acceptodds
Under review as a conference paper at ICLR 2027

LaunderBench: Is Your Data Laundered and then Used in LLM Training?

Abstract

Data laundering refers to an emerging threat that rewrites documents before training a language model. This threat will hide evidence of copyrighted data use from training-data provenance detection while preserving knowledge of such source data. However, the community has yet to establish an evaluation protocol that distinguishes whether the detector is simply underpowered, the laundering succeeded, or the model failed to learn. To address this confounding, we introduce LaunderBench, a benchmark grounded in three diagnostic criteria, namely *baseline detector auditability*, *audit evasion efficacy*, *source utility viability*. Specifically, LaunderBench trains three compute-matched models from a shared checkpoint: laundered (on rewrites), unlaundered (on originals), and filler-only (on background text alone), and audits all three on the original documents. This setup allows us to separate audit evasion from detector weakness, and distinguish whether the model actually learned from the sources or merely drifted during background training. Evaluating across model scales (Pythia-1.4B to 6.9B), architectures (Pythia and GPT-Neo), 4 data corpora, and 9 rewriting methods reveals three findings: 1. rewrite-trained models consistently learn source knowledge, but the utility gap lost relative to unlaundered training widens as training proceeds; 2. the acquired source knowledge does not translate into higher detectability; 3. under strict false-positive constraints, the relative evasion rankings of rewriting methods can invert. These findings show that reliable provenance audits must evaluate detector baseline power alongside strict false-alarm budgets, which LaunderBench operationalizes to enable rigorous benchmarking of laundering-resilient data provenance audits.

Primary area:
datasets and benchmarks
Keywords:
training-data provenance detection, data laundering

Reviews

Among:
Shape:
1234this paper, Top 15%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_Ki7mOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper is on data laundering, which a model is trained on rewritten versions of documents so that membership-inference audits run on the originals fail. The paper argues that prior evaluations cannot tell apart three cases: the detector was weak to begin with, the rewriting really did hide the data, or the model did not learn from the rewrites. The paper proposes LaunderBench, which trains three matched models from the same Pythia-1.4B checkpoint: one on original documents mixed with filler text, one on rewrites mixed with filler, and one on filler only. By auditing all three models on the original documents, the researchers evaluate detection success through AUROC and true positive rates alongside utility measured by perplexity reduction. The experiments find: (1) Models trained on rewrites still learn from the source documents, but less than models trained on the originals, and the gap grows with more training. (2) When the model has seen the data only a little, detectors that use the model alone barely work even without rewriting; only the detector that compares against a reference model works. (3) Which rewriting method looks hardest to detect depends on the metric: the ranking by AUROC can differ from the ranking when almost no false positives are allowed.

Critical strengths
  • The paper points out an interesting question that a low detection score after rewriting could simply mean the detector was weak from the start. The three-model design (originals, rewrites, filler only) separates these cases cleanly.
  • The main experiments on Pythia-1.4B are broad: four corpora, nine rewriting methods, two seeds, several training lengths, and several source ratios. The detectors are also grouped by what access they need (target model only, extra prefix text, or a reference model), so methods with different requirements are not compared as if they were equal. This makes the results more convincing than a study with one rewriting method, one detector, or one training setting.
  • The benchmark is easy to extend, since new detectors can be tested on the released checkpoints without retraining.
Critical weaknesses
  • The utility metric and the detectors rely on the same signal, the model's likelihood on the original documents. Utility is the perplexity reduction on the originals relative to the filler-only model, and the Reference detector thresholds almost the same quantity per document. As a result, the rewriting methods rank in the same order on both detection and utility in Table 1, and the paper does not test whether a rewrite actually hides the data or just makes the model learn less. A model that learned the facts without the exact wording would be scored as low utility, even though that is the most concerning form of laundering. The utility criterion (gain > 0) is also too weak: every setting passes it, including SAGE-R, where most factual entities are masked out. A utility measure that does not depend on the verbatim text, such as question answering on the facts in the source documents, and a control experiment in which an unlaundered model is trained with less exposure so that it reaches the same gain as the laundered model, which would show whether rewriting hides the data or the model has simply learned less.

  • The paper claims coverage across model scales and architectures, but the experiments on the larger Pythia models and GPT-Neo (Appendix F) do not follow the paper's own protocol. They train only the laundered model, with no unlaundered or filler-only counterpart, use the pretrained checkpoint as the reference, and measure perplexity on the rewritten training texts instead of the originals. Without these controls, none of the three criteria the paper proposes can be checked in these settings, so it is unclear whether the detection numbers reflect real evasion or whether the models learned anything about the original sources. In practice, the three main findings are supported only on Pythia-1.4B. It would be better to rerun a subset of these experiments with the full three-model setup.

