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Under review as a conference paper at ICLR 2027

Watermark Basins: Black-Box Detection of Distilled LLMs

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Abstract

Proprietary language models and their reasoning traces are vulnerable to API-based distillation, where an adversary trains a student model on the teacher model outputs. To provide evidence of distillation, model providers can watermark the teacher outputs, aiming to leave radioactivity in the student outputs. Existing black-box detectors search for such radioactivity using token-level statistics from the suspect model’s outputs. However, token-level signals are not always detectable; for instance, when the teacher model is distilled at a low temperature. In this work, we discover watermark basin, a persistent signal that enables more reliable watermark detection: during fine-tuning, the watermarked teacher traces embed a distinct, watermark key-specific geometric signal in the parameter space that lies orthogonal to the ordinary task-specific fine-tuning subspace. Building on this, we introduce Watermark Basin Alignment (WM-Basin), a black-box watermark detector that queries through the suspect model’s API, without requiring access to its weights or logits. In particular, WM-Basin maps the generated text into gradient representations using a fixed clean probe model, projects out the ordinary fine-tuning task directions, and verifies if the residual gradient is aligned with the watermark basin induced by the watermark key. We evaluate WM-Basin extensively across diverse teacher models and student architectures (spanning 135M to 8.2B parameters) distilled on mathematical reasoning. Under a strict 0.1% false-positive rate, WM-Basin detects 79% of distilled models at n-gram=1 and 45% at n-gram=3, substantially improving the state-of-the-art token-level baseline (29% and 1.3%, respectively). Furthermore, because the watermark signal resides in a persistent basin, it survives aggressive post-distillation modifications, including further fine-tuning, parameter quantization, pruning, and reinforcement-learning post-training

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
Distillation detection, watermarking

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_6td9OpenReview ↗
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Paper summary

This paper proposes Watermark Basin Alignment (WM-Basin), a black-box method for detecting whether a suspect language model was distilled from a watermarked teacher. The key observation is that supervised fine-tuning on watermarked teacher outputs may transfer a watermark-specific signal into the student model's parameters, even when conventional token-level watermark statistics become difficult to detect.

The method first maps text generated by the suspect and reference teacher models into gradient representations using a fixed probe model. It then removes dominant directions estimated from clean models using principal component analysis (PCA) and measures the cosine similarity between the resulting residual gradients. Finally, it ranks the claimed watermark key against independently sampled decoy keys to obtain a non-parametric p-value.

The authors evaluate WM-Basin across 24 student architectures, four teacher models, and four watermarking schemes. They report a true positive rate (TPR) of 79% at a nominal 0.1% false-positive rate (FPR) for unigram detection and 45% for trigram detection, substantially outperforming the sampled-token baseline. Additional experiments investigate distillation temperature, the proportion of watermarked training data, model architecture, watermark schemes, quantization, pruning, continued supervised fine-tuning, and reinforcement-learning post-training.

The paper presents an interesting alternative to token-level watermark detection and provides extensive empirical evidence that watermark-related information can be recovered from the outputs of distilled models. However, the strength of the evidence for the proposed parameter-space geometry, the scope of the statistical guarantees, and the practical cost and generality of the detection procedure require further consideration.

Critical strengths
  1. The paper addresses an important limitation of existing black-box watermark detection: token-level evidence can become weak when teacher outputs are sampled at low temperatures or when exact context recurrence is limited. WM-Basin instead compares gradient representations derived from the suspect's outputs and keyed teacher references. The reported improvement is substantial. At a 0.1% nominal FPR, the paper reports 79% TPR for unigram detection and 45% for trigram detection, compared with 29% and 1.3%, respectively, for the baseline. This provides convincing empirical motivation for investigating representations beyond token-level statistics.

  2. The evaluation spans 24 student architectures, four teachers, four watermarking schemes, and several post-distillation modifications. The authors also examine the effects of the watermarked-data fraction, distillation temperature, and training configuration. Importantly, the paper reports cases where detection deteriorates, including continued SFT and audits outside the distillation domain. These experiments make the submission more informative than an evaluation limited to one student architecture or one watermarking scheme.

Critical weaknesses
  1. The evidence for the proposed watermark basin geometry and its causal interpretation is incomplete. The evidence supporting the proposed watermark basin geometry and its causal interpretation is incomplete. The residual decomposition in Section 2.2 serves only as a diagnostic tool and cannot establish that the residual is uniquely attributable to the watermark or approximately orthogonal to general related task variation, as other differences between the two fine-tuning runs such as stochastic optimization and data order effects may also contribute to the residual, the subsequent directional sweep also fails to independently prove the existence of a persistent basin with the claimed geometry. More critically, there lacks a clear empirical bridge between the white-box geometric observation of actual parameter updates and the gradient alignment signal from the separate probe model used in the black-box WM Basin method.

