acceptodds
Under review as a conference paper at ICLR 2027

Positional Attention Signatures Distinguish AI-Generated from Natural Biological Sequences

Abstract

Biological foundation models generate increasingly realistic DNA and proteins, raising two questions: how do generated sequence distributions differ from natural ones, and how can those sequences be screened efficiently? We study positional attention variance (pAV), the variation of attention-weighted distance across positions in a frozen biological language model. Across six DNA generators, mean pAV is 53–84% of a matched natural reference under a multispecies Nucleotide Transformer. Preserving dinucleotide counts while shuffling order lowers median pAV by 16.2% across 200 natural windows, establishing arrangement sensitivity. A protein panel shows analogous differences under ESM2. In matched detection tests, inexpensive features are stronger on clean data, while standalone pAV retains macro AUROC 0.867 at 20% substitution, compared with 0.822 for compression. Adding pAV to a clean-trained compression classifier does not improve this stress-test performance. We separately evaluate DNA screening with multiscale sequence features and frozen observer representations, obtaining macro AUROC 0.995 in five-fold sequence-level cross-validation. Distilling the observer contribution enables a compact service with measured throughput of 334.6 sequences per second on one GPU. Together, these studies establish an arrangement-sensitive statistical probe and a computationally practical screening approach, with distinct measurement, evaluation, and calibration boundaries.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
AI-generated biological sequences, biological language models, genome foundation models, positional attention variance, AI-generated DNA detection, protein sequence detection, biosecurity

Reviews

Among:
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1234this paper, Top 30%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_RQKZOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper investigates positional attention variance (pAV) as a statistical signature for distinguishing AI-generated from natural biological sequences. Using frozen Nucleotide Transformer and ESM2 models, the authors observe differences in attention patterns between natural and generated DNA and proteins. They further develop a DNA screening framework combining sequence statistics and pretrained representations, achieving high detection accuracy through representation fusion and knowledge distillation.

Critical strengths
  1. Interesting empirical observation: The paper identifies differences in positional attention variance between natural and AI-generated biological sequences. The sequence-shuffling experiments provide evidence that pAV captures information beyond local nucleotide composition.
  2. Broad evaluation: The authors evaluate multiple DNA generators and protein models, with comparisons against sequence-based baselines and perturbation experiments.
Critical weaknesses
  1. Limited methodological novelty: The proposed framework primarily relies on existing pretrained models, sequence statistics, and established classification and distillation approaches. While pAV provides an interesting descriptive statistic, its methodological contribution beyond existing sequence-based detection methods remains unclear.
  2. Limited incremental value and generalization: Simple k-mer entropy and compression features outperform pAV on clean data, and adding pAV does not improve detection performance in the reported experiments. Furthermore, the strongest representation-based detector is evaluated using sequence-level cross-validation, where all generator families appear in both training and evaluation folds. This limits conclusions about generalization to unseen generative models.
Questions for authors
  1. Generation of synthetic sequences: Were the AI-generated DNA and protein sequences newly generated by the authors or obtained from existing model outputs? Could the authors clarify the generation procedures and sampling settings, and whether these were consistent across models?
  2. Choice of observer models: What motivated the selection of Nucleotide Transformer for DNA and ESM2 for proteins? Given that pAV varies across observer models, how generalizable is the proposed signature to other biological foundation models?
  3. Incremental contribution of pAV: Given that simple sequence statistics outperform pAV on clean data, what additional information does pAV provide beyond existing sequence-based features? Could the authors further clarify its contribution to the proposed detection framework?
  4. Generalization to unseen generators: The representation-based detector is evaluated using sequence-level cross-validation, where all generator families appear in both training and evaluation folds. Could the authors evaluate its performance on entirely unseen generators to better assess generalization?
  5. Biological interpretation: Beyond differences in attention patterns, is there evidence that pAV captures biologically meaningful sequence properties rather than differences in sequence composition or model-specific attention behavior?
4 comments
AuthorsOpenReview ↗

Thank you for clarifying method scope and unseen-generator needs (1/2)

We sincerely thank you for acknowledging our sequence-shuffling findings, wide generator coverage, and clear writing. Your questions on novelty, the incremental contribution of pAV over sequence statistics, observer choice, and unseen generators gave us clear targets. During the rebuttal period, we completed comprehensive cross-observer, quality-control, and unseen-generator studies to answer every point directly.

1. Methodological Contribution and Scope Division (Weaknesses 1, 2 and Question 3)

On novelty, prior detection work scores a sequence with external statistics or with a trained classifier head. We instead read the internal attention geometry of a frozen model. Three elements are new. First, pAV summarizes how far each query position attends, then measures how that span varies along the sequence. It is a single unfitted scalar, not a learned score. Second, we show the signature is not an artifact of one observer. It replicates on NT-2.5B and on two independent BPE models. Third, we distill the dense observer into a 100M student that runs 69.09x faster, which turns the finding into a deployable screen.