  • The paper would be stronger if it also evaluated laundering-aware audits [1] and dataset-level inference [2], not only document-level audits on the verbatim originals.

  • The training setup is quite different from how LLMs are really trained, so I am not sure how much the numbers mean. The filler data is only 1,000 documents from the Pile training split, which Pythia has probably already seen in pretraining, and each one is repeated about 40 times. The paper says the filler-only model gets worse on the originals because of domain drift, but I think it is more likely just overfitting to this small set. This matters because utility is measured against this baseline, so the gains can look bigger than they are. In fact, in 62 of 72 cases the rewrite-trained model gets worse on the originals in absolute terms as training goes on. Also, each source document is seen 8–12 times, while in real pretraining a document is usually seen about once, so the setting is closer to fine-tuning with heavy memorization. I suggest using a larger filler set without repetition, adding the pretrained checkpoint as a baseline, and testing the case where each source is seen only once.

  • The description of the surrogate-selected rewriting is inconsistent. Section 3.1 says five candidate rewrites are generated for each document and the one with the lowest surrogate detection score is kept. Appendix A.1 instead says five prompt variants are tested on the first 20 documents of each corpus, and the best prompt is then used to rewrite all remaining documents. These are different procedures, and the appendix version seems to be the one actually used (Table 3 also calls it "surrogate-selected prompt"). If so, the adversary is much weaker than the main text suggests, since nothing is selected per document.

[1] Combating Data Laundering in LLM Training. Li et al., arXiv 2026. [2] LLM Dataset Inference: Did You Train on My Dataset? Maini et al., arXiv 2024.

Questions for authors
  1. If an unlaundered model is trained with less exposure so that its gain matches that of a laundered model, is the laundered model still harder to detect?
  2. Do the three main findings still hold on Pythia-2.8B, Pythia-6.9B, or GPT-Neo when the unlaundered and filler-only models are also trained?
  3. Does the filler-only model's perplexity on the originals still rise when the filler is a larger set of documents that were not in pretraining and are not repeated?
  4. Which surrogate-selection procedure was actually used: the per-document candidate selection in Section 3.1 or the per-corpus prompt selection in Appendix A.1?
13 comments
AuthorsOpenReview ↗

Response Overview

Thanks for your constructive review! We ran new controlled experiments to address each of your concerns and will incorporate all updates into the revision. Below is a quick overview before the detailed responses:

  • W1 & Q1 (Equal-gain controls): When we adjust source quotas so that rewritten models achieve the same perplexity gain over θ0\theta_0 as original-text models, the rewrites are no harder to detect on average Reference AUROC (lower detectability appears mainly at strict zero-FP recall). By contrast, rewrites that stay harder to detect (such as 5%-quota SAGE and SAGE-R) fall short of the original-text gain, confirming a lossy trade-off between evasion and lost gain that motivates the proposed three-model protocol for evaluating laundering.
  • W1 (Non-verbatim utility & SAGE-R): We will narrow "source knowledge" to source sequence-modeling utility. Unseen paraphrases confirm general sequence adaptation without a fact-specific advantage. We conducted factual cloze probe studies, showing no QA gain over θ−\theta^- even on verbatim training (leaving downstream QA open), and we clarify why ΔPPLS>0\Delta\mathrm{PPL}_{\mathcal S} > 0 serves strictly as a sanity check paired with lost gain.
  • W2 & Q2 (Scale & architecture): A new full three-model check on Pythia-2.8B (Wikipedia, 313 updates) reproduces our primary utility and detection ordering.
  • W3 (Dataset-level & paraphrase audits): Adding corpus-level rank tests recovers strong detection even for target-only detectors, and 4-paraphrase query averaging flags every tested laundered model under reference calibration without inflating false alarms on θ−\theta^-.
  • W4, Q3 & W5, Q4 (Non-repeating filler & Section 3.1 fix): Replacing the 1,000-doc filler pool with 40,064 non-repeating Pile documents on Wikipedia and arXiv stops θ−\theta^- from degrading, keeps all tested rewrites better than θ0\theta_0 through 1,252 updates, and preserves our core detection findings. We will also correct Section 3.1 to match the executed per-corpus prompt selection in Appendix A.1.

Please find the full details and tables below. We hope these additions resolve your concerns.

AuthorsOpenReview ↗

Responses to Reviewer Ki7m (Part 1/5)

W1 & Q1: "The utility metric and the detectors rely on the same signals ... If an unlaundered model is trained with less exposure so that its gain matches that of a laundered model, is the laundered model still harder to detect?"

Thanks for the constructive question. Indeed, both ΔPPLS\Delta\mathrm{PPL}_{\mathcal S} and all verbatim-query detectors score target likelihoods on the original documents. Thus, this shared signal means that lower detectability and lower verbatim learning move together (fixed-quota comparisons in Table 1), leaving genuine evasion confounded with simply learning less.

