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Under review as a conference paper at ICLR 2027

Privacy-Preserving Clinical Speech Embeddings under Multi-Recording Identity-Linkage Attacks

Abstract

Privacy in learned representations can fail under repeated observation. An embedding that appears privacy-preserving on its own may reveal identity when information from multiple recordings of the same person is combined. We study this problem in clinical speech and introduce MoIRAGE (Multi-observation Identity-Resistant Adversarially Generated Embeddings), a framework for privacy-preserving representation learning under repeated observations. MoIRAGE separates an input embedding into clinically relevant content and an identity-related component, discards the original identity-related component, and replaces it with a synthetic alternative before generating the released embedding. The model is trained against identity-linkage attacks that jointly analyze multiple recordings, while clinical-consistency and diversity objectives preserve clinically relevant information and prevent representation collapse. At inference time, MoIRAGE does not require the participant's diagnosis label. We evaluate MoIRAGE on the UNMC clinical speech dataset using pooled held-out predictions from five participant-disjoint outer folds covering 137 participants, including 127 with clinical labels. MoIRAGE retains performance on the target clinical task, achieving an AUROC of 0.643 compared with 0.567 for the original embeddings. With a single recording (K=1), the strongest identity-linkage AUC* decreases from 0.778 to 0.528, close to chance. With 20 recordings (K=20), the strongest identity-linkage AUC* decreases from 0.963 for the original embeddings to 0.811 with MoIRAGE, while TPR at 1% FPR decreases from 0.474 to 0.036. Ablation experiments identify replacement of the identity-related component as the central mechanism underlying the privacy reduction, while a teacher-free variant shows similar behavior on Bridge2AI without speaker-teacher supervision. These results show that privacy cannot be adequately evaluated from single observations alone: identity leakage can increase as repeated measurements become available, and MoIRAGE explicitly addresses this multi-observation threat model while retaining performance on the target clinical task.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
privacy-preserving embeddings, clinical speech, representation learning, identity privacy

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
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Paper summary

This paper proposes a privacy protection technique called MoIRAGE, which prevents identification of participants in clinical speech datasets, specifically when participants engage in mutliple recordings. Existing privacy defenses are not designed to protect against multi-observation adversaries, or they overly degrade the clinical utility of a model. This new approach seperates each speech signal into a clinical component and an identity related component. The identity component is then replaced with a synthetically generated sample. This protected sample can then be safely embedded and released to the public. Training objectives aim to maximize clinical utitlity and minimize accuracy of mutli-sample MLP adversary models. Regularization is also applied to prevent the synthetic component from giving all samples the same embedding (degeneration).

The method is evaluated on held out test datasets and attack models that were not included in training. MoiRAGE is compared with several baselines and is shown to improve the privacy-utility tradeoff. Additonal analyses show that the main contributor to privacy is the synthetic replacement for the identity signal, while the trained resistance against multi-sample attackers provides a smaller addiitonal benefit.

Critical strengths

The authors very strongly motivate the importance of their work, especially during the related works section. Their evaluation of the quality of the approach is extremely thorough, using several other baselines model as comparison, training different types of attack models, and reporting worst case results over several folds. This gives the reader high confidence that this privacy approach outperforms all other existing methods for this context. The exploration of how much different components contribute to privacy was very interesting, as was the extension to Bridge2AI. The figures included in the paper are high quality and contribute well to overall understanding.

Critical weaknesses

Section 4 lacks some important details about the training procedure, which are left for the appendix. I think some of these details need to be brought back into the main text to help with reader understanding. Specifically:

  1. More detail on where the synthetic identity component is sampled from
  2. Equation (5) includes several variables that are undefined (ρ,ϕ,ψ\rho,\phi,\psi)
  3. What exactly is the clinical utility constraint and how does it differ from preserving clinical information?

Throughout the paper, acronyms TPR and FPR are used without linking to their meanings.

The discussion lacks critical reflection, and instead tends to summarize the main contrubutions like a conclusion. I would appreciate a deeper discussion of the limitations, and suggestions of how critical improvements, like privacy gurantees, could be incorporated. Additionally, it would be interesting to consider whether this approach could extend beyond speech-data into other datatypes.

Questions for authors

-Is this privacy approach unique to speech data, if so why?

-Are the attack assumptions realistic? What is the current standard for protecting privacy of participants in clinical speech data?

-The paper states that this approach does not 'anonymize' participants: is this because that would degrade clinical utility too far? Would anonymization occur if the synthetic replacement for the identity component was random noise?

1 comment

Thank you for the thoughtful review. We revised Sections 3-4, the Discussion, and the appendices to clarify the synthetic replacement mechanism, attacker design, utility constraint, and limitations.

W1. Synthetic identity sampling. MoIRAGE learns a 32-dimensional class-conditional diagonal Gaussian prior jointly with the encoder and decoder. At release, the source identity component is discarded and replaced by a sample combined with the deterministic content posterior mean. No diagnosis label is required at inference: the conditioning class is sampled from TRAIN class frequencies. Standard-normal and unconditional prior substitutions yield similar results, so our contribution does not depend on the specific prior distribution.

W2. DeepSets attacker. We clarified Eq. (5). A shared encoder processes each embedding; mean and population-standard-deviation pooling produces a permutation-invariant set representation (standard deviation is zero for K=1K=1). A set-level network and symmetric head predict whether two collections belong to one participant. DeepSets is used during training, while independent attacker families are used for evaluation (Sec. 4; App. H).

W3. Clinical utility constraint. Clinical prediction, teacher distillation, and release consistency preserve task information. Separately, the dual constraint penalizes clinical loss exceeding 105% of its warm-up reference, discouraging degradation during privacy optimization. Appendix C specifies the complete objective, weights, training schedule, and dual updates.

W4. TPR/FPR. We now define True Positive Rate (TPR) and False Positive Rate (FPR) at first use. Under corrected size-controlled evaluation at K=10K=10, TPR at 1% FPR falls from 0.738 to 0.018, and rank-1 identification from 0.876 to 0.087 (Table 1; App. L).

Q1. Extension beyond speech. Factorization, synthetic replacement, and collection-level adversarial training operate on embeddings and could extend to other longitudinal modalities. However, we validate only speech-derived representations, not imaging or wearables. The Bridge2AI variant removes ECAPA supervision but remains speech-based (Sec. 6.4).