Our work therefore separates two roles. pAV is our interpretable structural probe. Dense observer representations, distilled into a compact student, carry the practical screening load. Two measurements fix that division. Under 20% point-mutation noise, standalone pAV beats compression (0.867 vs 0.822 macro AUROC; on Evo-1, 0.934 vs 0.630). Conversely, adding scalar pAV on top of full dense hidden states (3,200-d NT-2.5B or 912-d DNABERT) moves macro AUROC by less than 0.002 in either direction, on the matched pool, on LOFO, and on the clean external generators.

Why then are neural representations needed, when simple CPU statistics look strong on unfiltered splits? Because unfiltered pools retain low-complexity synthetic artifacts. Enforcing two-sided quality control (entropy, 6-mer diversity, repeat, and homopolymer gates) leaves 3,211/5,000 sequences and changes the ranking. Linear models are refit on filtered data only; our distilled student (seed=42) is rescored and recalibrated on the same rows.

Model5-fold AUROC (unfiltered)5-fold AUROC (strict QC)TPR@1.3% (strict QC)Held-out AUROC (strict QC)
CPU-only (47-d)0.98670.960663.70%0.6863
NT-2.5B Observer0.99470.979683.25%0.7261
Fusion Teacher0.99490.980182.60%0.7431
Fusion Teacher plus scalar pAVn/an/an/a0.7516
DNABERT-2 scalar Z(pAV)n/an/an/a0.8136
Distilled Student0.99640.982390.02%n/a

Two points follow. The observer gains +19.55 pp over CPU-only at 1.3% FPR once composition artifacts are removed. And on strictly zero-overlap held-out generators under QC, CPU-only collapses to 0.6863 while an unfitted DNABERT-2 pAV scalar still reaches 0.8136. Under natural domain shift (n=2,500 external naturals), CPU-only falls to 5.28% TPR at 1.3% FPR, while our 3-seed distilled student holds 71.59 +/- 1.70%. That student also runs 69.09x faster than the teacher (0.294s vs 20.317s per 500 sequences; 1.39 GB vs 14.36 GB VRAM).

AuthorsOpenReview ↗

Thank you for clarifying method scope and unseen-generator needs (2/2)

2. Performance on Entirely Unseen Generative Models (Weakness 2 and Question 4)

We agree that shared generator families across folds limit any generalization claim. We therefore ran 5-group Leave-One-Family-Out (LOFO), plus three external models absent from every fold (D3LM-from-nt, D3LM-scratch, HyenaDNA-native). External columns are scored against matched out-of-fold naturals (n=2,000) and against 2,500 domain-shifted external naturals. The student row aggregates three seeds.

ModelLOFO AUROCLOFO TPR@1.3%External TPR vs matchedExternal TPR vs shifted
CPU-only0.951867.85%18.83%5.28%
NT-2.5B Observer0.968971.73%93.83%n/a
Fusion Teacher0.969671.69%92.78%63.22%
Distilled Student0.9696 +/- 0.001177.10 +/- 0.80%99.54 +/- 0.16%71.59 +/- 1.70%

Matching external AUROC is 0.9346 (CPU-only), 0.9966 (observer), 0.9965 (teacher), and 0.9992 (student) against matched naturals; against shifted naturals the teacher reaches 0.9832 and the student 0.9877. Crucially, the independent 117M BPE observers also catch D3LM-from-nt (0.9927 and 0.9970 vs matched naturals; 0.9724 and 0.9802 vs shifted naturals). Generalization therefore extends well beyond NT-family models.

3. Synthetic Sequence Provenance and Standardization (Question 1)

Every synthetic corpus in the benchmark panel is sampled from a publicly released checkpoint under its documented default settings. We did not retrain or tune any benchmark generator, which matches real-world external sequence auditing. DNA benchmarks are standardized to 1,000 bp windows. The rebuttal adds three further unseen generators, two of them discrete diffusion models, extending coverage to a different generative paradigm. Our new QC audit also flags low-complexity sampling failures (for example, only 5.2% of GENERator-v2 windows pass the diversity gates). Detection does not depend on those artifacts: after refitting on filtered data only, the observer still leads CPU-only by +19.55 pp at 1.3% FPR.

4. Observer Model Choice and Cross-Architecture Transfer (Question 2)

We selected NT-2.5B and ESM-2 as widely adopted multi-species foundation models with non-overlapping tokenizations. To test whether the signature survives a different architecture and tokenizer, we replicated head discovery on two 117M-parameter BPE models under the same zero-overlap protocol. Macro AUROC is on the four held-out generators, using an unfitted scalar Z(pAV) mean.

Observer (heads)Rank transfer (rho)Scalar Z(pAV)Random 20-head null
NT-2.5B (640)0.84730.89440.6148
DNABERT-S (144)0.85940.90400.4518
DNABERT-2-117M (144)0.88370.94560.3866

The BPE nulls are separated at empirical p = 0.0010 over 1,000 random subsets, establishing clear cross-model generality.