To separate the two (answer to Q1), we conducted 3 controlled comparisons at 313 optimization updates by adjusting source-token quotas within the fixed 313-update budget, so that models match on source perplexity reduction over the pretrained checkpoint θ0\theta_0. We found that rewritten models that reach the original-text learning gain are no harder to detect on average under threshold-free Reference AUROC (ΔAUROC≥+0.006\Delta\text{AUROC} \ge +0.006), whereas lower detectability appears only at the strict zero-false-positive threshold (TPR0/60\mathrm{TPR}_{0/60}, where most bootstrap confidence intervals span zero).

Gain-matched exposure controls at 313 updates. Because cycling a small filler pool degrades θ−\theta^- at later steps, we fix the budget at 313 updates and match source perplexity reductions over θ0\theta_0 (ΔPPLS(0)\Delta\mathrm{PPL}_{\mathcal S}^{(0)}) across three setups: (i) lowering original-text quotas from 5% to 2.25% and 3.0% against 5%-quota rewrites under repeated filler across all four corpora; (ii) using 40,064 non-repeating Pile filler documents on Wikipedia and arXiv to compare single-pass originals (each source seen once) against single-pass rewrites and against 10% and 20% quota rewrites (which also alter filler allocation); and (iii) comparing those 10% and 20% non-repeating-filler rewrites against our earlier 313-update multi-pass 5% original-text baseline under the same non-repeating filler pool. Positive θ0\theta_0 gains below indicate lower source perplexity than θ0\theta_0, and positive ΔAUROC\Delta\text{AUROC} indicates higher detectability on the rewritten model (by Reference detector):

Original Baseline (313 Updates)Rewrites Matching Original θ0\theta_0 GainRef. ΔAUROC\Delta\text{AUROC}Strict TPR0/60\mathrm{TPR}_{0/60} and Seed Notes
2.25% Originals (repeated filler, 4 corpora)Lexical & Syntactic only (23/72 runs)+0.006 (mean)Lower point estimates in most matched runs; 17/23 95% CIs span 0
3.0% Originals (repeated filler, 4 corpora)Syntactic only (4/72 runs)+0.013 (mean)Lower in half of matched runs; 2/4 95% CIs span 0
Single-pass Originals (non-repeating filler)10% & 20% Wiki SAGE (all 4 runs; no arXiv or SAGE-R)+0.009 to +0.059Reference AUROC ≥\ge Originals in every matched run
5% Multi-pass Originals (non-repeating filler)20% Wiki SAGE, seed 137 only (+0.03 pp gain)-0.023 (seed 137)Seed 137 95% CI [−0.038,−0.011][-0.038, -0.011]; seed 42 misses gain (-0.03 pp), CI spans 0

What this means for evaluating laundering. For rewritten runs that fall below the original-text θ0\theta_0 gain threshold (including all 5%-quota SAGE and SAGE-R runs), lower detectability remains tied to lower verbatim learning. Against original-text likelihood audits, laundering therefore is considered a lossy trade-off rather than lossless hiding: aggressive rewrites suppress detectability by forfeiting part of the verbatim sequence gain (lost gain), which is why LaunderBench pairs detection with lost gain against unlaundered training. Tracking both metrics still remains necessary because shifts in the upper tail of non-members H\mathcal{H} decouple Reference trajectories and strict TPR0/60\mathrm{TPR}_{0/60} rankings from ΔPPLS\Delta\mathrm{PPL}_{\mathcal S}, while our further responses below (Parts 2/5 and 4/5) remove the verbatim-text coupling on both sides via unseen paraphrases and multi-paraphrase audit queries.

AuthorsOpenReview ↗

Responses to Reviewer Ki7m (Part 2/5)

W1: "A model that learned the facts without the exact wording would be scored as low utility ... The utility criterion (gain > 0) is also too weak: every setting passes it, including SAGE-R, where most factual entities are masked out."

We agree that original-text perplexity measures distributional sequence modeling rather than abstract factual recall, and we will replace "source knowledge" with source sequence-modeling utility in the revision to reflect this more precisely.

