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Under review as a conference paper at ICLR 2027

Shift-Aware Score Transport for Privacy Auditing Without Retraining

Abstract

Privacy auditing empirically assesses privacy leakage by using membership inference attacks to establish lower bounds on privacy loss. We consider an observational auditing setting in which the auditor cannot insert canaries, control data inclusion, or retrain the target model, and must instead rely on fixed sets of known members and non-members. This setting is relevant for large deployed models or when retraining is restricted by computational or access constraints. In this case, non-members available for auditing may differ in distribution from the training data, causing membership-inference scores to be skewed due to the distribution shift. We address this problem by estimating the counterfactual in-distribution non-member score distribution using the available out-of-distribution (OOD) non-members. Our proposed method learns the relationship between data representations and membership-inference scores from OOD non-members and transports it to the target covariate distribution. Because this transport may become unreliable under extrapolation or imperfect conditional invariance, we further introduce a conservative correction calibrated directly to the nominal transported privacy level. We construct controlled calibration tasks from the available non-member data to estimate how representation-space displacement inflates the audit, and use this estimate to correct the transport-induced audit error. Across multiple datasets with distribution shifts, our method yields substantially more stable privacy estimates while retaining tighter lower bounds than baselines.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
Privacy auditing, membership inference attack, distribution shift

Reviews

Among:
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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.33 over 3 reviews, above 96% of the others.
Reviewer_vypiOpenReview ↗
Rating
4(+1)
Confidence
3
Informativeness
2
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2
Soundness
3
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Paper summary

This paper tackles the challenge of running membership inference attacks (MIAs) in an observational setting, where one only has black box access to the model being attacked, cannot retrain the model, and cannot intervene in the training process. MIAs require both training and non-training data to run, and a key challenge with running MIAs in observational settings is to obtain non-training members from the same distribution as the training members. A common issue e.g. with MIAs on LLMs was that the distribution shift between training and non-training members was unaccounted for, which inflated attack success scores.

To tackle the "inflation" caused by distribution shift, the paper proposes correcting the out-of-distribution (OOD) non-member attack scores to more closely match the in-distribution (ID) non-member scores. To achieve the correction, the member in-distribution scores are used as reference. A key assumption in the paper is that one can learn a representation ZZ of the data (both IID and OOD data) such that, conditioning on the representation, the score distribtution is identical among OOD and IID non-member samples. With this assumption, the authors propose learning a relationship between scores and representation ZZ, via either linear regression or quantile regression. Then, samples ziz_i can be sampled from the represantion ZZ of member samples, and used to transport the non-member scores via the learned relationship between ZZ and scores.

Because the conditional independence assumption need not hold, the authors then propose a conservative correction on the scores. Their experimental results show that the final MIA success after the correction is closely beneath the "ground truth" MIA success with access to IID non-members.

Critical strengths
  • The idea of correcting for the distribution shift by transporting scores from the out-of-distribution population to in-distribution population is appealing. It seems an easier feat than approaches which try to e.g., generate synthetic non-member samples.
  • The experimental results clearly show the risk of MIA inflation due to distribution shift. The authors compare to relevant prior work. Results show the validity of the method in tackling the inflation and achieving conservative differential privacy lower bounds that are close to the ground truth.
Critical weaknesses
  • The key assumption/observation in the paper is the conditional independence of scores under a representation ZZ. However, there is not much intuition provided for why this should be the case. This requires more explanation and motivation since the whole methodology is based on this assumption. I also did not come away with a clear sense of why we should expect Assumptions 2-4 hold, and it was not clear if the correction methodology and its assumption are standard in the statistics literature. My main concern is that I did not come away with a clear intuition for why the transport should even work, given that all we have is member scores based on a model that memorizes.

  • Since the assumptions of the paper are hard to verify in practice, the validity of the methodology rests on experimental results. Running the experiments on a third dataset would be useful.

  • The section "source-to-target" displacement introduced a lot of new terminology without much explanation, and I could not follow. Maybe you can add additional explanation in the Appendix?

