acceptodds
Under review as a conference paper at ICLR 2027

Does Distillation Leave a Trace? Source Detectability in Complex Post-Training Pipelines

Abstract

Model post-training pipelines routinely distill data from multiple source models, across different domains and over multiple stages of training. Without proper reporting, it becomes difficult to determine which sources contributed to a released model, raising concerns around IP enforcement and safeguard circumvention. This raises a fundamental question: _do complex post-training decisions affect distillation source detectability_. We present the first systematic study of this question. We build a controlled testbed of 169 models distilled from ten source models across 14 settings, varied across different post-training design decisions. For each source, we test whether the model distilled from it shows greater similarity to that source than reference models trained on alternative sources. We find that while detectability magnitude varies by source and domain, it is largely preserved across post-training choices such as multi-domain distillation, target-model changes, and further on-policy distillation. One key exception: mixing multiple sources within the same domain generally degrades detectability for involved sources, though cross-domain mixing does not. Finally, under more realistic audit assumptions, where reference models do not exactly match the distilled model's pipeline, we find that signals based on the distilled model's likelihoods prove fragile, while stylistic signals remain robust. We release our models, data, and code to support future work on distillation detection and improving our understanding of post-training mechanisms.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
knowledge distillation, synthetic data, model provenance, distillation detection, post-training, model auditing

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
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Paper summary

This paper presents a systematic study of whether distillation source detectability survives realistic post-training pipelines, finding that detectability is largely preserved except under same-domain multi-source mixing, with likelihood-based signals being fragile under realistic audits while stylistic signals remain robust.

Critical strengths

The motivation is highly meaningful. Distillation is indeed a widely used means by which models appropriate the capabilities of other models, and being able to establish a reasonable trace would be a valuable contribution to the research community.

Critical weaknesses

Weakness 1: The claims of this paper are not well matched by what it actually does. The target models used for validation are too small, the task domains are not sufficiently diverse, and the exploration of OPD is far from adequate. Under these conditions, the authors cannot convincingly answer whether distillation leaves a trace.

Weakness 2: Many works on fingerprinting have discussed this problem from their own perspective — for example, that data, or datasets generated by distilled models, may naturally carry fingerprints that cannot be erased through distillation. I think such works should be included in the comparisons of this paper, as they fundamentally study the same traceability problem and are equally applicable to the distillation setting.

Weakness 3: The paper ignores the most obvious adversarial case: a motivated distiller can cheaply wash traces via paraphrasing, back- translation, or semantics-preserving augmentation, which alter lexical form while keeping the content distilled from the source. Such augmented data should still count as distilled, but would evade the paper's robust stylistic signal, directly undermining the IP- enforcement motivation.

Questions for authors

See Weaknesses.

5 comments

We thank the reviewer for their feedback. We address each concern below.

Experimental scope (Weakness 1): Our goal is not to establish whether distillation is universally detectable, but to characterize how source detectability changes across realistic post-training decisions. To study this at breadth, we construct a lineage-known testbed of 166 models spanning ten source models, five student targets (1B–7B), four task domains, and multiple post-training strategies.

Target size. While compute limitations prevent us from distilling over larger base models (e.g., 32B+), small models such as those at the scale we study are still practical and popular targets for distillation. Furthermore, our preliminary trends from 1.5B to 7B indicate detectability is stable and even slightly increases as the target model size increases. However, we will clarify the 7B ceiling as a limitation and agree it would be valuable to see if the trends continue at even larger distillation target scales, but leave this for future work.

Domain diversity. This is an axis we explicitly scale over within our computational limits. Our four domains — code, math, if/chat, and science — are common, high-utility choices for distillations, and we also study how detectability changes when domains are mixed. We agree that coverage over more domains would make interesting future research directions.

In general, we believe these experiments provide useful evidence about the conditions under which distillation leaves detectable traces in a controlled, documented setting. We agree with the reviewer that there is room to scale the testbed further; however, to our knowledge, it already covers the most diverse set of post-training settings studied with known lineage, and we release it to support future extensions. If there is a particular scale, domain, or other aspect the reviewer considers essential, or expects to behave differently, we would welcome the specifics so we can discuss them further or prioritize them in the revision.

We discuss extended OPD results in a followup comment.

Extended OPD case study (Weakness 1): To see whether longer training changes our OPD findings, we conduct an additional experimental OPD run on two of the first stage distilled models (Oss-120b and Ds-v3.2) with Qwen3.5 27B as the OPD source. We increase the number of training prompts to 10000 (10x) and increase the LR to 1e-5 (10x). For the scope of the rebuttal, we limit it to just two first stage distilled models given the time constraint, but for the next iteration of the paper, we plan to expand the longer OPD run to all sources.

We evaluated checkpoints every 1,000 prompts under two reference settings: matched OPD references, which undergo the same second-stage training, and mismatched single-stage references, which do not. Note that in the matched setting, since we only train two longer OPD models (Oss-120b and Ds-v3.2 first-stage distills), we only have one matched null for each audit. Thus, the starting margins for the single-source matched setting will be larger than with the full null set. However, we are more interested in the change in margin over continued OPD, which this proxy experiment illustrates well.

