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Under review as a conference paper at ICLR 2027

Reverse ToBlend: Analyzing Detection Signals under Token-Level Multi-Model Blending

Abstract

Detectors and attribution tools for AI-generated text usually assume one model per passage; token-level blending breaks this by drawing each short continuation from a different model in a pool. What a defender can recover from such text remains open, even with every pool model available: machine generation, blending, or the model behind each word. We study this case with likelihood statistics from every pool model, supervised text classifiers, and 600 new continuations whose generating model is logged at every step. Encouragingly, detection is reliable: a classifier over pool likelihoods reaches AUROC of at least 0.85 in all 36 pool, domain, and generation settings, and a fine-tuned RoBERTa classifier is stronger on one of two pools. Both complement an off-the-shelf detector, RADAR, in all 18 settings where it applies. At the same time, how text was blended is hard to recover: on the logged continuations, blended and single-model text separate with AUROC of at most 0.58, and word attribution reaches 41.3% (25% chance) even with the logged decoding distributions. We examine two four-model pools across three English domains. Detection and source tracing thus appear to be distinct problems: detection alone says little about which models wrote a passage.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
machine-generated text detection, model attribution, multi-model blending, decoding-aware attribution, likelihood and entropy, supervised detection baselines, evaluation methodology

Reviews

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1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_5KLnOpenReview ↗
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Paper summary

This paper presents an empirical study of text generated through token-level blending across multiple LLMs. It introduces a benchmark with generation logs to evaluate detection, blend identification, and token-level attribution. Experiments, over two four-model pools and three domains, show good detection performance, but limited ability to distinguish blended from single-model text or attribute words to their generating models.

Critical strengths

The matched generation setup and detailed source logs help assess whether accurate text detection is accompanied by reliable source attribution.

Critical weaknesses
  1. The paper does not clearly establish what new findings its token-level benchmark adds beyond related multi-LLM authorship research, such as the uncited CollabStory (NAACL Findings 2025).
  2. The findings are based on only two fixed pools of older, small models with full probability access. Their relevance to modern post-trained models and less restrictive access settings remains unverified.
Questions for authors
  1. In Contribution (3), the paper presents 41.3% as a bound on word-level provenance recovery. Does the bound refer to the best observed attribution accuracy, or an upper limit on recoverable provenance? If the former, what new insight does this result provide, and why is it highlighted as a main contribution? If the latter, what evidence supports this interpretation?
  2. Attribution results confound model identity with decoding settings. How much of Llama-2’s higher attribution accuracy comes from its different decoding settings? Does the gap persist when all models use the same setting?
2 comments
AuthorsOpenReview ↗

Response to Reviewer 5KLn

Thank you for noting that the matched setup and source logs let us test whether accurate detection comes with reliable attribution.

Weakness 1: The paper does not clearly establish what new findings its token-level benchmark adds beyond related multi-LLM authorship research, such as the uncited CollabStory (NAACL Findings 2025).

Thank you for pointing to CollabStory [1], which we will cite and discuss. Its stories are written by up to five instruction-tuned LLMs, one sequential part of 180 to 900 words each, for authorship tasks such as single- versus multi-author classification. Our setting differs in granularity (the generator is redrawn for every chunk of one to five NLTK tokens and changes at 74.8% of adjacent word pairs at TL1), in control (the fixed-model arm shares prompts, loop, formatting, decoding, and stopping rule with the blended arm; Section 3.4), and in ground truth (every step's generator is logged, and white-box likelihoods give the per-chunk Bayes rule at TL1, up to NLTK re-spacing). The findings are complementary: CollabStory reports at least 0.8 F1 for single- versus multi-author classification at segment level, whereas at token level with matched pipelines the tested detectors separate blended from single-model text with AUROC of at most 0.58.

Weakness 2: The findings are based on only two fixed pools of older, small models with full probability access.