Q2. Realistic attack assumptions. We assume attackers can access released embeddings, know the release procedure, and train with separate labeled reference participants. They do not need a target's raw audio or diagnosis. Our task is linking collections to the same participant, not recovering a legal identity. We clarify that this protection complements consent, access controls, data-use agreements, and institutional governance (Secs. 3, 7).

Q3. Anonymity and random replacement. Clinical content can retain identity even after replacement. The content-only ablation remains highly linkable (AUC⋆=0.982\mathrm{AUC}^{\star}=0.982 at K=20K=20), so replacing one factor does not establish anonymity. At K=20K=20, Gaussian noise (σ=1\sigma=1) achieves linkage 0.622 but reduces clinical AUROC to 0.473. MoIRAGE achieves linkage 0.596 with AUROC 0.643. Our contribution is a better privacy-utility trade-off under repeated observations, not randomness alone. We claim neither anonymity nor differential privacy; formal guarantees require a defined privacy relation, bounded sensitivity, and repeated-release accounting (Secs. 6–7; App. K).

Discussion, limitations, and correction. We now acknowledge residual linkage, smaller eligible cohorts at larger KK, adaptive attackers, and limited clinical-task coverage. Bridge2AI is a development replication, with lower AUROC for 10 of 12 auxiliary conditions. As explained in our common response, we found a collection-size cue in the submitted evaluation and replaced the primary results with exact-KK, size-controlled evaluation of frozen release models and retrained attackers. Historical results are separately labeled.

We appreciate the reviewer's suggestions, which strengthened the clarity and scope of our claims.

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Paper summary

This paper studies identity-linkage risks in clinical speech embeddings under repeated observations. Even when an individual released embedding reveals little identity information, an attacker may recover participant identity by aggregating embeddings from multiple recordings. The proposed framework, MoIRAGE, decomposes an input representation into clinically relevant content and an identity-related component, replaces the original identity component with a synthetic sample, and generates a released embedding. Training combines collection-level adversarial objectives, clinical prediction and consistency losses, and anti-collapse regularization. The primary release setting does not require the target participant’s diagnosis label.

Critical strengths

The paper addresses a practically important privacy problem that single-observation evaluation can underestimate. Clinical speech datasets often contain multiple tasks, visits, or longitudinal recordings from the same participant, making the accumulation of identity evidence a realistic concern. By placing repeated observations at the center of both method design and evaluation, the paper highlights a limitation of conventional recording-level privacy assessment. This perspective has value beyond the particular implementation and may inform privacy evaluation for other longitudinal health representations. In addition, the paper provides a relatively thorough and transparent assessment of both effectiveness and limitations. The evaluation goes beyond aggregate linkage AUC to consider strict operating points, participant retrieval, multiple attacker families, and component ablations.

Critical weaknesses

Related work already considers pseudo-speaker distribution learning, identity replacement, and privacy-preserving representation learning, but the quantitative baselines primarily consist of Gaussian perturbation, a content-only representation, and INLP. The ablations support the importance of replacement within the current architecture, but they do not establish whether MoIRAGE improves over a reasonably implemented existing identity-replacement approach or whether its learned class-conditional prior is preferable to simpler alternatives.

Questions for authors
  1. What are the actual collection sizes at each reported K ?
  2. How are negative pairs constructed in the final evaluation?
1 comment

Thank you for recognizing the importance of repeated-observation privacy and identifying the missing identity-replacement comparisons. We agree that internal ablations alone are insufficient. We added baselines, tested simpler priors, and corrected an evaluation confound revealed by your questions.

W1. Comparison with existing replacement methods. We compared three embedding-level adaptations on the same UNMC TEST representation: pool-based pseudo-speaker replacement, sampled pseudo-speaker replacement, and identity-subspace removal. These adapt existing ideas; they are not reproductions of waveform-anonymization systems. Subspace-removal rank was tuned on development data. Corrected, exact-KK UNMC TEST results are:

MethodK=1K=1 AUC*K=5K=5 AUC*K=20K=20 AUC*Clinical AUROC
Original embeddings0.7880.9440.9890.567
Gaussian noise (σ=1\sigma=1)0.5220.5340.6220.473
Subspace removal0.6460.8770.9880.578
Pool pseudo-speaker0.6900.8730.9730.549
Sampled pseudo-speaker0.5050.6440.7430.517
MoIRAGE0.5200.5910.5960.643

Sampled pseudo-speaker replacement is slightly better at K=1K=1 (0.505 versus 0.520), which we explicitly acknowledge. At K=20K=20, however, its linkage is 0.743 versus 0.596 for MoIRAGE, with lower clinical AUROC (0.517 versus 0.643). Removing synthetic replacement yields linkage 0.982, and removing multi-observation training increases it to 0.852 at K=20K=20. This supports replacement combined with collection-level adversarial training (Sec. 6.2; App. K, Tables 6 and 7).

W1. Is the class-conditional prior necessary? We also evaluated release-time substitutions using a standard-normal or unconditional Gaussian prior. At K=20K=20, their linkage/clinical AUROC pairs are 0.600/0.644 and 0.580/0.643, versus 0.596/0.643 for MoIRAGE with its learned class-conditional prior. Appendix R separately reports development-fold retrained-prior sensitivity. We do not claim the class-conditional prior is independently novel or superior. The contribution is the combination of factorization, stochastic replacement, multi-observation training, and repeated-observation evaluation.

Q1. What were the actual set sizes? In the submitted evaluation, nominal KK used min⁡(K,available)\min(K,\mathrm{available}). Mean effective set sizes at K=1,2,5,10,20K=1,2,5,10,20 were 1.00, 1.95, 4.65, 8.44, 12.70, respectively. A size-only score achieved AUC* 0.895 at nominal K=20K=20, because positive and negative pairs differed in set-size matching. We therefore replaced the primary evaluation with exactly KK disjoint participant-day observations on each side, excluded ineligible participants, and retrained evaluation attackers separately for each KK. MoIRAGE release models and checkpoints remained frozen. Corrected original/MoIRAGE linkage is 0.788/0.520 at K=1K=1 and 0.989/0.596 at K=20K=20. At K=20K=20, 35 participants qualify; the submitted nominal K=50K=50 result was not an exact-50 test. Eligible populations differ across KK. Original values are labeled diagnostics. We disclose that training and checkpoint selection also used variable-size sets, whose potential influence remains (Sec. 5; Apps. D, G).

