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Paper summary
The paper studies feature unlearning when retained features and labels remain accessible but revoked feature values do not. BMCR fine-tunes a model after replacing the revoked coordinate with independent draws from a declared bounded range. The analysis relates replacement risk to direct coordinate dependence and, under additional assumptions, to prediction-level proximity to retraining and finite-checkpoint risk transfer. Experiments cover seven tabular datasets, three architectures, multiple deletion settings, structural baselines, and attribute-inference audits.
Critical strengths
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The access restriction is concrete and useful. The paper distinguishes declared support, existing preprocessing information, aggregate statistics, and per-example revoked values, rather than comparing methods as though they had identical access (Tables 1 and 5). The replacement rule is simple to implement under this restriction.
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The squared-loss decomposition gives a clear explanation of why independent replacement penalizes direct coordinate dependence. The paper also distinguishes this dependence from information recoverable through retained features and states the support and regularity assumptions. These distinctions are important for interpreting feature-unlearning results.
Critical weaknesses
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The structural-baseline results are incompatible with the stated baseline and metric definitions. Section 5, pp. 7–8, and Appendix W define FPE by removing the target input entirely and fine-tuning the reduced network. RIPV holds retained inputs fixed and varies only the revoked coordinate. FPE must therefore have zero RIPV under deterministic evaluation, irrespective of its utility or fine-tuning quality. Yet Table 3(a) reports 0.042, and Tables 42–48 report 0.039–0.045. The stated zero-and-freeze SFI construction presents a similar concern. The downstream-refitting explanation on p. 9 does not resolve this: even an unretrained FPE is invariant to an absent input. If stochastic evaluation causes the positive variance, it must be separated from coordinate dependence. Until the implementation, metric and tables are reconciled, this central comparison cannot establish BMCR’s advantage in direct-dependence reduction over structural removal.
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Table 35 (Appendix T, p. 60) needs a precise definition of its uncertainty. It compares the same removed-feature configurations at epochs 1 and 1500 and reports a paired change. If all three columns give standard deviations over the same paired observations, the change SD cannot be smaller than the absolute difference between the two epoch SDs. For RIPV, the reported SDs of 0.0112 and 0.0034 require a change SD of at least 0.0078, but the table gives 0.0060. For TRI, the corresponding lower bound is 0.034, versus the reported 0.029. Rounding cannot explain either gap. Different aggregation levels or a mixture of SD and SE could explain the numbers, but would need to be stated explicitly.
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Proposition 4.6(iii) has a valid response-stability argument, but its final comparison does not establish a nontrivial model-specific attribute-inference guarantee. For fixed f and queries determined by retained features, the assisted attack is itself a function of those features. Its risk is therefore already bounded below by the unrestricted retained-features-only infimum in Appendix E, p. 29, without any small-dependence assumption. The proof’s intermediate comparison with responses from the averaged predictor remains useful. However, that comparison is not the same as a feasible attacker without model access. Table 3(b) compares particular fitted attackers, not the unrestricted infimum. The theory and empirical benchmark need to be aligned; this is an interpretation issue, not a demonstrated false theorem.
Questions for authors
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What computation produces nonzero RIPV for FPE? Please provide the input wrapper and audit procedure, verify identical outputs when only the removed coordinate changes with model randomness fixed, and reconcile Tables 3 and 42–48. If another quantity was measured, please state it and reassess the comparison under the defined RIPV.
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What observation unit, sample count, aggregation rule, and uncertainty measure were used for each column of Table 35? Please reconcile the RIPV and TRI paired-change values with the two epoch columns, using the underlying paired records or a reproducible aggregation script.
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Is Proposition 4.6(iii) intended as stability relative to the averaged predictor, or as an advantage over a restricted attacker without model access? The former follows from the proof. For the latter, what restriction prevents the assisted predictor from belonging to the comparison class, and how does that restriction match Table 3(b)?
3 comments
W3 and Q3: Interpretation of Proposition 4.6(iii) and its relationship to the empirical attack benchmark.
