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Under review as a conference paper at ICLR 2027

OBSERVATION AND TRANSPORT LIMITS OF SOURCE-ONLY CONCEPT ERASURE UNDER DOMAIN SHIFT

Abstract

Concept erasure is often evaluated by whether a chosen probe can recover a nuisance variable from the resulting representation. This criterion does not establish whether a detector trained on source domains will retain its operating point on an unseen domain. Across pathology and natural-image benchmarks, we find that source-fitted linear erasure can remove the observed domain signal while leaving target false-positive rates largely unchanged. We explain this separation through two limitations. First, domain means expose only the content-averaged nuisance response; content-dependent responses can cancel under averaging, and finite-sample grouped means can misleadingly appear to recover them. Second, even perfect knowledge of the source nuisance geometry need not identify the target-optimal erasure subspace without assumptions connecting source and target domains. Target-oracle controls distinguish this transport limitation from limitations of the projector class. Finally, we compare adaptation strategies under two deployment objectives: false-positive-rate calibration and discrimination at matched false-positive rate. Direct threshold adaptation is effective for the first in the studied settings, although small adaptation sets have substantial uncertainty; feature-space adaptation can improve the second by changing the ordering of examples. These results support choosing an adaptation target according to the deployment objective rather than treating source-side erasure as a sufficient criterion for robustness.

Primary area:
transfer learning, meta learning, and lifelong learning
Keywords:
domain adaptation, domain generalization, concept erasure, representation learning, distribution shift, out-of-distribution detection, nuisance invariance, calibration

Reviews

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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_UBkROpenReview ↗
Rating
1(−1)
Confidence
3
Informativeness
1
Presentation
1
Soundness
2
Read review
Paper summary

This paper examines why source-domain concept erasure can succeed according to probe-based criteria while failing to preserve a detector operating point on an unseen target domain. The paper separates this failure into two proposed limitations, observation limitation and transport limitation. Finally, the paper distinguishes operating-point calibration from discrimination.

Critical strengths
  1. The paper identifies a useful conceptual distinction that is often overlooked in concept-erasure evaluation. The authors emphasize that reducing recoverability of a nuisance label on source data does not establish attenuation of the target nuisance direction or preservation of a operating point.

  2. The paper makes a serious effort to test alternative explanations. The manuscript also reports several hypotheses and corrections that did not survive stronger comparisons rather than presenting only favorable outcomes.

Critical weaknesses
  1. The main paper is not sufficiently clear or self-contained to support its broad claims. The manuscript introduces so many related but non-equivalent quantities, such as probe accuracy, observation-channel energy, held-out capture, nuisance transmission, complement preservation, transport regret, FPR calibration, etc. However, it provides no overview diagram or compact protocol table explaining how these quantities relate, what information each one requires, and which claims they support.

  2. The deployment evidence is specialized to one-class operating-point calibration and does not establish broad behavioral consequences of concept erasure. It is unclear whether source-side probe failure separates from downstream behavior in the same way for these settings.

Questions for authors
  1. Format Issue The submission does not appear to preserve the official ICLR format. In particular, the required running header, “Under review as a conference paper at ICLR 2027,” is absent throughout the manuscript. In addition, the bibliography appears to use a visibly and measurably smaller font than the default template. The authors should use the unmodified official ICLR template style.

  2. Reproducibility Does the submission commit to releasing code, nuisance trajectories, semantic partitions, target-adaptation splits, and all experiment manifests? The reproducibility statement describes the appendix but does not clearly promise a release.

  3. Can the authors state the exact scope of the main claim in one sentence? In general, the paper is hard to follow and not well written.

  4. Which results in the paper apply formally to nonlinear or higher-order erasure methods?

  5. One Obliviator result is based on an incomplete run. Why is this result retained in the empirical comparison, and does removing it change any conclusion?

  6. Can the authors provide a single overview figure or table mapping each experimental quantity to its role?

  7. The boldface and interpretation of Tables 1 and 2 are insufficiently explained. Table 1 bolds only the rank-threshold entries. Please state whether bold denotes nominal order-statistic validity, the best matched-budget result, or another criterion.

4 comments

considering the low quality of this work, and no response to all reviewers, I lower my rate from 2 to 1

AuthorsOpenReview ↗

Response to Reviewer UBkR (1/2): format, clarity, reproducibility, scope

Please see our general comment above for a summary of the revision.

