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Under review as a conference paper at ICLR 2027

ContamMorph: Do Transformed Views Add Membership Evidence After Fine-Tuning?

Abstract

Membership inference asks whether a passage was used to train a model. Auditors can average scores across reformatted or rewritten versions, but a detection gain may come from one transformation alone. We compare the original text, a fixed transformation, and their average to separate these effects. We randomly include or withhold short English passages during fine-tuning, using two corpora and models with 0.5 to 1.5 billion parameters. Our main case study is error-zone membership inference (EZ-MIA), which divides accumulated prediction improvements by accumulated losses. Line breaks improve this detector before averaging, largely through the released code's handling of a zero denominator. When some incorrectly predicted text pieces improve and none worsen, the code assigns zero, whereas the published rule ranks the passage first. One shared positive denominator constant restores strong detection in four model and corpus settings and in fresh training runs. At an intermediate training strength, the implementation choice moves EZ-MIA from the top two of six detectors to near the bottom. After correction, averaging rarely beats an original-text detector selected on other runs. We observe this pattern in twelve-run replications, when included passages form 5% of a larger training set, and with five separately generated paraphrases. Those paraphrases distinguish members from controls less well than the exact wording used in training, and their average performs worse. Auditors should compare every aggregate with both the original text and a prespecified transformed version.

Primary area:
foundation or frontier models, including LLMs
Keywords:
benchmark contamination, membership inference, transformation orbits, exchangeability, EZ-MIA, WikiMIA

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_TCdjOpenReview ↗
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1
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2
Informativeness
1
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1
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Paper summary

The paper performs an in-depth empirical analysis of the EZ-MIA method, and shows that adding line-breaks to the text inflates AUC because of the design of the score function. The authors propose to report the scoring rule, edge cases, zero rates, and per-view scores so that MIA scores can be interpreted correctly. Overall, the manuscript is poorly written, the paper is an empirical observation that might be a better fit for other venues such as online forums, and the research project as a whole can benefit from more human oversight.

Critical strengths

The paper raises a good point that edge cases should be more thoroughly reported in MIA methods.

Critical weaknesses

The writing is unclear and hard to follow.

The main point of the paper is that MIA methods should report their edge cases and provide per-transformation scores. The point can be argued without a paper. A case study on a single MIA method does not show generalization to other methods or reporting conventions.

Questions for authors

None

2 comments
AuthorsOpenReview ↗

Response to TCdj: the revision makes the empirical contribution directly assessable

Thank you for asking for a clearer contribution and stronger evidence beyond a reporting recommendation. The revised introduction now separates scoring behavior, calibration, and the incremental value of aggregation. Added and substantively revised passages are blue. Locations below refer to the revision.

1. The scoring example identifies a mechanism with a measured boundary

The same passage can score 0 as a paragraph and 2.67 with line breaks because formatting moves the released EZ-MIA score out of its zero-denominator fallback. In the short-passage intermediate-update study, the convention changes AUROC by .091–.227 and reverses its ranking among six detectors across 48 fits. The upstream 128-token GPT-2/WikiText replication finds one member zero among 30,000 scores, showing where this mechanism is negligible. Appendix G reports the original-setting and error-count controls.

2. The revised comparison distinguishes calibration from aggregation

Suppose training used a rewrite of the auditor's sentence. Detecting exposure to that source differs from detecting the exact string. The revised manuscript states this membership target before comparing the original, a selected available rewrite, and their aggregates.

The expanded paraphrase-training study contains 96 fits. Its stronger controls change the interpretation of the earlier positive result.

QuestionResult in revised Table 3, p. 9
Does the uncalibrated average beat a calibrated original?No supported gain. All 32 mean differences are negative and 31 adjusted intervals lie below zero
Does matched calibration help the aggregate beyond the original?All 32 adjusted aggregate-minus-original intervals are positive
Does the gain require aggregation beyond a selected calibrated view?OUT normalization supports 12/16 contrasts in six of eight conditions. All 16 Gaussian contrasts remain unresolved

Appendix F specifies held-out selection, adjustment families, shared-shadow dependence, and query cost. The shadow constructor knows the designated training paraphrase, which is excluded from scored audit views. The resulting claim is conditional on this access. It does not establish that averaging generally improves text membership inference.