  2. Limited justification for the key assumptions. The method relies on assumptions about the alignment between watermark-related directions and gradients from a separate probe model. The paper does not sufficiently explain why this alignment should hold or when it may fail.

  3. Unclear scope of the statistical guarantee. The decoy-key test relies on exchangeability assumptions, but the paper does not clearly distinguish guarantees averaged over randomly generated keys from false-positive control for a particular deployed key.

  4. Limited generalization across domains. Detection performance degrades when the audit domain differs from the domain used for distillation. This raises concerns about whether the method generalizes beyond the specific training and auditing settings evaluated.

  5. Unclear sensitivity to probe-model selection. Since the black-box detector relies on gradients from a separate probe model, its performance may depend on the probe model's architecture and training data. The paper does not sufficiently characterize this dependence.

  6. Limited evidence for robustness to alternative explanations. The experiments do not sufficiently establish whether the observed signal is specific to watermarking, rather than a broader artifact of distillation or differences in optimization trajectories.

Questions for authors
  1. How robust is the proposed watermark direction to training randomness? In Section 2.2, the watermark-specific residual is defined by subtracting the projection onto the task update from the total update of a watermarked student. Could the authors repeat this analysis across multiple independently trained clean and watermarked students, with matched initializations and training configurations, to determine whether the residual is reproducible and specifically associated with the watermark key rather than stochastic optimization or data-order effects?

  2. What is the theoretical or empirical evidence that the proposed geometric residual captures watermark-specific information rather than ordinary variation caused by stochastic training or distillation?

  3. How does the white-box geometric analysis justify the proposed black-box detector? In particular, why should gradients from a separate probe model preserve the watermark-related signal identified in the white-box analysis?

  4. How sensitive is the detector to the choice of probe model and audit domain? Can the authors provide evidence that the detection signal remains reliable across different probe models and domain shifts?

4 comments
AuthorsOpenReview ↗

Response to Reviewer 6td9

We appreciate your comments. Below we address each in detail, and we have also updated the draft accordingly (with revision highlighted in blue). We apologize for the unexpected delay, due to additional experiments.

W1: The evidence for the proposed watermark basin geometry and its causal interpretation is incomplete. The evidence supporting the proposed watermark basin geometry and its causal interpretation is incomplete. The residual decomposition in Section 2.2 serves only as a diagnostic tool and cannot establish that the residual is uniquely attributable to the watermark or approximately orthogonal to general related task variation, as other differences between the two fine-tuning runs such as stochastic optimization and data order effects may also contribute to the residual, the subsequent directional sweep also fails to independently prove the existence of a persistent basin with the claimed geometry. More critically, there lacks a clear empirical bridge between the white-box geometric observation of actual parameter updates and the gradient alignment signal from the separate probe model used in the black-box WM Basin method.

W6: Limited evidence for robustness to alternative explanations. The experiments do not sufficiently establish whether the observed signal is specific to watermarking, rather than a broader artifact of distillation or differences in optimization trajectories.

Q1: How robust is the proposed watermark direction to training randomness? In Section 2.2, the watermark-specific residual is defined by subtracting the projection onto the task update from the total update of a watermarked student. Could the authors repeat this analysis across multiple independently trained clean and watermarked students, with matched initializations and training configurations, to determine whether the residual is reproducible and specifically associated with the watermark key rather than stochastic optimization or data-order effects?

Q2: What is the theoretical or empirical evidence that the proposed geometric residual captures watermark-specific information rather than ordinary variation caused by stochastic training or distillation?

We appreciate your cautiousness. We now conduct additional experiments to address your concerns. We have also revised Section 2.2 accordingly.

The central question: is the residual due to the watermark key, or to training noise and the task? We fix a student model distilled from the teacher, and train a second student with the same key and texts, but with a different initialization and/or different data order, and compute each residual against a clean student with the same seed (Qwen2.5-3B, n-gram 3). If the residual were mostly noise, the second student's direction would have no/very little effect on the first student. This is tested in the experiment below.

We report the p-value after moving the first student model by the same distance along different directions. In particular, we include another student model’s watermark direction with a different key, the difference between two clean students, a random direction, and the task direction. These are used as reference points.

We also include the second student's watermark direction, obtained with the same watermark key, and different and/or different data order. As explained above, such a direction should have a high p-value to confirm that the residual is watermark key-specific (not merely noise). We repeat the same experiment 4 times and report the median p-value.

Direction used for the movep-value after the move
The student's own0.91
Second student, same key and texts, same initialization, different data order0.88
Second student, same key and texts, different initialization, same data order0.94
Second student, same key and texts, different initialization, different data order0.91
Student with another watermark key6.6e-11 to 8.1e-11
Difference between two clean students3.7e-10
Random direction5.0e-15
Task direction1.2e-5
AuthorsOpenReview ↗

Response to Reviewer 6td9 (continued, explaining the p-value table)

As shown in the table above, the direction from the second student (with the same key) removes detection under different/same initialization and different/same data order, as the student's own does. In addition, every other direction has little impact on the p-value. So, the residual is not noise. The residual is also separate from the task direction, which gives a negligible p-value. These results confirm that the residual is uniquely attributable to the watermark key, and approximately orthogonal to general related task variation.