Full access is the setting most favorable to the defender (Section 1): for attribution, an attributor with less access cannot exceed, in expectation, the Bayes accuracy of the full-access attributor for the same process. For blend specificity, detectors that require no pool likelihoods remain low, at 0.5443 for RoBERTa, 0.5357 for Binoculars, and 0.5179 for Fast-DetectGPT with the outside-pool OLMo-2-7B scorer (Tables 22 and 27), whereas the white-box likelihood-ratio test in our response to Reviewer gvSy separates the arms; detection itself requires no likelihood access (text-only RoBERTa: median TPR 0.975 and 0.953 at a 5% FPR threshold; Table 21). We will add a matched run with an instruction-tuned pool (Llama-3.1-8B-Instruct, Qwen2.5-7B-Instruct, Mistral-7B-Instruct-v0.3, Gemma-2-9B-it), and we will include those experiment results in the camera-ready version. Model scale remains a stated limit (nominal size 7B or less; Section 7); the instruction-tuned pool extends it to 9B, and the Limitations will keep scale as a boundary of the claims.

Question 1: Does the bound refer to the best observed attribution accuracy, or an upper limit on recoverable provenance?

At TL1 it is both, at the chunk level. Because each step's generator is drawn uniformly and independently of the text and of earlier draws, the exact-context attributor is the Bayes rule for this process up to NLTK re-spacing (see our response to Reviewer gvSy), so its chunk accuracy, 40.50% against 25% chance, estimates the upper limit for this pool, these decoding settings, and one-token chunks. The paper's 41.3% is the word-level accuracy of this rule (41.25% [40.65%, 41.84%]) and of the sampling-aware attributor (41.31%); the revision will state the bound at the chunk level and drop TL3 from it. With every pool model, its decoding settings, and the true chunk boundaries known, the optimal rule still misattributes most chunks: provenance is lost in the generation process itself rather than through a weak tool. It is a main contribution because it separates the two problems on the same texts: the frozen reader detects these blends with AUROC 0.9506 (Table 4), yet even the Bayes rule recovers 40.50% of chunks, so a detection alone says little about which models wrote a passage (Section 6).

Question 2: How much of Llama-2’s higher attribution accuracy comes from its different decoding settings? Does the gap persist when all models use the same setting?

Most of it. Llama-2 alone was sampled with its shipped temperature 0.6 and top-p 0.9 (Appendix B). Without the decoding transform it is the hardest member to attribute (31.9%, against 78.8% with it; Table 26), and the net gain from 36.53% to 41.31% comes entirely from Llama-generated words. In the classic pool, whose members share one configuration, the transform leaves accuracy unchanged (38.20% versus 38.19%; Table 28), so we do not expect the gap to persist under matched settings. We will run the advanced pool with matched decoding and include those experiment results in the camera-ready version.

References

[1] Venkatraman, S., Tripto, N. I., & Lee, D. (2025). CollabStory: Multi-LLM collaborative story generation and authorship analysis. In Findings of the Association for Computational Linguistics: NAACL 2025 (pp. 3665–3679). Association for Computational Linguistics. https://doi.org/10.18653/v1/2025.findings-naacl.203

Thanks for the response. For Weakness1, the response addresses my concerns. But for Question1, my main concern about the recovery bound remains unsolved. It is unclear wheather the 40.50% accuracy at TL1 setting is an estimate of the best available accuracy or due to the method’s limitation? This point is important to the Contribution (3). Thus, I keep my original rating.

Reviewer_gvSyOpenReview ↗
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Paper summary

This paper examines whether we can detect which AI model generated specific texts and trace back to its generators. The authors proposes three tasks. 1) Detect AI-generated text, 2) Distinguish blended texts from single models, and 3) Attribute individual words to each models. The results show strong AI vs. human discrimination in the tested settings, but weak performance between blended and fixed-model generation. I would position this work as an empirical analysis with evaluation framework, not a novel detector proposal.