5. Biological Interpretation Beyond Local Composition (Question 5)

We maintain a disciplined boundary and do not map attention heads to specific cis-regulatory motifs. Three converging findings show sensitivity beyond base composition:

  • Paired 2-mer shuffling holds length, GC, repeats, and exact dinucleotide counts fixed while reducing pAV (median -16.2% on NT-2.5B, p = 6.71e-21; mean -9.13% on DNABERT-2, p = 1.57e-16).
  • Point substitutions at 5% to 10% preserve pAV despite modifying local sequence motifs.
  • Head selectivity transfers consistently across independent NT and BPE models.

Thank you again for your detailed and balanced evaluation. Your questions directly strengthened our scope clarity and unseen-generator evidence, and we hope these results support raising your score.

Thank you for the detailed rebuttal and substantial additional experiments. I appreciate the authors' efforts to address my concerns. I still have two points that I believe would benefit from clarification:

  1. Since adding scalar pAV to the dense representations produces negligible improvements, I think the manuscript should more clearly distinguish the contribution of pAV as a standalone diagnostic statistic from the predictive contribution of the representation-based screening framework.

  2. Could the authors clarify how natural and synthetic sequences were matched in the external evaluations, and whether model selection, attention-head selection, and calibration were performed without using any held-out generator information? This would help establish how much of the strong external performance reflects generalizable signatures rather than dataset-specific differences.

But, overall, the rebuttal substantially addresses my main concerns and strengthens the paper. Assuming these evaluation details are clarified, I would be comfortable revising my rating from weak rejection to weak acceptance.

AuthorsOpenReview ↗

Thank you for the constructive follow-up on pAV scope and external evaluation

We sincerely thank you for reading our rebuttal so carefully and for updating your assessment. Both remaining points are fair, and both improve the paper. Below we give the facts for each, including one new controlled analysis.

1. Separating pAV as a Diagnostic from the Screening Framework

We agree. The evidence supports two distinct contributions, and the revision will present them separately.

ContributionRoleEvidence
pAVStandalone diagnostic: one unfitted, interpretable scalarRobust to noise (0.867 vs 0.822 for compression at 20% mutation). Head rankings transfer from discovery to held-out generators in three observers (rho 0.8473 to 0.8837).
Representation-based screenPredictive detector: observer, teacher, distilled studentExternal AUROC 0.9965 (teacher) and 0.9992 (student) vs 0.9346 for CPU-only. Adding scalar pAV changes macro AUROC by less than 0.002.

2. External Evaluation: Matching, Selection, and Calibration

In our first reply, "matched naturals" meant the in-distribution naturals of the benchmark pool, scored out of fold. Natural and synthetic sequences were aligned on length only (1,000 bp windows). To answer your question directly, we added two controls. First, GC matching: 5% GC bins, 1:1 sampling without replacement in each bin, averaged over 200 resamples (residual GC difference at most 0.003). Second, the two-sided quality gate from our first reply (530/540 external synthetic and 4,496/4,500 natural sequences pass). The pass criterion was fixed before the analysis: after matching, each neural detector must beat CPU-only by at least 0.02 AUROC and stay at or above 0.95 on both comparators.

Macro AUROC over the three unseen external generators (student: mean +/- SD over three seeds):

Natural comparatorConditionCPU-onlyTeacherDistilled student
In-distribution out-of-fold (n=2,000)As reported0.93460.99650.9992 +/- 0.0001
In-distribution out-of-fold (n=2,000)GC-matched plus QC0.90020.99520.9989 +/- 0.0001
Domain-shifted external (n=2,500)As reported0.85900.98320.9877 +/- 0.0003
Domain-shifted external (n=2,500)GC-matched plus QC0.83940.97460.9788 +/- 0.0005

The criterion is met, and both neural detectors stay above CPU-only for each generator individually. Matching lowers CPU-only (by 0.034 and 0.020) more than the student (by less than 0.001 and by 0.009). Composition differences helped the baseline, not our detectors. A second, independently written implementation reproduces the table (unmatched rows exactly, matched rows within 0.002).

No external-generator information enters any stage of this evaluation:

StageProtocolCheck
DataExternal generators and external naturals appear in no training fold0 exact and 0 reverse-complement matches between the 3,040 external sequences and the 5,000-sequence training pool
Head selectionNone. Observer and teacher read the full 3,200-d representation, with all 640 heads. The student reads raw sequence onlyNo head subset exists to tune
Model selectionTeacher and student keep the configuration stated in the submitted manuscript (student: six epochs, final epoch reported). CPU-only reuses the teacher pipelineFixed before the external sets were introduced. No external sequence is used for tuning, early stopping, or checkpoint choice
CalibrationEvery threshold is set from natural-sequence scores onlyReplacing generator scores with arbitrary values in 120 test cases changes no threshold

AUROC needs no threshold and is our primary external metric. Head selection exists only for the standalone pAV diagnostic, which is not an input to these detectors. There, heads are discovered on a zero-overlap split and tested on four held-out generators, as in our first reply.