You are right that the submitted version made the central argument harder to locate than it should have been. We have made substantive presentation changes rather than only adding explanations in the appendix.

Format (Q1). The revised PDF restores the running header, "Under review as a conference paper at ICLR 2027", on every page and uses the template's default bibliography size. The main paper ends on page 10, within the discussion-stage limit; the reproducibility and AI-use statements, references, and appendices follow it. We also corrected the figure-legend overlap raised by another reviewer.

The claim in one sentence (Q3). For erasers whose domain signal is estimated from source-domain first moments, removing that signal neither reveals the content-dependent nuisance response that was averaged away nor determines the target-relevant subspace; in our one-class detection experiments, this means that source-side erasure alone does not reliably preserve the target FPR operating point, while threshold adaptation and feature adaptation address different deployment objectives. The revision states the main claim in this form at the end of the introduction (the wording there differs slightly).

A readable map of the paper (W1, Q6). A new Table 1 in Section 3 organizes the quantities by the question they answer and the information they require. The important separations are: domain-probe accuracy tests recoverability; nuisance transmission tests attenuation of a measured direction; capture and regret test geometric match; and FPR, TPR and AUROC test what the detector actually does. None of these quantities alone certifies the next one. Sections 4–7 now each open with their claim and its evidence, and the diagnostic-to-intervention procedure is in Appendix C.4.7.

Scope of the deployment evidence (W2). We agree that the deployment evidence is specific to one-class operating-point calibration, and the title, abstract and main claim are scoped to it; we make no claim about classification or generation. What is not tied to the detector: the observation identity and its finite-sample bias, transport regret, and Theorem 3 are statements about statistics and subspaces, and the order-statistic and ROC facts hold for any scalar score. The operating-point results are replicated for residual, Mahalanobis and kNN detectors (Appendix C.2.4).

Reproducibility (Q2). The new statement makes an explicit commitment to release the experiment code, controlled nuisance trajectories and generation scripts, semantic partitions, target adaptation and evaluation splits, and per-experiment configuration, seed and feature manifests, together with pinned upstream commits and patches. Derived medical features are subject to the relevant dataset licenses; extraction scripts will be provided in any case. This is a commitment in the revised manuscript, not a claim that the artifacts are already public.

AuthorsOpenReview ↗

Response to Reviewer UBkR (2/2): theoretical scope, omitted run, tables

Three remaining points deserve a precise answer.

Which results apply to nonlinear or higher-order erasure (Q4)? The revision adds a formal-scope table (Appendix C.4.8). The observation decomposition in Proposition 1 applies to first-moment channels such as LEACE with one-hot domain labels. Equation 3 and the cross-fitting correction concern estimation of grouped-mean operators and do not depend on the eventual eraser. The differential transfer inequality applies to differentiable erasers through their Jacobians. The transport-regret results, including the worst-case lower bound of Theorem 3, concern rank-rr projector selection rules, even when those rules use source statistics of arbitrary order; they do not prove a limit for every nonlinear transformation. Order-statistic calibration and ROC invariance apply to any fixed scalar score. The empirical claims about MANCE++ and DANN remain descriptive.

Why was Obliviator in the original table (Q5)? We originally included a partial run for transparency, but that presentation implied a comparison the experiment did not support. We have removed it from all comparative tables and conclusions. Appendix C.3.5 documents the incomplete optimization, including an SVD failure and the subsequent collapse of the representation before the method's stopping rule was met. The LEACE, MANCE++ and DANN results are unchanged, and the claims of the revised paper do not rely on Obliviator.

What did boldface mean (Q7)? Your references to the original Tables 1 and 2 correspond to Tables 3 and 4 in the revision, because the paper now begins with an overview table and a nonlinear-outcome table. In revised Table 3, bold marks the lowest calibration error among the matched-budget arms only where the rank threshold is a nominally valid order statistic, k≥19k \ge 19 at α=0.05\alpha = 0.05. At k=5k = 5 and k=10k = 10 the cutoff is clipped to the maximum observed score, with expected FPR 1/(k+1)1/(k+1) rather than 0.05, so those entries are not bolded; the geometry-all arms use more data and are excluded from that comparison. Revised Table 4 has no bold entries. These conventions are now stated in the captions.