Critical strengths
  1. Separating detection, blend identification, and source attribution is useful. The experiments show why success at detecting generated text should not be treated as evidence that its generators can be identified.
  2. The matched generation experiment is a strong control. Blended and fixed-model text share the same prompts, generation loop, formatting, and stopping procedure, helping isolate model switching from other generation artifacts. The provenance logs provide ground truth for attribution.
  3. The authors include meaningful baselines and report results. RoBERTa outperforms the component reader on the advanced pool, and boundary recovery performs worse than predicting a change at every word boundary. Prompt-grouped evaluation, formatting controls, and uncertainty estimates also strengthen the analysis.
Critical weaknesses
  1. Overall presentation makes the study difficult to follow. Definitions, results, qualifications, and interpretation are spread across the main text and appendices. The relationships between the historical corpus, matched experiments, text representations, and evaluation rules require considerable reconstruction by the reader.
  2. The figures do not communicate the central argument clearly enough. Especially Figure 1 combines generation, score decomposition, feature construction, and evaluation in one crowded diagram, while the matched blended-versus-fixed comparison is not prominent. Figure 4 also combines boundary analyses with detector-fusion results, making its organizing message unclear.
  3. The discussion needs more works. The paper reports many comparisons but spends less time explaining which observations support the main conclusions, which alternative explanations remain, and how far the findings extend. The conclusion largely repeats results. Some subsection titles are also lengthy or organized around a reported number rather than the underlying question.
  4. The appendix contains substantial evidence, but its connection to the main claims is difficult to track. Appendix C, titled “Relocated Discussion,” combines interpretation with protocol details and additional results. A compact map linking each central claim to its experiment, control, and supporting table would help readers assess the evidence.
  5. The language of “bounds” on recoverability needs clarification. Low performance across the tested blend classifiers establishes an empirical limitation of those methods, rather than a general upper bound. The exact-context attribution experiment provides stronger evidence under its assumptions, but the scope of its optimality and its relationship to word-level accuracy need to be stated more precisely.
  6. Attribution is partly confounded with decoding configuration. Llama uses different temperature and top-p settings from the other models, and sampling-aware attribution is much more accurate for Llama. The overall improvement therefore does not clearly separate model identity from decoding differences.
  7. Overall, generalizability is limited. The study uses two fixed pools of older open models, three English domains, and white-box access to every generator. The complete matched classifier comparison is concentrated on the advanced pool at TL1; the additional settings extend only selected analyses. Length filtering also removes a substantial fraction of historical examples, which limits the population covered by the headline results.
Questions for authors
  1. What precisely supports the claimed bounds on blend detection and attribution? Please distinguish observed performance from an optimality result under a specified generation and observation model.
  2. How does attribution change when temperature, top-p, and top-k are matched across generators? How much of the sampling-aware improvement comes from recognizing decoding settings?
  3. How do the principal detection conclusions change on the full corpus, and are examples excluded by length matching systematically different from those retained?
  4. Could the main text more clearly distinguish strong AI-versus-human discrimination from failure of the planned detector rule?
  5. Could the paper be reorganized around its three central questions, with a clear link from each question to the experimental design, result, and interpretation? A simpler Figure 1 and a better-organized appendix would substantially improve readability.
2 comments
AuthorsOpenReview ↗

Response to Reviewer gvSy (1/2)

Thank you for the detailed review and for recognizing the separation of detection, blend identification, and source attribution. The paper positions itself the same way as your summary: it uses the component reader as an analysis instrument, not as a new detection method (Section 2), and offers an evaluation framework that tests detection, blend specificity, and attribution separately (Section 6). This part answers Weaknesses 1 to 5 and Questions 5 and 1; Part 2 answers Weaknesses 6 and 7 and Questions 2 to 4.

Weakness 1: Overall presentation makes the study difficult to follow.

Weakness 2: The figures do not communicate the central argument clearly enough.

Weakness 3: The discussion needs more works.

Weakness 4: The appendix contains substantial evidence, but its connection to the main claims is difficult to track.

Question 5: Could the paper be reorganized around its three central questions, with a clear link from each question to the experimental design, result, and interpretation?

Yes. The results will follow the three questions (detection, blend specificity, word attribution), each linked to its design, result, and interpretation, with Table 4 moved into the main text. A notation table will define the two data sources (the historical corpus and the provenance-logged matched arms), the four text views (V0, V1, V2-lite-mask, V2-lite-text), the frozen and trained readers, and the two rule sets (Table 1 and the Appendix J rules), and state which result uses which. Figure 1 will have three columns, with both matched arms, blended and fixed-model, drawn in the middle with their shared prompts, loop, and stopping rule, and the score-decomposition box moved to the appendix; Figure 4 will be split into its boundary and fusion analyses. The discussion will state each conclusion's evidence, remaining alternatives, and scope, and Section 6 will close on the interpretation rather than the numbers: detection and source tracing are distinct problems, blending leaves a likelihood trace that the tested detectors miss, and attribution stays limited even for the Bayes rule. Subsection titles will state questions rather than results, for example "Can words be traced to their generators?" in place of "Logged Attribution Reaches 41.3%" (Section 5.4). A claim-to-evidence map will link each central claim to its experiment, control, and table, and Appendix C will separate interpretation from protocol details and additional results.