Questions for authors
  • Given that linear and quantile transport give different results, in practice would you recommend running both of them and taking the max of the lower bounds produced by each method?
1 comment
AuthorsOpenReview ↗

Response to Reviewer vypi

Thank you for the informative review. We address your concerns below.

Weaknesses:

W1

The key assumption in the paper is the conditional independence of scores under a representation. However, there is not much intuition provided for why this should be the case.

We have added an explanation of the intuition behind this assumption on page 4, lines 213–215. Our intuition is that, for a fixed target model, the MIA score of a non-member is determined by the input and the model's behavior. Therefore, when conditioning on the full input (XX), the non-member score mechanism is domain-invariant for a deterministic scoring rule. However, directly modeling MIA scores as a function of high-dimensional inputs is challenging. We therefore introduce a pretrained representation and assume that it preserves sufficient score-relevant information for the conditional score distribution to remain invariant across domains (Assumption 1).

As discussed in Section 4.2, conditional invariance may fail when the representation does not preserve sufficient information or when the distributions have limited support overlap. This motivates our shift-aware correction. Since the true transport-induced audit error is unobservable, we construct within-OOD calibration tasks along the estimated OOD-to-IID shift direction, where both predicted and observed non-member scores are available.

It was not clear if the correction methodology and its assumption are standard in the statistics literature.

This approach is motivated by the established statistical framework of counterfactual distribution inference [1], which estimates a counterfactual outcome distribution by combining a conditional outcome model with a different covariate distribution. This is also why we name Section 4.1 counterfactual score transport. Therefore, the transport has been explored in literature, while our proposed calibration tasks are novel and constitute the key contribution of this work.

We acknowledge that our assumptions are strong and may be hard to verify directly in practice. Our theorem therefore provides sufficient conditions for conservativeness relative to the oracle IID audit, while our experiments provide empirical evidence of the method’s effectiveness. We have clarified this limitation in the discussion section, lines 535-536.

My main concern is that I did not come away with a clear intuition for why the transport should even work, given that all we have is member scores based on a model that memorizes.

We clarify that we have access to both member and OOD non-member data, which can be used to learn the IID non-member scores. Specifically, we learn the relationship between representations and scores from OOD non-members, and use member representations to characterize the target input distribution. The intuition is that, if representations capture the factors governing non-member scores, the relationship learned from OOD non-members can transfer to the target population. This is basically counterfactual distribution inference.

Because this transfer may be imperfect, we construct controlled transport tasks within the observed OOD data, where true scores are available, and measure the resulting audit errors. These tasks motivate a displacement-dependent correction.

W2

Running the experiments on a third domain would be useful.

To further evaluate the generalizability of our method, we have conducted additional experiments on Criteo, extending our evaluation beyond image classification and language modeling to click-through rate prediction. Details can be found in Appendix C.4. Specifically, we consider February 15, 2015 as the source day. We introduce natural temporal distribution shifts by using OOD non-members collected 7 and 23 days after the source day.

The new Figure 7 shows that corrected quantile transport provides tighter bounds than corrected residual transport. With a 7-day gap, the distribution shift is relatively mild and has a negligible effect on the audit results. With a 23-day gap, the shift becomes more pronounced, and the uncorrected audit substantially overestimates privacy leakage. In contrast, our corrected methods produce conservative and tight bounds. These additional results further demonstrate the effectiveness of our method in a different application domain and under naturally occurring temporal distribution shifts.

W3

The section "source-to-target" displacement introduced a lot of new terminology without much explanation.

We have expanded the explanation of the source-to-target displacement section in Appendix D.5 to clarify each component in detail.

Questions:

In practice would you recommend running both of them and taking the max of the lower bounds produced by each method?

Yes, this is exactly what we proposed in the discussion section, lines 528-530.

[1] Chernozhukov et al. . Inference on counterfactual distributions. Econometrica, 2013.

