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Paper summary
The paper studies LLM unlearning under two forms of subsequent access: alternative queries that may still elicit a forgotten fact, and continued fine-tuning that may restore its accessibility. It proposes neighbourhood-robust unlearning (NRU), which periodically mines queries against the current model, maintains a probe buffer, and minimizes a per-item soft maximum of NPO losses over the original and mined queries. An optional extension evaluates this objective after simulated benign fine-tuning using a first-order update.
The main evaluation uses Qwen2.5-3B-Instruct on a relation-level TOFU split, with 59 reference-answerable forget items. It combines ten strategies with eight queries per strategy, same-entity anchor questions, a retraining oracle, detector sensitivity checks, and continued-training evaluation. Query augmentation reduces measured recovery at similar anchor accuracy, although the main matched-utility comparisons use unequal training budgets. Within NRU-G, refresh and soft-maximum aggregation help at 32 epochs, but response-conditioned generation shows no detectable additional benefit, and inexpensive fixed augmentation performs better at comparable anchor accuracy. The joint query/weight-space variant does not achieve a satisfactory robustness–utility operating point. Additional RWKU and Llama experiments document settings in which the evaluation cannot meaningfully distinguish the methods.
Critical strengths
- The evaluation separates information accessibility from collateral damage in a useful way.
The relation-level split and same-entity anchor set make it possible to detect methods that obtain low recovery by damaging an author's other facts. Reporting query-based recovery, direct-question suppression, and utility together is therefore consequential to interpreting unlearning performance. The reference-versus-retraining-oracle comparison provides a useful detector sanity check: the reported rule yields recovery of 0.83 versus 0.08, while the judge-only rule fails to distinguish the two adequately (Tables 5–6). The alternative detector rules and second-model-family judge further strengthen the comparative evidence, while the paper appropriately acknowledges that these checks do not establish semantic ground truth.
- The controlled comparisons and transparent negative results make the empirical study informative.
The paper distinguishes matched-anchor comparisons, equal-epoch comparisons, and component ablations rather than treating them as interchangeable. It includes fixed-pool, uniform-replay, same-data, nonadaptive-generator, and shuffled-probe controls. At 32 epochs, removing the soft maximum or refresh increases recovery by 0.096 and 0.090, respectively, with author-cluster bootstrap intervals and multiplicity correction for the prespecified contrasts (Table 1c). The authors also explicitly report the absence of a detectable benefit from response conditioning, the stronger performance of inexpensive fixed augmentation, and the utility collapse of the longer-trained stability arms. This transparency makes the findings more useful and prevents low recovery alone from being mistaken for successful, utility-preserving unlearning.
Critical weaknesses
- The central disclosure metric is not sufficiently validated against independent semantic judgments.
All three detector rules that pass the instrument gate retain a lexical-overlap requirement. Consequently, agreement across these rules, or replacement of the semantic judge while keeping that requirement, does not establish sensitivity to semantically correct disclosures expressed with different wording. Appendix G explicitly states that there is no independently labelled sample and that detector sensitivity to paraphrased disclosure, and errors on unlearned models other than the oracle, remain unestimated. On the provided stratified sample of 200 turns, an independent entailment model fires on 0.31 of responses whereas the reported conjunction fires on 0.09. This disagreement does not establish which detector is correct, but it makes independent adjudication important. Reference/oracle separation is a useful control, yet it cannot rule out method-dependent false negatives on the responses used to rank unlearning methods. Since the paper's main contribution is empirical and its endpoint is information recovery, this unresolved measurement issue materially limits confidence in the conclusions.
- The incremental value of the adaptive and joint NRU construction remains insufficiently established, including as a diagnostic contribution.
At 32 epochs, fixed-suite NAU has recovery around 0.16 with anchor accuracy 0.44, whereas NRU-G has recovery around 0.25 with anchor accuracy 0.43, at substantially higher measured per-epoch cost (Tables 3, 7, and 8). The response-denied generator also shows no detectable disadvantage. Thus, the successful refresh and soft-maximum ablations explain performance within NRU-G but do not establish an advantage over simple query augmentation. These negative findings are valuable; however, their explanation remains incomplete because the effects of restricted mining coverage and the permissive training detector are not isolated.
The weight-space extension likewise provides no demonstrated useful joint operating point: NRU-G + stability has recovery 0.72 at 16 epochs, while its recovery of 0.05 at 32 epochs accompanies anchor accuracy of only 0.13 and rises to 0.26 after continued training (Table 9). The strongest fixed-suite methods are not evaluated after continued training (Section 5.4). Moreover, the informative method comparison remains confined to the small Qwen/TOFU-Rel setting, since the RWKU and Llama extensions cannot distinguish the central effects (Appendix I). Together, these gaps leave the proposed mechanisms and their failure modes less decisively understood than would be needed for a strong methodological or diagnostic contribution.