Weakness 5: The language of “bounds” on recoverability needs clarification.

Question 1: What precisely supports the claimed bounds on blend detection and attribution? Please distinguish observed performance from an optimality result under a specified generation and observation model.

The two results have different status. For blend specificity, "at most 0.58" is the best observed value across the tested detectors, an empirical limit of these methods, and the revision will say so. The optimal reference under white-box access is the passage-level likelihood-ratio test between the blended and fixed-model hypotheses: computed with raw per-word likelihoods, it separates the matched TL1 arms with AUROC 0.9766 [0.9640, 0.9877], against 0.5757 for the trained reader. Blending thus leaves a trace that the pool's likelihoods reveal but the tested detectors miss. We will also compute this test under the logged decoding transforms, and we will include those experiment results in the camera-ready version. For attribution at TL1, an optimality result holds under a specified model. Generation: each step draws one member uniformly and independently of the text and of earlier draws, the member samples its chunk under its logged decoding configuration, and the stopping rule does not depend on the draw. Observation: the full text, white-box access to all members and their decoding settings, and the chunk boundaries. The posterior then factorizes across steps, so the per-chunk maximum a posteriori rule is the Bayes rule; with a uniform prior it equals the exact-context likelihood argmax (Section 5.4, Appendix J), up to NLTK re-spacing in 0.74% of steps. Its 40.50% chunk accuracy therefore estimates the best expected chunk accuracy of any attributor for this pool, these decoding settings, and k = 1, so source tracing stays limited even where blending is detectable. The paper's 41.3% is the word-level accuracy of this rule (41.25%) and of the sampling-aware attributor (41.31%), and the revision will state the bound at the chunk level. The TL3 figure comes from a word-level attributor and will be removed from Contribution (3).

AuthorsOpenReview ↗

Response to Reviewer gvSy (2/2)

Weakness 6: Attribution is partly confounded with decoding configuration.

Question 2: How does attribution change when temperature, top-p, and top-k are matched across generators? How much of the sampling-aware improvement comes from recognizing decoding settings?

Most of the improvement reflects decoding. Llama-2 used its shipped temperature 0.6 and top-p 0.9, and the other members temperature 1 and top-p 1, all with top-k 50 (Appendix B). In the matched TL1 run, the net gain from 36.53% to 41.31% comes entirely from Llama-generated words (4,116 more correct, against 2,449 fewer for the other members). In the classic pool, whose members share one configuration, the transform leaves accuracy unchanged (38.20% versus 38.19%; Table 28). We therefore expect identity-only attribution to stay at the raw-argmax level (36.53%), which would strengthen the conclusion that source tracing is hard. We will report this decomposition and run the advanced pool with matched decoding; we will include those experiment results in the camera-ready version.

Question 3: How do the principal detection conclusions change on the full corpus, and are examples excluded by length matching systematically different from those retained?

The new matched experiment applies no length filter and shows the same detection picture on all 300 pairs: the frozen reader separates blended from human text with AUROC 0.9506 [0.9321, 0.9662] (Table 4). For the historical corpus, we computed the analyses that Section 3.2 mentions. Without the caliper, the reader reaches AUROC of at least 0.85 in all 36 cells of the evaluation view, V2-lite-mask (lowest 0.8662 [0.8392, 0.8915]), and excluded and retained rows are detected alike: the reader's excluded-minus-retained difference ranges from −0.0171 to 0.0276, with no interval excluding zero. Exclusion falls most on Writing (34% to 38% of evaluation-view rows, against 18% to 21% for SQuAD and XSum). Length alone separates the classes strongly only in the original-text view (median AUROC 0.9586 and 0.9631 on all pairs), not in the evaluation view (0.5982 and 0.6038), and with length as a covariate the reader stays at or above 0.85 in every evaluation cell. The camera-ready version will include these tables. Where the paper already reports both versions, the caliper leaves the conclusions unchanged: on a fixed subset of 240 human and 240 blended advanced-pool passages, the reader's gain over RADAR is 0.1072 [0.0710, 0.1446] on all rows and 0.1304 [0.0850, 0.1732] after the caliper (Table 3), and the outside-scorer sign-pattern counts are identical before and after matching in 11 of 12 pool, view, and domain rows (Table 10).