Reviewer_GE8EOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
3
Presentation
3
Soundness
2
Read review
Paper summary

This paper studies how to conduct reliable privacy auditing under distribution shift between member and non-member data, in settings where the target model cannot be retrained. Existing observational privacy auditing methods typically estimate a lower bound on privacy leakage using the MIA scores of known members and non-members. However, when the available non-members are drawn from a distribution different from that of the training data, MIA scores may simultaneously reflect membership information and distribution shift, leading to an overestimation of privacy leakage. To address this problem, we propose a two-stage framework. First, we extract data representations using a frozen pre-trained model and learn the conditional relationship between representations and MIA scores on OOD non-members. This relationship is then transferred to the target distribution represented by the member representations, in order to estimate the missing IID non-member score distribution. Second, recognizing that conditional score invariance and support overlap may fail to hold, we propose a shift-aware conservative correction. Specifically, our method estimates the representation-space shift direction from OOD non-members to IID members, constructs source-target slab tasks with varying displacement magnitudes within the OOD data, and measures the transport-induced audit error using the known target slab scores. We then fit an upper bound on how the audit error grows with displacement via high-quantile regression, and subtract the estimated error from the transported privacy lower bound to achieve a conservative correction. Experimental results show that uncorrected observational auditing can substantially overestimate privacy leakage, whereas the proposed method yields privacy lower bounds that are closer to the oracle and more informative than existing correction baselines across multiple settings.

Critical strengths

[1] The research problem has clear practical significance, and the methodology directly targets the ultimate goal of privacy auditing.

This paper considers models that have already been deployed, cannot be retrained, and whose sample inclusion process is beyond the auditor's control — a setting that is particularly important for large-scale models and third-party privacy auditing. Rather than directly improving the accuracy of MIA score prediction, the authors define the correction target as the transport-induced audit error, i.e., the effect of the transport operation on the final μ-GDP privacy lower bound. This design aligns more closely with the practical objective of privacy auditing, since score-level prediction error does not necessarily translate into audit-level error. In my view, modeling and calibrating the transport error directly at the audit-metric level constitutes a valuable contribution of this work.


[2] Shift-aware calibration offers a practical approach for estimating unknown transport errors using available data, supported by convincing empirical results.

The paper constructs observable source-target transport tasks within the OOD non-members and varies the representation-space displacement to estimate how the audit error changes. This enables the authors to correct counterfactual transport outcomes without access to ground-truth IID non-member scores. The approach naturally integrates conditional score modeling with uncertainty calibration.

Critical weaknesses

[1] The core theoretical guarantees rely on strong calibration assumptions that are difficult to verify, and it remains unclear whether practical implementations satisfy them.

The most critical contribution of this paper is the construction of calibration tasks within OOD data to estimate the audit error induced by the true OOD-to-IID transport. However, Assumption 2 essentially requires that the upper tail of the error distribution from within-OOD calibration tasks conservatively covers the error of the true cross-domain transport. In realistic observational auditing scenarios, IID non-member scores are unobservable, making this assumption difficult to verify directly. Moreover, the conditional score variation mechanism between two OOD slabs may not be representative of the true OOD-to-IID shift, particularly in the presence of conditional invariance violations or severe support mismatch.

Furthermore, Assumption 4 requires the estimated error envelope to provide uniform upper confidence coverage over the entire calibration interval (Equation 25). In practice, however, the method fits calibration pairs using 0.95 quantile regression and accounts for estimation uncertainty via bootstrap. In general, fitting a conditional quantile does not automatically yield a high-confidence upper bound that simultaneously covers the entire interval. The paper does not adequately explain how the specific quantile regression and bootstrap procedures satisfy the property required by Equation (25).


[2] A gap remains between the theoretical guarantees and the practical usage of the method, particularly regarding complex distribution shifts and design choices.

The authors define a single shift direction based on the whitened difference in representation means, and use a scalar displacement as the predictor of audit error. However, high-dimensional distribution shifts cannot necessarily be adequately characterized by mean displacement alone. For instance, two distributions may exhibit similar means while differing substantially in covariance structure, multimodality, or the conditional score mechanism. Consequently, similar displacements do not necessarily correspond to similar transport-induced audit errors.

Moreover, Theorem 1 requires the target displacement to lie within the calibration interval. As explicitly stated in Appendix A, when the target displacement exceeds the maximum value covered by the calibration tasks, the same conservativeness guarantee no longer holds. This stands in some tension with the method's stated goal of handling severe distribution shifts.