Matched Setting

OPD promptsOss-120b LLOss-120b clsfDs-v3.2 LLDs-v3.2 clsf
0 (first stage only).565.880.668.771
1k.539.859.649.774
2k.518.846.634.771
3k.503.821.622.748
4k.492.803.612.729
5k.485.780.606.718
6k.479.775.601.709
7k.474.766.598.715
8k.471.770.596.704
9k.469.758.594.708
10k.467.757.593.706

Mismatched Setting

OPD promptsOss-120b LLOss-120b clsfDs-v3.2 LLDs-v3.2 clsf
0 (first stage only).087.623.099.217
1k.095.602.109.220
2k.098.586.113.216
3k.099.561.114.201
4k.099.539.114.181
5k.099.519.113.176
6k.098.514.112.166
7k.098.504.112.176
8k.097.506.112.164
9k.097.495.112.165
10k.097.495.112.166

Under matched OPD references, In the matched setting, both LL and classifier margins drop early and then level off as OPD continues. For LL, the drop comes from the reference models becoming better at modeling the unseen audit source traces through OPD even while the audited model’s fit to its own source varies little. This narrows but does not fully close the gap, as seen by the narrowing slowing with continued OPD. For the classifier, the drop comes from the audited model, whose first-stage lexical signal is partly washed out by OPD towards the second stage source. However, this also levels off, which we suspect is due to rollouts being on-policy and the divergence to the teacher converging.

Under **mismatched single-stage references, likelihood margins remain relatively stable, consistent with our original results, while classifier margins decline noticeably then similarly level off with continued OPD **. This supports the observations from the matched settings, as the OPD leaves the audited model’s fit on its first-stage source intact, whereas it slightly drifts away lexically from the first-source (though the drift levels out).

Downstream performance: We also evaluated coding performance before and after extended OPD using HumanEval and HumanEval+ (greedy pass@1):

SourceBenchmarkSFTOPD 10k
OSS-120BHumanEval.433.506
HumanEval+.421.439
DS-v3.2HumanEval.659.738
HumanEval+.604.689

Both students improve on these coding benchmarks, suggesting that the longer OPD stage changes model capability while earlier source traces remain detectable.

We will include new results/claims with the complete longer OPD model set in the next revision of the paper

Relationship to fingerprinting work (Weakness 2): We agree this literature is closely related and will expand our discussion of it. We clarify that our three similarity scores are directly drawn from natural fingerprinting works: the classifier is a common technique for learning lexical source idiosyncrasies [1, 2], the likelihood score is directly drawn from [3, 4], and the embedding score closely resembles the semantic representation intuition from [5]. We describe these in Section 3.2 and will make the connection explicit in the Related Works section. We highlight that watermarking and deliberate fingerprinting strategies also tackle the same traceability problem, but require the source owner to embed the signal in advance and support auditing only from the owner’s side. We discuss this direction in the Related Works section as well. Our scope is black-box signals that do not assume prior intervention by the source owner and we believe the three scoring methods provide good coverage over the (lexical, logit, and semantic) surfaces where detection signals may exist. We save other directions, such as watermarking, to future work. If the reviewer considers a specific method within this scope to be missing, we would be glad to discuss them and, where feasible, evaluate it on our testbed.

Adversarial trace removal (Weakness 3): We agree that this is a practical threat model and our study currently does not test it. We clarify that deliberate adversarial trace removal is outside our scope; for this work, we focus on understanding how common post-training decisions impact detectability of natural, non-adversarial distillation. Our setting is a prerequisite to studying specific subsettings such as adversarial rewriting since whether an adversary can remove detectability only becomes a well-posed question once it is established where benign pipelines preserve one. Some recent work [6] also notes that source-specific token choices largely persist under rewriting by another model, which makes the trade-off between detectability, paraphrase strength, and downstream performance an interesting follow-up direction. We will discuss the non-adversarial scope in the limitations section and acknowledge it as future work.

[1] Sun, M., Yin, Y., Xu, Z., Kolter, J. Z., & Liu, Z. (2025). Idiosyncrasies in large language models. arXiv. https://arxiv.org/abs/2502.12150

[2] Panfilov, A., Schmotz, D., Shumailov, I., Beurer-Kellner, L., Schaeffer, J., Prabhu, A., Geiping, J., & Andriushchenko, M. (2026). Stealing reasoning traces from proprietary LLM APIs. arXiv. https://arxiv.org/abs/2608.09867

[3] Rawat, R., Chen, S., Anand, A., Duan, M., Rotsted, B., & Min, S. (2026). Reference-based distillation detection in LLMs. arXiv. https://arxiv.org/abs/2607.09692

[4] Liu, K., Yan, S., Miao, R., Wang, B., Shen, C., Zhang, J., & Ye, J. (2026). Where did this sentence come from? Tracing provenance in LLM reasoning distillation. arXiv. https://arxiv.org/abs/2512.20908