Fig. 3 on Page 5 in the main paper also plots the trend (varying the moving distance). We have revised the explanations. In particular, Subfigures A, B, and C show that the seeds have little impact on watermark detection.


We are also happy to take further questions regarding the white-box basin attribution.

AuthorsOpenReview ↗

Response to Reviewer 6td9 (part 2, focusing on the proposed black-box detector)

W2: Limited justification for the key assumptions. The method relies on assumptions about the alignment between watermark-related directions and gradients from a separate probe model. The paper does not sufficiently explain why this alignment should hold or when it may fail.

Q3: How does the white-box geometric analysis justify the proposed black-box detector? In particular, why should gradients from a separate probe model preserve the watermark-related signal identified in the white-box analysis?

These questions are similar to W3 and Q2-3 of Reviewer vPEX.

To clarify:

WM-Basin was a diagnostic tool to discover the existence of watermark key-specific direction in the white-box setting (as demonstrated in the above table). In the black-box setting, we use the same intuition: to discover the watermark key-specific direction in some gradient space. Note that the probe model was not used to reconstruct/align with the suspect’s update. We do the following instead.

We take a separate, clean probe model and compute its gradients on two input texts:

  • A: on the teacher's watermarked traces,
  • B: on the suspect's outputs.

If the gradients for Case A and Case B are similar, it is likely that the suspect model’s output contains the teacher’s watermarked traces, which means that the student is distilled from the teacher. This is because for Case A, the probe model will be updated towards directions that contain the watermark-key specific information. Case B will lead to similar directions, if the suspect's outputs also contains similar watermark traces. (Note that we have filtered out the common task directions using PCA.) We have revised Section 2.3 to include the explanations.

The direct evidence we look for in the black-box detector is therefore cosine similarity between gradients, presented below. For the student model distilled under the claimed watermark key, the similarity should be higher than all other 999 random keys. The table below confirms this evidence (0.494 vs 0.397) and that the gradient alignment is a reliable signal to detect the claimed watermark key. Our main result (Table 1) is also built upon it, demonstrating high TPR under low FPR.

Suspect modelClaimed keyOther 999 keysFlagged at 0.1% FPR
Distilled students (1,200 models)0.4940.39745.4%
Clean models (141 settings × 100 claimed keys)-0.003-0.0070.10%

This table is added to in Appendix F (Page 38, Table 30).

For a better understanding, you may also observe that our detection is key specific, rather than an artifact due to distillation alone. We already test this (see Fig. 4 with n-gram=3 on Page 9): 50 students distilled from the same teacher with the same recipe but under different watermark keys are never flagged by WM-Basin.

This key-specific property also holds in the black-box setting, where we rank gradients according to similarities. In Table 29 on Page 38, we show that training a new student model distilled under the same key still lead to reliable detection (the cosine similarity ranks at the top), while students distilled under other keys and clean students do not.

In conclusion, distillation alone does not produce the signal; the watermark key does.

As we have discussed in the submitted draft, such gradient alignment fails when the detection is out of the distillation task domain, and when the teacher’s output goes through aggressive paraphrasing, and when the student model is continued to SFT on clean data. We have clarified the scope in the abstract and the introduction.

AuthorsOpenReview ↗

Response to Reviewer 6td9 (part 3, focusing on keys and probe models)

W3: Unclear scope of the statistical guarantee. The decoy-key test relies on exchangeability assumptions, but the paper does not clearly distinguish guarantees averaged over randomly generated keys from false-positive control for a particular deployed key.

Our experiment setup follows the established convention of the literature, as in Kirchenbauer et al., 2023; Kuditipudi et al., 2023; Fernandez et al., 2023; Dathathri et al., 2024 and in the radioactivity baseline (Sander et al., 2024). In those papers, the results are averaged over random draw of the watermark key.

Indeed, a fixed deployed key could have a higher FPR than average and we were aware of the discrepancies among keys when we designed the evaluation. For transparency, Fig. 7 on Page 25 reports the performance on individual keys.

To resolve the issue for a particular deployed key, one can calibrate to the empirical FPR. We have added new results in Table 14 on Page 25 and include the discussion on Page 24. Note that a worst-case, fixed deployed key is not an issue specific to our watermark basin detector, it is also presented in other methods. Table 14 shows that even under such worst cases, our method still leads in performance.

W4: Limited generalization across domains. Detection performance degrades when the audit domain differs from the domain used for distillation. This raises concerns about whether the method generalizes beyond the specific training and auditing settings evaluated.