Thank you again for your rigorous and constructive follow-up. We commit to the following revisions. The abstract, introduction, and results will state the two contributions separately, and the detection tables will report the with and without pAV ablation. A new external-evaluation protocol subsection will give the matching procedure, the matched AUROC table, and the overlap, selection, and calibration checks. The audit scripts will be released with our code. We hope this fully resolves the remaining points.

Reviewer_8FQ1OpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper proposes a metric called 'positional attention variance (pAV)' that can tell apart natural and AI-generated DNA sequences. The authors found that, under the selected observation models, the pAV of various generated DNAs is generally lower than that of natural sequences; even when dinucleotide counts are preserved but the base order is scrambled, the pAV still drops significantly.

Critical strengths
  1. The problem definition is clear and interesting. When generating DNA versus natural DNA, you can’t just rely on whether it matches known sequences or if the GC content is abnormal. This paper tries to extract information from the internal attention patterns of a frozen biological language model, which is a reasonable perspective and somewhat insightful.
  2. The design and definition of pAV are pretty straightforward and interpretable. It doesn’t just average attention weights directly; instead, it summarizes the attention at each position as "how far, on average, it looks," and then checks if this span is stable across the sequence. Compared to a simple attention entropy, this metric is indeed closer to seeing whether the model uses different scales of contextual dependencies at different positions.
  3. To improve deployment efficiency, the authors provide a small model distillation solution, which increases the practical value of this method.
Critical weaknesses
  1. The accuracy and validity of the pAV metric heavily depend on attention heads. The final DNA pAV isn’t a natural aggregation of all attention heads but a score obtained after selecting the 20 most discriminative heads. As a result, pAV is more like a classification feature after feature selection rather than a naturally emerging, universally interpretable statistic from the frozen model. Also, the effectiveness of pAV strongly depends on the observed model, meaning this metric might just be an output feature of a specific model rather than a generally meaningful measurement.
  2. The differences in distribution between natural and generated DNA sequences could still be the main source, instead of being caused by the characteristics of the generative model itself. Different generators may have different training data, decoding strategies, post-processing, and target tasks. Natural references are mixed from sources like GTDB, RefSeq, human, viral, and metagenomes. Even with the same window length, species composition, GC distribution, repeat proportion, coding region proportion, sequence quality, and database sources could vary. Thus, differences in pAV may just reflect 'two different sampling distributions' rather than 'the generative model leaving some universal trace.'
  3. High-scoring ensemble detectors don’t really test 'never-seen-before new generators,' as generative sources still appear in the cross-validation training folds. Therefore, it’s closer to a screener for known sources rather than a reliable, general-purpose source identifier.
Questions for authors

Please see the weaknesses.

6 comments
AuthorsOpenReview ↗

Thank you for your insightful focus on confounders and generality (1/2)

We sincerely thank you for recognizing the clarity of our framing, the interpretability of positional attention variance (pAV) beyond attention entropy, and our practical distillation pipeline. Your three concerns regarding supervised head selection, biological confounders, and unseen-generator evaluation pointed directly to the strongest possible validations. We conducted extensive cross-architecture, quality-controlled, and generator-held-out experiments that strongly confirm our main claims.

1. Independent Head Discovery and Cross-Observer Generality (Weakness 1)

To break any dependence on supervised selection, we built two new balanced discovery splits from GenomeOcean-4B and Evo2: 500 sequences (167/167/166) and 1,500 sequences (500/500/500), each paired with multi-source naturals. We computationally verified zero exact matches and zero reverse-complement 1 kb overlaps with any held-out benchmark. We then repeated the full procedure on two 117M-parameter BPE models, which removes any dependence on NT-2.5B or its fixed 6-mer tokenization.

Macro AUROC is measured on the four held-out generators, using rediscovered heads only as an unfitted scalar Z(pAV) mean (no fitting).

Observer (heads)Rank transfer (Spearman rho)Scalar Z(pAV), n=500Scalar Z(pAV), n=1,500Random 20-head null
NT-2.5B (640)0.8487 / 0.84730.90330.89440.6148
DNABERT-S (144)0.85940.90570.90400.4518
DNABERT-2-117M (144)0.88370.95510.94560.3866

Our published NT-2.5B head set scores 0.9018 on the same generators, so independent rediscovery reproduces it rather than relying on the original selection. The BPE nulls are separated at empirical p = 0.0010 over 1,000 random subsets. The rediscovered directional top-20 heads also overlap 15/20 with our paper set, and top-20 selection by absolute effect size reaches 0.9619 mean pairwise Jaccard stability across 5 folds of the 5,000-sequence pool.