[5] Wu, Z., Zhao, H., Wang, Z., Guo, J., Wang, Q., & He, B. (2026). LLM DNA: Tracing model evolution via functional representations. arXiv. https://arxiv.org/abs/2509.24496

[6] Tang, Y.-C., & Yen, A.-Z. (2026). Imprinting: Knowledge distillation can shift student behavior. arXiv. https://arxiv.org/abs/2610.18517

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

The paper studies whether the source of distillation remains detectable across source mixtures, domain mixtures, different target models, and a subsequent on-policy-distillation stage. It constructs a lineage-known testbed and compares source-continuation likelihood with a lexical source classifier, using margins relative to reference students trained from alternative sources. It finds source- and domain-dependent detectability, degradation under same-domain source mixing, and different sensitivity of the two scores to reference-model mismatch.

Critical strengths
  1. The lineage-known experimental design addresses an important limitation of attribution studies on real models whose training history is unknown. Varying sources, domains, targets, and training stages within a documented construction is a useful empirical contribution.

  2. The paper treats reference-model construction as part of the audit problem and reports negative results as well as successful detections. The mismatched-reference, ineffective-embedding, and prefix-probing experiments help reveal which conclusions depend on the score and audit setup.

Critical weaknesses
  1. The central source-mixing comparison is not adequately separated from changes in the reference distribution. Section 3 motivates students and null models that differ only in source, but Figure 3 compares 54k/90k mixture students with 18k single-source reference students; the fixed-total 18k mixture also changes each source's contribution. The cross-domain source mixtures use related unmatched comparisons. The paper itself shows that cardinality/capability mismatch shifts likelihood margins and explicitly discusses this confound in Appendix C.3. Consequently, the likelihood changes do not uniquely identify the effect of mixing, and near-preservation can also conceal offsetting effects. The classifier results are useful complementary evidence, but their dependence on co-source negatives and the stronger prefix probe should be considered before generalizing to detectability itself.

  2. The audit's calibration and the stability of small effect differences are not established. Positive-source margins under the known training lineages do not demonstrate false-positive behavior when the candidate source is absent; increasing a true-positive margin under mismatch is not itself a measured false positive. Negative-control audits with independent reference models are needed, alongside justification that the sign-flip test's stated assumptions hold and adequate multiplicity/uncertainty reporting. Such controls must not include the audited checkpoint as its own reference, which would mechanically constrain the margin. The single-seed training protocol and single sampled response per probe also leave no training/resampling noise floor for changes of a few hundredths. These limitations matter for the main robustness and fragility conclusions, rather than only for significance reporting.

Overall assessment: I currently lean against acceptance, narrowly. The study and testbed are useful, but the main mixing comparison and the interpretation of audit robustness require stronger control of reference mismatch and statistical calibration. Matched references, valid negative controls, and a measured variation scale could materially change my assessment.

Questions for authors
  1. Can matched mixture references be constructed by replacing the audited source while preserving co-sources, total cardinality, and training recipe? Which main conclusions survive a matched comparison?
  2. What false-positive rates and margin distributions are obtained when auditing a candidate source absent from the student? Please use reference checkpoints independent of the audited checkpoint and report calibration under both matched and mismatched settings.
  3. Please quantify training-seed and response-resampling variation for representative configurations, report the randomization count and numerical p-values, and clarify how the selected probe population affects the inferential claim.
  4. Does the cross-target likelihood effect persist with a common text-level normalization, such as per-byte likelihood? A calibrated/reference-normalized score would help determine how much fragility belongs to the raw per-token score.
  5. Given the explicitly limited OPD setting in Section 4.4, how much did this stage change capability or output behavior? Please also provide an inventory reconciling the advertised model count and settings.
6 comments

We thank the reviewer for the detailed assessment and constructive suggestions. We conducted additional experiments to address the concerns about reference construction and statistical calibration.

Matched multi-source references (Weakness 1; Question 1): We agree that comparing multi-source models against single-source references may construe mixing effects on source detectability with other factors such as different data cardinality. To address this, we trained additional matched multi-source models, fixing two sources {Oss-20B, QwQ} and varying the third across five sources {Glm, Olmo, Qwen3, Exaone, Ds-v3.2}. Each model uses 54k examples (18k per source) with the same training setup, differing only in the third source. We also recomputed the single-source baselines using the same five candidate sources.

