compared compression and paraphrasing on the same source documents, retaining only pairs within ±10% document length and ±5 pp AI-word coverage (Gemini-2.5-Flash, 62 matched pairs; detection rate at 5% FPR). Compression remains harder to detect for DeskLib (−10.48 pp), GigaCheck (−13.98 pp), and OOD-LLM-Detect (−8.06 pp), with 95% confidence intervals excluding zero.
  3. Fixed coverage. At the same target sentence coverage, compression is harder to detect than paraphrasing or expansion (Appendix F.2).
  4. Edit magnitude. From v3 to v4, AI coverage increases from 40% to 50%, while cumulative normalized Levenshtein distance remains nearly unchanged (0.414 vs. 0.416) and sentence-level recall decreases from 0.248 to 0.220. The stepwise edit distance at v4 (0.308) is substantially larger than at the polishing stages (0.112 at v1 and 0.045 at v8), so the drop occurs despite substantial textual revision (Table 12, Appendix E.4).

W2.4: The claim that intermediate versions are “harder than both endpoints” also requires a prevalence-independent metric. AUROC is reported only at the document level with v1 to v8 pooled, and F1-AI is undefined at v0, so per-version AUROC or balanced accuracy is needed to support this comparison.

To address the reviewer's concern, we have added per-version document-level AUROC to the main text (Table 4 in Section 5; full results in Appendix E.7, Table 17). Each version is compared with the human v0 documents, and AUROC is averaged over the four domains and the three primary generators.

Reviewer_sg2mOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

The paper introduces OpAI-Bench for evaluating AI-text detection during cumulative editing of human-written documents. A deterministic, nested sentence selection expands each source into nine versions, combining increasing sentence coverage with polishing, paraphrasing, style rewriting, compression, and expansion. The primary subset contains 15,722 source documents, 31,088 generator-specific trajectories, and 279,792 versioned samples across four domains and three generators; Qwen3-8B supplies a held-out generator evaluation. The benchmark labels AI-revised regions at document, sentence, word, and character-span resolutions. Experiments compare existing detectors, prompted LLMs, and adapted models. Controlled analyses vary operation and coverage and compare cumulative with independent editing. Results suggest that detection depends on operation, domain, and revision history, with compression often producing a local performance drop. The main contribution is the trajectory benchmark and its diagnostic evaluation, rather than a new detector.

Critical strengths
  1. A useful and substantial trajectory resource. OpAI-Bench preserves nine cumulative versions over four domains, with deterministic sentence selection and source-grouped splits (Secs. 3.2 and 4.2). This makes revision history inspectable and supports matched comparisons that static final-output datasets cannot directly provide. The scale and explicit provenance make this the strongest reason to consider acceptance.

  2. The analysis goes beyond the scheduled trajectory. Section 5.2 and Appendix E vary coverage within operations, compare operations at fixed coverage, and contrast independent with cumulative edits, including a second editing generator. Macro-F1, FNR, and document AUROC further qualify the raw accuracy/F1 trends. These controls support a useful, appropriately detector-dependent picture of detection failures.

Critical weaknesses
  1. The supplied implementation does not yet substantiate the reported evaluation. GenAI-Sentence training saves unmerged LoRA parameters, but its inference loader explicitly drops the adapter tensors. Its prediction mapper also assigns successive subword predictions directly to whitespace words and truncates the list, which shifts labels when words contain multiple subwords. A synthetic check reproduces that alignment failure. These issues could affect the sentence-level comparisons and adaptation claims. Separately, eval.py computes only aggregate document metrics; the supplied GPT wrapper uses GPT-5.2 and a single document label, whereas Appendix F.2 specifies GPT-5.4 with per-sentence arrays. These may be packaging discrepancies, but the actual table-producing scripts, checkpoints, and corrected output checks are needed before I can trust the benchmark conclusions. This is the main reason for my recommendation.

  2. The operation/history findings need stronger quantitative qualification. Fixed sentence coverage is a useful control, but compression and expansion deliberately impose different length ranges, changing sentence length and realized word coverage. The current results do not separate those effects from other operation-specific signals. The independent-versus-cumulative comparisons also lack paired effect estimates, sample counts, and uncertainty. Macro-F1/FNR and pooled document AUROC are helpful, but they do not fully resolve these comparisons. Reporting realized coverage and length-stratified effects, with uncertainty clustered by original source, would clarify how much of the claimed diagnostic insight survives these controls. This matters more than adding further detectors.