We agree that a source-statistic result, a subspace theorem and an observed detector outcome should not be treated as interchangeable. The main-text overview and the scope table are meant to let the reader see exactly which statement each section makes.

AuthorsOpenReview ↗

Response to the rating change

Thank you for the note, and we apologize that our responses came late in the discussion period. We have now uploaded a revised PDF and posted a general response and point-by-point replies to all three reviewers. The revision addresses each of your questions: the official template with the running header and default bibliography size (Q1), an explicit release commitment (Q2), a one-sentence statement of the main claim (Q3), a formal-scope table for nonlinear and higher-order erasers (Q4), removal of the incomplete Obliviator run (Q5), an overview table of all quantities and the information each requires (W1, Q6), and stated bold conventions (Q7). We would be grateful if you would consider the revised version before finalizing your assessment.

Reviewer_LxyAOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper investigates why removing domain-related information from learned representations does not necessarily improve anomaly detection on unseen domains. They mention two limitations. First, observation limitations arise when domain-mean statistics fail to capture content-dependent nuisance variations that cancel during averaging. They analyze this using a conditional second-moment decomposition and cross-fitting. Second, transport limitations occur when nuisance directions identified in source domains do not transfer to the target domain. The authors introduce transport regret to quantify this mismatch and provide a theoretical non-identifiability result showing that source information alone cannot always determine the optimal target subspace.

Their experiments show that source-based concept erasure can remove observed domain information without significantly improving target false-positive rates (FPR). They also compare feature adaptation with direct threshold calibration, finding that threshold adjustment can substantially reduce FPR, while feature adaptation can improve discrimination. Overall, the paper emphasizes that removing source-domain information does not guarantee robustness to domain shifts and that calibration and discrimination should be evaluated separately.

Critical strengths

The paper provides a clear and explanation of why concept erasure may fail under domain shift. Instead of showing that existing methods perform poorly on unseen domains, the authors investigate the underlying reasons and distinguish between two different limitations: observation and transport. This distinction is useful because it separates the information that can be recovered from source-domain statistics whether that information remains relevant in the target domain. They provided theoretical and experiments to support that. In particular, the conditional second-moment analysis helps explain how averaging across semantic classes can hide nuisance variations, while the cross-fitting experiments distinguish genuine improvements from finite-sample estimation bias. The use of target-oracle projectors is another strong aspect of the experimental design, as it helps determine whether poor performance is caused by limitations of the projection method itself or by the inability to identify the appropriate nuisance directions from source data.

The experiments cover both controlled transformations and real-world domain-shift benchmarks. The authors show that removing domain information from the representation is not always necessary to achieve the desired operating point, and that directly adjusting the detection threshold can be more effective when the objective is to control false positives. At the same time, they correctly point out that threshold adjustment cannot improve the ranking of normal and anomalous samples, whereas feature adaptation may improve discrimination. This provides a useful perspective on selecting adaptation strategies according to the actual deployment objective. Finally, the paper is generally careful about the scope of its conclusions, acknowledging that the theoretical results do not establish an impossibility for all concept-erasure methods and that some experimental findings depend on the available target-domain information.

Critical weaknesses

Plot formatting: In figure 1, the legends of image in the left plot is covered with the bar plot.

Generalization beyond first moment erasure: The principal observation theorem concerns nuisance information exposed through first-moment summaries.More expressive erasure methods can use richer statistics or nonlinear transformations. The paper includes some comparisons, including MANCE and Obliviator, but notes that its Obliviator experiment did not reach its stopping criterion. Therefore, the available evidence is insufficient to establish that richer erasure methods suffer from the same observation limitation.

Theoretical results are not completely address the detection problem: The author introduce transport regret that measures the loss of nuisance-energy capture, not anomaly detection performance. The paper acknowledges this distinction, but does not sufficiently bridge it.

limited novelty relative to existing work: The authors explicitly acknowledge that previous research has already shown that concept-erasure methods can struggle on unseen data. The paper's main novelty is therefore the combination and application of existed ideas, rather than a fundamentally new theoretical mechanism.

Questions for authors

Given that previous studies have already identified generalization limitations of concept-erasure methods, could the authors clarify what new theoretical or practical insights the proposed observation–transport decomposition provides beyond existing work? In particular, can the proposed quantities be used to predict when source-based erasure will fail on unseen domains, rather than only explaining the failure afterward? An experiment demonstrating this predictive capability would help establish the novelty and practical significance of the framework.