Q2. How were evaluation negatives constructed? Each eligible participant contributes disjoint enrollment and probe collections. Within each TEST fold, every enrollment is compared with every eligible probe. Diagonal comparisons are positives; all other pairs are negatives. At K=1K=1, the pooled five-fold evaluation contains 137 positive and 3,618 negative pairs. At larger KK, only eligible participants enter this all-to-all comparison. Diagnosis matching is used in balanced attacker TRAIN batches, not to restrict the primary TEST negatives. This distinction and trial counts are now documented in Appendix G.

An anonymized supplementary ZIP includes corrected evaluation and baseline code. Your questions exposed a material confound and helped us support a narrower claim: MoIRAGE reduces empirical multi-recording identity linkage while retaining performance on the primary clinical task, without a claim of anonymity or differential privacy.

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Paper summary

This paper addresses an important and under-studied problem — identity linkage across multiple released clinical speech embeddings — with a degree of empirical honesty and internal rigor that I found genuinely refreshing. The evaluation is a model for adversarial-privacy work (strongest-observed-attacker reporting with the train/eval gap disclosed, within-diagnosis negative sampling, participant- and day-disjoint protocols, and candid disclosure of sampler bugs that were fixed and re-run), and the mechanistic analysis is a contribution in its own right: the ablation chain convincingly isolates synthetic identity replacement as the causal lever, while the dispersion scaling (R−1.03R^{-1.03} against the predicted 1/R1/R) and variance decomposition give a quantitative account of why residual linkage persists. I re-derived the paper's single formal identity, verified all ten loss weights in Eq. (21), the symmetry of the comparison score, and the abstract-to-table cross-checks, and found them correct to an unusual degree; claims are carefully calibrated throughout, with no anonymity or differential-privacy guarantee overstated. The work needed before submission lies in four themes rather than in the core contribution: the mathematical presentation, correct in its essentials, needs local cleanup of notation, definitions, and a few supporting derivations; related-work coverage, strong for clinical speech, has gaps in adjacent literatures that would sharpen the positioning; the otherwise excellent reproducibility apparatus still omits some concrete details;, given that residual linkage remains substantial (0.811 at K=20K{=}20), the framing of the practical privacy benefit — and the prose itself — would benefit from tightening.

Critical strengths
  • A correct, appropriately scoped formal derivation (App. M, p. 21). The paper's only formal derivation — the covariance-averaging identity Cov(1R∑rϵijr)  =  Σrel/R\mathrm{Cov}\Big(\frac{1}{R}\sum_{r}\epsilon_{ijr}\Big) \;=\; \Sigma_{rel}/R — was re-derived during review and is correct under its explicitly stated independence assumption ("If ϵijr\epsilon_{ijr} has covariance Σrel\Sigma_{rel} and is independent across releases"), exact at the R=1R = 1 edge, and stated with a sound ∀R≥1\forall R \geq 1 quantifier. There are no theorems, and none are needed: the assumptions burden is correctly matched to an empirical paper, and no empirical observation is dressed up as a formal guarantee.

  • Exact loss-weight consistency (Eq. (21), Appendix C, p. 15). All ten loss weights in the total objective cross-verify exactly against their defining prose (0.750.75, 2.02.0, 2.02.0, 2.5×10−42.5 \times 10^{-4}, 0.020.02, 0.60.6, 1.51.5, 0.20.2, 1.5/0.75/0.021.5/0.75/0.02), and the pseudocode loss set matches. This level of weight consistency is rare and worth preserving through revision.

  • A quantitatively supported dispersion law, with appropriate hedging (§1, p. 2). The dispersion series (0.711,0.355,0.140,0.069,0.0340.711, 0.355, 0.140, 0.069, 0.034 for R=1,2,5,10,20R = 1, 2, 5, 10, 20) matches 0.711/R0.711/R to within 0.0020.002 at every point, numerically supporting the fitted R−1.03R^{-1.03} exponent, and the variance-decomposition shares sum to exactly 100.0%100.0\%. The hedged wording ("repeated-release variation decreases approximately as 1/R1/R") is appropriate; you may wish to add a brief clause noting that with five points and a single fitted parameter the fit is near-automatic, so readers weight it correctly.

  • Evaluation honesty beyond the norm for adversarial-privacy work (§6.3, p. 8; App. G, p. 17). Strongest-observed-attacker reporting, with the train/eval attacker gap disclosed (a statistical MLP reaches an AUC⋆\mathrm{AUC}^{\star} of 0.8110.811, "compared with 0.6590.659 for the DeepSets attacker used during training" at K=20K = 20); negative pairs sampled within diagnosis group "so that the clinical label alone cannot solve the attack"; participant-disjoint attacker training; enrollment/probe day-disjointness; and candid disclosure of two sampler bugs, with unit tests added and pre-correction results discarded.

  • Claims calibrated to evidence throughout (§6.2, pp. 7–8; App. P, p. 24). Five explicit statements that no anonymity or formal/differential-privacy guarantee is provided; residual risk reported plainly (0.8110.811 at K=20K = 20; 0.8540.854 at K=50K = 50); the utility result correctly disclaimed because the confidence interval includes zero ("rather than as evidence that MoIRAGE improves diagnosis"); and scope self-limited precisely ("one main clinical task, two cohorts, and one input feature family per cohort"), with Bridge2AI explicitly framed as a development replication rather than a confirmatory test. The words "significant" and "state-of-the-art" — and any anonymity claim — appear nowhere.

  • A mechanistic analysis that identifies the causal lever (§1, p. 2). The ablation chain isolates synthetic identity replacement as the central privacy mechanism: "Removing synthetic identity replacement increases K=20K = 20 linkage to 0.9560.956" (from 0.8110.811), versus 0.8750.875 without multi-observation training and 0.8380.838 without ECAPA. The random-effects analysis is quantitative and verified — replacement-induced dispersion decreases as R−1.03R^{-1.03} against the predicted 1/R1/R — and the variance decomposition (82.9/14.8/2.3%82.9/14.8/2.3\%) explains why residual linkage persists.

  • Thoughtful threat-model and trial design (App. G, p. 17). Negative pairs are sampled within diagnosis group "so that the clinical label alone cannot solve the attack"; enrollment and probe are day-disjoint; the attacker may know the mechanism (privacy does not depend on keeping MoIRAGE secret); the release is label-blind and the attacked setting is the label-blind release; and effective-set-size rules avoid reusing recordings within a trial.