Questions for authors
  1. Which exact code and checkpoints produced the GenAI-Sentence results? Please explain whether the LoRA adapters were merged or restored during inference, and how subword predictions were aligned to benchmark words and sentences. The supplied loader discards the LoRA tensors, and a two-word synthetic example exposes a subword-to-word alignment error. Corrected or alternative code with before/after results would materially affect my confidence in the sentence-level and fine-tuning claims.

  2. Can you provide the actual table-producing evaluation path? In particular, please reconcile Appendix F.2's GPT-5.4 per-sentence classifier with the supplied GPT-5.2 document classifier, and provide the sentence/word/span aggregation scripts, span matching or rasterization rule, truncation policy, model/checkpoint identifiers, and prediction manifests. Please also identify the construction/validation scripts promised in the reproducibility statement; the archive mainly provides detector infrastructure. A reproducible path to representative main and ablation results could resolve much of my concern.

  3. How large are the operation and history effects after accounting for length and realized coverage? Please report ablation sample counts, realized sentence/word coverage, length distributions, paired source-level differences, and uncertainty. Length-stratified comparisons and document AUROC or recall at a fixed validation-calibrated FPR for each v0-versus-vi comparison would help determine whether the conclusions hold beyond threshold and prevalence effects. The existing Macro-F1/FNR and two-generator ablations are acknowledged.

  4. What was actually validated during dataset construction? Please quantify the manual audit sample and agreement or pass rates for semantic preservation, single-sentence validity, operation adherence, and provenance projection, including generator/domain breakdowns and rejection/retry counts. The paper states that automatic validation and manual verification were used, but gives no corresponding audit statistics. This would strengthen confidence in the benchmark as a reusable resource.

10 comments
AuthorsOpenReview ↗

Response to Reviewer sg2m [1/8]

We thank the reviewer for the careful and detailed review and for recognizing OpAI-Bench as a useful and substantial trajectory resource with explicit provenance, as well as the value of our controlled analyses. We have uploaded a revised version to accommodate all your suggestions. Below, we further provide detailed clarifications for each of your questions:

W1.1: The supplied implementation does not yet substantiate the reported evaluation. GenAI-Sentence training saves unmerged LoRA parameters, but its inference loader explicitly drops the adapter tensors. Its prediction mapper also assigns successive subword predictions directly to whitespace words and truncates the list, which shifts labels when words contain multiple subwords. A synthetic check reproduces that alignment failure. These issues could affect the sentence-level comparisons and adaptation claims.

Thanks for carefully examining our implementation. We clarify that the experiments reported in the paper were conducted using separate training and inference scripts for each fine-tuned detector. After completing the experiments, we developed a unified interface to improve reproducibility and make the implementations easier to reuse. However, the initial supplementary material included an earlier version of this unified interface rather than the original scripts used to produce the reported fine-tuned results, and some of its wrappers retained settings from preliminary experiments. To address this, we have updated the supplementary material to include the original detector-specific scripts, trained model checkpoints, saved predictions, and evaluation scripts used to compute the reported results.

Regarding LoRA adapters, the fine-tuned GenAI-Sentence results were produced using evaluation/infer_genai_sentence.py. This script loads the trained model together with its saved LoRA adapters using PEFT, rather than discarding or merging them. We verified this by running inference with the released checkpoint and confirming that the resulting predictions match those saved during the original experiments. This confirms that the reported fine-tuned results were obtained with the trained adapters correctly loaded.

Regarding subword alignment, the zero-shot GenAI-Sentence checkpoint was reproduced using the authors' official training code on M4GT-Bench Subtask C, since pretrained weights were not publicly available. In the original implementation (MixedTextDataset.__getitem__), the label of word i is assigned to subword position i, and the label list is truncated to the maximum length. Our zero-shot inference follows the same convention to remain consistent with how that checkpoint was trained. The reviewer's synthetic check assumes conventional word-to-subword alignment, which differs from the labeling convention used to train this checkpoint. Importantly, our fine-tuned GenAI-Sentence model uses explicit word-to-subword alignment through word_ids() in both training and inference, assigning each word the prediction of its first subword token. Therefore, the positional mapping identified in the zero-shot wrapper is not used in the fine-tuned evaluation and does not affect the reported adaptation results.