3. The revision states what the study contributes and where it stops

The evidence shows how the same apparent transformed-query advantage can arise from a scoring fallback, calibration, or additional views. The calibrated single-view control determines which explanation the data support. This comparison changes the paper's own earlier positive interpretation, as the abstract and Section 5 now state.

Main Table 5 reports a validated LoRA recipe. Appendix F adds a limited 3B diagnostic and upstream neighbourhood/SPV-MIA integrations, with material deviations retained. These additions broaden the evaluation without turning one detector's fallback into a universal defect or claiming complete coverage of attack pipelines. The introduction presents the examples before the protocol terminology, and the conclusion states each finding with its comparator and scope.

AuthorsOpenReview ↗

Remaining questions on the revision

Thank you for your review. The revised manuscript and our updated responses are now available. Are there any remaining concerns that you would like us to clarify or address? We would be happy to provide further details.

Reviewer_i57KOpenReview ↗
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2
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Informativeness
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Paper summary

ContamMorph asks whether averaging membership-inference scores over transformed views of a passage adds evidence beyond one prespecified transformation. Membership is randomized during fine-tuning of 0.5–1.5B models on 32-word WikiMIA and arXiv prefixes. They showed that line breaks raise EZ-MIA's AUROC from .67 to .95 mainly because the released code scores zero-denominator cases as zero. Correcting this restores detection and changes detector rankings at mid-strength updates. After correction, averaging rarely beats a held-out-selected original-text detector, and averaging paraphrases lowers AUROC.

Critical strengths
  1. The diagnosis is clean with exact parity with upstream code on 129,600 scores and a denominator-only intervention that isolates the mechanism.
  2. Randomized inclusion gives true membership labels and avoids the date-proxy confound (embeddings predict WikiMIA dates at .97–.99).
  3. Held-out detector selection, twelve-run replications and Bonferroni bounds make the null results credible.
  4. The authors report openly which analyses were post hoc and which prospective predictions failed.
Critical weaknesses
  1. The core finding is one tool's code/paper mismatch, which by the authors' own bound affects at most ≈0.7–5% of members in EZ-MIA's original setting.
  2. Results are confined to 32-word passages and models of at most 1.5B parameters.
  3. The aggregation question is tested only with simple means of 3 layout views or 5 paraphrases; SPV-MIA and neighbourhood attacks are only local adaptations.
Questions for authors

Please answer these following questions:

  1. The fallback's frequency but notes the upstream evaluation was not rerun; can authors rerun EZ-MIA's own 128-token, full fine-tuning setting?
  2. Does the paraphrase result hold when the model is trained on a paraphrase and audited with the original?
  3. Does "aggregation rarely helps" still hold with end-to-end SPV-MIA and neighborhood pipelines?
  4. Why did the authors' frozen 1.5B width-sensitivity prediction fail, and does it indicate the effect shrinks with model size?
4 comments
AuthorsOpenReview ↗

Response to Reviewer i57K, Part 1: original-setting replication and calibrated controls

Thank you for the questions about the upstream setting, training wording, complete attack pipelines, and the failed prediction. The revised manuscript incorporates the completed follow-ups and reorganizes the introduction around scoring, calibration, and aggregation. Added and substantively revised passages are blue. Locations below refer to the revision.

1. The original 128-token setting bounds the scoring effect

The upstream GPT-2/WikiText full-fine-tuning experiment uses 10,000 members and 10,000 controls per seed, 128 tokens, three epochs, and learning rate 1e-4. The results across three seeds are:

SettingReleased-rule AUROCMember zero ratePublished minus released AUROC
Full fine-tuning, 128 tokens.983–.9900–.01%.0000–.0001
Same full checkpoints, scored at 32 tokens.832–.8531.91–2.45%.0176–.0228
Validated LoRA, 128 tokens.753–.7580%0

The full-fine-tuning result contains one member zero among 30,000 scores. Appendix G, Table 37 on p. 41, reports this boundary directly. Main Table 5 and Appendix F report the separately validated LoRA recipe, selected by validation loss and tested on three independent seeds. The fallback is negligible in the tested original-length regime and becomes more frequent when the same full-fine-tuning checkpoints are scored at 32 tokens. The historical borrowed-XSum LoRA result remains separate.