SourceLL: Single → MixtureClassifier: Single → Mixture
Glm.282 → .182.740 → .169
Olmo.154 → .061.424 → .052
Qwen3.160 → .118.522 → .099
Exaone.144 → .109.329 → .179
Ds-v3.2.078 → .097.225 → −.073

We find that same-domain source mixing still weakens detectability under matched references. Classifier margins decrease for all five sources (0.15–0.57); likelihood margins decrease for four of five (0.035–0.10), with a small increase for Ds-v3.2. For the classifier, mixing still dilutes the source’s lexical characteristics in the student’s outputs. For likelihood, the student’s own fit to the audited source changes little, dropping only for Glm, the source most dissimilar to its co-sources. We find the margin shrinks mainly because the matched references fit the unseen audit source’s traces better than the single-source references do. This is particularly influenced by how well the co-source can help model the audit source, e.g. substantially for Olmo, and not at all for Ds-v3.2. Likelihood detectability under mixing can therefore fall in two ways: the distilled model fits the audit source dissimilar to its co-sources less well, or the co-sources make the audited source easier for references to model. Both depend on which sources are mixed, consistent with Section 4.1.

We also repeated the prefix-probing experiment from Appendix C.4 in the matched setting:

Sourcesingle-sourceno prefixprefix16margin difference
Glm.740.169.385.216
Ds-v3.2.225−.073.119.192
Exaone.329.179.277.098
Qwen3.522.099.088−.011
Olmo.424.052.006−.046

It improves classifier margins for Glm (+0.216), Ds-v3.2 (+0.192), and Exaone (+0.098), but not Qwen3 (−0.011) or Olmo (−0.046). Again, while prefix probing can extract source-specific lexical characteristics that can recover the detectability gap, cases like Qwen3 and (especially) Olmo where the audit source is similar to co-source can make audit source idiosyncrasies harder to surface, making prefix probing less effective.

Co-source negatives in classifier training. We retrained the source classifiers without the two fixed co-sources (Oss-20B, QwQ) as negative examples. The classifier-margin drops remain substantial:

SourceSingle → Mixture (co-sources excluded)
GLM.75 → .09
OLMo.58 → −.02
Qwen3.48 → .01
EXAONE.39 → .19
DS-v3.2.25 → −.07

If the presence of co-source negatives in classifier training was playing a large role in the classifier margin drops, we’d expect the margin differences to be smaller than with the original classifiers. This suggests the lexical characteristics of sources in a mixture are indeed diluted, and margin drops are not simply inflated by how the classifiers were constructed.

"The cross-domain source mixtures use related unmatched comparisons." We agree that matched references would be the ideal complement to Section 4.2. Training them was not feasible during the rebuttal, so we will add them in the next iteration alongside the unmatched comparisons. We do highlight two existing results that further suggest the preservation we report is not an offsetting effect of cardinality mismatch. First, the mismatch is on additional out-of-domain traces, and Figure 4 shows that 54k such traces from the audited source itself (4d-72k) raise margins by under 0.02 on average in every domain. The 36k here come from other sources, so any offset would likely be smaller. Second, the classifier demonstrates robustness to cardinality mismatch (Figure 15) and shows the clearest per-source preservation.

These experiments are smaller in scale than those in the paper because of time and compute limits during the rebuttal. We will train the remaining 3-source mixtures (still fixing Oss-20B and QwQ) in the code domain for the next iteration, as well as performing the matched experiment for the multi-source, multi-domain setting.

Negative controls and false positives (Weakness 2; Question 2; part of Question 3): We agree that positive-source margins alone do not establish false-positive behavior. We therefore audited students not trained on the candidate source, with neither the audited checkpoint nor the candidate source’s own distilled models among the references.

For the matched setting, we count FPs across 4 different settings (with their own subsetting counts in parentheses) — single-source (4), mixed domain (8), target (4), cardinality (3) — with 90 audits each, totaling 1710 negative control audits. We report the merged FPR for brevity as the FPR across methods is about the same per setting; we do report the range of FPRs for reference. For the mismatched setting, we show a subset of settings (mismatched target, size, cardinality, and multi-source) to illustrate where FPRs noticeably increase. Alongside the FPRs per method, we include the margin distribution over the audits (represented as the median with the 5th-95th percentiles). We will include a full breakdown of FPR over all settings with their margin distributions as figures in the next iteration of the paper.

SettingLL FPRLL margin, median (5th, 95th)Classifier FPRClassifier margin, median (5th, 95th)
Matched references (19 settings, 1,710 audits)10.7% (10.0% - 11.1%)−.365 (−.805, .093)7.1% (4.4% - 7.8%)−.458 (−.853, .098)
Mismatched target (Qwen-1.5B vs. Llama-1B)26.7%−.276 (−.627, .235)5.6%−.519 (−.872, .115)
Mismatched size (7B vs. 1.5B)20.0%−.439 (−.843, .231)7.8%−.511 (−.864, .127)
Mismatched data size (18k vs. 1.5k)27.8%−.271 (−.607, .220)6.7%−.484 (−.889, .168)
Multi-source vs. single-source refs22.9%−.056 (−.350, .045)0.0%−.420 (−.787, −.220)

We find that likelihood-based audits produce more false positives when the audited student is more capable than its references, consistent with our findings where FNR increases when the distilled model is less capable than the references. Classifier-based audits are largely unaffected (bar the multi-source case, where FPR drops to 0%). However, even with matched references, both methods produce false positives. For example, under LL, the 10% of flagged audits are typically cases where the model was distilled from a source similar to the audited one (e.g., Oss-20b ↔ Oss-120b). Similar cases occur with the classifier method.