To examine the exact scenario you raised, i.e., training texts that preserve facts while replacing surface wording, we contrast SAGE [1] (which retains factual anchors while suppressing lexical overlap) directly against SAGE-R (which masks out factual entities) across our unseen-paraphrase and a set of newly constructed fact cloze probes. We conducted the supplementary studies as follows:

Probe and ScopeQuantity MeasuredEmpirical Outcome
Whole unseen paraphrases (Wikipedia, 18 repeated-filler cells)Source-over-held-out ΔPPL\Delta\mathrm{PPL} on syntactic rewriting and both SAGE generators95% CIs >0> 0 in all 18/18 trajectory cells (lexical and SAGE-R not run)
Factual spans, summed (Wikipedia, non-repeating filler)Source-over-held-out conditional log-likelihood gain summed per entity/date/number span vs. θ−\theta^-95% CIs >0> 0 on lexical (from 313 up.) and SAGE (both seeds at 1,252 up., plus seed 137 at 626 up.); spans 0 on SAGE-R at all steps
Content words, per-token (Wikipedia & arXiv, non-repeating)Source-over-held-out conditional log-likelihood gain per content-word token vs. θ−\theta^- (nats/token)Unlaundered >0> 0 at all steps; at 1,252 up., >0> 0 on lexical (both corpora) and Wiki SAGE-R (seed 42), spanning 0 at 313–626 up. and on SAGE
Factual minus matched non-factual (Wikipedia, 1,252 up.)Within-paraphrase per-token gain difference against non-factual content words with similar loss under θ−\theta^-95% CIs span 0 in every condition and seed (e.g., per-token factual-span gain is 0.057–0.063 on SAGE, with seed 42 lower CI at -0.002, vs. 0.127–0.139 on Originals)
Four-way factual cloze QA (Wikipedia, 313 up., 5% quota)Top-1 conditional log-likelihood accuracy vs. θ0\theta_0 and θ−\theta^-Failed positive control: unlaundered originals achieved 33.3%, matching θ−\theta^- (33.3%) vs. θ0\theta_0 (32.5%)

Fact-preserving rewrites (SAGE) and the QA extraction boundary. On the detectability side, fact-preserving paraphrasing does not become invisible. At 1,252 non-repeating-filler updates, Reference still detects SAGE with 0.988 AUROC on Wikipedia and 0.947 on arXiv (gain-matched comparisons are present in Part 1/5, paraphrase-query audits in Part 4/5). On the utility side, SAGE transfers positive likelihood gains to unseen paraphrases at the document and summed factual-span levels, yet its per-token factual-span gain is roughly half of Original training and the within-document factual minus matched non-factual difference spans zero across all runs. Moreover, as [2] suggest, verbatim pretraining memorization does not guarantee extractable QA knowledge without explicit QA fine-tuning, whereas paraphrasing may facilitate downstream QA extraction (consistent with [1] reporting preserved LLM-judged QA utility under 3-epoch LoRA fine-tuning on LLaMA-3.2-3B).

To probe factual recall directly on our checkpoints, we built a four-way cloze test from the Wikipedia sources (non-verbatim factual prompts with 1 true answer and 3 distractors) and scored each candidate completion by its conditional log-likelihood under the 313-update models. However, even unlaundered verbatim training achieved only 33.3% top-1 accuracy, matching the unexposed filler-only model θ−\theta^- (33.3% vs. 32.5% on θ0\theta_0). Because this probe failed its positive control even on verbatim training, we consider downstream factual QA an open boundary and leave it as an important future direction.

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

The paper studies whether rewriting documents before training makes the use of these doc harder to detect while still preserving training benefits on these data. To investigate this, the paper has built a set of oracle models (models trained on original documents, rewritten documents, and background text alone) and a series of evaluations. Its main contribution is a controlled evaluation protocol. It compares the models with known training data, which helps distinguish successful evasion from a weak detector or an ineffective training procedure.

Critical strengths
  1. The original-text and background-only models address two important alternative explanations for weak detection.

  2. The workload should be praised.

  3. Good design of the evaluation, e.g., reporting detection under strict false-positive limits is more informative than reporting AUROC alone.

  4. Clearly written.

Critical weaknesses
  1. The evidence for knowledge retention is narrower than the wording sometimes suggests.

  2. In false-positive setting, each corpus has only 60 held-out negative documents. One false positive already corresponds to approximately 1.67%. The reported 1% setting allows zero observed false positives on those 60 documents?

Questions for authors

Relative gains over the filler-only model can increase while prediction on the originals worsens. Could you also evaluate factual questions derived from the sources and compare them against the starting checkpoint?

4 comments
AuthorsOpenReview ↗

Response Overview

Thanks for your constructive feedback! Below is a quick overview before the detailed responses:

  • W1 & Q1 (Comparison vs. starting checkpoint θ0\theta_0 & factual retention): Prediction on the originals worsened late in our submitted runs only because a small background filler set was repeated ~40 times; early in training (and through 1,252 updates when using non-repeating filler documents), every tested rewrite predicts the originals better than θ0\theta_0. However, 4-choice factual questions from the sources show no accuracy gain over the filler-only control even on verbatim originals, so we agree with W1 and will narrow "source knowledge" to source sequence-modeling utility.
  • W2 (1% FPR on 60 negatives): We confirm that a 1% false-positive budget allows zero observed false positives (0/60), will relabel the metric as TPR0/60\mathrm{TPR}_{0/60} in Table 1 and Section 4, and will note the corresponding 95% upper bound on the population false-positive rate.