Our detection is strongest in the domain the student was distilled on. This fits our scope: the test checks whether a specific capability of the teacher was distilled rather than any arbitrary task, e.g., computer use or cyber security rather than general translation. We have revised abstract and introduction to state this clearly.

W5: Unclear sensitivity to probe-model selection. Since the black-box detector relies on gradients from a separate probe model, its performance may depend on the probe model's architecture and training data. The paper does not sufficiently characterize this dependence.

Q4: How sensitive is the detector to the choice of probe model and audit domain? Can the authors provide evidence that the detection signal remains reliable across different probe models and domain shifts?

Probe-model selection may seem tricky at the first sight. However, based on our results, the detector works with every probe model we tested, and every probe beats the token baseline. The probe changes the detection rate mainly at a strict FPR; a weaker probe model gives fewer student model detection.

As suggested, we now add some new results. In Appendix. D.6 (Table 18 on Page 30), we test 10 probe models from four model families. At n-gram 1, every probe detects all 87 students that both detectors can score, at every FPR. At n-gram 3 and 0.1% FPR, the probe model could change the TPR from 34% to 89%. Still, every probe result stays above the token baseline (3%).

More insights on variations of the probe model can be found in Table 19 on Page 31, where we show that warming up the probe model can have a more distinguished effect on watermark detection.


We hope the new experiments on the watermark direction, the probe and the per-key thresholds address your concerns about soundness. If they do, we would be grateful if you would consider raising your score.

Reviewer_vPEXOpenReview ↗
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Paper summary

The paper studies black-box detection of language models distilled from watermarked teacher outputs. Existing detectors look directly for an excess of watermark-favored tokens in outputs from a suspect model, which becomes unreliable when contexts do not recur or when the teacher uses low-temperature sampling. The paper proposes WM-Basin. It represents suspect and teacher completions using gradients of a fixed probe model, projects these gradients to a lower-dimensional space, and removes principal directions estimated from clean models. It then computes the cosine alignment between the residual suspect gradient and reference gradients generated under the claimed watermark key and many decoy keys. The rank of the claimed key gives a non-parametric p-value. Experiments cover 24 student architectures, four teachers, four watermark schemes, several sampling temperatures, different audited domains, compression, continued training, and paraphrasing. WM-Basin substantially improves detection over the sampled-token baseline in the default setting, but its black-box signal is strongly degraded by continued clean SFT, domain mismatch, and moderate or aggressive paraphrasing.

Critical strengths
  • WM-Basin addresses a practically relevant setting: the verifier needs neither suspect weights nor logits nor the original distillation data.
  • Mapping outputs into a common probe-gradient space and removing dominant clean-task directions is a clever way to aggregate weak signals that are missed by token-level tests.
  • The gains over the sampled-token baseline are large in the default setting. At a nominal 0.1%0.1\% operating point, the reported overall TPRs are 79%79\% versus 29%29\% for n-gram 11, and 45%45\% versus 1.3%1.3\% for n-gram 33.
  • The method is tested across a broad range of student architectures, teachers, watermark schemes, temperatures, and probe models.
  • The use of disjoint training, build, and test prompt pools avoids an obvious source of leakage.
  • The key-randomization test provides a clean finite-sample marginal validity argument without assuming a parametric distribution for the alignment score.
  • The paper reports important failure modes instead of hiding them, especially domain mismatch, continued SFT, and paraphrasing.
Critical weaknesses
  1. The robustness claim is substantially overstated. Continued clean SFT nearly eliminates black-box detection: at n-gram 33 and a 1%1\% threshold, TPR falls to 1%1\% on the reasoning corpus and 4%4\% on the multilingual corpus. These updates retain a useful model and can improve benchmark accuracy. This conflicts with the abstract's claim that the signal survives further fine-tuning.
  2. Paraphrasing is an effective key-agnostic evasion. Moderate or aggressive rewriting before distillation largely defeats WM-Basin while preserving or improving student utility. This is particularly important because the adversary does not need to know the secret key or the detector.
  3. The “watermark basin” interpretation is not convincingly established. The white-box visualization uses one student and a watermark direction defined from the difference between paired watermarked and clean updates. Moving back along this constructed residual and observing reduced detection is partly expected. The black-box detector, meanwhile, uses gradients in a separate probe model and explicitly does not reconstruct the suspect's update. The results support a key-specific gradient-alignment signal, but not necessarily a shared parameter-space basin.
  4. The false-positive guarantee is marginal over keys. For a fixed key, the appendix reports substantial heterogeneity: at a nominal 5%5\% level, the worst observed key reaches a 26.2%26.2\% empirical false-positive rate. The exact exchangeability argument remains valid when averaging over the random generation of the production key, but it does not provide the same conditional guarantee for a particular deployed key. The empirical null sample is also too small to validate per-key behavior at 0.1%0.1\%.
  5. The detector is operationally expensive and domain-specific. The default setup uses 999 decoy keys, 512 teacher traces per key, approximately 450 GPU-hours to build one reference bank, and roughly 1,900 suspect queries. The bank or task subspace must be rebuilt when important components change. Detection also falls sharply outside the distillation domain.
  6. The headline comparison does not consistently use the strongest baseline. Entropy weighting materially improves the token-level baseline in the appendix. Although WM-Basin still leads in the reported subset, the strongest baseline should be used for the main 1,200-model comparison and headline numbers.
Questions for authors
  1. How do you reconcile the abstract's claim that WM-Basin survives further fine-tuning with Table 7, where continued SFT reduces its TPR to approximately the false-positive rate?
  2. Can you provide direct evidence that probe-gradient alignment tracks the true watermark component of the suspect's weight update across multiple keys, seeds, and student architectures?
  3. What evidence distinguishes a genuine parameter-space basin from key-specific similarity in the output distributions represented by the probe gradients?
  4. Can production keys be screened before deployment to remove poorly calibrated keys? If so, how would you preserve statistical validity after this selection procedure?
  5. Can you evaluate conditional false-positive rates for fixed keys at the claimed 0.1%0.1\% operating point using a substantially larger and fully independent null population?
  6. Why is the entropy-weighted baseline not used for the main cross-architecture comparison? Please report the headline results against the strongest available baseline.
  7. Have you tested combinations of inexpensive evasions, such as low-temperature collection followed by paraphrasing and clean SFT?
  8. What is the expected end-to-end monetary cost of one reference bank and one audit under realistic hosted-model API prices?
6 comments
AuthorsOpenReview ↗