“...justification that the sign-flip test's stated assumptions hold…” We clarify that, because each margin subtracts the maximum over references, our test is conservative under exchangeability: a model not distilled on the audit source rarely beats the other references (evidenced by the margin distributions). Technically, this breaks the symmetry assumed in footnote 1, but in the direction that reduces false positives. As mentioned above, the FPs observed generally involve distilled models with sources similar to the audit source or when capability mismatches occur due to mismatches between the audited and reference models (for LL mostly), reflecting properties of the margin measure rather than the test being miscalibrated.

“...and adequate multiplicity/uncertainty reporting…report the randomization count and numerical p-values…” We use Π=106\Pi = 10^6 random permutations per test, giving a p-value floor of 10−610^{-6}. We will state this in Algorithm 1 and add a table of numerical p-values for every reported experiment in the Appendix. For multiplicity, we use Bonferroni correction over all audits (658 for LL, 678 for classifier) under a given method. We highlight that most significant results lie at the p-value floor of 10−610^{-6} and remain significant even under correction. For those that don’t, these are the tests where the margin is very small, such as when the audit source is very similar to one of the reference sources (e.g., the R1-distills) or the margin decreased as a result of a post-training decision such as source mixing. We’ll make sure to flag these cases as weakly detectable, but our main conclusions do not depend on them.

Our analysis framework in Section 3 is designed to study how post-training decisions affect the detectability of a source that was used, not to serve as a calibrated attribution method. We will clarify this distinction in the revision, state that a positive margin alone does not guarantee correct source attribution, and include all results above. We also release our testbed so calibrated audit methods can be developed against it.

Training and response-sampling noise (Weakness 2; Question 3): We agree that smaller margin differences require a measured variation scale. Since repeating every training configuration is computationally expensive, we first ran a smaller experiment to estimate this cross-training-run variation.

For two sources (Oss-120B and Ds-v3.2), we randomly sampled five new 4.5k subsets from the original 18k code traces and distilled a model on each, keeping the training setup fixed. Including the original 4.5k student, we report the mean and standard deviation across six models:

SourceLL margin (mean ± SD)Classifier margin (mean ± SD)
Oss-120B.104 ± .004.591 ± .009
Ds-v3.2.070 ± .006.216 ± .007

The observed variation is small, with a maximum standard deviation of 0.006 for likelihood and 0.009 for the classifier. We use these estimates to revisit the smaller margin differences reported in the paper. Specifically, we use 222\sqrt{2} as the noise interval: 2\sqrt{2} because each effect size is a difference between two distilled models’ margins, and 2 for an approximately 95% range. We verify “preservation” (no clear detectability degradation) claims by showing that the margin differences lay within this noise interval, and we verify detectability degradation claims by showing the magnitude of the drop lies outside the interval.

Most findings remain unchanged. However, we will refine two observations. First, the matched 3B and 7B likelihood margins (Section 4.3) show small increases rather than remaining unchanged. Second, classifier margins for science in the mixed-source, mixed-domain setting (Section 4.2) decrease by more than the reference noise interval, an exception to the per-source preservation we report. We speculate the science prompts may overlap most with other domains, so science-specific lexical behavior is elicited less cleanly. We will make sure to acknowledge this in the next iteration of the paper.

We clarify that we use the average margin differences across sources relative to the noise interval to establish systematic effects. We also acknowledge the interval is measured only in the single-source setting, but we consider it appropriate because our effect sizes are measured as differences from a matched single-source audit. We plan to finish the reference noise floor establishment for the remainder of the sources for the next round of the paper, as well as train resampled variants for 1-2 configurations for other settings such as multi-source and larger target. We will report this full analysis in the appendix.

Noise intervals from response sampling. We regenerated outputs at temperature 0.7 to get a sense of the variation scale from resampling. In the code single-source setting with Qwen 1.5b models, we sample continuations from the same probe set 2 additional times. Likelihood requires resampling the source models’ continuations; due to serving limitations during the rebuttal period, we perform resampling over a subset of the smaller sources. The classifier requires only the students’ generations, so we resampled all ten. Each standard deviation is over three samples.

SourceClassifier margin (mean ± SD)
Olmo.354 ± .008
QwQ.254 ± .006
Exaone.363 ± .004
Ds-v3.2.195 ± .006
Qwen3.355 ± .016
R1-Llama.017 ± .003
R1-Qwen−.002 ± .004
Glm.612 ± .005
Oss-120B.633 ± .003
Oss-20B.471 ± .007
SourceLL margin (mean ± SD)
QwQ.041 ± .0006
R1-Qwen.006 ± .0002
Exaone.141 ± .0003
Oss-20B.102 ± .0010
Glm.272 ± .0010
Oss-120B.115 ± .0002

The noise from response resampling is noticeably smaller than noise from training run randomness for LL, and comparable for classifiers. We will complete the response resampling experiments before the next iteration of the paper.