The same cross-observer independence holds under the paired 2-mer shuffle control on 200 windows (144 heads each, zero sequence truncation across 19,144 sequences):

StatisticDNABERT-SDNABERT-2-117M
All 144 heads, pAV change-4.36% (p = 5.12e-6)-9.13% (p = 1.57e-16)
All 144 heads, separation AUROC0.62230.7108
Disjoint top-20 scalar Z(pAV)not separated-0.290 SD (p = 6.88e-16)

These replications confirm that pAV captures a cross-model signal rather than an NT-2.5B artifact.

AuthorsOpenReview ↗

Thank you for your insightful focus on confounders and generality (2/2)

2. Biological Confounders, GC Matching, and Two-Sided Quality Control (Weakness 2)

Your concern is that the gap may reflect two different sampling distributions rather than a generative trace. We addressed this at three levels. First, within-sequence: the paired dinucleotide shuffle holds length, GC, repeat counts, and every 2-mer count identical inside each 1 kb natural window, and pAV still drops by 16.2% in the median on NT-2.5B (p = 6.71e-21) and 9.13% in the mean on DNABERT-2 (p = 1.57e-16). Second, across datasets, on the four held-out generators:

Condition (held-out generators)Macro AUROC
Raw0.9018
Low-complexity windows filtered0.8685
GC distributions matched0.8698

Third, we enforced strict two-sided quality control (entropy, 6-mer diversity, repeat, and homopolymer gates) on both classes. On the 5,000-sequence pool, 1,999/2,000 natural and 1,212/3,000 synthetic sequences pass (3,211 total), which removes the low-complexity synthetic artifacts that inflate simple statistics. Each linear model is then refit on filtered data only; our distilled student (seed=42) is rescored and recalibrated on the same rows.

Model5-fold AUROC5-fold TPR@1.3%Held-out AUROCHeld-out TPR@1.3%
CPU-only (47-d)0.960663.70%0.68638.23%
NT-2.5B Observer0.979683.25%0.726116.44%
Fusion Teacher0.980182.60%0.743118.26%
Fusion Teacher plus scalar pAVnot runnot run0.751623.97%
DNABERT-2 scalar Z(pAV)not runnot run0.8136not run
Distilled Student (seed=42)0.982390.02%not runnot run

Removing quality confounders therefore widens, not narrows, the margin of neural methods over statistical baselines.

3. Generalization to Completely Unseen Generator Families (Weakness 3)

We tested this two ways: 5-group Leave-One-Family-Out (LOFO), and three clean external models never seen in any fold (D3LM-from-nt, D3LM-scratch, HyenaDNA-native). External results are reported against both matched out-of-fold naturals (n=2,000) and 2,500 domain-shifted external naturals. Student rows are three seeds.

ModelLOFO AUROCLOFO TPR@1.3%External TPR vs matchedExternal TPR vs shifted
CPU-only0.951867.85%18.83%5.28%
NT-2.5B Observer0.968971.73%93.83%n/a
Fusion Teacher0.969671.69%92.78%63.22%
Distilled Student0.9696 +/- 0.001177.10 +/- 0.80%99.54 +/- 0.16%71.59 +/- 1.70%

Corresponding external AUROC against matched naturals is 0.9346 for CPU-only, 0.9966 for the observer, 0.9965 for the teacher, and 0.9992 for the student. Crucially, the independent 117M BPE observers also catch D3LM-from-nt (0.9927 and 0.9970 vs matched naturals; 0.9724 and 0.9802 vs shifted naturals), which rules out NT-family memorization of a fine-tuned relative.

We deeply appreciate your sharp focus on biological confounders and cross-generator validation. We hope these new cross-observer, quality-controlled, and unseen-generator results resolve your concerns and support raising your score.

Thanks for the authors' detailed responses and additional experiments, which have largely address my concerns, especially W3. Regarding W2, my remaining concern is mainly about the generalizability of the screening ability. The new experiments have ruled out some key confounding factors, but uncontrolled biological differences and differences in data sources could still affect the distinction results. The fact that neural methods outperform statistical baselines doesn’t by itself eliminate this concern. I suggest the authors clearly acknowledge and discuss this limitation, and avoid phrasing that implies the confounding of biological distributions has been completely ruled out.
As for W1, independently reselecting heads addresses the potential dependencies between the discovery set and the test set, but this process still uses labels of natural sequences versus generated sequences for supervised selection. Therefore, the statement that it “break any dependence on supervised selection” is a bit too strong.

Reviewer_o9GLOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper studies positional attention variance (pAV), the variance across query positions of attention-weighted token distance in frozen biological language models. With a supervised, fixed selection of NT-2.5B attention heads, it reports lower mean pAV for six generated DNA corpora and a decrease under dinucleotide-preserving shuffling of natural windows. Aggregate protein and observer comparisons extend this descriptive analysis. Matched detection experiments show that inexpensive entropy and compression features outperform pAV on clean data, while standalone pAV exceeds the compression baseline's macro AUROC at the highest tested substitution rate of 20%. A separate DNA screening study combines observer representations with multiscale sequence statistics and distills the observer contribution into a smaller student, reporting high sequence-level cross-validation AUROC and a finite-batch GPU service benchmark.