W1.2: Separately, eval.py computes only aggregate document metrics; the supplied GPT wrapper uses GPT-5.2 and a single document label, whereas Appendix F.2 specifies GPT-5.4 with per-sentence arrays. These may be packaging discrepancies, but the actual table-producing scripts, checkpoints, and corrected output checks are needed before I can trust the benchmark conclusions. This is the main reason for my recommendation.

We would like to clarify the evaluation path. The updated supplementary material includes the saved predictions, the model checkpoints, and the scripts that produce the reported tables. evaluation/aggregate.py and evaluation/aggregate_finetuned.py compute the evaluation metrics from the saved predictions, and evaluation/make_tables.py builds Tables 3 and 22–25 (Tables 3 and 10–13 in the original submission) from these metrics and verifies each result against the reported values. The corresponding commands are provided in REPRODUCE.md.

Regarding the GPT wrapper, the reported LLM-as-detector results were obtained using GPT-5.4, with per-sentence labels and confidence scores, as specified in Appendix G.2 (Appendix F.2 in the original submission). The GPT-5.2 wrapper in the initial supplementary material was from an earlier experiment, was not used to produce the reported results, and has now been replaced. Gemini 3 Flash and Claude Haiku 4.5 were also evaluated using the same per-sentence prompting protocol.

AuthorsOpenReview ↗

Response to Reviewer sg2m [2/8]

W2.1: The operation/history findings need stronger quantitative qualification. Fixed sentence coverage is a useful control, but compression and expansion deliberately impose different length ranges, changing sentence length and realized word coverage. The current results do not separate those effects from other operation-specific signals.

Thanks for raising this concern. As discussed in Section 5.2 and Appendix F, our existing ablations examine AI coverage and editing operations separately. In particular, Ablation 2 compares compression, paraphrasing, and expansion at fixed target sentence coverage (25%, 50%, and 75%). To further distinguish operation-specific detection differences from changes in text length and realized AI-word coverage, we conducted additional source-paired, matched, and regression-adjusted analyses using the Gemini-2.5-Flash test subset.

We first examined realized AI coverage and edited-sentence length across operations (Table R1). Despite nearly identical sentence coverage (51.4%), compression produces shorter edited sentences and lower AI-word coverage than paraphrasing and expansion.

Table R1. Realized AI coverage and edited-sentence length at 50% target sentence coverage (Gemini-2.5-Flash, all splits). AI-sentence and AI-word coverage denote the percentages of sentences and words labeled as AI-edited, respectively. Edited-sentence length is the median number of words in AI-edited sentences.

OperationAI-sentence coverageAI-word coverageMedian edited-sentence length (words)
Compression51.4%43.5%15
Paraphrasing51.4%51.2%20
Expansion51.4%60.6%29

We then compared compression and paraphrasing using source-paired detection rates, matching, and regression adjustment (Table R2). After matching, compression remains harder to detect for DeskLib (−10.48 pp), GigaCheck (−13.98 pp), and OOD-LLM-Detect (−8.06 pp), with 95% confidence intervals excluding zero. The difference also persists for GigaCheck after regression adjustment (−11.89 pp; 95% CI [−20.41, −3.24]), and the adjusted estimates for the other detectors remain negative.

Table R2. Compression-minus-paraphrase detection-rate differences (pp; 95% source-bootstrap CIs). Detection rate is the percentage of AI-edited documents detected at 5% FPR. Raw denotes the paired difference without additional controls; Matched retains source pairs with similar document length (±10%) and AI-word coverage (±5 pp); Adjusted controls for log document length and AI-word coverage using source-by-coverage fixed effects. Results cover 25%, 50%, and 75% target coverage (Gemini-2.5-Flash test split; 120 paired sources, 62 matched). Thresholds are cross-fitted on human v0 documents. Negative values indicate lower detection under compression.

DetectorRawMatchedAdjusted
DeskLib−16.11 [−21.11, −11.11]−10.48 [−18.57, −3.23]−3.71 [−11.78, 3.90]
E5-Small−7.22 [−11.39, −3.06]−4.84 [−11.29, 0.00]−4.22 [−9.67, 3.20]
GigaCheck−19.17 [−24.72, −13.61]−13.98 [−23.66, −6.45]−11.89 [−20.41, −3.24]
OOD-LLM-Detect−5.56 [−9.17, −2.22]−8.06 [−16.13, −1.61]−6.81 [−15.13, 2.63]

These findings provide additional evidence that the lower detectability of compression is not explained entirely by differences in length and realized AI-word coverage.