It would be good if you can include at least one well-controlled comparison with a higher-order or nonlinear erasure method trained to completion, and distinguish three possibilities: the method recovers additional nuisance information, the method removes that information but fails to transfer, or the method damages semantic information.

2 comments
AuthorsOpenReview ↗

Response to Reviewer LxyA (1/2): nonlinear comparison and figure

Please see our general comment above for a summary of the revision.

Thank you for the specific request to distinguish what the nonlinear experiments actually show. The earlier comparison did not make those outcomes clear enough.

Figure 1. The overlapping legend has been moved below the panels in the revised PDF.

More expressive erasers. We now separate the cases you asked about in Table 2 of the revision:

  • Additional nuisance information is recovered. On Camelyon17, LEACE leaves MLP domain-probe accuracy at 0.971, whereas MANCE++ reduces it to 0.690 (from 0.982 without erasure). This is a meaningful improvement, but not complete nonlinear guardedness.
  • That improvement does not repair the target operating point. Target FPR is 0.848 without erasure and 0.855 after MANCE++, the same value observed after LEACE in this audit. The MANCE++ result is descriptive for the two WILDS target hospitals; we do not interpret it as a general impossibility for stronger methods.
  • An intervention can instead damage detection. In the DANN sweep, anomaly AUROC falls from 0.920 to 0.358–0.585 at the smallest nonzero adversarial weight. Importantly, DANN's domain probe remains high (0.989 → 0.978). We therefore treat this as evidence of destructive adaptation, not as a successful nonlinear-erasure experiment.

We also agree about Obliviator. Its original row came from an incomplete run and should not have sat alongside completed evaluations. It is now removed from the comparison tables and conclusions. Appendix C.3.5 explains the stopping and numerical issues: after an SVD fallback, the MLP probe remains 0.957–0.965 after the first iteration, while the representation subsequently collapses before the method reaches its adversary-accuracy stopping condition. We make no claim about Obliviator under the conditions studied by its authors.

This answers the three-way diagnostic question with the evidence we have, but we do not claim to have established a universally converged nonlinear-erasure benchmark. In particular, Proposition 1 concerns first-moment observation channels; it is not extended to MANCE++, DANN or Obliviator.

AuthorsOpenReview ↗

Response to Reviewer LxyA (2/2): prediction and detector-level link

We agree with the distinction at the center of your review: transport regret measures lost nuisance-energy capture, not detector error. Our earlier presentation moved too quickly between the two.

The revision now states the link explicitly in Section 6. Along a nuisance path, the local change in FPR depends on the signed alignment of the score gradient with nuisance motion at the decision boundary (Theorem 4):

F′(d)=fSd(τ) E[∇s⊤UE∣Sd=τ].F'(d) = f_{S_d}(\tau)\, \mathbb{E}\left[\nabla s^\top U_E \mid S_d = \tau\right].

By contrast, energy capture weights nuisance directions globally, so a geometric improvement need not translate into an FPR improvement. The corresponding empirical capture–FPR correlations are weak or negative (Appendix C.2.4). The boundary relation is only local, and its approximation degrades outside the observed range. We therefore use regret to diagnose subspace mismatch, and measured FPR, TPR and AUROC for claims about deployment.

Your novelty and prediction question led to a new experiment. In the nested leave-one-domain-out test, each forecast uses other source domains only; there is no target oracle and no target sample. Across 13 independent target domains from Camelyon17, PACS and Office-Home, this procedure correctly anticipates no FPR reduction greater than 0.02 from erasure at the domain level. It also flags all ten domains whose post-erasure FPR exceeds 2α2\alpha, with three false alarms. But it does not forecast the actual FPR well: absolute error 0.322, versus 0.310 for predicting the nominal rate (Appendix C.2.8). We regard this limitation as part of the result, not something the decomposition solves.

The more distinctive contribution, in our view, is the finite-sample conditioning result: the apparent improvement from random grouping (+0.016) disappears under cross-fitting (+0.001), whereas the semantic-grouping effect survives (+0.015 → +0.033; Section 5). This identifies a measurable confound in evaluating richer source statistics. The transport experiments then show why observing more source nuisance and identifying the appropriate target intervention are separate questions. We have rewritten the contributions and the scope statement around this narrower claim.