Questions for authors

Q1

CINIC-10 [1] contains images from the original CIFAR-10 training set. Since the target model is trained on CIFAR-10, how do the authors ensure that all CINIC-10 samples used as OOD non-members are absent from the target model's training set?

Q2

Can you explain more about why the proposed methods exhibit a substantial loss of privacy evidence even in the IID setting?

Q3

About Assumption 2: Assumption 2 requires that the upper tail of the error distribution over the within-OOD calibration tasks conservatively dominate the error incurred by the true OOD-to-IID transport. Could the authors further clarify under which distribution shift mechanisms this assumption is more likely to hold?

In particular, when the true shift involves not only representation mean displacement but also covariance shift, multimodal shift, or violations of conditional score invariance, can the internal calibration tasks still provide a reliable error upper bound?


References

[1] https://github.com/BayesWatch/cinic-10/blob/master/README.md

2 comments
AuthorsOpenReview ↗

Response to Reviewer GE8E (1/2)

Thank you for recognizing the practical significance of our work and for your helpful review. We address your concerns below.

Weaknesses

W1

In realistic observational auditing scenarios, IID non-member scores are unobservable, making Assumption 2 difficult to verify directly.

We acknowledge that Assumption 2 is strong and may be hard to verify directly in practice. Our theoretical result therefore provides sufficient conditions under which the proposed correction is conservative relative to the oracle IID audit. To empirically assess the effectiveness of our approach, as discussed in our responses to W2 and Q3 below, we designed calibration tasks where the target displacement exceeds the calibrated range to test whether Assumption 2 still holds. We also conducted controlled synthetic experiments with varying levels of distribution shift to investigate the conditions under which our method may fail. Although these results cannot formally verify Assumption 2, they provide empirical evidence supporting the effectiveness and conservativeness of our calibration approach. We have clarified the limitation of Assumption 2 on page 8, lines 408-411.

Lastly, as we discussed in the Discussion section: While our method does not provide formal validity guarantees under realistically verifiable assumptions, establishing such guarantees under distribution shift remains challenging for existing observational auditing approaches as well. PANORAMIA [1] does not provide a theoretical lower bound on the privacy loss and zero-run auditing paper [2] also relies on assumptions that are hard to verify in practice. Addressing this challenge is an important direction for future work.

The paper does not adequately explain how the specific quantile regression and bootstrap procedures satisfy the property required by Equation (25).

We have added clarification of the conditions required in Equation 25 on Appendix D.4. We agree that fitting a conditional quantile does not automatically yield a high-confidence upper bound covering the entire calibration interval simultaneously. One possible approach to establishing Equation 25 is to bootstrap the reference data, reconstruct the calibration tasks, refit the conditional quantile curve, and construct a simultaneous upper confidence band using the maximum deviation across the interval. Our current implementation bootstraps the entire auditing pipeline, including reference-data resampling, transport fitting, calibration, and correction. It therefore captures resampling variability in the final corrected estimate, including variability introduced by calibration.

W2

However, high-dimensional distribution shifts cannot necessarily be adequately characterized by mean displacement alone. For instance, two distributions may exhibit similar means while differing substantially in covariance structure, multimodality, or the conditional score mechanism.

We would like to highlight that the distribution shifts considered in our experiments are not limited to mean shifts. We have quantified the shifts for all datasets in Appendix D.1. The new Figure 10 shows that all datasets exhibit shifts in both the mean and covariance structure of their representation distributions. Despite these shifts, our method consistently produces meaningful privacy lower bounds that remain relatively close to the oracle IID audit.

These findings suggest that, although our scalar displacement does not capture every aspect of high-dimensional distribution shifts, it can still serve as a useful empirical predictor of transport-induced audit error, even when the underlying distribution shift involves changes beyond the mean. Nevertheless, we acknowledge that this representation may be insufficient for certain distribution shifts, and we have added the clarification of this limitation on page 10, lines 530-535, in the revised manuscript.

When the target displacement exceeds the maximum value covered by the calibration tasks, the same conservativeness guarantee no longer holds.