Weakness 7: Overall, generalizability is limited.

White-box access is the setting most favorable to the defender (Section 1): an attributor with less access cannot exceed, in expectation, the Bayes accuracy given in our answer to Question 1, and detectors that need no pool likelihoods separate blended from fixed-model text with AUROC of at most 0.5443 (Tables 22(a) and 27). Detection holds within each domain: the 36 evaluation cells in which the reader reaches AUROC of at least 0.85 span all three domains (Tables 5 and 6), and the Limitations keep the claims to these English corpora. We will add a matched TL1 run with an instruction-tuned pool (Llama-3.1-8B-Instruct, Qwen2.5-7B-Instruct, Mistral-7B-Instruct-v0.3, Gemma-2-9B-it) that repeats the detection, blend-specificity, and attribution analyses, so that the matched classifier comparison covers a second pool, and we will include those experiment results in the camera-ready version. Length filtering is addressed in our answer to Question 3.

Question 4: Could the main text more clearly distinguish strong AI-versus-human discrimination from failure of the planned detector rule?

Yes. The reader discriminates strongly, with AUROC of at least 0.85 in all 36 cells. The planned rule fails on superiority over both supervised classifiers (6 of 18 classic cells, none of 18 advanced) and on the null band in four classic cells (Table 2). We will name it the detector superiority rule and state this distinction in the abstract and introduction.

Reviewer_MC5hOpenReview ↗
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Paper summary

This paper conducts an in-depth investigation into the detection and attribution of AI-generated text in the face of token-level multi-model blending attacks. The authors point out that existing detection research often conflates identifying machine-generated text with identifying the generation strategy or specific model. The paper constructs a matched benchmark dataset containing detailed provenance logs, and strictly decouples the evaluation into three independent tasks: Detection (distinguishing between human and machine generation), Blend Specificity (distinguishing between blended and single-model generation), and Word Attribution (locating the true generating model for each word).

Experimental results show that: (1) provided there is white-box access to the candidate pool, a detector (Reader) based on in-pool likelihood statistics and a fine-tuned RoBERTa can reliably detect blended text (AUROC ≥ 0.85), and are complementary to out-of-distribution detectors (RADAR); (2) However, distinguishing between hybrid text and single-model text is extremely difficult (AUROC ≤ 0.58); (3) Even when utilising complete decoding distribution logs, the upper bound for word-level attribution accuracy is only 41.3 per cent (compared to a random baseline of 25 per cent). Through an algebraic decomposition of the Fast-DetectGPT score identity and a large number of controlled experiments, the paper demonstrates that ‘likelihood decreases whilst entropy increases’ is not a characteristic unique to mixed generation. It ultimately reaches the important conclusion that a high detection rate does not equate to the ability to trace origins; the two are entirely distinct problems.

Critical strengths

The experimental design is rigorous. The study introduced provenance-logged matched generation experiments, ensuring that mixed-text and single-model text were entirely consistent in terms of prompts, generation loops and stopping conditions, thereby providing an unbiased ‘gold standard’ for evaluation. Analysis plans and decision rules were pre-registered and strictly enforced following the experiments. The authors openly acknowledged and reported negative results where ‘no detector claim’ was made; such scientific integrity is extremely rare and admirable in the current field of AI safety.

Comprehensive baseline and ablation analysis: this study not only compares zero-shot metrics such as Margin, Binoculars, Fast-DetectGPT, but also supervised methods including RoBERTa, character n-grams and out-of-distribution detectors. It further provides a detailed analysis of the impact of feature masking and text cleaning on the results, with the experiments covering an broad scope.

Critical weaknesses

Word-level attribution overlooks the sequence dependencies inherent in autoregressive generation All attribution methods including raw argmax, sampling-aware and exact-context, assign each word independently to a generative model. However, ToBlend’s generative process exhibits a strong sequence structure: the model is sampled in blocks of k tokens, and the same model may be sampled consecutively multiple times. This implies that the generative model labels of adjacent words are highly correlated. The paper does not attempt any sequence-level attribution methods, such as: (a) Hidden Markov Models (HMM), which treat the generative model as a hidden state and word likelihood as the observed probability; (b) Conditional Random Fields (CRF), which utilise transition probabilities between the labels of neighbouring words.