Questions for authors
- Clarification: What does query variation recover beyond the original question?
For NPO and the principal query-neighbourhood methods, please report the original forget question's reproduction rate under the same detector used for the probe evaluation. What fraction of facts are not reproduced under the original question but are subsequently recovered by another query? In particular, the comparison between suppression S0 = 0.37 and neighbourhood recovery = 0.51 does not by itself establish how many disclosures a direct-question evaluation would miss. A paired analysis would materially strengthen or qualify the interpretation of P1.
- Measurement validation: Do the conclusions survive independent adjudication of semantic disclosure?
Can the provided response sample be independently labelled, including detector-negative responses that may disclose the fact through paraphrase, and with representation from the main unlearning methods as well as the reference and oracle? Please report the detector's precision and recall and whether the principal method comparisons remain consistent with the adjudicated labels. Changing the semantic judge while retaining the lexical gate does not address errors shared by that gate.
- Targeted control: What explains the absence of an observed benefit from response-conditioned mining?
Section 7 identifies both restricted mining coverage and a permissive training detector as possible explanations, but neither is tested. What fraction of buffered probes actually disclose the target fact under a validated criterion? Can the adaptive, response-denied, and fixed-suite comparisons be examined with matched item coverage and probe budgets? This would help distinguish a limitation of response conditioning from a limitation of the training neighbourhood constructed in the current implementation.
- Evidence for the second-axis conclusion: How do the strongest query-neighbourhood baselines behave after continued training?
Section 5.4 omits NAU + anchor, DRO-NAU + anchor, and NRU-S from the continued-training evaluation. Can their recovery and both utility measures be reported after the same 100-step procedure? For the joint method, are intermediate-epoch results available that preserve utility while achieving meaningful unlearning? These results would materially affect the practical assessment of joint robustness and the interpretation of the failure observed at the two reported operating points.
3 comments
Response to Reviewer 89kr (2/2)
W2 (second half). The operating point of the weight-space extension
Your reading is correct, and the runs you asked for sharpen it. Table 9(a) (p. 23) now reports both stability arms at 20 and 24 epochs. From recovery 0.69 and 0.61 at 20 epochs they change by -0.01 and +0.05 under continued training, and from 0.50 and 0.35 at 24 epochs by +0.06 and +0.14 (Appendix H.2, p. 20). At 24 epochs NRU-G + stability thus has recovery 0.35 at anchor accuracy 0.44, and 0.49 after continued training. NAU + anchor at 32 epochs has 0.16 at the same anchor accuracy, and 0.40 after continued training. One encouraging point: the fine-tune removes less of their suppression (0.10 to 0.29) than of any arm trained on queries alone (Section 1, p. 1). Yet their recovery nears the oracle's only at 32 epochs, where their anchor accuracy falls to 0.13. The two-axis arms therefore do not yet reach a useful joint operating point. Section 5.4 (p. 8) presents this as an analysed result, with its mechanism, and we see a different simulated fine-tune as the way forward.
Q4. Continued training for the strongest fixed-suite methods
Table 9(a) (p. 23) now includes NAU + anchor and DRO-NAU + anchor at 16 and 32 epochs, with anchor and retain accuracy before and after the same hundred-step procedure for every arm. Recovery rises from 0.29 to 0.55 and from 0.16 to 0.40 for NAU + anchor, and from 0.44 to 0.58 and from 0.18 to 0.40 for DRO-NAU + anchor. NRU-G rises from 0.25 to 0.47 at 32 epochs. The share of suppression lost at 16 epochs is 0.58 for NAU + anchor and 0.37 for DRO-NAU + anchor (Appendix H.2, p. 20). The fixed-suite arms are therefore no more stable than the others, and the paper now states the range over the eight arms trained on queries alone: 0.34 to 0.68 (Section 5.4, p. 8). NRU-S is the one arm of your list that we were not able to run through continued training in the discussion period; Section 5.4 (p. 8) and Section 7 (p. 9) note this. We do not expect it to change the conclusion, for two reasons that the paper prints. NRU-S trains on the same suite as NAU + anchor and reaches the same recovery at 32 epochs (0.16 for both; Table 3, p. 16). And every query-only arm that we did measure, the two fixed-suite arms included, loses 0.34 to 0.68 of its suppression. This is an expectation, not a measurement, and the paper makes no claim about NRU-S after continued training.