We have conducted additional experiments to investigate this setting, as detailed in Appendix D.2. We acknowledge that our current assumptions do not provide theoretical guarantees in this setting, as it requires extrapolation beyond the displacement range covered by the calibration tasks. To investigate this case empirically, we specifically design calibration tasks such that the target displacement exceeds the maximum displacement observed during calibration. New Figures 11 and 12 report the comparison of estimated privacy bounds across narrower displacement calibration. Using smaller displacements does not consistently increase or decrease the final audit bound, which shows the robustness of our method in this extrapolation setting. Across all experiments, the predicted audit errors conservatively dominate the true audit errors. New Figures 13 and 14 provide empirical evidence supporting Assumption 2 in this setting.

AuthorsOpenReview ↗

Response to Reviewer GE8E (2/2)

Questions:

Q1

How do the authors ensure that all CINIC-10 samples used as OOD non-members are absent from the target model's training set?

The CINIC-10 test set consists of 10,000 images from the CIFAR-10 training set, 10,000 images from the CIFAR-10 test set, and 70,000 images from ImageNet. We sample 10,000 OOD non-members exclusively from the CIFAR-10 test and ImageNet subsets, excluding all images originating from the CIFAR-10 training set. This ensures that the sampled non-members do not overlap with the target model's training data. We added the clarification in Appendix B, lines 784-788.

Q2

Can you explain more about why the proposed methods exhibit a substantial loss of privacy evidence even in the IID setting?

The loss of privacy evidence is primarily due to the conservative correction introduced in our method. Since this correction accounts for potential transport-induced errors, it can reduce the estimated privacy lower bound even in the IID setting, where such a correction may not be necessary. Note that the baselines also exhibit a loss of privacy evidence in this setting. As shown in Figure 3, our methods remain robust under distribution shifts, which is our primary objective. This reflects a trade-off between conservativeness and auditing effectiveness. When the data distributions are known to be IID, our method may not be the optimal choice, as existing auditing methods specifically designed for the IID setting may achieve tighter privacy lower bounds. We have added this discussion on page 9, lines 478-495.

Q3

Could the authors further clarify under which distribution shift mechanisms this assumption is more likely to hold? In particular, when the true shift involves not only representation mean displacement but also covariance shift, multimodal shift, or violations of conditional score invariance, can the internal calibration tasks still provide a reliable error upper bound?

We have designed synthetic experiments to control the shift level and demonstrated under what cases our method works and fails in Appendix D.3. As discussed above, our method is not restricted to mean shifts. All four datasets in our experiments exhibit differences in both the mean and covariance structure of their representation distributions. Despite these shifts, our method produces meaningful privacy lower bounds that remain relatively close to the oracle IID audit.

More generally, Assumption 2 is more likely to hold when the within-OOD calibration tasks can adequately capture the transport-induced audit error along the actual OOD-to-IID shift. In particular, this is more plausible when there is sufficient overlap between the source and target distributions and the relationship between displacement and transport-induced audit error remains reasonably stable.

To further investigate the applicability and limitations of Assumption 2 under different distribution shifts, we conducted additional controlled experiments on synthetic data. Details of the synthetic experiments can be found in Appendix D.3. We generate training samples and independent IID non-members from the same population: X∼N(u,Id)X\sim N(u,I_d). We then introduce distribution shifts by generating OOD non-members from Y∼N((1−t)u,Id+(t2)/4uuT)Y\sim N((1-t)u,I_d+(t^2)/4uu^T). We vary the shift level over t∈[0,2,4,16,64]t\in [0,2,4,16,64], which simultaneously changes the mean and covariance structure of the raw non-member distribution.

As shown in the new Figure 15, corrected residual transport produces tighter privacy lower bounds than corrected quantile transport for shift levels up to t=16t=16. However, at t=64t=64, neither method produces a meaningful estimate. To better understand this failure, we additionally visualize the domain-propensity distributions in the new Figure 16. The results show that the overlap between the two distributions becomes extremely limited at t=64t=64, suggesting that severe support mismatch contributes to the failure of our calibration procedure. Although these results cannot formally verify our assumptions, they provide empirical evidence supporting the effectiveness and conservativeness of our calibration approach.