Please find the full details below. We hope these additions and discussions address your concerns.

AuthorsOpenReview ↗

Responses to Reviewer uEmW (Part 1/2)

W1 & Q1: "The evidence for knowledge retention is narrower than the wording sometimes suggests. Relative gains over the filler-only model can increase while prediction on the originals worsens. Could you also evaluate factual questions derived from the sources and compare them against the starting checkpoint?"

Thanks for raising this, and we completely agree. Lowering perplexity on source documents shows that the model predicts those text sequences better, not that it has retained abstract factual knowledge. In the revision, we will replace phrases such as "preserving/learning source knowledge" with source sequence-modeling utility (and original-text modeling gain).

To address this concern, we have conducted new experiments and answered: (1) whether the continued-trained models actually improve on predicting the originals relative to the starting checkpoint θ0\theta_0, and (2) whether that improvement reflects factual knowledge retention or narrower sequence-modeling utility.

Comparison against θ0\theta_0 (why predictions on the originals worsened).

We compared all continued-trained models directly against the pretrained starting checkpoint θ0\theta_0 and found that models do improve on the originals relative to θ0\theta_0 once background filler overfitting is removed. In our previous results, absolute perplexity worsened late in training because a small pool of 1,000 filler documents was repeated ~40 times. At 313 updates (before filler repetition causes overfitting), all 72/72 rewritten models predict the original sources better (lower perplexity) than θ0\theta_0.

Moreover, when we replace that cycled pool with 40,064 non-repeating Pile documents (each seen once) on Wikipedia and arXiv, the filler-only model stops worsening on the originals, general Pile validation perplexity improves by 2.0% to 3.1% over θ0\theta_0, and every tested rewritten model continues to beat θ0\theta_0 on the originals through 1,252 updates (positive values below mean lower perplexity than θ0\theta_0; full details are in our response to Reviewer Ki7m, Part 5/5):

Training SetupSource Perplexity Improvement vs. θ0\theta_0 (Originals / Rewrites)Filler-Only Model vs. θ0\theta_0Rewritten Models Beating θ0\theta_0
Repeated filler (1,000 docs), 313 updates (4 corpora)+5.98% / +2.44%+0.09%72 / 72 (all 95% CIs >0> 0)
Repeated filler (1,000 docs), 626 updates (4 corpora)+9.68% / +1.91%-5.15%54 / 72 (49 with 95% CI >0> 0)
Repeated filler (1,000 docs), 1,252 updates (4 corpora)+14.29% / -2.84%-23.08%26 / 72 (26 with 95% CI >0> 0)
Non-repeating filler (40,064 docs), 1,252 up., Wikipedia+19.36% / +12.60% (Lexical), +9.70% (SAGE), +4.54% (SAGE-R)+2.94%All 6 / 6 tested runs
Non-repeating filler (40,064 docs), 1,252 up., arXiv+15.67% / +9.06% (Lexical), +5.79% (SAGE)+2.47%All 4 / 4 tested runs

Factual questions and unseen paraphrases

Although models genuinely lower perplexity over θ0\theta_0, we agree with W1 that lowering perplexity does not establish factual knowledge retention. We conducted new non-verbatim evaluations that confirm this directly (full breakdowns are in our response to Reviewer Ki7m, Part 2/5).

  • 4-choice factual questions vs. θ0\theta_0: We built a 4-choice factual question test from our Wikipedia sources (1 true answer and 3 distractors per prompt, scored by log-probability). Before continued training, θ0\theta_0 achieved 32.5% accuracy; after 313 updates, even models trained directly on the verbatim originals achieved only 33.3%, identical to the unexposed filler-only model (33.3%), with rewritten models in the same ~33% range. This observation is consistent with prior studies on LLM pretraining [1], whose authors argue that training LLMs with next-token autoregressive prediction lowers text perplexity without automatically surfacing as zero-shot QA accuracy unless the LLM is explicitly fine-tuned for QA tasks.
  • Facts vs. other words in unseen paraphrases: Even when models are scored on new, unseen paraphrases of the Wikipedia sources (where they do predict paraphrases of training sources better than paraphrases of held-out documents), inside each paraphrase they improve by nearly the same amount on factual spans (entities, dates, and numbers) and on non-factual content words (such as nouns and verbs) that were equally hard for the filler-only model to predict.

In short, both experiments show that training helps the model predict the source text's vocabulary and phrasing as a whole rather than selectively memorizing its facts.