Q1. What query variation recovers beyond the original question
Thank you for this question; the analysis it prompted supports P1 directly. New Table 10 (p. 24) reports three shares of the 59 answerable items, for eight arms at 16 and 32 epochs: the share whose forget question reproduces the fact under the same detector, recovery within eight queries, and the share reached only by other queries. For NPO at 16 epochs these are 0.27, 0.51 and 0.27, and recovery exceeds direct reproduction by +0.24 [+0.11, +0.37] (Appendix H.3, p. 23). So about half of the facts that the probes recover are facts that the forget question does not reproduce. At 32 epochs the three shares are 0.01, 0.16 and 0.16, so a check on the forget question alone would miss nearly every recovered fact. For NAU + anchor the shares are 0.19, 0.29 and 0.18 at 16 epochs and 0.04, 0.16 and 0.14 at 32. For NRU-G they are 0.37, 0.50 and 0.15, then 0.11, 0.25 and 0.16. This is the paired reading of P1 that you asked for. Suppression of 0.37 is a likelihood measure, so it is not comparable with these detector rates. Section 5.1 (p. 6) now states the 16-epoch figures.
Confinement to Qwen and TOFU-Rel
We agree, and the paper says so (Section 7, p. 9). Appendix I had noted that a sweep below 16 epochs was needed on Llama-3.2-3B, and we ran it at 4 and 8 epochs (p. 25). It does not open a window for comparison: NPO has barely unlearned there (recovery 0.77 and 0.78), NRU-G recovers 0.03 more at 4 epochs (unadjusted p = 0.02), and only response mining recovers less (0.03 at 8 epochs, with anchors at 0.32). At 32 epochs, as at 16, every arm is under the oracle's rate. Neither Llama nor RWKU can therefore arbitrate between objectives.
Change. Section 1 (p. 1), Section 5.1 (p. 6), Section 5.3 (p. 8), Section 5.4 (p. 8), Section 7 (p. 9), Appendix G (p. 18), Appendix H.2 (p. 20), Appendix H.3 (pp. 23-24), Table 9(a) (p. 23), Table 10 (p. 24) and Appendix I (p. 25).
Thank you again for the care in your review. We hope these measurements answer your questions, and we would be grateful if you would reconsider your assessment in their light.
Thank you for your response. I understand your point to some extent, but your reply was too long for me to examine in detail; therefore, I will keep my rating as it is. I apologize for any consequences this may cause.
Response to Reviewer 89kr (1/2)
Thank you for a careful, constructive and fair review; it is the kind of review that improves a paper. It led to new measurements for Q1, Q3 and Q4 and to a correction under Q2. Every change is blue. Part (2/2) answers the second half of W2 (the weight-space extension), Q4 and Q1.
W1 and Q2. Validation of the detector against independent judgments
Your concern is well taken, and we want to be precise about how far the revision goes. The detector is checked against a retraining oracle and against two further judges, but it is not yet validated against human labels, and Section 7 (p. 9) now says so up front. Three points in Appendix G (p. 18) bear on the concern; we first explain why labels are not yet reported.
Why labels are not yet reported. A validation that settles your question needs annotators who are independent of us and blind to the arm and to the detector's verdict, at least two of them so that their agreement can be reported, and enough labelled turns per arm to test whether missed disclosures differ between arms. The 200-turn sheet cannot carry the per-arm part: it holds equal numbers from the four agreement cells, not from each arm. We were not able to arrange such a study within the discussion period, and we felt that a small sample labelled by the authors would not do justice to your concern. We have therefore stated the limitation clearly and released the sheet unscored, and we regard independent adjudication as the natural next step.
W2 (first half) and Q3. Why response-conditioned mining shows no benefit
Thank you for pointing out that the submitted text named two explanations without testing either. Appendix H.3 (pp. 23-24) now tests both, and the abstract now states that the generator does not beat NPO at identical epochs (p. 1).
Two caveats remain, and the paper states them. The lower anchors leave the 32-epoch reading of the coverage control open, and the response-denied generator was not rerun at matched coverage. The reason for the second is that the adaptive and the response-denied generator already mine the same generator-train entities with the same strategies (Section 4, p. 5), so that pair is matched by design. A three-way match would need a second suite cut to the response-denied buffer and its own training runs, which we did not make. Section 5.3 (p. 8) now cites these results, and Section 7 (p. 9) states them where the submitted text said "neither was tested".