...how the selected probe population affects the inferential claim. Our probes are the highest-ranked prompts under the heuristic defined in Appendix. B.2.2 chosen from a larger random pool, so our significance claims hold for prompts selected to elicit source-distinguishing behavior rather than for arbitrary prompts. We will explicitly state this is in Section 3.3. We also clarify that only source-model responses are used in the selection process, so chosen prompts do not directly favor the true distilled models over references. We also compare this method against randomly sampled probes in Appendix B.2.4. If the reviewer had a different aspect of probe selection in mind to discuss, we would be glad to address it.

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

This paper investigates how multi-source, multi-domain, and multi-stage post-training affects the detectability of distillation sources. The authors construct a controlled testbed of 169 distilled models from ten source models across 14 settings, using likelihood scores and stylistic classifiers to detect source traces. The results show that source traces generally persist, but mixing sources within the same domain weakens detection, while likelihood-based signals are more sensitive than stylistic classifiers to reference-model mismatch.

Critical strengths
  1. The research question is practically relevant. Identifying distillation sources in complex training pipelines is important for model provenance and training transparency.

  2. The experiments are comprehensive. The authors systematically examine source mixtures, domain mixtures, target models, and subsequent training, providing valuable empirical findings.

  3. The analysis of reference-model mismatch is insightful. It shows how model capability and training data size can confound likelihood-based detection, offering useful guidance for practical audits.

Critical weaknesses
  1. Multi-source models are mainly compared against single-source references, which may differ not only in source identity but also in the number of sources, total training data, and training steps. I suggest adding reference models with the same data size and mixture configuration, replacing only the source being audited.
  2. The subsequent-training experiment is limited in intensity. The second-stage OPD uses only 1,000 problems with a learning rate of 10−610^{-6}. The preservation of source traces may partly reflect limited changes to the model. I suggest varying the training intensity and reporting changes in task performance.
  3. Robustness to training randomness is not sufficiently established. The paper does not report results across multiple independent training seeds for the key settings, leaving it unclear whether some smaller differences in detectability are stable.
Questions for authors
  1. Does the finding that same-domain source mixing weakens detection still hold when reference models use the same data size and mixture configuration, replacing only the source being audited?

  2. What are the false-positive rates of the two detection methods on models not trained on the audited source, particularly when reference models are mismatched?

  3. How much does the second-stage OPD change model performance or behavior? Do earlier source traces remain detectable with more training problems or update steps?

5 comments

We thank the reviewer for the helpful suggestions. We conducted additional experiments to address the concerns.

Matched multi-source references (Weakness 1; Question 1): We agree that comparing multi-source models against single-source references may construe mixing effects on source detectability with other factors such as different data cardinality. To address this, we trained additional matched multi-source models, fixing two sources {Oss-20B, QwQ} and varying the third across five sources {Glm, Olmo, Qwen3, Exaone, Ds-v3.2}. Each model uses 54k examples (18k per source) with the same training setup, differing only in the third source. We also recomputed the single-source baselines using the same five candidate sources.

SourceLL: Single → MixtureClassifier: Single → Mixture
Glm.282 → .182.740 → .169
Olmo.154 → .061.424 → .052
Qwen3.160 → .118.522 → .099
Exaone.144 → .109.329 → .179
Ds-v3.2.078 → .097.225 → −.073

We find that same-domain source mixing still weakens detectability under matched references. Classifier margins decrease for all five sources (0.15–0.57); likelihood margins decrease for four of five (0.035–0.10), with a small increase for Ds-v3.2. For the classifier, mixing still dilutes the source’s lexical characteristics in the student’s outputs. For likelihood, the student’s own fit to the audited source changes little, dropping only for Glm, the source most dissimilar to its co-sources. We find the margin shrinks mainly because the matched references fit the unseen audit source’s traces better than the single-source references do. This is particularly influenced by how well the co-source can help model the audit source, e.g. substantially for Olmo, and not at all for Ds-v3.2. Likelihood detectability under mixing can therefore fall in two ways: the distilled model fits the audit source dissimilar to its co-sources less well, or the co-sources make the audited source easier for references to model. Both depend on which sources are mixed, consistent with Section 4.1.

We also repeated the prefix-probing experiment from Appendix C.4.

Sourcesingle-sourceno prefixprefix16margin difference
Glm.740.169.385.216
Ds-v3.2.225−.073.119.192
Exaone.329.179.277.098
Qwen3.522.099.088−.011
Olmo.424.052.006−.046

It improves classifier margins for Glm (+0.216), Ds-v3.2 (+0.192), and Exaone (+0.098), but not Qwen3 (−0.011) or Olmo (−0.046). Again, while prefix probing can extract source-specific lexical characteristics that can recover the detectability gap, cases like Qwen3 and (especially) Olmo where the audit source is similar to co-source can make audit source idiosyncrasies harder to surface, making prefix probing less effective.

Given rebuttal compute limits, we tested the above five mixtures. We plan to extend this to the remaining sources and include both mat comparisons in the revision.