AuthorsOpenReview ↗

Response to Reviewer sg2m [3/8]

W2.2: The independent-versus-cumulative comparisons also lack paired effect estimates, sample counts, and uncertainty.

Thanks for raising this concern. As discussed in Section 5.2 and Appendix F.3, Ablation 3 compares cumulative and independent editing under the same operation and coverage schedule. To further quantify these differences, we conducted an additional source-paired analysis using the Gemini-2.5-Flash ablation, comparing both editing settings across revision stages (v1–v8). We report unadjusted and length- and coverage-adjusted performance differences, together with 95% confidence intervals (Table R3).

Table R3. Paired cumulative-minus-independent performance differences (pp; 95% source-bootstrap CIs) across v1–v8 (Gemini-2.5-Flash test split; 115 paired sources). Document-level performance is measured by detection rate at 5% FPR, with thresholds cross-fitted on human v0 documents; sentence-level performance uses balanced accuracy. Unadjusted differences average paired source-level estimates. Adjusted differences control for log document length and realized AI-word coverage using source-by-version fixed effects, additionally controlling for sentence length at the sentence level. Positive values indicate higher performance under cumulative editing.

LevelDetectorUnadjusted Δ (pp)Adjusted Δ (pp)
DocumentDeskLib+4.8 [1.9, 8.2]+2.5 [−0.3, 5.7]
E5-Small+5.3 [2.2, 8.3]+2.1 [−0.7, 5.4]
GigaCheck+4.3 [−1.6, 10.3]+0.9 [−6.2, 8.2]
OOD-LLM-Detect+0.8 [−1.4, 2.8]+0.5 [−1.6, 2.5]
RADAR+2.6 [0.5, 5.0]+1.8 [−0.1, 3.6]
SentenceGPT-5.4+9.6 [8.3, 10.8]+5.1 [4.0, 6.1]
Gemini 3 Flash+5.7 [4.1, 7.3]+2.9 [1.6, 4.2]
Claude Haiku 4.5+6.0 [4.6, 7.3]+4.2 [3.0, 5.3]

As shown in Table R3, cumulative editing yields higher detection rates for several document-level detectors before adjustment, including DeskLib (+4.8 pp) and E5-Small (+5.3 pp). After adjusting for document length and realized AI-word coverage, these differences become smaller, and their confidence intervals include zero.

At the sentence level, all three LLM-based detectors retain positive differences after adjustment, with cumulative editing yielding higher balanced accuracy for GPT-5.4 (+5.1 pp), Gemini 3 Flash (+2.9 pp), and Claude Haiku 4.5 (+4.2 pp). Their 95% confidence intervals exclude zero, indicating that the differences persist after accounting for the measured length and coverage factors.

These findings provide further quantitative evidence that cumulative revision history influences detection performance, particularly at the sentence level, even after accounting for differences in text length and realized AI-word coverage. The v4 decline also occurs under independent editing (Appendix F.3), with magnitude varying across detectors and generators; for Gemini-2.5-Flash edits it is comparable or larger for most detectors (e.g., DeskLib AUROC at v4 minus the mean of v3 and v5: −0.204 independent vs. −0.126 cumulative). The decline therefore does not depend on accumulated re-editing alone, whereas the effect of revision history appears mainly in sentence-level detection.

W2.3: Macro-F1/FNR and pooled document AUROC are helpful, but they do not fully resolve these comparisons. Reporting realized coverage and length-stratified effects, with uncertainty clustered by original source, would clarify how much of the claimed diagnostic insight survives these controls. This matters more than adding further detectors.

Thanks for this comment. Following your suggestion, we have addressed these concerns through the additional analyses reported in our responses to W2.1, W2.2 and Q3. Table R1 reports realized sentence- and word-level coverage and edited-sentence length, and Table R4 (Q3) adds document-length distributions. Length is controlled in Table R2 by matching source pairs within ±10% document length and by regression adjustment for log document length and AI-word coverage. Table R3 provides paired cumulative-versus-independent estimates with 95% confidence intervals, and all confidence intervals are obtained by bootstrap resampling of original source documents, accounting for clustering by source. Beyond Macro-F1, FNR and pooled AUROC, Q3 further reports per-version recall at a fixed 5% FPR and per-version AUROC (Table R5). Together, these analyses provide a more direct assessment of the factors underlying the observed detection patterns.