These findings provide further empirical evidence that our method can handle distribution shifts involving changes beyond the mean, while also illustrating its limitations under extreme distribution shifts. The importance of sufficient overlap is also consistent with the impossibility result of [2], which demonstrates that, under non-overlapping distributions, no pp-valid observational audit algorithm can obtain informative privacy guarantees.

[1] Kazmi et al. . Panoramia: Privacy auditing of machine learning models without retraining. NeurIPS, 2024.

[2] Cebere et al. . Privacy auditing with zero (0) training run. arXiv:2605.14591, 2026.

Reviewer_c1hMOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper proposes a new scheme for observational privacy auditing. One of the main issues of such audit is that the auditor doesn’t have access to non members coming from the same distribution as members. The authors propose to fix this issue by creating counterfactual membership scores using score transport. They first learn a model on OOD non-members to predict (non-member) membership score from data representation (an embedding of the original data). Then they estimate the distribution of IID non-members' scores using residual or quantile transport, sampling embeddings from the IID member distribution.

Transport learned on OOD data can artificially inflate privacy estimates. As a consequence authors proceed to a calibration step. They divide OOD non-member data into tiles ordered along an axis from more OOD like to more IID like. They learn how audit error varies with transport distance. They use this calibration step to estimate the 95 percentile of the error and correct the obtained audited value. Finally authors use bootstrap to account for finite sample uncertainty.
Authors validate their approach on image and test dataset and provide empirical privacy lower bounds tighter than previous work.

Critical strengths

The paper targets an important and very relevant issue for practical auditing of already deployed machine learning systems with no available non-members. This is particularly relevant in a state of thing where foundation model are trained on web scale training set with no or limited IID non-member data.

Their proposed methodology takes a different approach compared to previous work is quite interesting and is well supported by theory. Authors make the assumptions needed in order to obtain a valid privacy lower bound clear and discuss possible failure cases. The paper appear sound and rigorous.

Critical weaknesses
  • I think the paper is lacking more details about the auditing f-DP in one run procedure (Mahloujifar et al 2025). Even if it is not the contribution this paper makes, it is still an important piece of the auditing scheme and the paper lacks more details about how to obtain μ^\hat{\mu}. In particular, I think the one run auditing schemes proposed by Mahloujifar et al 2025, require Bernoulli sampling with each audit example being included in training set with probability ½. We can’t perform sampling prior to model training when evaluating an already trained model so I am wondering if the μ\mu value you obtain with μL(c,k,n)\mu_L(c,k,n) is still valid without Bernouilli sampling?

  • In order for the procedure to produce a valid lower bound on the privacy parameter μ\mu authors make several assumptions. I think the paper could benefit from more experiments in order to study how those assumptions hold in practice. In particular I am interested in the assumption that residual distribution is invariant across covariates and domains. It appears to me as a strong assumption for a valid linear residual transport and would be curious to see if it holds for the experiments you conducted.

MINOR: I recognise space is limited for ICLR submission but the paper is quite dense and packed with different mathematical tools making it sometimes hard to follow.

Questions for authors
  • I did not understand how you obtain the actual transported non-member MIA scores to be used for the audit from the distribution of transported non member scores. how do you obtain individual (scalar) MIA scores to run the actual audit?

  • In Appendix B you say you sweep across different possible values of c [1000,2000,3000,4000] and report the largest obtained lower bound. Do you apply any correction to account for the multiple statistical test?

  • Finally, It seems that the audit procedure needs to retrain models a significant number of times due to calibration step and bootstrap. I would be curious to know for one audit what is the number of fitted models? How long does one audit run take? Does the running time motivate the choice to project original data in an embedding space?

4 comments
AuthorsOpenReview ↗

Response to Reviewer c1hM (1/2)

Thank you for recognizing the importance of the research problem and for your careful review. We address your concerns below.

Weaknesses:

W1

I think the paper is lacking more details about the auditing f-DP in one run procedure...We can’t perform sampling prior to model training when evaluating an already trained model so I am wondering if the μ\mu value you obtain with μL(c,k,n)\mu_L(c,k,n) is still valid without Bernoulli sampling?