Extended OPD experiments (Weakness 2; Question 3) To see whether longer training changes our existing OPD findings, we conduct an additional experimental OPD run on two of the first stage distilled models (Oss-120b and Ds-v3.2) with Qwen3.5 27B as the OPD source. We increase the number of training prompts to 10000 (10x) and increase the LR to 1e-5 (10x). For the scope of the rebuttal, we limit it to just two first stage distilled models given the time constraint, but for the next iteration of the paper, we plan to expand the longer OPD run to all sources.

We evaluated checkpoints every 1,000 prompts under two reference settings: matched OPD references, which undergo the same second-stage training, and mismatched single-stage references. Note that in the matched setting, since we only train two longer OPD models (Oss-120b and Ds-v3.2 first-stage distills), we only have one matched null for each audit. Thus, the starting margins for the single-source matched setting will be larger than with the full null set. However, we are more interested in the change in margin over continued OPD, which this proxy experiment illustrates well.

Matched Setting

OPD promptsOss-120b LLOss-120b clsfDs-v3.2 LLDs-v3.2 clsf
0 (first stage only).565.880.668.771
1k.539.859.649.774
2k.518.846.634.771
3k.503.821.622.748
4k.492.803.612.729
5k.485.780.606.718
6k.479.775.601.709
7k.474.766.598.715
8k.471.770.596.704
9k.469.758.594.708
10k.467.757.593.706

Mismatched Setting

OPD promptsOss-120b LLOss-120b clsfDs-v3.2 LLDs-v3.2 clsf
0 (first stage only).087.623.099.217
1k.095.602.109.220
2k.098.586.113.216
3k.099.561.114.201
4k.099.539.114.181
5k.099.519.113.176
6k.098.514.112.166
7k.098.504.112.176
8k.097.506.112.164
9k.097.495.112.165
10k.097.495.112.166

Under matched OPD references, both LL and classifier margins drop early and then level off as OPD continues. For LL, the drop comes from the reference models becoming better at modeling the unseen audit source traces through OPD even while the audited model’s fit to its own source varies little. This narrows but does not fully close the gap, as seen by the narrowing slowing with continued OPD. For the classifier, the drop comes from the audited model, whose first-stage lexical signal is partly washed out by OPD towards the second stage source. However, this also levels off, which we suspect is due to rollouts being on-policy and the divergence to the teacher converging.

Under mismatched single-stage references, likelihood margins remain relatively stable, consistent with our original results, while classifier margins decline noticeably then similarly level off with continued OPD. This supports the observations from the matched settings, as the OPD leaves the audited model’s fit on its first-stage source intact, whereas it slightly drifts away lexically from the first source (though the drift levels out).

Downstream performance: We also evaluated coding performance before and after extended OPD using HumanEval and HumanEval+ (greedy pass@1):

SourceBenchmarkSFTOPD 10k
OSS-120BHumanEval.433.506
HumanEval+.421.439
DS-v3.2HumanEval.659.738
HumanEval+.604.689

Both students improve on these coding benchmarks, suggesting that the longer OPD stage changes model capability while earlier source traces remain detectable.

We will include new results/claims with the complete longer OPD model set in the next revision of the paper

Robustness to training randomness (Weakness 3): We agree that measuring variation across training runs is important, especially when comparing small differences in detectability. Since repeating every setting would require substantial compute, we ran a smaller experiment to estimate this variation.

For two sources (Oss-120B and Ds-v3.2), we randomly sampled five new 4.5k subsets from the original 18k code traces and distilled a model on each, keeping the training setup fixed. Including the original 4.5k student, we report the mean and standard deviation across six models:

SourceLL margin (mean ± SD)Classifier margin (mean ± SD)
Oss-120B.104 ± .004.591 ± .009
Ds-v3.2.070 ± .006.216 ± .007

The observed variation is small, with a maximum standard deviation of 0.006 for likelihood and 0.009 for the classifier. We use these estimates to revisit the margin differences reported in the paper. Specifically, we use 22σ2\sqrt{2}\sigma as the noise interval: 2\sqrt{2} because each effect size is a difference between two distilled models’ margins, and 2 for an approximately 95% range. We verify “preservation” (no clear detectability degradation) claims by showing that the margin differences lay within this noise interval, and we verify detectability degradation claims by showing the magnitude of the drop lies outside the interval.

Most findings remain unchanged. However, we will refine two observations. First, the matched 3B and 7B likelihood margins (Section 4.3) show small increases rather than remaining unchanged. Second, classifier margins for science in the mixed-source, mixed-domain setting (Section 4.2) decrease by more than the reference noise interval, an exception to the per-source preservation we report. We speculate the science prompts may overlap most with other domains, so science-specific lexical behavior is elicited less cleanly. We will make sure to acknowledge this in the next iteration of the paper.