Response to Reviewer vPEX

We really appreciate your comments. Below we address each in detail, and we have also updated the draft accordingly (with revision highlighted in blue). We apologize for the unexpected delay, due to additional experiments.

W1: The robustness claim is substantially overstated. Continued clean SFT nearly eliminates black-box detection: at n-gram and a threshold, TPR falls to on the reasoning corpus and on the multilingual corpus. These updates retain a useful model and can improve benchmark accuracy. This conflicts with the abstract's claim that the signal survives further fine-tuning.

Q1: How do you reconcile the abstract's claim that WM-Basin survives further fine-tuning with Table 7, where continued SFT reduces its TPR to approximately the false-positive rate?

To clarify: Continued SFT removes the signal from the text generated by the student, which the black-box detector reads. However, in the open-weight/white-box setting, the detector can still detect such traces from the student model weight, reaching 98% and 100% TPR at 5% FPR (Table 7 on Page 10). The previous abstract was ambiguous regarding the difference. We have now revised the abstract accordingly: "continued supervised fine-tuning on clean data can remove it from the student's outputs."

W2: Paraphrasing is an effective key-agnostic evasion. Moderate or aggressive rewriting before distillation largely defeats WM-Basin while preserving or improving student utility. This is particularly important because the adversary does not need to know the secret key or the detector.

We agree that strong paraphrasing evades the watermark detection. We already report it as a limitation in the conclusion section. More details are shown in Appendix E.3 (see Table 26 on Page 35).

That said, paraphrasing also effectively evades detection for the token-based baseline (see Table 26). We provide additional insights to the reasons. One may continue from there to build stronger detection methods:

  1. Paraphrasing removes the watermark from the teacher's traces before distillation happening on the student model. In particular, the watermark detector (Sander et al. 2024) flags only 55% / 17% / 7% of the teacher's traces in the rewritten text after mild / moderate / aggressive paraphrasing, but 91% before paraphrasing. As a consequence, little evidence is left for any subsequent radioactivity test.

  2. An ideal white-box verifier should know that the student was trained on the paraphrased teacher outputs rather than the original ones (the ideal column in Table 26 on Page 35). Under such a setup, the detection rate is still high, and is also much higher than the setup where the white-box verifier does not know that the student was trained on the paraphrased teacher outputs (the original column in Table 26).

Therefore, a promising starting point to tackle evasion due to paraphrasing is to make the verifier learn that i) the paraphrasing has already happened, and ii) exactly what the paraphrase has done to the teacher’s output. We defer further investigations to future work.

Q7: Have you tested combinations of inexpensive evasions, such as low-temperature collection followed by paraphrasing and clean SFT?

As suggested, we add the combination results to Table 27 on Page 36. In particular, with low temperature and mild paraphrasing, WM-Basin still detects 40-65% of the students at 5% FPR, against at most 5% for the token-based baseline. Adding clean reasoning SFT then removes the signal for WM-Basin and the baseline, as clean SFT alone already does (see Table 7 on Page 10).