2. Paraphrase training now has the strongest single-view controls

The expanded study uses 96 para1-trained fits, 12 per condition. Membership means source exposure through para1. The original and para2–para5 are available audit views. Para1 is excluded from scored views.

ComparisonSupported result
Uncalibrated aggregates vs calibrated originalAll 32 mean differences are negative, with 31 adjusted intervals below zero
Matched calibrated aggregates vs calibrated originalAll 32 adjusted intervals are positive
OUT aggregate vs selected OUT-calibrated view12/16 positive intervals, covering both aggregates in six of eight conditions
Gaussian aggregate vs selected Gaussian viewAll 16 intervals unresolved

Table 3 on p. 9 summarizes the result. Appendix F, Tables 29–31, reports nested held-out selection and the 64-primary/32-secondary comparison families. The broader uncalibrated claim is withdrawn. The supported result is conditional on shared shadows using the same designated training paraphrases. It does not establish calibration transfer to independently generated training wording.

AuthorsOpenReview ↗

Response to Reviewer i57K, Part 2: model scale, attack coverage, and the failed prediction

Thank you for the questions about complete attack pipelines and the frozen prediction. Appendix F reports the new 3B and upstream-code checks. Appendix G preserves the earlier analyses separately. Added and substantively revised passages are blue. All locations below refer to the revision.

3. Model and attack coverage have expanded with explicit limits

Table 35 on p. 39 adds 24 fits on Qwen2.5-3B/WikiMIA. The exact-text aggregates remain below the selected controls. After paraphrase training, original-plus-four gains +.040 [.011, .070] over the selected original at weak updates and an unresolved +.021 [−.014, .057] at intermediate updates. These are uncalibrated comparisons.

Table 36 reports upstream-code integrations on six matched Qwen2.5-0.5B/WikiMIA targets per attack, three per update strength.

DetectorWeak AUROCIntermediate AUROC
Published-rule EZ-MIA.797.979
Neighbourhood integration.511.739
SPV-MIA integration.636.982

Neighbourhood uses the original BERT/dropout generator with 100 neighbours and decoded-text normalization. SPV-MIA completes generation, reference training, perturbation, and scoring through the original scoring call path. Its intermediate-minus-EZ difference is +.003 [−.008, .014], unresolved under a two-comparison adjustment across update strengths.

SPV's auxiliary prompt corpus and reference-trainer port remain material deviations, with article-level disjointness and numerical trainer parity unverified. These integrations test original-text detection. They do not establish whether aggregating these attacks over views helps. Appendix G retains the historical adaptations separately.

4. The failed prediction remains a failed prediction

Appendix G explains that the 1.5B corrected-view penalties, .078 and .079 AUROC, exceed the frozen ±.05 tolerance. The released-rule line-break gain remains +.259, with 313/900 member zeros. The failure concerns the predicted corrected-view penalty. It does not establish a model-size trend. The revision retains the historical scoring-convention label and the failure rather than replacing it with the later 3B diagnostic.

5. The revised introduction explains the question before the protocol

The introduction starts with a concrete example and separates scoring conventions, calibration, and aggregation. Each result names the membership target and single-view comparator. The conclusion in Section 5 restricts the negative finding to tested exact-text training and states the conditional OUT-normalized benefit after paraphrase training. It does not claim that aggregation is generally ineffective.

The original main study uses 32-word passages. The upstream check uses 128-token sequences, and the 3B extension retains WikiMIA. These extensions broaden the measured coverage without establishing a universal length threshold, a model-size trend, or a calibrated 3B gain.

AuthorsOpenReview ↗

Remaining questions on the revision

Thank you for your review. The revised manuscript and our updated responses are now available. Are there any remaining concerns that you would like us to clarify or address? We would be happy to provide further details.