We agree with this precise distinction between the validity of the inequality and the informativeness of its comparator. In the fixed-model setting, the final comparison with the unrestricted retained-features-only infimum does not establish a nontrivial dependence-sensitive attribute-inference guarantee. The intermediate response-stability result remains valid and useful. We will revise the proposition and the associated empirical interpretation to make this distinction explicit.
1. The unrestricted comparison does not require small residual dependence.
Let and write the model-response vector as
For fixed and queries determined by , any assisted attack
is itself a measurable function of . Therefore,
\ell_{\mathrm{att}}(A(Z,r_f(Z)),X_i) \right] \ge \inf_h \mathbb E\!\left[ \ell_{\mathrm{att}}(h(Z),X_i) \right]$$ already holds without a dependence-dependent remainder. Thus, although the final inequality in Proposition 4.6(iii) is mathematically valid, interpreting its remainder as a nontrivial bound on excess model-assisted leakage over this unrestricted optimum is too strong. We will remove that interpretation. **2. The substantive result is stability under replacement-averaged responses.** The intermediate argument in Appendix E supports a precise alternative statement. Define $$\bar f(z)=\mathbb E_{T\sim q}[f(z,T)], \qquad \bar r_f(z)=\bar f(z)\mathbf 1_k.$$ For the same fixed attack map $A$, consider $$\mathcal{R}_f(A) = \mathbb{E}\big[\ell_{\mathrm{att}}\big(A(Z, r_f(Z)), X_i\big)\big]$$ and $$\mathcal{R}_{\mathrm{avg}}(A) = \mathbb{E}\big[\ell_{\mathrm{att}}\big(A(Z, \bar{r}_f(Z)), X_i\big)\big].$$ Under the existing assumptions that the queries lie in $[a,b]$, $A$ is uniformly $L_A$-Lipschitz in the response vector under the $\ell_\infty$ norm, and the attack loss is uniformly $\lambda$-Lipschitz in the estimated attribute, the proof gives $$\left| \mathcal R_f(A)-\mathcal R_{\mathrm{avg}}(A) \right| \le \lambda L_A\kappa(f), \qquad \kappa(f)=2\left[L_f(b-a)D_q(f)\right]^{1/3}.$$ Indeed, $$\big\lvert\mathcal{R}_f(A) - \mathcal{R}_{\mathrm{avg}}(A)\big\rvert \le \lambda L_A\, \mathbb{E}_Z \lVert r_f(Z) - \bar{r}_f(Z) \rVert_\infty$$ $$\le \lambda L_A\, \mathbb{E}_Z \sup_{t\in[a,b]} \big\lvert f(Z,t) - \bar{f}(Z)\big\rvert$$ $$\le \lambda L_A\, \kappa(f).$$ where the final step follows from Lemma D.8 and the existing argument in Appendix E. This bounds how much removing the coordinate-dependent variation in the responses can change the risk of the same stable attack. We will restate Proposition 4.6(iii) in this form. Crucially, $\bar r_f(Z)$ is a model-dependent reference. Although it is mathematically a function of retained features, a practical attacker without model access need not know or be able to compute it. We will therefore not describe this reference as a feasible attacker without model access. Similarly, $D_q(f)=0$ implies equality between the actual and averaged response channels, but does not imply that a finitely trained attacker gains nothing from the common response $\bar f(Z)$. That response may still provide a useful learned transformation of the retained features.3. Table 3(b) evaluates fitted attackers, not the unrestricted population optimum.
The retained-feature random forest in Table 3(b) achieves . This is an empirical baseline produced by a particular fitted predictor, rather than the optimum over all measurable functions of . The reported results are:
| Attacker inputs | Reported | Increase over the fitted retained-feature baseline |
|---|---|---|
| Retained features only | 0.669 | — |
| Retained features + original-model responses | 0.813 | +0.144 |
| Retained features + retrained-model responses | 0.678 | +0.009 |
| Retained features + BMCR-model responses | 0.686 | +0.017 |
These measurements support a specific empirical conclusion: under the evaluated attack protocol, BMCR substantially reduces the reconstruction improvement observed with the original model's responses, and its attack score is numerically close to that of the retrained reference. They do not estimate advantage over the unrestricted retained-feature optimum or establish statistical equivalence to retraining.