Critical strengths
  1. The paired transformation study provides a useful empirical observation. The reported dinucleotide-preserving control changes pAV while retaining length, GC content, and exact dinucleotide counts. The median decrease of 16.2%, with 159/200 windows decreasing, is recoverable from the supplied scores (p. 5, Section 5.2; p. 14, Appendix C, Table 5). This supports arrangement sensitivity beyond the matched statistics for the specified observer and head set, giving the descriptive study substance beyond a classification result.

  2. The matched baselines and negative results make the empirical account informative. The paper reports stronger inexpensive baselines on clean data and a different degradation pattern for standalone pAV under substitution (p. 7, Table 1 and Section 5.4). It also reports that adding pAV to the tested compression classifier does not improve performance (p. 15, Table 6). Together with the explicit separation of the descriptive and screening studies (p. 2; p. 7, Section 5.5), these comparisons clarify the statistic's practical limits.

Critical weaknesses
  1. The descriptive contribution needs stronger independent validation and characterization. The score uses supervised head selection (p. 3, Section 3.1), while original discovery-set membership is incomplete and discovery/test independence is explicitly not established (p. 7, Section 5.3; p. 13, Appendix B). This matters because selected-head macro AUROC is 0.908, versus 0.645 for all heads and 0.615 for random subsets (p. 14, Table 4). Fixing the selected heads for later experiments does not resolve the discovery-independence question. Moreover, the dinucleotide-preserving control establishes sensitivity beyond the matched counts but does not distinguish responses to higher-order local statistics from other positional organization (p. 5, Section 5.2; p. 14, Table 5). In my assessment, the resulting insight remains narrowly characterized, and its independent validation is unresolved. These limitations weaken the contribution without establishing that leakage occurred or that the observation is incorrect.

  2. The screening study does not isolate the incremental value of its neural components. The pipeline combines observer features and multiscale sequence summaries in a linear classifier, then distills its observer-logit contribution (p. 4, Sections 3.3-3.4; p. 16, Appendix F). The paper and supplied artifacts do not report a CPU-only classifier fitted and evaluated on the same 5,000 sequences and folds (p. 8, Table 2; p. 16, Appendix F). Strong entropy/compression results on a separate panel (p. 7, Table 1) motivate this control but cannot establish equivalence across panels. A student trained on labels alone, without teacher targets, is also not reported, so the specific benefit of distillation remains unresolved. The high AUROC supports within-panel discrimination, but the added value over a simpler classifier is undetermined, limiting the demonstrated practical contribution.

Questions for authors
  1. Head-discovery independence: What data and ranking procedure produced the 20 heads, and can available records establish disjointness between discovery and subsequent evaluation (p. 7, Section 5.3; p. 13, Appendix B)? If the membership cannot be recovered, can a training-only selection followed by a separate evaluation test whether the reported pattern persists?

  2. Incremental screening value: On the exact sequences and folds used for Table 2 (p. 8) and the student evaluation (p. 16, Appendix F), how does a separately fitted classifier using only the 47 CPU features compare with the full teacher and student? Is a student trained on labels alone, without teacher targets, available as a control? These comparisons would materially affect the assessment of the neural components' added value and computational cost.

  3. Interpretation of the descriptive finding: Do existing analyses distinguish pAV's response to higher-order local sequence statistics from other aspects of positional organization beyond the dinucleotide-count control (p. 5, Section 5.2; p. 14, Table 5)? Clarifying the available evidence and its limits would help assess the depth of the empirical contribution.

2 comments
AuthorsOpenReview ↗

Thank you for emphasizing discovery independence and matched ablations (1/2)

We thank you for your thoughtful assessment, your recognition of our paired 2-mer transformation controls, and your note on our transparent negative results (Table 6). Your review identified two key empirical gaps: a strictly zero-overlap head discovery check and same-panel 5,000-sequence, 5-fold ablations comparing CPU-only against a label-only student. We executed every requested experiment in full, along with three-seed distillation, two-sided quality-control, and cross-observer validations.

1. Strictly Zero-Overlap Head-Discovery Validation (Weakness 1 and Question 1)

To establish airtight discovery-test independence, we constructed two new balanced discovery splits paired with multi-source natural references. They draw 500 sequences (167/167/166 synthetic samples) and 1,500 sequences (500/500/500) from GenomeOcean-4B and Evo2. We computationally verified zero exact sequence matches and zero reverse-complement 1 kb overlaps between these splits and every held-out evaluation corpus. We then repeated the entire procedure on two independent BPE observers.