Reviewer_mdPsOpenReview ↗
Rating
4(+1)
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper introduces OpAI-Bench, a new AI-generated text detection benchmark for progressive human–AI revision. Unlike existing benchmarks, OpAI-Bench explicitly constructs and preserves intermediate revision states across multiple AI editing operations applied to human-written text.

The benchmark supports detection at the document, sentence, token, and span levels, covering nine revision versions per sample, five AI editing operations, and four domains. Experimental results show that detection performance varies with editing intensity, domain, and operation, with intermediate revisions being the hardest to detect.

Critical strengths
  • Strong motivation to move beyond purely human- or AI-written documents.
  • One of the first benchmarks to systematically capture progressive AI editing across multiple intermediate revision stages.
  • Good coverage of editing operations and revision stages.
  • Comprehensive analysis across revision stages and domains, providing new insights beyond static detection benchmarks.
Critical weaknesses
  • Editing procedure and realism: I understand the motivation for shuffling sentences to avoid positional bias. However, wouldn't an autoregressive model typically revise a document from beginning to end, conditioning later edits on previously edited sentences? This seems different from your setup, where, if I understand Section 3 correctly, sentences are selectively edited in a shuffled order. For example, you might edit sentence 2 in the first iteration and sentence 1 in the second. Under a more conventional left-to-right editing process, however, sentence 2 would likely be revised conditioned on the already edited sentence 1. This could lead to different, potentially more realistic editing behaviour than in your current setup. Could you clarify how your procedure accounts for this?

  • Detector selection: The benchmark would benefit from including more recent and competitive detectors. For document-level zero-shot detection, the evaluation includes FDGPT and RADAR, both dating back to 2023. I would strongly recommend evaluating more recent approaches, such as RepreGuard (Chen et al., 2025) or IRM (Lie et al., 2025).

    • In addition, I would strongly suggest evaluating methods that explicitly measure the degree of AI editing, as this would provide a particularly natural evaluation for your benchmark. Relevant approaches include EditLens and MGT probes, both of which capture AI editing strength.
  • Preservation of factual content (Line 238): You state that the prompts instruct the model to preserve names, numbers, and other factual details. However, how do we know that the model consistently follows these instructions and does not inadvertently alter factual information? This issue could become particularly pronounced in your cumulative editing setup, where errors may propagate across revision stages. Have you assessed factual consistency across revisions? If not, could you provide evidence that this is not a significant issue?

  • Related work: Please consider updating the reference to DetectRL with DetectRL-X (Wu et al., 2026). I would also recommend discussing TSM-Bench (Quaremba et al., 2025), which similarly considers various AI text editing operations.

Minor Comments

  • Citation formatting: Incorrect citation style in Line 45 and Lines 196 onward.

References

Chen, Xin, et al. "Repreguard: Detecting llm-generated text by revealing hidden representation patterns." Transactions of the Association for Computational Linguistics 13 (2025): 1812-1831.

Liu, Runheng, et al. "Zero-shot detection of llm-generated text via implicit reward model." Advances in Neural Information Processing Systems 38 (2026): 167683-167709.

Quaremba, Gerrit, et al. "Linear Probing Provides Robust and Efficient Detection of Machine-Generated Text." arXiv preprint arXiv:2608.24780 (2026).

Quaremba, Gerrit, et al. “TSM-Bench: Detecting LLM-Generated Text in Real-World Wikipedia Editing Practices.” The Fourteenth International Conference on Learning Representations, 2026, https://openreview.net/forum?id=zimuL7ZmIi.

Thai, Katherine, et al. "Editlens: Quantifying the extent of ai editing in text." International Conference on Learning Representations. Vol. 2026. 2026.

Wu, Junchao, et al. "DetectRL-X: Towards Reliable Multilingual and Real-World LLM-Generated Text Detection." Proceedings of the 64th Annual Meeting of the Association for Computational Linguistics (Volume 1: Long Papers). 2026.

Questions for authors

see above

5 comments
AuthorsOpenReview ↗

Response to Reviewer mdPs [1/3]

We thank the reviewer for the constructive feedback and encouraging assessment of OpAI-Bench, which are definitely helpful for us to improve the quality of the paper. We have uploaded a revised version to accommodate all your suggestions. Below, we further address each of your concerns raised in the review.