Thanks the authors for the detailed response and the additional experiments. With the 128-token replication, the Qwen2.5-3B extension and calibrated aggregation make this paper better. However, the 128-token result also shows that the scoring effect is negligible in the original EZ-MIA setting, so the main finding remains specific to short passages and small models. Therefore, I keep my score.

Reviewer_YubKOpenReview ↗
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Paper summary

The paper researches whether averaging membership scores over transformed versions of a passage adds evidence beyond the original text and beyond a single fixed transformation. These labels come from randomly including 32-word WikiMIA and arXiv passages when fine-tuning Qwen2.5-0.5B and pythia-1.4b. The main finding concerns EZ-MIA. Its released code scores zero-loss passages as 0, while its paper ranks them as members. Line breaks avoid this case, which explains most of their apparent benefit. After the rule is fixed, averaging rarely beats the best original-text detector, and averaging with paraphrases lowers detection.

Critical strengths
  • The paper finds and explains a real mismatch between EZ-MIA's paper and its released code. It shows the mechanism clearly and reproduces it in fresh training runs. At moderate training strength, this choice moves EZ-MIA from second to last of six detectors, which matters for anyone comparing methods through released code.
  • The experiments are careful. The random inclusion avoids the date bias in WikiMIA labels and the main protocols were fixed before training and failed predictions are reported openly.
Critical weaknesses
  • It’s unclear how far the bug matters. It shows up because the passages are very short and the models train on them heavily. The authors never ran EZ-MIA’s original setup. So we don’t know whether real users of EZ-MIA would hit this problem.
  • The averaging results are mostly what you’d expect. The models were trained only on the exact original wording. Reworded versions are bound to look less familiar to the model, so averaging them in drags the score down. A fair test would be a model trained on reworded copies.
  • The paper misses the closest prior work on averaging over views, especially in image membership inference, where querying several augmented copies and combining the scores is standard and is known to help, mainly when the model was trained with those augmentations (Choquette-Choo et al., 2021; Carlini et al., 2022; Zarifzadeh et al., 2024)
Questions for authors
  • How often does the zero-score issue actually show up in EZ-MIA’s own setup, for example GPT-2 on WikiText with 128 token sequences, under both full + LoRA fine-tuning? If it rarely happens there, the finding may only matter for very short passages.
  • In the strong settings, just counting a passage’s wrong predictions already gets .983 to 1.000 AUROC. How does that simple count compare with EZ-MIA in the weak and mid settings?
  • the Gaussian analysis says the best way to combine views uses unequal weights, but the main experiments only try a plain average and a rank average. If you learn the weights on other runs, or calibrate each view first as LIRA / RMIA do, do the views beat the best original-text detector?
  • The line-break views add tokens the model never saw during training, and those tokens carry most of the members’ loss (85.9% to 96.8%). Do you see these views as the same content? What do the results look like for all detectors if those inserted tokens are left out?
  • Every paraphrase experiment trains only on the exact wording, so it makes sense that paraphrases score worse. What happens if you train some runs on paraphrased copies of the members? And how close are your generated paraphrases to the originals compared with WikiMIA’s own paraphrases?
8 comments
AuthorsOpenReview ↗

Response to Reviewer YubK (Part 1 of 4: Original setup and error count)

Thank you for the specific questions. We added upstream replication, error-count comparisons, calibrated aggregation, boundary rescoring, and paraphrase-training experiments.

W1 / Q1: EZ-MIA's own setup

We ran the authors' code on GPT-2/WikiText: 128 tokens, 10,000 members and 10,000 nonmembers, three epochs at learning rate 1e-4, three seeds. Full fine-tuning uses the upstream configuration. LoRA uses the authors' XSum adapter settings because no WikiText LoRA configuration ships. Recomputed released-rule scores agree with upstream within 2.3e-5 per sample.