Separate results on low-temperature collection (Table 2 on Page 8, Table 15 on Page 26), paraphrasing (Table 26 on Page 35), and clean SFT and RL (Table 7 on Page 10, Table 23 on Page 34) are also included in the submission.

AuthorsOpenReview ↗

Response to Reviewer vPEX (part 2, focusing on the white-box basin and the black-box detector)

This response focuses on addressing W3, Q2, and Q3, all related to the white-box basin and the black-box detector.

The probe model was not used to reconstruct/align the suspect's update. The white-box parameter-space basin evidence is the high p-value when moving the student model towards certain directions. The black-box, probe model evidence is the high gradient similarity in the probe model's gradient space. We explain their differences in more detail next, and point to the new results in the revised PDF.

Watermark basin: The watermark direction is defined over the student model's weight space such that moving the student model along this direction can change the watermark detection; moving along other directions does not remove the detection.

As you point out, moving back along the student's own residual is partly expected by construction. The revision therefore takes the direction from other students (new Fig. 3 on Page 5; all four students in Fig. 11 on Page 38; Table 28 on Page 37). In the table below, we move a student model along different directions by the same distance, and test each against the white-box detector. The watermark direction taken from a different student, trained on the same watermarked texts, also removes detection, whether the two students differ in seed, LoRA initialization or data order. This confirms that the direction is not tied to one student. On the other hand, other directions (the watermark direction of another key, the difference between two clean students, a random direction, the task direction) do not remove the detection; the task direction removes it only once the model breaks (GSM8K below 30%). The watermark direction is therefore specific to the key and its watermarked texts.

Direction of the move (same distance)White-box p-value (median over 4 students)
watermark direction of the same key (different student, same texts)0.91
watermark direction of the same key, other texts2.0e-7
watermark direction of another watermark key6.6e-11 to 8.1e-11
difference between two clean students3.7e-10
random direction5.0e-15
task direction (clean SFT)1.2e-5

Before the move, every student is detected (p ≤ 2.9e-10); "detected" means p ≤ 0.001.

Black-box detector (via the probe model): the black-box detector is based on a similar idea, but we measure radioactivity in the gradient space of the probe model. In particular, we take a separate, clean probe model and compute its gradients on two input texts:

  • A: on the teacher's watermarked traces,
  • B: on the suspect's outputs.

If the gradients for Case A and Case B are similar, it is likely that the suspect model's outputs contain the teacher's watermarked traces, which means that the student is distilled from the teacher. This is because for Case A, the probe model will be updated towards directions that contain the watermark-key specific information. Case B will lead to similar directions if the suspect's outputs also contain similar watermark traces. Note that we have filtered out the common task directions using PCA. We have revised Section 2.3 to include the above explanation for the black-box detector. New in the revision, we check that a student's outputs alone carry the watermark (Table 29 on Page 38): a new model trained only on the 1,900 answers of a distilled student ranks that student's watermark first among 1,000 candidates, against ranks 122-542 for answers of a clean student or of a student with another watermark.

The direct evidence for the black-box detector is therefore cosine similarity between gradients, presented below. For the student model distilled under the claimed watermark key, the similarity should be higher than with all other 999 random keys. The table below confirms this evidence (0.494 vs 0.397). Our main result Table 1 is built upon it, enabling us to detect distilled models with high TPR under low FPR.

Suspect modelClaimed keyOther 999 keysFlagged at 0.1% FPR
Distilled students (1,200 models)0.4940.39745.4%
Clean models (141 settings × 100 claimed keys)-0.003-0.0070.10%

This table is now added to Appendix F (Page 38, Table 30).

AuthorsOpenReview ↗

Response to Reviewer vPEX (part 3, focusing on keys and costs)

W4: The false-positive guarantee is marginal over keys. For a fixed key, the appendix reports substantial heterogeneity: at a nominal level, the worst observed key reaches a empirical false-positive rate. The exact exchangeability argument remains valid when averaging over the random generation of the production key, but it does not provide the same conditional guarantee for a particular deployed key. The empirical null sample is also too small to validate per-key behavior at.

We follow the convention of existing work (Kirchenbauer et al., 2023; Kuditipudi et al., 2023; Fernandez et al., 2023; Dathathri et al., 2024) as well as the radioactivity baseline (Sander et al., 2024), averaging results over randomly selected keys. We do not bound the false-positive rate of one deployed key, and the revised Section 2.1 refines our scope.

In fact, we were aware of the discrepancies among keys when we designed the evaluation. For transparency, we also report the performance on individual keys in Fig. 7 on Page 25.

To resolve the issue for a particular deployed key, one can calibrate to the empirical FPR. We have added new results in Table 14 on Page 25 to show this. Note that a worst-case, fixed deployed key is not an issue specific to our method, it also appears in other methods. Table 14 (Page 25) shows that even under such worst cases, our method still leads in performance.