Thank you for raising this good point! We have added the discussion on page 4, lines 187-191, to clarify the conditions under which one-run f-DP auditing is valid in the observational setting. We agree that sampling prior to model training is not feasible when auditing an already trained model. In our setting, we assume that the auditor has access to equal-sized subsets of members and non-members independently sampled from PP and QQ, respectively. When P=QP=Q, μ\mu remains a valid lower bound in the observational setting because the observed membership labels behave like randomized inclusion bits. However, when P≠QP\neq Q, the uncorrected μ\mu is no longer guaranteed to be a valid lower bound, which motivates the correction proposed in our method.

W2

I think the paper could benefit from more experiments in order to study how those assumptions hold in practice.

To empirically assess the effectiveness of our approach, we have designed calibration tasks where the target displacement exceeds the calibrated range to test whether assumption 2 still holds in Appendix D.2, and constructed synthetic experiments to control the shift level to investigate under what conditions our method fails in Appendix D.3.

Specifically, our theorem requires the target displacement to lie within the calibrated range and the stated assumptions to hold. When the target displacement exceeds the maximum calibrated displacement, our assumptions do not provide theoretical guarantees. To investigate this setting, we designed calibration tasks where the target displacement exceeds the calibrated range. New figures 11 and 12 report the comparison of estimated privacy bounds across narrower displacement calibration. Using smaller displacements does not significantly increase or decrease the final audit bound, which shows the robustness of our method in this extrapolation setting. Across all experiments, the predicted audit errors conservatively dominate the true audit errors. New figures 13 and 14 provide empirical evidence supporting Assumption 2 in this setting. More details are provided in Appendix D.2.

To further investigate the applicability and limitations of our assumptions under different distribution shifts, we conducted additional controlled experiments on synthetic data. Details of the synthetic experiments can be found in Appendix D.3. We generate training samples and independent IID non-members from the same population: X∼N(u,Id)X\sim N(u,I_d). We then introduce distribution shifts by generating OOD non-members from Y∼N((1−t)u,Id+(t2)/4uuT)Y\sim N((1-t)u,I_d+(t^2)/4uu^T). We vary the shift level over t∈[0,2,4,16,64]t\in [0,2,4,16,64], which simultaneously changes the mean and covariance structure of the raw non-member distribution.

As shown in the new Figure 15, corrected residual transport produces tighter privacy lower bounds than corrected quantile transport for shift levels up to t=16t=16. However, at t=64t=64, neither method produces a meaningful estimate. To better understand this failure, we additionally visualize the domain-propensity distributions in the new Figure 16. The results show that the overlap between the two distributions becomes extremely limited at t=64t=64, suggesting that severe support mismatch contributes to the failure of our calibration procedure. Although these results cannot formally verify our assumptions, they provide empirical evidence supporting the effectiveness and conservativeness of our calibration approach.

In particular I am interested in the assumption that residual distribution is invariant across covariates and domains….and would be curious to see if it holds for the experiments you conducted.

We have added an empirical diagnostic to validate the residual invariance assumption. Specifically, we compare held-out nonmember residual CDFs across the IID and OOD domains. Details can be found in Appendix D.1 The new Figure 10 shows substantial discrepancies for DomainNet and CINIC-10, and almost no discrepancies for arXiv and CIFAR-10-C. These findings indicate that exact residual invariance does not hold uniformly across our experiments. It can also explain the failure of linear residual transport on CINIC-10.

AuthorsOpenReview ↗

Response to Reviewer c1hM (2/2)

MINOR: I recognise space is limited for ICLR submission but the paper is quite dense and packed with different mathematical tools making it sometimes hard to follow.

We have added an explanation of the intuition behind our method and provided additional explanations of the key components in Section 4.3. Moreover, at the beginning of Section 4, we have explicitly connected Figure 1 and Algorithm 1 to Sections 4.1–4.3 to provide a clearer roadmap of the methodology.

Questions:

Q1

How do you obtain individual (scalar) MIA scores to run the actual audit?

To obtain individual scalar scores, we extract evenly spaced quantiles from this distribution using linear interpolation and assign them to individual non-member records according to their score ranking. These individual transported scores are then used to compute the transported audit bound. We have added the clarification on page 6, lines 277-280.