W1: Editing procedure and realism: I understand the motivation for shuffling sentences to avoid positional bias. However, wouldn't an autoregressive model typically revise a document from beginning to end, conditioning later edits on previously edited sentences? This seems different from your setup, where, if I understand Section 3 correctly, sentences are selectively edited in a shuffled order. For example, you might edit sentence 2 in the first iteration and sentence 1 in the second. Under a more conventional left-to-right editing process, however, sentence 2 would likely be revised conditioned on the already edited sentence 1. This could lead to different, potentially more realistic editing behaviour than in your current setup. Could you clarify how your procedure accounts for this?

Thanks for the comment. We clarify that shuffled sentence selection does not imply context-independent rewriting. The shuffle determines which sentences are selected for editing, not their order within the document. At each stage, selected sentences are revised using their surrounding paragraph as context, including edits accumulated from previous stages. Thus, later revisions take previously edited content into account.

Moreover, editing is cumulative: once selected, a sentence remains in the editing set and is passed for rewriting again at subsequent stages. In the reviewer's example, sentence 2 is initially edited at v1, while sentence 1 is still human-written. When sentence 1 is subsequently selected at v2, sentence 2 remains in the cumulative editing set, allowing it to incorporate the revised sentence 1 as part of its context in later stages rather than permanently retaining its earlier wording.

Regarding realism, our benchmark is designed to reflect progressive AI-assisted writing, where users may revise different parts of a document over multiple rounds. These revisions are not independent: each stage builds on the preceding version, allowing previously edited sentences to be revisited as their surrounding context evolves. Thus, our procedure models a plausible form of localized human–AI collaboration while preserving the cumulative revision history central to our benchmark.

This procedure is described in Section 3.2 and Figure 1.

AuthorsOpenReview ↗

Response to Reviewer mdPs [2/3]

W2: Detector selection: The benchmark would benefit from including more recent and competitive detectors. For document-level zero-shot detection, the evaluation includes FDGPT and RADAR, both dating back to 2023. I would strongly recommend evaluating more recent approaches, such as RepreGuard (Chen et al., 2025) or IRM (Lie et al., 2025). In addition, I would strongly suggest evaluating methods that explicitly measure the degree of AI editing, as this would provide a particularly natural evaluation for your benchmark. Relevant approaches include EditLens and MGT probes, both of which capture AI editing strength.

Thanks for the suggestion. Our original evaluation already includes recent methods such as OOD-LLM-Detect (2025) and GigaCheck (2024), alongside established detectors. To further strengthen the benchmark, we additionally evaluated RepreGuard (Chen et al., 2025) and EditLens (Thai et al., 2025) across all nine revision stages and four domains, averaged over the three primary generators.

As shown in Table R1, the performance of both detectors varies across domains and revision stages. At v1, RepreGuard detects fewer than 1% of AI-edited essays and news articles, while EditLens detects fewer than 8% of essays, reports, and news articles. Performance improves at higher AI coverage, with EditLens reaching 100.0% F1-AI on essays at v8 and RepreGuard reaching 74.9% on the same domain. However, RepreGuard's F1-AI declines from v3 to v4 across all four domains, consistent with the intermediate-stage detection difficulties observed in our original evaluation.

Table R1. Document-level accuracy / F1-AI (%) across revision versions (mean over the three primary generators).

DetectorVer.EssaysReportsNewsAbstracts
RepreGuardv099.3 / –68.0 / –99.7 / –52.8 / –
v10.8 / 1.732.9 / 49.50.3 / 0.653.3 / 69.5
v21.8 / 3.530.8 / 47.00.7 / 1.456.8 / 72.4
v37.0 / 12.639.8 / 56.72.6 / 4.970.0 / 82.2
v42.9 / 5.725.9 / 41.10.9 / 1.757.6 / 73.0
v532.6 / 38.248.5 / 62.515.3 / 21.879.2 / 87.9
v653.1 / 64.157.5 / 70.426.6 / 31.587.8 / 93.3
v749.0 / 59.847.7 / 60.622.1 / 28.083.4 / 90.6
v863.3 / 74.954.6 / 67.925.2 / 30.885.7 / 92.1
EditLensv098.9 / –94.2 / –97.9 / –56.1 / –
v13.1 / 5.97.7 / 14.47.4 / 13.452.3 / 68.6
v214.2 / 24.019.6 / 32.124.6 / 34.966.2 / 79.4
v338.0 / 51.830.8 / 42.942.4 / 51.477.3 / 86.7
v448.3 / 63.237.7 / 52.740.1 / 50.577.7 / 87.3
v573.4 / 81.650.4 / 59.351.3 / 59.984.9 / 91.4
v695.0 / 97.460.5 / 69.669.6 / 78.896.4 / 98.1
v798.9 / 99.571.7 / 79.171.8 / 80.096.7 / 98.3
v8100.0 / 100.071.7 / 79.376.2 / 84.198.6 / 99.3