We clarify that we use the average margin differences across sources relative to the noise interval to establish systematic effects. We also acknowledge the interval is measured only in the single-source setting, but we consider it appropriate because our effect sizes are measured as differences from a matched single-source audit. We plan to finish the reference noise floor establishment for the remainder of the sources for the next round of the paper, as well as train resampled variants for 1-2 configurations for other settings such as multi-source and larger target, and add it to the appendix.

False-positive rates (Question 2): We also evaluated false positives by auditing students that were not trained on the candidate source, ensuring that the audited student was never included in its own reference set.

For the matched setting, we count FPs across 4 different settings (with their own subsetting counts in parentheses) — single-source (4), mixed domain (8), target (4), cardinality (3) — with 90 audits each, totaling 1710 negative control audits. We report the merged FPR for brevity as the FPR across methods is about the same per setting. For the mismatched settings, we show a subset of settings (mismatched target, size, cardinality, and multi-source) to illustrate where FPRs noticeably increase. We will include a full breakdown of FPR over all settings in the next iteration of the paper.

SettingLL FPRClassifier FPR
Matched references (1,710 audits)10.7% (10.0% - 11.1%)7.1% (4.4% - 7.8%)
Mismatched target (Qwen-1.5B vs. Llama-1B)26.7%5.6%
Mismatched size (7B vs. 1.5B)20.0%7.8%
Mismatched cardinality (18k vs. 1.5k)27.8%6.7%
Multi-source vs. single-source refs22.9%0.0%

We find that likelihood-based audits produce more false positives when the audited distilled model is more capable than its references, consistent with our findings where FNR increases when the distilled model is less capable than the references. Classifier-based audits are largely unaffected (bar the multi-source case, where FPR drops to 0%).

However, even with matched references, both methods produce false positives. For example, under LL, the 10% of flagged audits are typically cases where the model was distilled from a source similar to the audited one (e.g., Oss-20b ↔ Oss-120b). Our analysis framework in Section 3 is designed to study how post-training decisions affect the detectability of a source that was used, not to serve as a calibrated attribution method. We will clarify this distinction in the revision, state that a positive margin alone does not guarantee correct source attribution, and include these results. We also release our testbed so calibrated audit methods can be developed against it.

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General Response and Summary of Main Rebuttal Experiments

We thank the Area Chair and reviewers for their time and constructive feedback. We summarize the additional experiments conducted during the rebuttal and how they address the main concerns raised. Complete responses to each reviewer’s individual points can be found in their respective threads.

Matched reference experiments (Vvud, iKZV). Reviewers asked that multi-source models be audited against matched references. We trained five multi-source models that fix two sources and vary the third, so that each model and its references share co-sources, data size, and training recipe, differing only in the audited source. The main result largely holds: same-domain source mixing weakens classifier-based detectability for all five sources and likelihood-based detectability for four of five. The experiment also refines our explanation of how the likelihood signal changes under mixing, which we will update in Section 4.1. We will complete this for the remaining sources, and run the corresponding experiment for the multi-domain, multi-source setting, before the next iteration.

Extended on-policy distillation (Vvud, iKZV, NSoS). Reviewers requested that the multi-stage OPD experiments be conducted at greater intensity. We extended second-stage OPD to 10k prompts (10×) with a 10× higher learning rate for two first-stage distilled models, auditing every 1k prompts. For both sources tested, the first-stage source remains detected at every checkpoint, and the new experiments refine our observations: against single-stage references, likelihood margins remain unchanged while classifier margins decline early and then level off. A supplementary matched comparison shows an early-drop-then-plateau pattern for both methods. We will replace the original setting in Section 4.4 with these results and complete the extension for the remaining first-stage models before the next iteration.

Noise intervals (Vvud, iKZV). Reviewers asked for a noise interval quantifying variation from training-run and response-sampling randomness. For two sources, we trained five additional distilled models each on randomly sampled 4.5k-trace subsets with the training setup fixed, and found small run-to-run variation: a standard deviation of at most 0.006 for likelihood and 0.009 for the classifier. We also resampled responses three times per probe and found the resulting variation is negligible for likelihood and comparable to training variation for the classifier. Revisiting the paper’s effect-size claims against these intervals leaves most findings unchanged and refines two, which we will update: in Section 4.2, a drop in classifier margins for science in multi-source, multi-domain models; and in Section 4.3, a slight increase in likelihood margins for larger targets. We will add this analysis to the appendix and train resampled variants for one or two configurations in other settings (e.g., multi-source) before the next iteration.

Negative controls and false positives (Vvud, iKZV). Reviewers requested a false-positive analysis that audits distilled models not trained on the candidate source. We ran this negative-control analysis across all settings, with both matched and mismatched references. False positives under likelihood rise when the audited model is more capable than its references, while classifier audits are largely unaffected. This corroborates our existing mismatch analysis, and we will include these results in the next iteration.

We believe the rebuttal substantially strengthens the evidence supporting the paper’s central findings. We hope the Area Chair will weigh the original contribution (a known-lineage testbed covering multiple post-training axes and the resulting findings on when distillation sources remain detectable) alongside the additional controlled experiments.

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

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