Q2

Do you apply any correction to account for the multiple statistical test?

Thank you for pointing this out. We did not apply a multiple-testing correction in the initial submission but now have added new results with correction in Appendix C.2.

We adopt the same procedure for both our method and all baselines. This practice–sweep across different possible values of guess counts and report the largest obtained lower bound—has also been commonly adopted in prior privacy-auditing work [1,2]. Though this is a common practice, without a correction, the selected maximum can affect the nominal confidence level. Therefore, we apply Bonferroni correction [3,4] to maintain the nominal confidence level. Since we consider only 4 guess counts, applying the Bonferroni correction results in slightly more conservative privacy lower bounds across all methods. The largest relative decrease is 15.7%, observed for corrected quantile transport on CINIC-10, where the lower bound decreases from 0.5262 to 0.4434. Nevertheless, the correction does not change the relative ranking of the methods or our overall conclusions. Our methods continue to provide robust privacy lower bounds under OOD distribution shifts. The results can be found in the new Figure 6.

Q3

I would be curious to know for one audit what is the number of fitted models? How long does one audit run take?

Each audit involves 50 calibration runs and 200 bootstrap repetitions, resulting in a total of (200+1)×50=10,100(200+1)\times 50=10,100 fitted models. Importantly, we do not need to retrain the target model. The fitted models are lightweight MLPs used for score transport, rather than the target model itself. Further implementation details are provided in Appendix B. We report the running time for each benchmark below. Each job used a single NVIDIA Tesla V100 GPU. As on CIFAR-10-C, 5 severities have similar running time, we report severity level=1 here. The full tables can be found in Appendix C.3.

Corrected residual transport:

DatasetTime per slab (s)Time per bootstrap (s)Time per full audit (h)
CIFAR-10-C (severity 1)0.5431.681.67
CINIC-100.3121.911.13
DomainNet0.3227.561.45
arXiv0.9052.932.66

Corrected quantile transport:

DatasetTime per slab (s)Time per bootstrap (s)Time per full audit (h)
CIFAR-10-C (severity 1)0.5839.272.01
CINIC-100.4231.401.66
DomainNet0.5458.782.75
arXiv0.7545.122.35

Does the running time motivate the choice to project original data in an embedding space?

Regarding the use of the embedding space, as discussed in the paper on page 5, lines 216-218, directly modeling MIA scores as a function of high-dimensional input data is challenging. Therefore, we instead perform score transport in a lower-dimensional representation space, which makes the relationship between data representations and MIA scores easier to model. We have added the clarification on page 4, lines 213-215.

[1] Steinke et al. . Privacy auditing with one (1) training run. NeurIPS, 2023.

[2] Mahloujifar et al. . Auditing f-differential privacy in one run. ICML, 2025.

[3] Dorseuil et al. . Reliable estimation of differential privacy under selection bias. arXiv:2610.27021, 2026.

[4] O. J. Dunn, Multiple comparisons among means, JASA, 1961.

Thank you for the additional experiments, clarification and answers to the question.
The rebuttal addresses several of my concerns and has strengthened my confidence in my initial positive assessment. I was initially somewhat hesitant about my recommendation, but the additional explanations and experimental results have made me more confident in recommending acceptance.

AuthorsOpenReview ↗

Response to Reviewer c1hM

Thank you very much for your response. We are glad that our additional experiments and explanations have addressed your concerns, and we really appreciate your positive assessment of our work.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Global comment

We thank all three reviewers for their careful reading and constructive feedback. A common suggestion across the reviews was to provide additional experiments to investigate how our assumptions hold in practice.

We have now updated the submission PDF with additional explanations and experimental results addressing the reviewers' comments. All revisions are highlighted in blue for ease of reference. In the main text, we have focused on clarifying our assumptions, methodology, and experimental findings. The newly conducted experiments are presented in the appendix, where we have also added a table of contents, with new sections highlighted in blue, to help reviewers easily locate the relevant results.

We sincerely thank the reviewers again for their valuable feedback, which has helped us substantially improve the clarity and empirical evaluation of our work.

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

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