Beyond binary detection, we also evaluated EditLens's continuous editing-degree scores (Table R2). These generally increase with target AI coverage, for example from 0.010 at v0 to 0.455 at v8 on essays. However, they exhibit non-monotonic changes and substantial domain variation. The mean score on news decreases from 0.094 at v3 to 0.081 at v4 despite increasing coverage, and the score on abstracts decreases from 0.333 at v6 to 0.313 at v7. Even at full target coverage (v8), scores remain relatively low for reports (0.189) and news (0.210). These results extend OpAI-Bench's evaluation to editing-degree estimation and highlight the challenges of tracking AI involvement consistently throughout progressive revision.

Table R2. EditLens editing-degree score (0–1) across revision versions (mean over the three primary generators).

Domainv0 (0%)v1 (15%)v2 (25%)v3 (40%)v4 (50%)v5 (60%)v6 (75%)v7 (90%)v8 (100%)
Essays0.0100.0150.0370.0870.0990.2210.3620.4040.455
Reports0.0260.0290.0460.0660.0720.1330.1630.1910.189
News0.0170.0240.0530.0940.0810.1450.1950.1990.210
Abstracts0.0790.0910.1230.1710.1550.2310.3330.3130.341

We have incorporated these additional experiments into the revised paper (Section 4 and Appendix E.5).

AuthorsOpenReview ↗

Response to Reviewer mdPs [3/3]

W3: Preservation of factual content (Line 238): You state that the prompts instruct the model to preserve names, numbers, and other factual details. However, how do we know that the model consistently follows these instructions and does not inadvertently alter factual information? This issue could become particularly pronounced in your cumulative editing setup, where errors may propagate across revision stages. Have you assessed factual consistency across revisions? If not, could you provide evidence that this is not a significant issue?

Thanks for raising this concern. We clarify that our editing prompts explicitly require factual preservation (Section 3.2, Appendix H). To verify this under cumulative revision, we conducted two complementary evaluations: an LLM-based factual-consistency assessment and a full-data lexical audit. First, we assessed 27,309 AI-edited sentence instances from 300 revision trajectories, stratified across domains, generators, and dataset splits. Using GPT-6.1 Sol as an independent judge, we compared revisions against both their preceding versions (v_{t-1}→v_t) and the original documents (v_0→v_t), identifying altered facts, unsupported additions, and factual omissions while excluding stylistic or semantically equivalent changes.

Table R3. Factual-consistency issue rates (%) across revision stages. Overall reports pooled stepwise rates.

Evaluationv1v2v3v4v5v6v7v8Overall
Altered facts (stepwise)0.690.770.290.800.360.360.340.140.38
Any issue, incl. additions/omissions (stepwise)1.381.721.062.553.600.870.600.221.31
Altered facts vs. v_0 (cumulative)0.691.090.741.271.301.511.621.51—

As shown in Table R3, factual alterations occur in only 0.38% of evaluated sentence edits (1.31% including additions and omissions). The higher rates at v4 and v5 reflect factual omissions during compression (1.4%) and unsupported additions during expansion (3.2%). Cumulative alterations rise to approximately 1.5% but remain relatively stable after v6, with the lowest stepwise rate at v8 (0.14%).

Second, a full-data lexical audit shows that 99.91% of edits introduce no new numerical values, 99.14% of non-compression edits preserve input numbers, and 99.45% introduce no new name-like tokens. These results indicate that factual deviations remain uncommon under cumulative revision. We have incorporated these additional factual-consistency analyses and results into the revised manuscript (Appendix D).