Increasing null samples has a very small impact, based on the new results in Table 13 on Page 25, where we increase the null samples from 141 to 252.

Q4: Can production keys be screened before deployment to remove poorly calibrated keys? If so, how would you preserve statistical validity after this selection procedure?

This is a reasonable idea and matters in practice. In fact, it has been discussed in the literature, e.g., TextSeal (Sander et al., 2026) and AutoMark (Gloaguen et al., 2026).

That said, there is no single universally accepted screening for all watermark methods. For our method, the statistical validity of the rank test depends on the exchangeability of the keys, e.g., for 0.1% FPR, we need 1000 keys that are identical and independent. Namely, the random process for generating these 1000 keys should be i.i.d., to ensure exchangeability. Therefore, for any screening process applied to the production watermark key, the same process must be independently and identically applied to the decoy keys as well. For example, if one screens the production key based on its FPR on clean text, then the same process should also be applied to the decoy keys.

Q5: Can you evaluate conditional false-positive rates for fixed keys at the claimed operating point using a substantially larger and fully independent null population?

As suggested, we have conducted more experiments: adding 37 new clean models, for 252 settings from 80 models in total, and measuring the false-positive rate of each fixed key on them. From Table 13 on Page 25, we observe no notable difference in the FPR (252 settings vs 141 settings).

W5: The detector is operationally expensive and domain-specific. The default setup uses 999 decoy keys, 512 teacher traces per key, approximately 450 GPU-hours to build one reference bank, and roughly 1,900 suspect queries. The bank or task subspace must be rebuilt when important components change. Detection also falls sharply outside the distillation domain.

Q8: What is the expected end-to-end monetary cost of one reference bank and one audit under realistic hosted-model API prices?

Most of the cost is paid once, and one audit is cheap. We record about 1,300-1,400 USD for the one-time bank cost (for generating traces under 1000 keys), and about 3 USD for each audit, at 0.1% FPR.

In order to pay less, one can also choose a smaller decoy key size while tolerating a higher FPR, as reported in the table below. We have added this discussion to Appendix C.4 and Table 10 on Page 21.

Decoy key sizeCost (USD)Lowest FPR it can testTPR at 5% / 1% / 0.1% (n-gram 3)
20190–1925%75.8 / - / -
100282–2891%79.7 / 61.9 / -
1,000 (paper)1,320–1,3830.1%80.2 / 65.2 / 45.4

W5 (continued): the detector is domain specific.

We acknowledge that detection is strongest in the distilled domain, and the revised abstract and introduction state this scope: WM-Basin is designed to detect whether a specific capability has been distilled, with detection focused on the domain in which the student was distilled rather than arbitrary out-of-domain tasks.

Reviewer_5zwQOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
3
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Paper summary

The paper proposed an idea: the student model is pushed into a key‑specific watermark basin:

The basin forms an anisotropic (asymmetric) geometric structure: large‑magnitude weight modifications along the task direction do not easily drive the model out of the basin; by contrast, even a small displacement along the watermark direction can erase the watermark signal.

Key property: Common model modifications such as quantization, pruning, and post‑training via reinforcement learning (RL) move weights almost exclusively along the task direction and barely perturb the watermark direction. As a result, the model remains inside the watermark basin and the signal is preserved.

Without knowledge of the watermark key, an adversary can hardly actively push the model out of this basin.

Authors propose an algorithm to detect distillation under the concept of the watermark basin.

Critical strengths

The watermark basin is a reasonable idea.

Critical weaknesses

The concept is reasonable, but the experimental results show that the detection still limited to the in-domain tasks

Questions for authors

How to give definite conclusion whether a model uses distilled texts to avoid false positives? false negatives are less important in such case.

1 comment
AuthorsOpenReview ↗

Response to Reviewer 5zwQ

Many thanks for finding the watermark basin a reasonable idea. In what follows, we address your comments in detail.

Q: How to give a definite conclusion whether a model uses distilled texts to avoid false positives? false negatives are less important in such cases.

In our experiments, we already consider false positive rates bounded by 0.1%, 1%, and 5% (see Table 1 on Page 7). This is controlled via selecting the proper p-value thresholds.

W: The detection is still limited to the in-domain tasks.

We acknowledge that detection is strongest in the domain the student was distilled on. We have revised the abstract and introduction to state this scope (highlighted in blue): WM-Basin is designed to detect whether a specific capability has been distilled rather than arbitrary out-of-domain tasks, e.g., computer use or cyber security rather than general translation.


We hope the answers address your concerns. If they do, we would be grateful if you could show more support for this submission, and we are happy to take further questions.

Comments on the paper

2 comments
AuthorsOpenReview ↗

General response to the AC and all reviewers: new experiments and revisions

We thank all reviewers for their careful reviews, and for finding the setting practically relevant (vPEX), the idea "reasonable" (5zwQ) and "a clever way to aggregate weak signals that are missed by token-level tests" (vPEX), the gains "large" and "substantial" (vPEX, 6td9), the evaluation broad, and reporting "important failure modes instead of hiding them" (vPEX).