The positive increment for the retrained model is also compatible with this interpretation. Its responses are functions of retained features alone, but supplying such transformations can help a finite fitted learner. An observed improvement over a particular fitted baseline therefore does not establish additional information beyond the retained features.
We will replace “data-only floor” with “fitted retained-feature baseline” and describe “Gain” explicitly as the observed increase in attack over that baseline. We will also remove the statements that these increments are predicted by Proposition 4.6(iii) or demonstrate removal of almost all model-specific leakage.
The empirical attack benchmark will be distinguished from a quantitative instantiation of the stability theorem. Such an instantiation would require verification of the response-Lipschitz and loss assumptions and a comparison of the same fixed attacker under actual and averaged responses. Table 3(b) does not currently perform that comparison.
4. Scope of the revision.
We will align Proposition 4.6(iii), its proof in Appendix E, Remark 4.7, and the corresponding abstract and contribution statements around the response-stability guarantee above. Table 3(b), its caption, and Appendix X will describe comparisons among fitted attackers without identifying the empirical baseline with an unrestricted inference optimum.
These revisions concern the formulation and interpretation of the attribute-inference result. The residual-dependence decomposition, prediction-level comparison with retraining, and the realistic-input and risk-transfer results in Proposition 4.6(i)–(ii) are unaffected.
The author sincerely thank the reviewer for their exceptionally careful and detailed review. Their comments led to several new analyses, which we describe below
W1 and Q1: Non-zero RIPV for SFI and FPE.
We thank the reviewer for this precise diagnosis. SFI and FPE cannot respond to xi, so under the defined RIPV both must be exactly zero. There is no other input path, and all methods use the same RIPV code.
What produced the non-zero values. RIPV was computed with the network in training mode, so dropout was active and every forward pass drew a fresh mask ξjr. The reported quantity was therefore n1∑jVarr[fξjr(x−i(j),Tjr)], which adds dropout-induced variance to the coordinate dependence. This term is present for any network with dropout, including FPE.
Input wrapper and audit procedure (corrected).
Verification. With dropout disabled, changing only xi leaves the output of every SFI and FPE model identical (maximum absolute difference 0 over all audit points and draws, all datasets, backbones, and seeds), so their RIPV is exactly 0.
Reconciling Tables 3 and 42–48. We recomputed RIPV in evaluation mode for all methods (TRI and MIA were re-evaluated in the same pass). In the per-dataset tables (now Tables 43–49), SFI and FPE have RIPV 0.000 on every dataset, and BMCR's RIPV also decreases because the same noise had inflated it. Table 3 is now explicitly the mean ± std across the seven datasets of these per-dataset values, so it can be reproduced from them.
W2 and Q2: Uncertainty in Table 35 (now Table 36).
For paired values over the same units, the SD of the change is at least the absolute difference of the two SDs. Equivalently, the reported values imply a correlation between epochs above 1 (1.33 for RIPV, 1.21 for TRI). The three columns therefore could not share an aggregation level, and the table did not say so.
What the original columns were. All three columns use the same n=30 Magic configurations (2 removed features × 3 backbones × 5 values of ε, each averaged over 3 seeds).
Grouping by ε keeps only the variation within groups, so it removed the variation between values of ε from the change column only. That is why its SD fell below the bound. Mixing these levels in one table was our error.
Corrected table. All columns are now mean ± SD across the same 30 configurations, with the change computed per configuration (epoch 1500 − epoch 1). The means are unchanged; only the SDs of the change differ:
Every row now satisfies the bound (e.g., RIPV: 0.0086 ≥ 0.0078; TRI: 0.037 ≥ 0.034). The caption and the text of Appendix T now state the unit, n=30, the aggregation rule, and that all entries are SDs. The aggregation script and the per-configuration records are included in the supplementary material.