Reviewer_HPd7OpenReview ↗
Rating
3
Confidence
2
Informativeness
3
Presentation
3
Soundness
3
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Paper summary

This paper studies whether source-fitted concept erasure improves detector robustness under domain shift. It distinguishes two limitations: first-moment domain summaries can miss content-dependent nuisance variation, and even complete source nuisance geometry may not identify the appropriate target erasure subspace. Controlled transformations, cross-fitted estimates, and target-oracle projectors are used to investigate these limitations. The paper also compares threshold and feature adaptation, distinguishing false-positive-rate calibration from discrimination at matched FPR.

Critical strengths
  1. The distinction between insufficient source observation and unsuccessful source-to-target transport provides a useful diagnostic framework. Target-oracle controls help distinguish limitations of source information from limitations of the intervention class.

  2. The comparison between semantic and matched random partitions, followed by cross-fitting, addresses a meaningful alternative explanation for apparent gains from conditioning. This analysis strengthens the empirical interpretation beyond reporting improved nuisance capture alone.

Critical weaknesses
  1. Several central observations have established precedents: probe recoverability does not establish behavioral relevance, source-side erasure need not generalize, and invariant representations do not by themselves guarantee target performance. The paper acknowledges these precedents, but the additional insight provided by its observation–transport decomposition remains insufficiently established. The finite-sample analysis appears more distinctive than the broader failure claims, and deserves clearer positioning as a central contribution.

  2. The observation decomposition uses a standard conditional second-moment identity, while the source-only impossibility construction permits target behavior unconstrained by source observations. These results clarify scope, but do not yet provide a strong practical criterion for predicting when erasure will fail. The paper also reports that some transport bounds are empirically uninformative, and nuisance-energy capture is not directly linked to detector FPR.

  3. Controlled transformations permit direct measurement of nuisance directions, but do not establish that the same mechanism explains naturally occurring domain shifts. The number of independent deployment domains is modest, and repeated semantic partitions or seeds do not increase that number. The incomplete nonlinear-erasure run further limits conclusions beyond the first-moment setting.

Questions for authors
  1. What is the strongest new conclusion beyond prior findings on erasure generalization and invariant-representation limitations? Can the authors demonstrate how the observation–transport decomposition changes a practical diagnosis or intervention choice?

  2. Can source-observable quantities predict erasure failure on held-out domains, without access to target-oracle geometry?

  3. Can the authors strengthen the real-shift evidence with more independent target domains and completed higher-order or nonlinear-erasure comparisons?

2 comments
AuthorsOpenReview ↗

Response to Reviewer HPd7 (1/2): novelty and intervention choice

Please see our general comment above for a summary of the revision.

Thank you for identifying the finite-sample analysis as the most distinctive part of the paper. We agree, and the revised introduction now puts it first.

What is new beyond earlier failure reports (Q1)? We do not claim novelty for the observation that a successful source-domain probe or an invariant representation need not imply good target behavior. The new question is why a particular source-side erasure fails: did its statistic miss the nuisance, is its projector class inadequate, or is the required target subspace not identified by the available source domains? These explanations call for different next steps, and the paper uses separate controls to distinguish them.

The cleanest new result concerns conditioning. For grouped means, the estimated second-moment operator contains an additive variance term, Eg[Σg/mg]\mathbb{E}_g[\Sigma_g/m_g] (Eq. 3). Splitting examples into more groups can therefore look like extra nuisance information even when the grouping label is random. In the matched-rank experiment, the random-partition gain changes from +0.016 with the naive estimator to +0.001 with cross-fitting, while the semantic-partition gain changes from +0.015 to +0.033 (Section 5, Figure 2). This is an evaluation pitfall, rather than another demonstration that erasure sometimes fails.

Does the diagnosis change what one should do? In the controlled transport experiment, a target-built projector of the same class, rank and energy objective improves calibration in all five materially miscalibrated configurations (Section 6). Conversely, convex or affine recombinations of source operators close only about 7% of the target-capture gap (Appendix C.2.2). These are diagnostic controls using privileged target information, not deployable methods. Together they indicate that projector expressiveness is not the missing ingredient in these configurations; the source family does not sufficiently identify the target geometry.