[1] Allen-Zhu & Li, Physics of Language Models: Part 3.1, Knowledge Storage and Extraction, ICML 2024

AuthorsOpenReview ↗

Response to Reviewer uEmW (Part 2/2)

W2: "In false-positive setting, each corpus has only 60 held-out negative documents. One false positive already corresponds to approximately 1.67%. The reported 1% setting allows zero observed false positives on those 60 documents?"

Yes, exactly. With 60 held-out negative documents per corpus, even a single false positive is 1/60≈1.67%1/60 \approx 1.67\%, so a 1% false-positive budget allows zero observed false positives on those 60 documents (whereas the 5% and 10% budgets allow at most 3 and 6 false positives). In other words, a source document is counted as detected at this operating point only if it scores strictly higher than all 60 held-out negatives.

To make this immediately clear to readers in the revision, we will relabel TPR@1%FPR as TPR0/60\mathrm{TPR}_{0/60} in Table 1 and Section 4, and explicitly note that observing 0 false positives out of 60 independent negatives corresponds to a one-sided 95% binomial upper bound of 4.9% (1−0.051/601 - 0.05^{1/60}) on the true population false-positive rate.


Thank you again for your clear and constructive feedback, which helped us verify our findings directly against the starting checkpoint θ0\theta_0 under a non-repeating filler set, tighten our utility terminology, and make the zero-false-positive threshold (TPR0/60\mathrm{TPR}_{0/60}) explicit. We will upload the revision incorporating all of these updates before the end of the discussion period.

If you have further questions, please do discuss them with us, and we will be there to address them; otherwise, we would be very grateful if you would consider updating your rating in light of these additions.

AuthorsOpenReview ↗

Revision Uploaded

Thank you again for your review. We have uploaded the revised paper, with changes in blue. In brief:

  • Retention wording: "source knowledge" is now "source sequence-modeling utility" throughout.
  • Comparison with the pretrained model: Table 1 reports gains against θ₀, with trajectories in Appendix D.5 (Table 14). The factual cloze probe is summarized in §4.1, and its result, including the failed positive control, is in Appendix D.6 (Table 16).
  • 60 negatives: the operating point is now TPR₀/₆₀ (§3.3, Table 1). The footnote in §3.3 states that 0/60 false positives bounds the population false-positive rate at 4.9% (one-sided 95%).

We hope these updates fully resolve your concerns. We would be grateful for your thoughts on it and on our responses, are happy to clarify anything further before the discussion closes.

Reviewer_FxvcOpenReview ↗
Rating
4(+1)
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

The paper studies the concept of 'data laundering', in which training data for LLMs is rewritten before training to prevent auditors from determining whether it was used for training. Malicious actors can use this to train LLMs on data they do not own, while making detection difficult for the true owners even through the released model.

More specifically, the paper studies how data laundering through rewriting allows LLMs to capture the utility of the original text (measured as perplexity on in-domain text), while being able to avoid detectability under audits (measured as being able to reproduce verbatim texts). The paper argues that as training continues, the detectability tends to plateau while the gains from training continue to grow. Thus, data laundering can make it difficult to detect data provenance.

Critical strengths
  1. The paper highlights the 'gap' between the utility of text rewriting and its detectability. This is a crucial result, that can drive important future developments in better methods to audit training data provenance than simply verbatim matching. The paper also does a decently good job of establishing the generalizability of its claims. The results are shown across different datasets, different data laundering techniques, different detectability methods, as well as a few different models.
  2. The paper also goes deeper into detectability results, which is not their main contribution, but I appreciated it. They explore when detectability should be considered actually useful (instead of just comparing two numbers), and explore both AUROC scores for aggregate behavior and TPR scores at various FPR thresholds to show in depth behaviors.
Critical weaknesses

There were no 'critical weaknesses', however, some smaller concerns and questions I have that made me give a decision of only weak acceptance instead of clear acceptance.

  1. The chosen techniques to measure both utility and detectability are just baseline techniques. For utility, the paper only looks at perplexity on in-domain texts, and not necessarily what downstream impact it might create on the model's performance or its ability to perform certain tasks. Similarly, for detectability, the paper only focuses on completing verbatim inputs. It's good that the authors very clearly acknowledge these as limitations, but given that better techniques do exist in both directions that are closer to how an LLM might get audited or used in the real world, it does leave an important gap.
  2. The work by (Li et al., 2026) (reference already in the paper) tackles a very similar problem to this paper, and I would have expected a better discussion of what makes this work stand apart. I do consider these papers to be 'parallel work', so it is okay if there are certain findings that are concurrent or also present in the other paper, but a better discussion of similarities and differences is needed. This brings me to a broader point, which some might consider a personal preference, but I believe is important to scientific papers. Related work discussions should not be delegated to the appendix, and I feel very strongly about this! I hope the authors will incorporate a proper related work section in the main text, taking advantage of the additional page if the paper is accepted.
Questions for authors