  • Honest treatment of failure modes (App. P, p. 24; App. O; App. B). A dedicated failure-cases appendix states plainly what the method does not do — identity is reduced, not removed; participant-level heterogeneity is unexplained ("The current work does not explain which speaker or recording properties cause this difference"); utility is preserved only on average. App. O reports that 1010 of 1212 auxiliary Bridge2AI conditions degrade, and App. B documents failed design variants — exactly the negative-result reporting the field needs.

  • Clean baseline provenance (§5, p. 6). All baselines ("the original embeddings, Gaussian perturbation, a content-only representation, and Iterative Nullspace Projection (INLP)") and all borrowed methods (WavLM, ECAPA, DeepSets, VIB) are third-party and re-implemented by the authors on their own data, so no prior-paper metric values are imported; there is no baseline-provenance mismatch and no self-citation cluster.

  • Defensible novelty positioning (§2, p. 3). External searches support the observation that "these directions are typically studied separately": no prior systematic repeated-observation linkage evaluation for released clinical embeddings was found (the closest conceptual prior work sits in the anonymization/ASV world), so the combination-novelty claim is defensible —, appropriately, no benchmark-SOTA claim is made.

Critical weaknesses
  • No external baseline (the strongest verified weakness). All comparators — "the original embeddings, Gaussian perturbation, a content-only representation, and Iterative Nullspace Projection (INLP)" (§5, p. 6), plus the ablations — are your own runs; there is no VoicePrivacy-style x-vector replacement or Chen et al. 2025 pseudo-speaker-distribution comparator, even though §2 describes Chen et al. as "closely related to the replacement component of MoIRAGE". We acknowledge the mitigations already present: validation-only INLP selection, a four-point σ\sigma sweep, best-operating-point reporting for baselines (Gaussian σ=1\sigma = 1 matches the no-ECAPA linkage only at much worse utility, stated plainly), and strongest-observed-attacker reporting with the train/eval gap disclosed. Still, adding one external replacement baseline adapted to embeddings would materially strengthen the empirical claims.

  • No sensitivity analysis for MoIRAGE's constants. No robustness results are reported for τ=0.5\tau = 0.5, Huber δ=0.5\delta = 0.5, the privacy ramp (epochs 25→8525 \to 85), the 0.12×0.12 \times target-eigenvalue floor, or the 0.30.3 effective-rank threshold; and the attacker capacity sweep — "width {64, 256}, depth {2, 3}, and training budgets {400, 800, 1600} steps" — covers only the main learned families at K=20K = 20 (App H, p. 18). A small robustness table, or an explicit scope note, would suffice.

  • The promised effective-set-size reporting is absent. App G (p. 17) commits to "report the operating point as all available and provide the mean effective set size" when availability saturates, yet no such numbers appear anywhere. With a median of 5050 chunks per participant, a full K=50K = 50 positive trial needs ≥100\geq 100 recordings (supportable by well under half the cohort), so it is ambiguous whether, e.g., 0.8540.854 (Table 4, K=50K = 50) is a fixed-KK or an all-available number. The repeated plateau values (cosine 0.6200.620 at K∈{20,30,50}K \in \{20, 30, 50\}; Bridge2AI cosine 0.5750.575 and original 0.9350.935 at K∈{5,20,50}K \in \{5, 20, 50\}) are consistent with saturation, but the paper never says so. The K=1→20K = 1 \to 20 headline trend is unaffected. Please report the mean effective set size per reported KK, plus one clarifying sentence.

  • The same-recording diagnostic is described but never reported. "A separate same-recording diagnostic receives two independent releases of the same recording" (App G, p. 17) and is said to be "reported separately" in App H, but no corresponding numbers appear in any table, figure, or prose (the cross-space results do appear, Tables 5 and 7). Please report the numbers or remove the description.

  • The Bridge2AI clinical-retention claim needs a pointer to App O. §6.4 (p. 8) states "Clinical information is also retained on Bridge2AI" without acknowledging that 1010 of 1212 auxiliary conditions decrease after transformation (App O / Table 9: muscle tension dysphonia 0.865→0.5750.865 \to 0.575, airway stenosis 0.904→0.7130.904 \to 0.713, PTSD 0.774→0.6060.774 \to 0.606). The sentence is true for the primary label (0.9480.948 vs. 0.9130.913, overlapping CIs), but one sentence pointing to App O would make the claim complete.

  • No confidence interval for the abstract's "close to chance". The abstract reports that the strongest identity-linkage AUC⋆\mathrm{AUC}^\star "decreases from 0.778 to 0.528, close to chance" (Abstract, p. 1), but the K=1K = 1 value has no interval anywhere, while K=20K = 20 is reported with one (0.8110.811 [0.779,0.838][0.779, 0.838], App I). Add the K=1K = 1 interval or soften the wording to "near chance".

  • Non-monotonic attacker columns without intervals or comment. The MoIRAGE attention-pooling column in Table 5 (p. 20) is non-monotonic (0.503→0.559→0.609→0.730→0.666→0.848→0.6750.503 \to 0.559 \to 0.609 \to 0.730 \to 0.666 \to 0.848 \to 0.675), and DeepSets dips at K=50K = 50 (0.674→0.6580.674 \to 0.658), with no per-cell CIs and no comment on the 0.848→0.6750.848 \to 0.675 swing. Per-KK retrained attackers plus saturation plus finite trials can produce this pattern (it is likely noise), but please add per-cell intervals or one commenting sentence.

  • The 0.8400.840 vs. 0.8110.811 gap is never reconciled. The 4545-run fold-seed study reports "mean attacker AUC⋆\mathrm{AUC}^\star was 0.840 with a between-run standard deviation of 0.039" (§6.3, p. 8 / App I), i.e., 0.840±0.0390.840 \pm 0.039, while the headline K=20K = 20 number is 0.8110.811 (pooled TEST, Table 1). These are different aggregations (mean of per-run AUCs vs. AUC of pooled predictions), but the text never reconciles the 0.0290.029 gap. One sentence would close it.

  • Unexplained "—" cells for the cross-space attacker at K=50K = 50. These appear in both Table 5 (p. 20, Original and MoIRAGE rows) and Table 7 (p. 23) with no stated reason; every other missing-cell pattern is protocol-explained except this one. Add one clause (presumably unsupported set size or protocol inapplicability).