We have updated the paper to address the reviewers' concerns. Here is a summary of the most common points.

TL;DR of the revision (in blue in the PDF)

  • Table 1 (Page 7): We added the entropy-weighted token test as a stronger baseline on all 1,200 students (Table 1). We have also updated the headline numbers in abstract. WM-Basin's TPR stays higher than both token tests in every overall setting.

  • Figure 3 (Page 5): We ran new experiments to test whether the watermark direction is real or an artifact of training randomness. Fig. 11 on Page 38 is the detailed illustration of Fig 3., which shows that the direction is set by the key and its training texts: students that differ only in seed, data order or LoRA initialization produce directions that work the same way. We have revised Sec. 2.2 accordingly.

  • We updated the abstract to state explicitly two limits that the introduction and conclusion already reported: continued clean SFT can remove the signal from the student's outputs, and detection is strongest in the distilled domain.

Details on common concerns

C1. Is the watermark basin a real phenomenon? The watermark direction: key or training noise?

Reviewer vPEX and Reviewer 6td9 asked whether the direction reflects the key or training noise, since we took it from the same student we then moved. We now take it from a second student trained on the same key and texts, with a different initialization, data order and dropout.

The new Fig. 3 in Sec. 2.2 shows the result: moving the first student along it removes detection (median p = 0.91 over 4 students), while equally long moves along another key's direction, the difference between two clean students, a random direction or the task direction leave all four students detected (p ≤ 0.001). See Tab. 28 on Page 37. So the key and its texts set the direction, not training noise.

C2. From the basin to the black-box detector.

Reviewers vPEX and 6td9 asked explicitly for a connection between the white-box analysis (Sec. 2.2) and the black-box detector (Sec. 2.3). Sec. 2.3 now explains this link, and two new results test it. A new model trained only on 1,900 answers of a student distilled under key A ranks key A first among 1,000 keys, against ranks 122-542 for answers of a clean or other-key student (Tab. 29 on Page 38). On the 1,200 students, the suspect's probe gradient aligns more with the claimed key than with the other 999 (cosine 0.494 vs. 0.397), while clean models align with none (-0.003 vs. -0.007; Tab. 30 on Page 38).

C3. False positives for one deployed key.

Reviewers vPEX and 6td9 asked whether the false-positive guarantee holds for a fixed, deployed key, and Reviewer 5zwQ asked how to rule out false positives. It holds over the random draw of the key, as in standard text watermarking (e.g., Kirchenbauer et al., 2023; Dathathri et al., 2024) and the radioactivity baseline (Sander et al., 2024), and Sec. 2.1 now says so.

To control a fixed key, we added 111 settings from 37 more clean models (252 settings from 80 models in total; per-key rates fall or stay about the same, Tab. 13 on Page 25) and set each key's own threshold on clean models: on the 111 held-out settings, the average FPR stays near nominal (4.0-5.7% at 5%, 0.5-1.0% at 1%), and WM-Basin still detects 78.6% of students against at most 47.1% for the token tests at 5% FPR, and 53.8% against at most 18.5% at 1% (Tab. 14 on Page 25). So a provider can calibrate to the deployed key.

C4. Detection outside the distilled domain.

All reviewers noted that detection drops outside the domain the adversary distilled (Tab. 5 on Page 9). This fits the use case: distillation campaigns target specific capabilities (Anthropic, 2026a), so a provider audits the capability it wants to protect, such as computer use or cybersecurity, with one reference bank per domain. We now state this scope in the abstract and introduction.

Single-reviewer questions. We also ran new experiments on:

  • combined evasions (low temperature, paraphrasing and clean SFT), and how much watermark survives paraphrasing (App. E.3, Tab. 27 on Page 36; Reviewer vPEX);
  • bank size and cost: the bank needs 512 teacher answers under each of 1,000 keys, once, and each audit about 1,900 suspect queries (App. C.4, Tab. 10 on Page 21; Reviewer vPEX);
  • retraining the probe, or warming up a new one on new same-domain data (App. D.6, Tab. 19(f) on Page 31; Reviewer 6td9).

We hope our responses address your concerns. We would be grateful if you would consider raising your score; we are happy to answer further questions.

AuthorsOpenReview ↗

Kind Reminder: Follow-up on Our Responses

Dear Reviewers and Area Chair,

As the discussion period is approaching its end, we would greatly appreciate it if you could take a moment to review our responses and let us know whether they adequately address your comments and concerns.

If you have any remaining questions or concerns, we would be grateful for your feedback so that we can provide further clarification before the discussion period closes.

Thank you very much for your time and thoughtful consideration.

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

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