Macro AUROC below is measured on the four held-out generators, using the rediscovered heads only as an unfitted scalar Z(pAV) mean.

Observer (heads)Rank transfer (Spearman rho)Scalar Z(pAV), n=500Scalar Z(pAV), n=1,500Random 20-head null
NT-2.5B (640)0.8487 / 0.84730.90330.89440.6148
DNABERT-S (144)0.85940.90570.90400.4518
DNABERT-2-117M (144)0.88370.95510.94560.3866

Our published NT-2.5B head set scores 0.9018 on the same four generators, so independent rediscovery reproduces it. The BPE nulls are separated at empirical p = 0.0010 over 1,000 random subsets. Two further checks support the selection step itself. The rediscovered directional top-20 heads overlap 15/20 with our paper set. Across 5-fold cross-validation on the 5,000-sequence matched pool, top-20 selection by absolute effect size reaches 0.9619 mean pairwise Jaccard stability. Fitting a 20-dimensional logistic regression on |Cohen d| heads instead of the unfitted scalar yields 0.9468 (n=500) and 0.9574 (n=1,500).

AuthorsOpenReview ↗

Thank you for emphasizing discovery independence and matched ablations (2/2)

2. Same-Panel 5,000-Sequence Ablations, Three-Seed Distillation, and Runtime (Weakness 2 and Question 2)

We trained and evaluated matched detectors on the exact same 5,000 sequences and 5 folds (StratifiedKFold, seed=7). Strict QC columns refit each linear model on the 3,211 sequences that pass two-sided quality gates. The student row is our seed=42 checkpoint, rescored and recalibrated on those same rows.

Model (same panel, same folds)AUROCTPR at 1.3% FPRAUROC, strict QCTPR, strict QC
CPU-only (47-d LR)0.986786.00%0.960663.70%
NT-2.5B Observer (3,200-d LR)0.994794.40%0.979683.25%
Fusion Teacher (3,248-d LR)0.994994.20%0.980182.60%
Label-only Student (BCE, ep 6)0.996397.43%not runnot run
Distilled Student (ep 6)0.996497.37%0.982390.02%

On the unfiltered panel every model saturates, so this split alone cannot separate them. Once low-complexity composition cues are removed, the observer leads CPU-only by +19.55 pp at 1.3% FPR.

The label-only control you requested is therefore best judged out of distribution. Below we report 5-group LOFO and three clean unseen external generators (D3LM-from-nt, D3LM-scratch, HyenaDNA-native) scored against 2,500 external naturals, over three seeds (42, 1042, 2042).

ModelLOFO AUROCLOFO TPR@1.3%AI prob. saturationExternal TPR@1.3%
CPU-only0.951867.85%n/a5.28%
Fusion Teacher0.969671.69%n/a63.22%
Label-only Student0.9713 +/- 0.003175.70 +/- 0.86%0.001149.69 +/- 2.83%
CPU+Label Student0.9815 +/- 0.001078.68 +/- 0.88%0.2564 +/- 0.019044.87 +/- 1.37%
Distilled Student0.9696 +/- 0.001177.10 +/- 0.80%0.0264 +/- 0.001171.59 +/- 1.70%

We report this honestly: CPU+Label wins on raw in-pool LOFO AUROC. However, it saturates its AI probabilities near 1.0 on 25.6% of LOFO synthetic sequences, against 2.6% for distillation. That overconfidence collapses its low-FPR transfer. Under domain shift, distillation leads Label-only by +21.91 +/- 3.99 pp and CPU+Label by +26.72 +/- 1.83 pp. Distillation therefore buys calibrated low-FPR transfer, not raw in-pool separation.

Warm-started H200 inference on n=500 windows of 1 kb:

ConfigurationSecondsThroughputPeak VRAMSpeedup
GO-100M Student (bf16)0.2941 +/- 0.00311,700.4 seq/s1,392.7 MB69.09x
Student plus CPU features2.6636187.7 seq/s1,392.7 MB7.63x
NT-2.5B Fusion Teacher20.317424.6 seq/s14,355.9 MB1.00x

3. Higher-Order Local Statistics vs. Positional Organization (Question 3)

We agree that within finite 1 kb windows, very high-order k-mer structure and positional organization cannot be fully orthogonalized. Our paired perturbation hierarchy instead resolves sensitivity across scales on the same 200 natural windows.

Paired controlNT-2.5B (median)DNABERT-2 (mean)
Reverse complement (noise floor)+1.8%+0.3%
2-mer shuffle (exact dinucleotides kept)-16.2%-9.13%
Codon-block shuffle-8.2%-6.80%
Order-1 Markov surrogate-16.2%-9.36%
Order-3 Markov surrogate-19.2%-8.90%
Order-5 Markov surrogate-25.8%-16.87%

Both observers place their largest drop at order 5. Meanwhile 5% to 10% point substitutions preserve pAV despite altering short motifs. We will frame this boundary precisely as sensitivity to multi-scale organization beyond 2-mer and 3-mer composition.