Some suggestions ->

  1. Have a related work section in the main paper. I think you're missing out on an important wider audience if you don't take the time to situate your work within the existing literature.
  2. I believe the utility results on out-of-distribution texts are quite important, and I do wish they were part of the main text as well. However, this is a softer suggestion, since the page limit can force certain choices.
  3. The use of two random seeds is good (better than just one seed, although more would have been better), but the results for them it seems are only shown for Figure 4, while they seem to be 'aggregated' in other results (actually, its not very clear which results are shown)? It would be nice to show the effect of random seeds more clearly to establish potential error limits (2 seeds is not enough for that, but at least you can clearly show the trends you do have).
  4. Measuring downstream utility can be complex, and might not always be 'extendable' from any setup. But using better detectability techniques beyond verbatim match is, in my opinion, certainly doable. This, of course, requires more experiments, and I'm always a little hesitant to ask for more experiments during rebuttal, but I do think it can make the claims a lot stronger.
6 comments
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Response Overview

Thanks for your encouraging review and thoughtful suggestions! We ran new detection and utility experiments to address your points and will incorporate all requested updates into the revision. Below is a quick overview before the detailed responses:

  • W1 & Q4 (Detection & utility beyond verbatim matching): On detection, we added two audits beyond scoring single verbatim documents: testing a whole collection of documents together and averaging scores across four LLM paraphrases, both of which substantially improve detection when a reference model is available. On utility, models still lower perplexity on unseen paraphrases of the sources, but show no accuracy gain on 4-choice factual questions.
  • W2 & Q1 (Related Work reorganization & discussion of Li et al., 2026): We will move Related Work into the main text and discuss the complementary roles of our study and Li et al. 2026
  • Q2 (Unseen-text utility in the main text): We will move our utility results on unseen texts (both held-out documents from the same domain and general out-of-domain Pile texts) from the appendix into Section 4.1 and Table 1.
  • Q3 (Random seed effects): We clarify that raw scores are never pooled across seeds before computing ROC curves, and we will add a seed-by-seed comparison table showing that overall AUROC and utility are very stable across seeds, whereas strict zero-FP recall is more sensitive to run-to-run variation.

Please find the detailed responses below. We hope these additions address your suggestions.

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Responses to Fxvc (Part 1/3)

W1 & Q4: "For utility, the paper only looks at perplexity on in-domain texts, and not necessarily what downstream impact it might create ... using better detectability techniques beyond verbatim match is, in my opinion, certainly doable."

Thank you for encouraging us to push further on detectability. First, we would like to clarify a small point of presentation: the six detectors evaluated in LaunderBench do not ask the model to generate or complete verbatim text; instead, they measure how likely the model finds a fixed document token by token (Section 2.2, Appendix C.1). More importantly, following your suggestion, we conducted two new detection experiments that move beyond checking individual verbatim documents (full tables are in our response to Reviewer Ki7m, Part 4/5).

Regarding more investigation of detection techniques

  1. Detecting a whole collection of documents together (dataset-level auditing): There is another setting where the data owner audits a collection of documents rather than a single document [1]. When we test all ~470 source documents per corpus as a set (against the 60 unseen documents), auditing becomes stronger without triggering false alarms on clean control models. For example, after 1,252 training steps at a 5% source token exposure, Min-K++ 20% (a reference-free detector) can only detect 3.9% of individual documents when no false alarms are allowed, yet testing the ~470 documents together as a set successfully flags 54 out of 72 laundered models (and 71 out of 72 already at 313 steps for the reference-based detector).

  2. Auditing with LLM-generated paraphrases instead of verbatim originals: We also evaluate the scenario adapted from [2] (the study to be discussed as you suggested). Instead of querying the model with the exact original text, we used external LLMs (Llama-3.1-8B and Gemma-2-9B) to rewrite each query document in four different styles and averaged the detector's score across the four paraphrases.

    • With a reference model, this 4-paraphrase-based audit reliably flags every tested laundered model (p<0.01p < 0.01), including entity-masked rewrites that verbatim original queries miss when using the pretrained model as the reference.
    • We also found that averaging all 4 paraphrase styles works better and causes fewer false alarms on clean control models than trying to pick a single "best" paraphrase style on a validation split (1.6% vs. 2.7% false alarms on average).
    • However, if the detector has no access to a reference model, single-document detection remains weak even with paraphrase queries (AUROC below 0.653).