  • Rounding inconsistency in the paired AUROC difference. "The paired AUROC difference is +0.075" (§6.2, p. 7), while the difference of the pooled Table 1 values is 0.643−0.567=0.0760.643 - 0.567 = 0.076 — almost certainly rounding of unrounded underlying values. Note the rounding, or report the difference of the rounded quantities.

  • K=30K = 30 appears without motivation. It shows up only as a Table 5 column; §5 (p. 6) states "We mainly evaluate K∈{1,2,5,10,20}K \in \{1, 2, 5, 10, 20\}", and K=50K = 50 is motivated in §6.1/§7. Add one clause or drop the column.

  • Table 3 column swap. In Table 3 (p. 19), the −ECAPA-\mathrm{ECAPA} and MoIRAGE columns conflict with three independent locations — §6.2 ("Elastic Net reaches an AUROC of 0.641 with MoIRAGE", p. 8; SVM MoIRAGE =0.652= 0.652), Table 4 (MoIRAGE utility 0.6430.643, −ECAPA-\mathrm{ECAPA} 0.6340.634), and App J ("For MoIRAGE, logistic-regression AUROC is 0.643", p. 19) — while Table 3 gives logistic regression −ECAPA-\mathrm{ECAPA} 0.6430.643 / MoIRAGE 0.6340.634 (Elastic Net 0.641/0.6270.641/0.627; SVM 0.652/0.6440.652/0.644). This is very likely a paper-side column swap; it is minor because the correct numbers appear in three other locations. Swap the two column headers (or cells).

  • The Bridge2AI feature-extraction configuration is missing. The vectors are described only as "task-level acoustic feature vectors rather than WavLM embeddings" (App F, p. 17) — no feature set, dimensionality provenance, normalization, PCA status, or extraction software is named, unlike the fully specified UNMC pipeline (App A/E). As described, the replication cohort cannot be re-derived. One paragraph mirroring App A/E would fix this.

  • The checkpoint-selection feasibility thresholds have no values. "A checkpoint must satisfy clinical-utility, covariance-trace, effective-rank, and attack thresholds before it is considered feasible" (App D, p. 15), but the thresholds are never given values, so the selection rule — lowest worst-case validation AUC⋆\mathrm{AUC}^\star among feasible checkpoints — is not executable as stated. Please report the four values.

  • INLP's selection criterion is unstated. "32 directions satisfy the predefined utility-feasibility criterion" (App K, p. 20), but the criterion's value is absent, so the baseline's tuning fairness cannot be audited. State the criterion.

  • The unit "row" is never defined. It is used in both chunk and participant-day senses across App A/C/D/F/G (e.g., "One epoch is one full-batch generator update over the training rows of a fold", App D, p. 15); App D's "For fold 0 this contains 2,360 rows" matches participant-day arithmetic (86×28.2≈2,42586 \times 28.2 \approx 2{,}425) rather than chunk arithmetic (≈6,400\approx 6{,}400 expected if rows = chunks at the mean of 75.175.1). Define the unit and reconcile the number.

  • Governance enhancements absent. No IRB protocol number is given ("an IRB-approved longitudinal study", Ethics Statement, p. 9), and there is no statement on whether derived embeddings or the frozen manifest are shareable, or under what terms/license. One clause each would close both gaps.

  • ECAPA is uncited at first use. §4 (p. 5) states "the identity-related representation is supervised using a frozen ECAPA speaker embedding" with no citation; Desplanques et al. 2020 appears only in App A. Cite it at first use in §4.

  • Novelty framing — keep it exactly as stated (§2, p. 3). The novelty claim is explicitly a combination claim — synthetic identity replacement, multi-observation adversarial training, and repeated-observation evaluation, brought together in a clinical embedding setting — and it is defensible as written: as §2 puts it, "these directions are typically studied separately." The closest prior art (Chen et al., 2025) is accurately characterized and cleanly differentiated (learned clinical embedding vs. resynthesized waveform), and no benchmark-SOTA claim is made anywhere in the paper. Please keep the claim framed exactly this way; the scoped, combination-level framing is the right one and reviewers should not push you toward a broader one.

  • Complete the VoicePrivacy citation chain (§2). The discussion currently cites the VoicePrivacy 2020 results overview and the 2024 challenge plan, but skips the 2022 results overview: Panariello et al., "The VoicePrivacy 2022 Challenge: Progress and Perspectives in Voice Anonymisation" (2024). Adding it in §2 completes the challenge-series chain (2020, 2022, 2024) and costs one line.

  • Anchor the linkage metrics to the linkability literature (§3 or §5). The linkage-metric apparatus — AUC⋆\mathrm{AUC}^{\star}, EER\mathrm{EER}, and TPR@FPR\mathrm{TPR}@\mathrm{FPR} (e.g., "We additionally report EER," §5, p. 6) — is introduced without a linkability-metric citation. Nautsch et al., "Preserving privacy in speaker and speech characterisation" (2019), is the foundational speech-privacy/linkability reference for these quantities; a single citation in §3 or §5 will satisfy reviewers coming from the voice-privacy community.

  • Acknowledge the ADReSS/ADReSSo/ADReSS-M benchmark series (§5 or Appendix P). The standard dementia-recognition-from-speech benchmark series — ADReSS; ADReSSo (Luz et al., "Detecting cognitive decline using speech only: The ADReSSo Challenge," 2021); and ADReSS-M ("An Overview of the ADReSS-M Signal Processing Grand Challenge on Multilingual Alzheimer's Dementia Recognition Through Spontaneous Speech," 2024) — is neither cited nor acknowledged, even though the cited Woszczyk et al. (2024) evaluates on ADReSS/ADReSSo. The omission is defensible on threat-model grounds: at ∼1\sim 1 recording per speaker, these corpora cannot support the multi-recording linkage protocol, whereas UNMC's median of 5050 recordings per participant is genuinely better suited. Still, one acknowledging sentence in §5 or Appendix P making exactly this argument would preempt the obvious reviewer question. If space allows, the newer PROCESS Challenge may also be mentioned as an optional emerging benchmark.