TrainingTokensAUROCZero rate: members / nonmembersF minus U
Full, 3 epochs, 3 seeds128.983–.9900–0.01% / 0%.000
Full, 1 epoch128.8170% / 0%.000
Full, lr 5e-5128.9220% / 0%.000
LoRA, 3 seeds128.524–.5290% / 0%.000
Full, 3 epochs, 3 seedsfirst 32.850–.876 (F)1.9–2.5% / .15–.22%.017–.023

F denotes the published scoring rule; U denotes the released rule. The 128-token full-fine-tuning result contains one member zero among 30,000 scores. EZ-MIA ranks first among the six tested detectors in every row.

This confirms your concern about scope: the discrepancy has negligible impact in the original 128-token regime. Rescoring the same checkpoints at 32 tokens makes it substantially more frequent. This comparison identifies length sensitivity without establishing that training strength is irrelevant. In our 32-word intermediate-update study, where competing detectors are stronger, the fallback costs .091–.227 AUROC and changes mean rank from 1.1–2.0 to 5.8–6.0 across 48 fits (Table 23). We will present both the failure and the regime where it is negligible.

Q2: Error-count baselines at weak and intermediate updates

The error count reaches .512–.524 AUROC after weak updates, versus .686–.801 for EZ-MIA (F). At intermediate updates, the respective ranges are .870–.921 and .970–.995. The paired advantage of F is .17–.29 and .07–.10, respectively; all adjusted fit-level intervals exclude zero (144 fits, 48-comparison Bonferroni family).

Negative error mass alone is more competitive, trailing F by .025–.080 at weak updates and .003–.016 at intermediate updates. In these weak and intermediate follow-up cells, the smoothed ratio P/(N+1)P/(N+1) matches F within .003 AUROC. These comparisons identify the fallback as the source of the observed scoring collapse; the error count alone does not explain F's performance. We will keep this conclusion separate from the strong-update cells where detectors approach saturation.


AuthorsOpenReview ↗

Response to Reviewer YubK (Part 2 of 4: Calibration and boundary rescoring)

Q3: Learned weights and calibration

Calibration helps substantially; its benefit must be separated from the contribution of additional views. Each method is fitted on the other eleven fits of a twelve-fit condition and tested on the held-out fit. The implementations are:

  • IN/OUT Gaussian likelihood-ratio calibration. We fit member and nonmember distributions to each source's mean log-likelihood, and sum per-view log-likelihood ratios for the aggregate. This is an IN/OUT adaptation of LiRA, not offline LiRA. Actual per-source counts range from 0–11 IN and 0–10 OUT observations; they are not eleven observations per class. When both counts are at least three, we use per-source standard deviations floored at .001. Otherwise we use pooled within-source variances; a missing class mean uses the population mean. Pooling excludes the evaluated source fold. Approximately 74% of evaluated source/fit cases use per-source variances.
  • OUT-mean-normalised rank aggregation. We subtract the source's mean OUT log-likelihood, rank the residual within the evaluated population without labels, and average these ranks over views. This is the precise reference-normalised procedure tested; it is not a reproduction of the full RMIA attack.
  • Learned weights. Logistic regression and shrinkage LDA use per-view features, with training and standardisation excluding both the evaluated fit and its source fold.

These shadow-model methods assume known membership in the other fits, giving the auditor more access than the paper's core detectors. The tested targets here were trained on exact text.

Gaussian calibration on the original reaches .876–.928 AUROC at weak updates, and OUT-normalised scoring reaches .921–.961, versus .686–.801 for the strongest uncalibrated detector. Relative to the same calibration on the original, Gaussian layout aggregation changes AUROC by −.002 to −.005, with adjusted intervals spanning zero. Adding five paraphrases changes it by −.037 to −.053 at weak updates and −.005 to −.009 at intermediate updates; those intervals exclude zero. OUT-normalised aggregation shows the same pattern. Learned likelihood weights gain at most .015 over their original-only counterpart and remain at least .03 below the held-out-selected original detector.

These are AUROC conclusions. At 1% FPR, Gaussian layout aggregation has higher point estimates in three of four weak-update conditions, for example .343 versus .314. With 300 controls per fit, 1% FPR corresponds to only three false positives. We will report operating-point uncertainty separately rather than infer that views contain no additional information.