The evaluation metrics for blend specificity are limited. AUROC is the only metric used to distinguish between blended generation and single-model generation. However, AUROC is insensitive to class imbalance and the shape of the score distribution. If the score distributions of blended text and single-model text overlap significantly, AUROC may approach 0.5, whilst the precision-recall curve (PR curve) or the true positive rate (TPR) at a specific operating point (such as 5% FPR) may show a meaningful separation. The paper does not report PR curves, calibration curves or confusion matrices at different operating points.

The assumption of a uniformly random ToBlend attack may not be solid. The ToBlend generation process assumes that, at each step, a model is selected from the four models with uniform probability. However, real-world attackers may employ non-uniform strategies (such as using a particular high-quality model 90% of the time and switching randomly the remaining 10 per cent of the time), or adaptive strategies such as selecting the most ‘natural’ model based on the current text content. The paper did not test detection or attribution performance under any non-uniform or adaptive blending strategies. If an attacker favours a particular model, the distribution of the in-pool likelihood statistic would change fundamentally, and the current conclusions may no longer hold.

Questions for authors

Seek weakness.

2 comments
AuthorsOpenReview ↗

Response to Reviewer MC5h (1/2)

Thank you for recognizing the provenance-logged matched design, the planned decision rules with openly reported negative results, and the breadth of the baselines. This part answers the first two weaknesses; Part 2 answers the third.

Weaknesses, paragraph 1: The paper does not attempt any sequence-level attribution methods, such as: (a) Hidden Markov Models (HMM), which treat the generative model as a hidden state and word likelihood as the observed probability; (b) Conditional Random Fields (CRF), which utilise transition probabilities between the labels of neighbouring words.

At TL1, which carries the headline attribution results, each step draws a pool member uniformly and independently of the text and of earlier draws (Appendix B.1), so the generators of adjacent chunks are independent by construction; the generator changes at 74.8% of adjacent word pairs (Section 5.4), close to the 75% expected under independence. The posterior over generators therefore factorizes across steps, and the per-chunk maximum a posteriori rule, which under the uniform draw is the exact-context likelihood argmax, is the Bayes rule for this process, up to NLTK re-spacing in 0.74% of steps. The exact-context attributor already scores each chunk under every member given exactly the text the loop encoded before it (Section 5.4), so the dependence of a chunk on its prefix enters every member's likelihood; what an HMM or CRF adds is structure over the labels of neighboring chunks. An HMM with the true transitions (all entries 1/4) returns the same decisions, and a CRF has no transition structure to learn, so neither can exceed the rule's chunk accuracy of 40.50% at TL1 in expectation. The paper's 41.3% is the word-level accuracy of this rule (41.25%) and of the sampling-aware attributor (41.31%), and the revision will state the bound at the chunk level. Sequence structure does matter for k > 1, and the reported TL3 figure comes from a word-level attributor. We ran the HMM at TL1 on the raw per-word likelihoods. Viterbi decoding with uniform transitions returns the per-word decision for every word (36.53%). Transitions fitted on labeled training folds (stay probabilities 0.2503 to 0.2536) change accuracy by 0.00 percentage points [−0.27, 0.26], and unsupervised Baum–Welch fitting changes it by −2.94 points [−3.51, −2.36]. On the fixed-model arm, where consecutive labels are informative, the supervised decoder fitted on that arm reaches 96.48% [94.60, 98.16], so the null on blended text reflects the independent draws rather than a weak decoder. We will state this argument in Section 5.4 and add a chunk-aware decoder at TL3, and we will include those experiment results in the camera-ready version.

Weaknesses, paragraph 2: AUROC is the only metric used to distinguish between blended generation and single-model generation.

Weaknesses, paragraph 2: The paper does not report PR curves, calibration curves or confusion matrices at different operating points.