  • Verify and tidy the Bridge2AI-Voice bibliography entry (References, p. 10). The entry prints DOI 10.13026/k81f-qr68, which resolves externally to the sibling DOI 10.13026/37yb-1t42 with identical title and authors — PhysioNet mints per-version DOIs, so a version alias is the likely explanation. Please verify that the printed string resolves as printed. The same entry also uses "et al." inside the bibliography (please give the full author list) and mis-capitalizes the dataset name as "Bridge2ai-voice" rather than "Bridge2AI-Voice" ("Bridge2AI-Voice: An ethically-sourced, diverse voice dataset linked to health information").

  • Dwork & Roth (2014) is acceptable, with an optional refinement (§2, p. 3). Citing Dwork & Roth (2014) for the composition phenomenon — "privacy can weaken when information from repeated releases is combined" — is a broad textbook citation, but it is tolerable as written because the §2 sentence is a general phenomenon statement rather than a specific technical claim. If space allows, a more specific composition reference could be considered; no change is required.

  • External-validity boundary is inherent, not a flaw — consider stating it explicitly (§5, p. 5; Appendix Q, p. 25). Because UNMC is private ("UNMC recordings cannot be redistributed by the authors," Appendix Q, p. 25), no same-benchmark comparator exists and the absolute numbers cannot be leaderboard-validated. Likewise, we found no published linkage or anonymization results on Bridge2AI-Voice, so the teacher-free replication appears to be the first privacy result on that cohort. As the paper itself notes, this is "an external development replication rather than a second confirmatory test" (§5, p. 5). All privacy/utility evidence therefore rests on a single group's pipeline; this is inherent to the datasets rather than a methodological flaw, but it bounds external validity. A single sentence in §2 or §5 making this boundary explicit would read as confidence rather than caveat.

  • Two further relevant works worth citing (§1/§2). Two externally identified works connect directly to your premise: Tayebi Arasteh et al., "The effect of speech pathology on automatic speaker verification: a large-scale study" (Scientific Reports, 2023), which provides large-scale evidence that pathological speech carries heightened, disorder-dependent re-identification risk — direct support for the §1 premise that clinical speech embeddings are identity-sensitive — and Tayebi Arasteh et al., "Federated Learning for Secure Development of AI Models for Parkinson's Disease Detection Using Speech from Different Languages" (Interspeech, 2023), on federated privacy-preserving clinical speech modeling. Consider citing both in §1/§2.

  • Give the effective-rank concept a reference (Appendix C, p. 14; Appendix N, p. 22). The effective-rank concept is used without a citation — "the entropy-based rank fraction" (Appendix C, p. 14) and "Effective rank is 23 of 64 dimensions," i.e., 2323 of 6464 (Appendix N, p. 22). Please add a Roy & Vetterli-style citation (Roy & Vetterli, "The effective rank: A measure of effective dimensionality," 2007) at first use so the entropy-based definition is properly attributed.

  • §3 — terminology for xi(j)x_i^{(j)}. The model section says "Let xi(j)x_i^{(j)} denote recording jj from participant ii", but everywhere else (App. A; Fig. 2 caption) x∈R64x \in \mathbb{R}^{64} is the WavLM-PCA embedding of a recording, not the recording itself. Suggest: "Let xi(j)∈R64x_i^{(j)} \in \mathbb{R}^{64} denote the embedding of recording jj from participant ii."

  • §3 / §6.1 / App. M — the zero-mean assumption behind "averaging out". The argument that "recording-specific and stochastic variation can average out" for the attacker implicitly requires E[δij]=0\mathbb{E}[\delta_{ij}] = 0 across recordings, but this is never stated in §3, §6.1, or App. M. App. E notes that background/vehicle acoustics are not explicitly removed — a plausible systematic per-participant bias that would violate zero-mean. Since the model is explicitly framed as explanatory, this is an implicit-assumption gap rather than an error; one sentence stating E[δij]=0\mathbb{E}[\delta_{ij}] = 0 (and cross-referencing the App. E caveat) closes it.

  • Eq. (4) (§4) vs. Eq. (11) (App. A) — which content variable is released. Eq. (4) releases z=norm(D(c,s~))z = \mathrm{norm}(D(c, \tilde{s})) written with cc, while App. A and the prose state that the released representation is the posterior mean μc\mu_c rather than a sample from q(c∣x)q(c \mid x). Suggest writing μc\mu_c in Eq. (4), or adding a parenthetical that cc denotes the posterior mean at release time.

  • §4 — bottleneck phrasing. "We apply a variational bottleneck to cc" slightly outruns what governs the release: the information constraint acts on the stochastic q(c∣x)q(c \mid x), while the released map is deterministic in μc\mu_c. App. A discloses this verbatim ("Stochasticity in the content branch is used only by the bottleneck objective"), so this is not misrepresentation — but §4 should mirror the disclosure with one clause, e.g., "...a variational bottleneck on the stochastic encoder q(c∣x)q(c \mid x); the released representation is the deterministic posterior mean."

  • Eq. (5) / App. G–H — standard deviation at K=1K = 1. The set summary concatenates the mean and standard deviation, but for a single-element set (K=1K = 1) the unbiased standard deviation is undefined and the population standard deviation is 00. The ddof convention is never documented, and every K=1K = 1 result (e.g., 0.5280.528 in Table 1) depends on it. One sentence in App. G/H stating the convention (population std, or unbiased with a defined K=1K = 1 fallback) suffices.

  • Fig. 4(a) caption — undefined DRD_R and colliding α^\hat{\alpha}. The caption's "predicted DR∝R−1D_R \propto R^{-1} scaling" uses DRD_R, which appears nowhere else in the paper and is never defined, and reports a fitted exponent α^=−1.03\hat{\alpha} = -1.03 that collides with the dual variable α\alpha of Eq. (20). Suggest defining DRD_R (e.g., the attainable disclosure at release count RR) and renaming one of the two symbols — e.g., β^=−1.03\hat{\beta} = -1.03 for the fitted exponent.

  • Fig. 4(b) / App. M — missing prediction formula. The "variance-based prediction of attainable identity signal" plotted in Fig. 4(b) is never written down, despite §6.1's explicit promise that "full derivations and variance-decomposition details are provided in Appendix M" — App. M currently contains only the 1/R1/R identity, the dispersion series, and the variance shares. As a result, the claimed r=0.99r = 0.99 fit is unverifiable from the text. Please add the prediction formula to App. M.

  • App. M — variance-decomposition estimator. The estimator behind the 82.9%/14.8%/2.3%82.9\% / 14.8\% / 2.3\% variance shares (Table 6) is unspecified — ANOVA-style on the random-effects model? moment-based? This is the same unfulfilled App. M promise. Please state the estimator explicitly (a sentence or two, or a citation).