Finally, the standard threshold baseline makes the deployment consequence concrete. With the same budget of 19 target-normal examples, the threshold arm has CEα=0.035CE_\alpha = 0.035 versus 0.401 for a rank-8 target-geometry correction (Table 4). This does not make threshold calibration a new algorithm, and it does not improve ranking. It shows why the intervention should be chosen for the actual objective: an FPR operating point, or discrimination at matched FPR.

AuthorsOpenReview ↗

Response to Reviewer HPd7 (2/2): prediction, real shifts, and scope

Your concern about prediction was important. We have now tested it directly, rather than relying on target-oracle geometry to explain the outcome after the fact.

Source-only forecasting test (Q2). For each held-out target TT, we first retain only the other domains SS. To predict behavior on TT, we refit the eraser, detector and threshold on S∖{p}S \setminus \{p\} and test on each p∈Sp \in S; only afterward do we evaluate the outer fit on TT. The target is never used to make its forecast. We ran this nested leave-one-domain-out protocol over 13 target domains: five Camelyon17 hospitals, four PACS styles and four Office-Home domains (Section 6; Appendix C.2.8).

Using a 0.02 FPR-improvement margin, the forecast predicts no useful reduction from erasure for 13/13 domains, and none is observed at the domain level. It flags the ten domains whose post-erasure FPR exceeds 2α2\alpha, with three false alarms. However, it fails to predict the magnitude of target FPR: mean absolute error 0.322, compared with 0.310 for simply predicting the nominal 0.05. The 13 domains are a small sample, and inner fits use one fewer source domain, so we present this as a limited, one-sided warning on these benchmarks, not a generally validated predictor. A source-only guarantee of success is also precluded in the worst-case construction of Theorem 3; that theorem does not rule out prediction under additional source–target assumptions.

How far does the real-shift evidence go (Q3)? We agree that controlled derivatives establish the mechanism only for controlled interventions. The naturally occurring shifts test the downstream FPR consequence, not identification of the same tangent geometry, and the revision makes that distinction explicit. Appendix B.4 now reports the independent domains behind each claim and keeps the Camelyon17 protocols separate; for example, the full nested hospital protocol gives FPR 0.565 → 0.574, while the smaller leave-one-centre-out tile protocol gives 0.484 → 0.481. Seeds and semantic partitions are not counted as new deployment domains. TCGA and 20 Newsgroups remain auxiliary audits, not part of the 13-domain forecast.

Beyond first moments. The first-moment observation result is not a theorem about all nonlinear erasers. MANCE++ reduces the Camelyon17 MLP probe from 0.982 to 0.690, yet target FPR remains 0.855; the DANN sweep instead shows loss of anomaly discrimination without achieving low domain-probe accuracy (Section 4; Appendix C.3). These comparisons are informative but limited. Theorem 3 applies to source-only rules returning rank-rr projectors, even when their source statistics are richer; it does not cover arbitrary nonlinear maps. We have narrowed the claims accordingly.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General response: summary of the revision

We thank the reviewers for their careful reports. We have uploaded a revised PDF; the main changes are concentrated in Sections 3–7 and the appendix. Table, section and appendix numbers in our replies refer to the revised PDF (the original Tables 1–4 are now Tables 3, 4, 7 and 8).

We have made the claim narrower and the evidence easier to follow. The paper is about source-fitted erasure and the operating point of a one-class detector under domain shift, not about a general failure of concept erasure. The revision now separates (i) what first-moment source statistics can observe, (ii) whether the source geometry identifies a useful target projector, and (iii) whether the resulting detector is calibrated. A new table in Section 3 specifies the information required by each diagnostic so that these distinctions are explicit.

The revision brings the existing cross-fitting result on grouped-mean bias to the foreground, explains the target-oracle and source-operator controls more directly, and adds a nested leave-one-domain-out experiment testing what source domains can forecast about an unseen one. We report its negative result as well: the source-only forecast detects lack of benefit from erasure on these domains but does not reliably predict the target FPR itself (Appendix C.2.8).

We have also clarified the formal scope for nonlinear erasers, removed the incomplete Obliviator run from comparisons, corrected Figure 1, restored the ICLR running header, clarified table captions, and added an explicit reproducibility and release commitment. The individual replies below address each concern and point to the relevant evidence.

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

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