We greatly appreciate your clear and constructive critique, which directly motivated our matched 5,000-sequence ablations and zero-overlap verification. We hope these complete empirical results address your remaining reservations.

Comments on the paper

2 comments
AuthorsOpenReview ↗

Thank You to the SAC, the AC, and All Reviewers

We sincerely thank the Senior Area Chair, the Area Chair, and all three reviewers for your time, careful reading, and constructive guidance. We are grateful both for your recognition of our problem setup and for the sharp questions you raised. Your feedback helped us design stronger controls and clarify the claims in our manuscript.

The goal of this work is to understand how frozen biological foundation models encode structural sequence organization beyond nucleotide frequency. Positional attention variance (pAV) reveals arrangement signatures across synthetic DNA and protein generators that evade local statistics under sequence noise. Beyond interpretability, distilling large observer representations into a lightweight detector makes practical genomic screening fast and accessible.

During the rebuttal period, we completed an extensive suite of new experiments to address every question raised by the reviewers. First, we built strictly zero-overlap head discovery splits on NT-2.5B and confirmed consistent head rankings and transfer. Second, we replicated both head selectivity and unseen-generator detection on two independent 117M-parameter BPE observers, DNABERT-S and DNABERT-2. Third, we enforced strict two-sided sequence quality control and verified that neural advantages widen once composition artifacts are removed. Fourth, we evaluated true Leave-One-Family-Out generalization and three clean unseen external generators under domain shift. Finally, we ran three-seed distillation ablations and warm-started H200 throughput benchmarks, measuring a 69.09x speedup and 10.3x lower GPU memory than the teacher pipeline.

We will publicly release all code, evaluation splits, quality-control pipelines, feature scripts, and trained checkpoints. Building on this release, we plan to develop a mature open-source software platform for the genomics and AI safety communities. Our goal is to help researchers and developers deploy DNA language models and lightweight sequence-auditing tools reliably on modest hardware. We hope these shared resources will support transparent biological data governance and responsible model deployment.

Thank you again to the Senior Area Chair, the Area Chair, and all reviewers for your time, thoughtful evaluation, and service to the community.

AuthorsOpenReview ↗

Summary of the revised paper, with our thanks to the SAC, AC, and reviewers

We sincerely thank the Senior Area Chair, the Area Chair, and all three reviewers for their time and careful reading. Your questions shaped this revision directly, and we are grateful for the constructive discussion.

Summary of revisions

We have uploaded a revised manuscript and an updated numerical supplement. The main changes are:

  1. Two separate contributions. The abstract, introduction, and discussion now present pAV as a diagnostic statistic and the representation-based detector as a screening tool. The detection tables report results with and without pAV.
  2. Head selection. The methods describe the top-20 score as a supervised, label-selected summary. A new section reports head selection repeated on discovery data with zero overlap with any evaluation set, and its transfer to four held-out generators in three observers (Section 5.4, Appendix B).
  3. Arrangement controls. All-head paired controls in two BPE observers, which use no labels and no head selection, appear next to the selected-head results (Section 5.2, Appendix C).
  4. Confounding. We added GC matching, a two-sided quality gate, and natural windows from six eukaryotic genomes. A new limitations paragraph lists the factors that remain uncontrolled, and all claims are scoped to the evaluated generators and natural panels (Sections 5.1 and 6, Appendix F).
  5. Held-out evaluation. We added leave-one-family-out evaluation and three external generators absent from all training folds, with the matching procedure and the leakage and calibration checks (Section 5.7, Appendix G).
  6. Ablations and cost. Same-panel ablations with CPU-only features and a label-only student, three-seed distillation results, and a direct GPU runtime comparison (Sections 5.6 and 5.8, Appendix H).
  7. References. We added citations for DNABERT-2, D3LM, knowledge distillation, dinucleotide-preserving shuffles, and the genome resources used.
  8. Reproducibility. The numerical supplement now includes the records behind every new table, and its script recomputes each reported value.

Why this work matters

Generative models now produce DNA that is increasingly hard to tell apart from natural sequence. As these outputs are shared and deposited, unlabeled synthetic sequences can enter public collections that the community treats as natural. Those collections underpin comparative genomics, functional annotation, and the training of the next generation of biological models. Once mixed in, synthetic records are difficult to trace and remove. We see provenance screening as part of the infrastructure that keeps natural sequence resources reliable. Our work is a step toward measurements and tools for that task.

Our commitment

We thank everyone for their support and encouragement during this discussion. We are committed to open science. Upon publication, we will release our code, evaluation splits, quality-control pipeline, feature scripts, trained checkpoints, and audit scripts. As AI-generated sequence data keeps growing, we hope these resources help the community protect the integrity of natural DNA databases, which are an irreplaceable scientific record.

Thank you again for your time and thoughtful guidance.

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

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