  • App. M — R2R^2 vs. RR typesetting. In the sentence "The 1/R1/R prediction gives R2 >0.9999> 0.9999 in each fold", the coefficient of determination is typeset identically to the release count RR inside a sentence that is itself about RR — genuinely confusing on first read. Suggest a proper superscript, R2>0.9999R^2 > 0.9999, or writing "coefficient of determination".

  • App. C, Eqs. (12)–(13) — pooling symbols and BCE variant. The bar-pooling symbols cˉ\bar{c}, zˉ(1)\bar{z}^{(1)}, zˉ(2)\bar{z}^{(2)} are never bound to the prose pooling definition ("Participant pooling concatenates the mean and standard deviation of that participant's rows"), and whether the BCE in Eq. (12) operates on logits is unstated — inferable only from the sigmoid in Eq. (13). Suggest binding each symbol explicitly (e.g., cˉ=concat(mean,std)\bar{c} = \mathrm{concat}(\mathrm{mean}, \mathrm{std}) over the participant's rows) and stating which BCE variant is used (with-logits vs. on probabilities).

  • App. C, Eqs. (17)–(18) — undefined indices and aggregates. The only definitions given are "Let u+u^+ and u−u^- denote positive and negative linkage logits and let τ=0.5\tau = 0.5". Left undefined are: the indices i,ji, j on ui+,uj−u^+_i, u^-_j; the aggregation over (i,j)(i, j) pairs (mean? sum?); the two-argument Huber0.5(⋅,0)\mathrm{Huber}_{0.5}(\cdot, 0); and uˉ+\bar{u}^+, uˉ−\bar{u}^-, uˉ\bar{u} — including which logits enter uˉ\bar{u}. One defining sentence each would make these equations self-contained.

  • App. C, Eq. (19) — eigenvalue notation and rank-fraction formula. λi\lambda_i is never introduced as the eigenvalues of the class-conditional covariance Σ\Sigma, and it collides with the loss weight λspk\lambda_{\mathrm{spk}} in Eq. (7). The effective-rank penalty (weight 4.04.0) has no formula — only the prose "activated when the entropy-based rank fraction falls below 0.30.3". Suggest renaming the eigenvalues (e.g., νi\nu_i), adding a defining clause ("let νi\nu_i denote the eigenvalues of Σ\Sigma"), and giving the rank-fraction formula explicitly, e.g., a normalized entropy of the spectrum such as

ρ=exp⁡(−∑ipilog⁡pi)d,pi=νi∑jνj,\rho = \frac{\exp\big(-\sum_{i} p_i \log p_i\big)}{d}, \qquad p_i = \frac{\nu_i}{\sum_{j} \nu_j},

or whichever form matches the implementation.

  • Name the Bridge2AI clinical label at first use (minor; §5, p. 5; App. F; Table 9). The primary Bridge2AI clinical label is never named in §5 or App. F: it appears only as "the binary clinical label used for clinical-utility evaluation" (§5, p. 5) and is identifiable as cognitive impairment only via Table 9's caption. Please state the label explicitly — cognitive impairment, with 118 controls / 35 positive — at first use in §5, so readers do not have to reverse-engineer the target of the clinical-utility evaluation from a table caption.
Questions for authors
  1. Given that all comparators are your own runs and Chen et al. is described as closely related, could you add an external replacement baseline adapted to embeddings and report its linkage/utility? If such a baseline matches or outperforms MoIRAGE, would you revise the empirical claims?

  2. Could you report the mean effective set size per reported KK and clarify whether the K=50K=50 results are fixed-KK or all-available? This is needed to interpret the plateau values and the 0.8540.854 linkage number.

  3. Could you provide a sensitivity analysis over MoIRAGE's constants (τ\tau, Huber δ\delta, privacy ramp, target-eigenvalue floor, effective-rank threshold) or an explicit scope note? Without it, the robustness of the headline results to these choices is unclear.

  4. Can you specify the Bridge2AI feature-extraction pipeline—feature set, dimensionality, normalization/PCA status, and software—as done for UNMC? Without this, the replication cohort cannot be re-derived as described.

  5. Could you report the four checkpoint-selection feasibility threshold values? Without them, the stated checkpoint-selection rule is not executable and the selection procedure cannot be audited.

  6. Can you provide an explicit code/artifact availability statement with a repository or release commitment and a license? This is a blocking reproducibility item that would materially change the assessment of the submission.

1 comment

Thank you for the detailed review. We added baselines, corrected the evaluation, expanded sensitivity studies, clarified methods, and uploaded anonymized supplementary code.

Q1. External identity-replacement baselines. We evaluated embedding-level adaptations of pool-based pseudo-speaker replacement, sampled pseudo-speaker replacement, identity-subspace removal, and Gaussian noise. Corrected UNMC TEST results:

MethodK=1 AUC*K=5 AUC*K=20 AUC*Clinical AUROC
Original0.7880.9440.9890.567
Gaussian (sigma=1)0.5220.5340.6220.473
Subspace removal0.6460.8770.9880.578
Pool pseudo-speaker0.6900.8730.9730.549
Sampled pseudo-speaker0.5050.6440.7430.517
MoIRAGE0.5200.5910.5960.643

Sampled replacement has slightly lower linkage at K=1, which we acknowledge. At K=20, MoIRAGE has both lower linkage and higher clinical AUROC. These are embedding adaptations, not waveform systems. Alternative release-time priors give similar results; we do not claim prior-specific novelty (Appendix K, Table 6).

Q2. Actual set sizes and protocol correction. The originally submitted evaluation used min(K, available) observations. Its mean effective set sizes at nominal K=1, 2, 5, 10, 20 were 1.00, 1.95, 4.65, 8.44, 12.70. This introduced a size-only linkage cue (AUC* 0.895 at nominal K=20). Our corrected evaluation uses exactly K disjoint participant-day observations on each enrollment and probe side, excludes participants without sufficient observations, and retrains evaluation attackers at each K. Release models and checkpoints are unchanged. Corrected original/MoIRAGE linkage is 0.788/0.520 at K=1 and 0.989/0.596 at K=20. Only 35 participants qualify at K=20; the earlier nominal K=50 results were not exact-50 evaluations. We label historical results separately and disclose variable-size sets in original training and checkpoint selection as a limitation (Sec. 5; Appendices D, G).