Q4: Same content, different tokens

Line-break views retain the words and their order but change tokenisation and context. We rescored all seven detector/rule combinations across 156 fits while masking each inserted line-break token and the following token from the scoring positions. Full-score recomputation first reproduced the stored scores exactly.

For released EZ-MIA, this masking changes AUROC from .960 to .796 at intermediate updates and .914 to .431 at strong updates; original-text scores are .806 and .404. Masking therefore removes most of the observed benefit, consistent with the denominator intervention. It does not undo the changed context for retained tokens.

The effect also depends on the detector: Min-k++ improves from .785 to .939 after masking at intermediate updates. The masked-position rank average differs from the held-out original detector by −.010 to +.011 across twelve conditions. We will describe this as a test of boundary-associated scoring positions, rather than claim that the inserted tokens are the only possible cause.

AuthorsOpenReview ↗

Response to Reviewer YubK (Part 3 of 4: Paraphrase training and single-view controls)

W2 / Q5a: Training on paraphrases

We ran 48 fits trained on para1: two model families × two corpora × two update strengths × six fits. Membership is defined at the source level: a source is a member if its designated rendering was included in fine-tuning. The auditor receives the original source but does not know the training rendering. All renderings of a source share its membership assignment and source fold.

Auditing the original with EZ-MIA (F) reaches .55–.59 AUROC at weak updates and .73–.77 at intermediate updates. The rank average of para2–para5 improves over the held-out-selected original-text detector by .008–.045 and .022–.053, respectively. That original-text comparator selects among six detectors. The trained para1 is an oracle reference, reaching .985–.996 at intermediate updates; it is unavailable to the ordinary auditor.

Does aggregation improve on one unseen paraphrase?

We added an exploratory saved-score comparison to answer this directly. U4 averages the ranks of para2–para5 under F. We compare it with fixed para2 and with one F-scored view selected among the original and para2–para5 on other fits, excluding the evaluated source fold. No evaluated labels choose the view. Para1 is excluded, and no audit string equals that source's trained rendering.

ConditionU4 minus fixed para2U4 minus selected F view, adjusted 95% CI
Qwen/WikiMIA, weak+.056+.018 [−.041, .076]
pythia/WikiMIA, weak+.033+.028 [−.014, .070]
Qwen/arXiv, weak+.035+.013 [−.048, .073]
pythia/arXiv, weak+.012+.018 [−.008, .045]
Qwen/WikiMIA, intermediate+.102+.055 [.004, .107]
pythia/WikiMIA, intermediate+.094+.056 [.022, .090]
Qwen/arXiv, intermediate+.102+.051 [.022, .081]
pythia/arXiv, intermediate+.101+.049 [.006, .092]

Intervals use paired fit-level differences across six fits and two-sided Bonferroni adjustment over 32 comparisons: eight conditions × two aggregates (U4 and original+U4) × two single-view controls. For U4, all four intermediate-update intervals exclude zero against both controls; none of the weak-update selected-view intervals does. Including the original yields .057–.070 over the selected F view at intermediate updates, also resolved in all four conditions.

This establishes an incremental aggregation benefit under the tested intermediate paraphrase-training recipe, beyond a single available F-scored view. It does not establish superiority over every detector or a calibrated auditor in this regime. The calibrated comparison in Part 2 uses exact-trained targets.

At 1% FPR, U4 improves TPR over fixed para2 by .077–.115 at intermediate updates, but all four adjusted intervals include zero. At 5% FPR, the changes are .136–.196, resolved in two of four conditions under a separate 32-comparison family. We will report these outcomes separately from the AUROC gain.

Mixed training: which audit texts were seen?

The additional twelve WikiMIA fits use one rendering per member in a single pass, allocated across the original and para1–para5: 50 of 300 members per rendering in each fit. Thus para2–para5 includes the trained rendering for 200 members; it is not an entirely unseen audit set. Its .046/.072 improvement over the selected original detector will be reported as mixed-exposure evidence, separate from the para1-only result above.

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

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