The two arms are balanced (300 blended and 300 fixed-model instances; Section 3.4), so the comparison involves no class imbalance. With 300 texts per class, precision at any threshold equals TPR/(TPR + FPR), so the PR curve is a pointwise transform of the ROC curve, and a usable operating point would appear as a TPR well above a low FPR. We computed these operating points with prompt-cluster intervals for every detector except RoBERTa, whose out-of-fold scores need a GPU rerun. Across both text views, TPR at 5% FPR is 0.000 to 0.060 and PR-AUC is 0.475 to 0.559 (0.5 at chance), so the low AUROCs do not hide a usable operating point, whereas the likelihood-ratio test of our general response reaches TPR 0.927 [0.673, 0.973] at 5% FPR on the original text. The probabilistic classifiers assign most texts probabilities between 0.4 and 0.6 (Brier scores 0.2445 to 0.2520, against 0.25 for a constant 0.5). We will add the RoBERTa rows, PR curves, reliability curves, and confusion matrices at 1%, 5%, and 10% FPR for each detector family, and we will include those experimental results in the camera-ready version.

AuthorsOpenReview ↗

Response to Reviewer MC5h (2/2)

Weaknesses, paragraph 3: The paper did not test detection or attribution performance under any non-uniform or adaptive blending strategies.

Weaknesses, paragraph 3: If an attacker favours a particular model, the distribution of the in-pool likelihood statistic would change fundamentally, and the current conclusions may no longer hold.

Random per-step selection is the published ToBlend scheme [1], implemented as a uniform draw (Appendix B.1), and it is the attack we analyze. The fixed-model arm is the limiting non-uniform schedule (one member with probability 1), and the frozen reader still separates it from human text with AUROC 0.8678 [0.8374, 0.8979], against 0.9506 for uniform blends (Table 4, original text), so detection holds at both ends of the range of mixing proportions. For the advanced pool at TL1, we will add a skewed schedule (a favored member drawn with probability 0.7), a sticky schedule (the member redrawn with probability 0.25 at each step), and two adaptive attackers: at every step each member proposes a chunk, and the attacker appends either the proposal with the highest likelihood under the member that wrote it or the one with the lowest pool margin, the per-chunk ingredient of the white-box blend score. For every arm, we will report detection against the human passages of the same prompts, blend specificity against a same-loop fixed-model arm, including the likelihood-ratio test, and balanced attribution accuracy, and we will include those experiment results in the camera-ready version. Balanced accuracy is the readout because raw accuracy under the 0.7 schedule rewards always naming the favored member, which is right at 70% of steps. Adaptive selection makes each draw depend on the text, so the TL1 optimality argument does not cover the adaptive arms, and their attribution results will be reported as measurements rather than as a bound.

References

[1] Huang, F., Kwak, H., & An, J. (2024). ToBlend: Token-level blending with an ensemble of LLMs to attack AI-generated text detection (arXiv:2402.11167). arXiv. https://doi.org/10.48550/arXiv.2402.11167

Comments on the paper

1 comment
AuthorsOpenReview ↗

General Response to the AC and All Reviewers

We thank the reviewers for their careful reading. They found the provenance-logged matched design rigorous, with planned decision rules and openly reported negative results (MC5h); the separation of detection, blend identification, and source attribution useful (gvSy); and the matched control strong (gvSy).

For attribution at TL1, each step's generator is drawn uniformly and independently, so the posterior over generators factorizes and the exact-context attributor is the Bayes rule for this process, up to NLTK re-spacing in 0.74% of steps. Its chunk accuracy of 40.50% (against 25% chance) therefore estimates the best attainable chunk accuracy for this pool and these decoding settings, and sequence models such as HMMs or CRFs cannot exceed it in expectation (MC5h, gvSy, 5KLn). For blend specificity, AUROC of at most 0.58 is the best value among the tested detectors, whereas a white-box likelihood-ratio test separates the matched arms with AUROC 0.9766 on raw per-word likelihoods; the revision will present blend specificity as a limit of the tested detectors, and attribution as limited even at the optimum (gvSy). Llama-2's shipped decoding configuration explains most of the sampling-aware gain; we expect identity-only attribution to stay at the raw-argmax level (36.53%), which the matched-decoding run will test (gvSy, 5KLn).

We have computed the TL1 HMM decoders, the operating points of the tested detectors, and full-corpus detection without the length caliper (MC5h, gvSy). We will add the likelihood-ratio test under the logged decoding transforms, a matched-decoding run, a chunk-aware decoder at TL3, the RoBERTa operating points, skewed, sticky, and adaptive switching schedules with detection, specificity, and attribution readouts, and an instruction-tuned pool. We will include those experimental results in the camera-ready version, together with the reorganization around the three questions and the discussion of CollabStory.

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

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