W4: Related work: Please consider updating the reference to DetectRL with DetectRL-X (Wu et al., 2026). I would also recommend discussing TSM-Bench (Quaremba et al., 2025), which similarly considers various AI text editing operations.

We thank the reviewer for these suggestions. We have updated the Related Work section to include DetectRL-X (Wu et al., 2026) and discuss TSM-Bench (Quaremba et al., 2026), clarifying their relationship to OpAI-Bench. While these benchmarks consider realistic detection scenarios and AI editing operations, OpAI-Bench focuses on cumulative human-to-AI revision trajectories, preserving intermediate versions and multi-granularity provenance under controlled AI coverage levels and editing operations.

We also thank the reviewer for pointing out the citation formatting at Line 45 and Lines 196 onward, which has been corrected.

Comments on the paper

2 comments
Area_Chair_9YkDOpenReview ↗

Please review the authors’ responses and join the discussion

Dear Reviewers,

The authors have responded to all reviews. Please read their responses and the other reviewers’ comments, then post a brief follow-up indicating which concerns, if any, remain and whether the responses have changed your assessment. If your concerns have been resolved, a short confirmation would also be helpful.

Thank you for your time and for contributing to the discussion.

Best regards,

Your AC

AuthorsOpenReview ↗

Summary of Our Rebuttal and Key Updates

We sincerely thank all reviewers for their careful reading, constructive feedback, and thoughtful suggestions. We have revised the manuscript to address the comments, adding analyses and evaluations that further support our findings.

We are encouraged by the positive comments from reviewers, including: strong motivation and one of the first benchmarks to capture progressive AI editing across intermediate revision stages [mdPs]; a useful and substantial trajectory resource whose scale and explicit provenance make revision history inspectable [sg2m, e5tR], "the strongest reason to consider acceptance" [sg2m]; good coverage of editing operations and comprehensive analysis across revision stages and domains [mdPs]; controlled analyses giving a useful, detector-dependent picture of detection failures [sg2m]; broad and carefully controlled evaluation across detector families and granularities, with a held-out generator [e5tR]; an actionable finding that compression is harder to detect at matched coverage [e5tR]; and a clear presentation [mdPs, sg2m].

We also thank the reviewers for their constructive suggestions, including those on newer and editing-degree detectors [mdPs]; factual consistency and dataset validation [mdPs, sg2m]; reproducibility, including evaluation scripts, checkpoints, and prediction manifests [sg2m]; operation and revision-history effects after controlling for length and AI coverage [sg2m]; compression-position ablations and per-version prevalence-independent metrics [e5tR]; and graded labels [e5tR]. We have addressed these points in our revised manuscript and responses.

Specifically, we have incorporated the following updates:

  • We have added two trajectory-level analyses, detection delay along each revision trajectory and score changes between consecutive versions of the same document, in Sec. 5.2 and Appendix E.6. [e5tR]
  • We have added a compression-position ablation that moves compression to v2 or v6, showing that the degradation moves with the compression step and supporting our finding that detectability depends not only on AI coverage but also on the edit operation (Sec. 5.2, Tab. 6, and Appendix F.5). [e5tR]
  • We have added per-version document-level AUROC to the main text (Tab. 4) and Appendix E.7, showing that the drop at v4 holds under a prevalence-independent metric. [e5tR, sg2m]
  • We have added a graded-label evaluation of token- and span-level detectors by edit magnitude and number of rewrites in Appendix E.8. [e5tR]
  • We have evaluated two additional detectors, RepreGuard and EditLens, including EditLens editing-degree scores, in Sec. 4 and Appendix E.5. [mdPs]
  • We have added an LLM-based factual-consistency assessment, a full-data lexical audit, provenance-consistency checks, sentence-validity and operation-adherence rates, and retry statistics in Appendix D. [mdPs, sg2m]
  • We have updated the supplementary material with the construction and validation scripts, the original detector-specific scripts, trained checkpoints, saved predictions, and table-producing evaluation scripts, with commands in REPRODUCE.md. [sg2m]
  • We have added CUDRT, DetectRL-X, and TSM-Bench to the Related Work in Sec. 2. [mdPs, e5tR]

All of these revisions have been incorporated into the updated manuscript and supplementary material. Detailed responses to the reviewers' questions and concerns, including additional analyses, are provided in our individual rebuttal responses. We thank the reviewers again for their valuable feedback.

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

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