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Paper summary
This paper examines the reliability of context-based evaluations of language-model unlearning. Experiments with synthetic relational facts show that models retrained without target facts can recover them from related context, motivating comparisons against retrained references under identical prompts. The authors evaluate 11 unlearning methods and introduce conflicting-context probes that reveal behavioral differences between selected unlearned models and retrained references, complementing generation and no-context candidate scoring. Additional experiments on Hubble demonstrate recovery of non-inferable random identifiers from biographical context after unlearning, and measure collateral effects on identifiers outside the forget set.
Critical strengths
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The paper provides a concrete experimental demonstration that contextual recovery alone can misidentify successful unlearning as failure. Retrained models recover inferable target facts with 54–91% accuracy when given the employer, compared with 8–13% without context (Figure 2; Table 3). This supports the practical recommendation to evaluate recovery against a retrained reference under identical prompts, helping distinguish reconstruction from retained knowledge from evidence of failed unlearning.
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The Hubble experiments provide useful complementary evidence for non-inferable targets. Seven healthy 8B SimNPO/WGA settings recover random identifiers with 89–98% accuracy from biographical context, compared with 11% for the no-exposure reference (Table 19). Evaluating identifiers outside the forget set also exposes collateral suppression (Figure 7; Table 20). These results strengthen the paper’s distinction between inferable facts and arbitrary identifiers and highlight the importance of evaluating selective forgetting.
Critical weaknesses
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The incremental diagnostic value of conflicting context remains insufficiently established. In the main sweep, no-context scoring combined with free generation already flags all 48 healthy models, matching the coverage obtained by combining no-context scoring with conflicting context (Table 10). Moreover, three of the five RMU settings missed by the one-sided no-context test already differ significantly from the retrained reference in the negative direction (Table 12), making them distinguishable through a two-sided comparison. The additional RMU experiments in Table 16 provide useful evidence, but the benefit beyond existing tests remains supported by a limited set of configurations. This limits the demonstrated significance of the proposed audit.
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Unresolved evaluation and replication issues weaken confidence in the empirical results. Appendix A.3 reports that the Llama sweep used an incorrect attention mask and that the unlearned checkpoints were unavailable for rescoring. Correcting the mask changes the stored original model’s wrong-employer result from 77% to 84% while leaving the retrained result unchanged, so using the same faulty scorer does not ensure cancellation of its effects. Separately, rebuilding the Qwen3 original model and repeating the RMU settings reduces true-sector retention under conflicting context from 63–73% to 50–57%, with three of five reruns failing the health checks (Appendix C.4). Corrected evaluations and an explanation of this variability are needed to establish the reliability of the reported findings.
Questions for authors
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What additional diagnostic value remains under comparable baselines? Table 10 shows that no-context scoring combined with free generation already flags all 48 healthy settings. For the key RMU cases, could you compare conflicting-context detection with no-context accuracy and two-sided margin tests, using matched candidate sets where possible? Please identify which settings exhibit additional detection or more reliable detection under these comparisons. Evidence of a consistent benefit would strengthen my assessment of the proposed test’s contribution.
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How sensitive are the Llama findings to the scoring correction? Could you provide corrected evaluations for a small, representative subset of the Llama settings supporting the main conclusions, including settings near the health or detection thresholds? If rerunning is necessary because the checkpoints are unavailable, applying both scorer versions to the same new checkpoints would help separate scoring effects from training variability. Please report whether the health classifications and differences from retrained references remain stable. Such evidence would substantially reduce my concern about the affected results.
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How reproducible is the key RMU phenomenon? Appendix C.4 reports substantial changes after rebuilding the Qwen3 original model and repeating the RMU configurations. Can the authors explain these changes through a comparison of the actual training configurations and checkpoints, and provide a small number of independent repetitions of the key five-epoch settings in Table 16? Reporting health checks and detection outcomes for each repetition would help establish how consistently the phenomenon occurs. Reproducing the effect under a fixed protocol would increase my confidence in the reliability of the findings.