Q3. Sensitivity. Appendix R reports 12 one-at-a-time retraining variants across six constants, two separately retrained prior alternatives, and attacker-capacity sweeps. Development linkage ranges approximately 0.51-0.57 at K=1 and 0.59-0.71 at K=5; clinical AUROC ranges approximately 0.60-0.65. Larger-K capacity checks use the original protocol and are labeled diagnostics.

Q4. Bridge2AI feature pipeline. Appendix F specifies 131 descriptors from Bridge2AI-Voice v3.0.0 static_features.tsv, generated upstream with b2aiprep (openSMILE eGeMAPS-style and Praat/Parselmouth features). We did not re-extract them. Processing uses TRAIN-median imputation, TRAIN-only standardization, PCA to 64 dimensions, and L2 normalization. The Bridge2AI analysis is a development replication based on 113 unique labeled validation participants, not an independent locked TEST. AUROC decreases for 10 of 12 auxiliary conditions (Sec. 6.4; Appendices F, O).

Q5. Checkpoint feasibility. Appendix D specifies validation clinical AUROC within 0.03 of original, minimum covariance trace 0.25, and minimum effective-rank fraction 0.20. Attack thresholds include release-to-release cosine AUC* <=0.75, original-to-release AUC* <=0.60, and fresh pair-attacker AUC* <=0.65; selected and fallback epochs are listed. Appendix C defines effective rank and its penalty.

Q6. Code, artifacts, and license. We uploaded an anonymized supplementary ZIP containing model and baseline code, exact-K evaluation, configurations, tests, robustness scripts, reproduction instructions, and an MIT license. Appendix Q documents seeds and the correction. Restricted UNMC recordings and participant-level data are not included.

Other corrections. We added the previously missing same-recording diagnostic (Appendix L, Table 9), size-controlled linkage intervals (MoIRAGE: 0.520 [0.502, 0.543] at K=1; 0.596 [0.545, 0.644] at K=20), and strict operating points (TPR at 1% FPR: 0.738 to 0.018 at K=10). The earlier 0.811 pooled AUC and 0.840 seed-run mean both belong to the original protocol and should not be compared to corrected values. We withdrew the unsupported Figure 4(b) correlation, retained the measured R^(-1.03) dispersion scaling, and reported development-fold variance shares of 87.3% / 11.2% / 1.5%. We acknowledge residual linkage and make no anonymity or differential-privacy claim.

We thank the reviewer for strengthening the evaluation and reproducibility.

Comments on the paper

1 comment

We thank all three reviewers for their thoughtful evaluations and constructive feedback. We have revised the manuscript, conducted additional experiments, corrected an evaluation issue, and uploaded an anonymized supplementary code package. We summarize the major changes below.

1. Correction of repeated-observation privacy evaluation

While investigating reviewer questions about effective collection sizes, we identified a collection-size cue in the originally submitted protocol. The earlier evaluation used min(K, available) observations per set, allowing collection-size differences to influence linkage scores. A size-only diagnostic achieved AUC* 0.895 at nominal K=20. We corrected this issue by requiring exactly K disjoint participant-day observations in each enrollment and probe collection, excluding ineligible participants, and retraining evaluation attackers at each K. The MoIRAGE release models and checkpoints remained unchanged.

The corrected UNMC TEST results are:

ObservationsOriginal AUC*MoIRAGE AUC*
K=10.7880.520
K=50.9440.591
K=100.9850.613
K=200.9890.596

The original results are retained separately as historical diagnostics. We also disclose that variable-size collections were used during original adversarial training and checkpoint selection, whose potential influence cannot be retrospectively eliminated. Participant eligibility decreases with K, with 35 participants eligible at K=20.

2. Stronger baselines and mechanism validation

We added embedding-level adaptations of pool-based pseudo-speaker replacement, sampled pseudo-speaker replacement, and identity-subspace removal, together with alternative synthetic-prior experiments. At K=20, sampled pseudo-speaker replacement achieves linkage AUC* 0.743 and clinical AUROC 0.517, compared with 0.596 and 0.643 for MoIRAGE. Gaussian noise (sigma=1) achieves linkage 0.622 but reduces clinical AUROC to 0.473. Removing synthetic identity replacement increases K=20 linkage to 0.982, while removing multi-observation training increases it to 0.852. Alternative prior distributions produce similar results, indicating that the specific class-conditional prior is not the main source of the improvement.

We therefore clarify our contribution as the combination of identity-related replacement, multi-observation adversarial training, and repeated-observation privacy evaluation, rather than claiming novelty for each component individually.

3. Additional statistical and robustness analyses

We added twelve one-at-a-time training sensitivity experiments, two retrained-prior alternatives, attacker-capacity analyses, corrected confidence intervals, and strict operating-point evaluations. At K=10, TPR at 1% FPR decreases from 0.738 to 0.018, and rank-1 identification decreases from 0.876 to 0.087. Clinical AUROC is 0.643 for MoIRAGE versus 0.567 for the original embeddings. The paired difference is +0.076 with a 95% confidence interval of [-0.010, 0.163]. Since this interval includes zero, we claim clinical information is retained, not that diagnostic performance is significantly improved. We also expanded the repeated-release analysis, added the previously missing same-recording diagnostic, and replaced the unsupported Figure 4(b) correlation with a development-fold variance decomposition.

4. Methodological clarity and reproducibility

We expanded the descriptions of the DeepSets attacker, synthetic prior, clinical utility constraint, loss functions, checkpoint thresholds, effective-rank regularization, and Bridge2AI preprocessing. An anonymized supplementary ZIP now provides the implementation, configurations, corrected evaluation procedures, baseline implementations, robustness scripts, reproduction instructions, and MIT license. Restricted clinical recordings and participant-level data are not distributed.

5. Scope and limitations

We clarified that Bridge2AI provides an external development replication, not an independent confirmatory TEST evaluation. We also acknowledge that 10 of 12 auxiliary clinical conditions show reduced AUROC following transformation. Residual participant linkage remains detectable, especially under repeated observations. MoIRAGE reduces empirical identity-linkage risk under the evaluated threat model but does not guarantee anonymity or differential privacy.

We appreciate the reviewers' suggestions. They helped us identify an important evaluation confound, strengthen comparisons with existing methods, improve reproducibility, and present a more precise account of MoIRAGE's contributions and limitations.

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

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