Regarding more investigation of utility

Because lowering perplexity on text does not automatically mean the model can solve downstream tasks, we will narrow our wording from "source knowledge" to source sequence-modeling utility in the revision. We also tested two non-verbatim utility setups (detailed in our response to Reviewer Ki7m, Part 2/5):

  • Unseen paraphrases: Models trained on rewritten sources still achieve lower perplexity on new, unseen paraphrases of those sources than on unseen paraphrases of held-out documents from the same domain. Inside those paraphrases, however, the model improves equally on factual spans (entities, dates, numbers) and on non-factual content words (such as common nouns and verbs) that were equally hard for the unexposed control model θ−\theta^- to predict, showing general text adaptation rather than fact-specific learning.
  • Multiple-choice factual questions: When we tested 4-choice factual questions derived from our Wikipedia sources at 313 updates, even models trained directly on the verbatim original documents scored no significantly better than an unexposed control model (33.3% vs. 33.3% accuracy, compared to 32.5% before continued training). This partly aligns with the findings of prior studies on LLM pretraining [3], where the authors found that simply continued language-modeling exposure lowers text perplexity without automatically surfacing as zero-shot question-answering accuracy unless the model is fine-tuned for QA style questions. We therefore consider utility for downstream tasks (e.g., evaluated by QA tasks) as an explicit open direction for future work.

[1] Maini et al. Dataset Inference: Ownership Resolution in Machine Learning, ICLR 2021

[2] Li et al. Combating Data Laundering in LLM Training, arXiv 2026

[3] Allen-Zhu & Li, Physics of Language Models: Part 3.1, Knowledge Storage and Extraction, ICML 2024

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Responses to Reviewer Fxvc (Part 2/3)

W2 & Q1: "The work by (Li et al., 2026) ... a better discussion of similarities and differences is needed. ... Have a related work section in the main paper."

We completely agree that Related Work belongs in the main paper. Using the additional 10th page allowed in the revision, we will move Related Work from Appendix G into a dedicated main-text section situating our benchmark within membership inference, dataset-level auditing, copyright traps, and concurrent data-laundering work, including a clear comparison with Li et al. (2026) [1].

Here we would like to clarify that, while [1] and LaunderBench tackle the same overarching problem (rewriting training data to evade provenance audits while retaining training value), these two works play complementary roles:

  • A detector plug-in based on active searching vs. a controlled diagnostic benchmark. [1] focus on building a stronger active audit algorithm (called synthesis data reversion): starting from the original query documents, their method uses an auxiliary LLM and iterative feedback from the target model to rewrite the audit queries so they better match the laundered training style. This way the detection performance of existing detectors (which all rely on verbatim queries and compute token-level likelihoods) is arguably to be recovered. By contrast, LaunderBench is an evaluation protocol and benchmark designed to untangle why and when an audit succeeds or fails. By training three compute-matched models from the same starting checkpoint (one on rewrites, one on verbatim originals, and one on background filler text alone), LaunderBench aims to separate genuine laundering evasion from three common confounds: a detector that was already weak on verbatim data, a rewrite that simply prevented the model from learning much, and background domain drift.

  • Detection signal recovery vs. multi-axis trade-off characterization. [1] ask how much detection signal an auditor can actively recover by adapting query phrasing to the target model. Our work asks how auditor access tiers, strict low-false-positive budgets, and training exposure shape the trade-off between retained source-sequence modeling and detectability across 9 rewrite procedures and 4 corpora. Rather than competing, the two works thus complement each other. LaunderBench will provide a controlled testbed on which future active query-rewriting detections like [1] can also be benchmarked and evaluated under false-alarm controls.

Q2: "I believe the utility results on out-of-distribution texts are quite important, and I do wish they were part of the main text as well."

Thank you for the suggestion! We will bring the unseen-text perplexity results from Appendix D.2 into Section 4.1, covering two types of unseen text (with additional experiments, as presented in our response to Reviewer Ki7m part 5/5). We briefly summarize the findings here:

  1. General out-of-domain Pile validation texts: In our original runs, cycling a small pool of 1,000 background filler documents ~40 times caused perplexity on general Pile validation text to rise late in training (+24% to +35% at 1,252 updates). When we replace that small pool with 40,064 non-repeating Pile documents (each seen once) on two corpora (Wikipedia and arXiv), general out-of-domain perplexity improves by 2.0% to 3.1% relative to the starting checkpoint across all steps.

  2. Unseen documents from the same domain: Across every run in both setups, perplexity drops substantially more on the actual training sources than on the 60 unseen held-out documents from the same corpus (even in runs where perplexity on unseen same-domain documents rises slightly by 0.17% to 3.46% relative to the background-only model). This implies that rewrite-trained models learn specifically from the injected source documents rather than merely shifting toward the broader domain.

[1] Li et al. Combating Data Laundering in LLM Training, arXiv 2026

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