acceptodds
Under review as a conference paper at ICLR 2027

Forgetting That Sticks: Quantization-Permanent Unlearning via Circuit Attribution

Abstract

Standard unlearning evaluations measure behavioral suppression in full precision, immediately after training, despite quantization being a common deployment transformation for language models. Prior works have shown that 4-bit post-training quantization can reverse machine unlearning. We show this is a systematic dual failure. Gradient-based methods that achieve meaningful forgetting lose it under compression, while methods that survive quantization barely change the model. Both failures have the same root cause. Across all baselines, per-parameter RMS updates are 47 to 828× below the canonical NF4-calibrated floor used in our implementation, so updates diffused across billions of parameters cannot clear quantization bin boundaries, a consequence we formalize as a **sparsity-permanence tradeoff**. We present **MANSU** (**M**echanistic-**A**ligned **N**ull-**S**pace **U**nlearning), which addresses this tradeoff by treating it as an update-budget allocation problem. Causal circuit attribution isolates a compact, causally implicated forget circuit, a diagonal-Fisher mask restricts updates to retain-safe coordinates within that circuit, and a quantizer-calibrated magnitude floor, applied post-hoc, makes the resulting update deployment-visible, which we verify directly on the trained checkpoints. Matched controls (the same floor applied to a random circuit, an inverse circuit, a globally projected update, and a Fisher-ratio selective baseline) show that neither circuit concentration nor magnitude flooring alone reproduces this behavior in the reported ablations. We additionally introduce **Circuit Attribution Divergence (CAD)**, a mechanistic verification metric providing evidence of circuit-level structural change beyond behavioral suppression, corroborated by independent linear-probe and activation-patching analyses. Across multiple model families and WMDP hazard domains, MANSU consistently yields a non-positive NF4 PTQ gap while retaining substantially higher general capability than aggressively optimized baselines, whereas gradient ascent, for instance, partially reverses under compression (BF16 forget 0.260 to NF4 0.310, PTQ gap +0.050). We scope our boundary-crossing analysis to NF4 and report GPTQ and INT8 results separately as empirical transfer checks.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
Machine Unlearning, Large Language Models, Quantization, NF4, Mechanistic Interpretability, Circuit Attribution, Quantization-Robust Unlearning, Continual Learning

Reviews

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1234this paper, Bottom 1%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.00 over 3 reviews, above 0% of the others.
Reviewer_WwQrOpenReview ↗
Rating
1
Confidence
4
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

This paper tries to look at the problem of quantization and its effect on machine unlearning. It is known that quantization can have the unwanted effect of reversing machine unlearning. They show that compression can cause reversal of machine unlearning and that models that can retain unlearning after quantization barely change the model. In view of this they introduce two mechanistic frameworks, namely Mechanistic-Aligned Null-Space Unlearning (MANSU), which they suggest addresses the above issue, and Circuit Attribution Divergence (CAD), a metric that provides evidence of circuit level structural change beyond behaviour suppression.

Critical strengths

The paper tries to study an important problem in the literature, that of the effects of compression on machine unlearning algorithms. Since models are generally transferred and stored through compressive means the unwanted effect of a compression algorithm destroying forgetting capability is an important research problem.

Critical weaknesses
  1. The paper is extremely poorly written and at times reads like a bunch of bullet points with no real narrative of what the authors are trying to tell the reader. Even the description of the problem they are trying to address is not well stated and I had to read the paper several times and do a literature search myself to understand the context better.
  2. The technical theorems, propositions and lemmas are often stated with poor context making it difficult for the reader to gain insight into what the authors are trying to do. I had to read the technical analysis, section 5 as well as Section D, several times and even then I found myself getting lost with regards to what exact insight the authors are trying to get across.
  3. There are parts of the papers that make no sense. For example, their discussion section 7 makes absolutely no sense to me. It is unclear what the authors are trying to tell the reader. This sort of writing occurs in several parts of the paper, e.g. first paragraph of section 5. I commend the authors for being upfront with their use of AI in their AI statement but it is crystal clear the authors have made no effort in trying to exposit in a better way the AI led research they have carried out. If one is going to use AI to help in the actual research then it is the duty of one to make sure they exposit that outcome of that research in a way that is understandable for human readers. The authors have not done this making it impossible to understand what they are trying to get across to the reader.
Questions for authors
  1. I found it almost impossible at times to parse the theorems, propositions and lemmas in your paper. Can you give a clear explanation of what proposition 1is supposed to be telling us?
  2. In Theorem 1 I am confused as to what is HccH_cc? Also, in that theorem you assume the loss has Hessian that is PSD. This is almost never true though right? It would imply convexity of the loss function I would think, which makes the analysis extremely simple.
  3. Figure 2 must have been made with an LLM as it makes absolutely no sense to me. Can you please explain what on earth this figure is trying to show the reader?
  4. I also have no idea what you are trying to say in the limitations section in section 7. Can you elaborate on this? It would be much easier if you said exactly what the limitations of MANSU and CAD are separately.
2 comments
AuthorsOpenReview ↗

Response to reviewer WwQr

In one paragraph, models are usually quantized to 4 bits before deployment. Prior work has shown that this can bring back knowledge that unlearning had removed. We show why. Unlearning methods change each weight by much less than the gap between two 4-bit values, so rounding snaps most weights back to where they were. MANSU (i) finds the small set of weights causally responsible for the target knowledge, (ii) restricts the update to those weights while protecting retain performance, and (iii) makes each changed weight move at least one 4-bit step, so the change survives rounding. The answers below address each question directly. The same fixes are reflected in a revised version of the manuscript.

Proposition 1: the tradeoff it formalizes.

Spreading a fixed retain-safety budget over more parameters forces each one's update to shrink, since the same budget is divided more ways. Concentrating it into fewer parameters lets each move further before the retain constraint is violated. Formally, every coordinate satisfies a worst-case bound driven by the smallest per-parameter Fisher value in the circuit, unconditionally, and a sharper estimate using the mean Fisher value holds under the equal-magnitude allocation gradient ascent produces in practice. For Llama-3.1-8B, updating the full parameter set this way moves each weight about 380 times below the deployment rounding floor, which is why no existing method survives quantization without first shrinking which parameters it touches.

Theorem 1: the missing notation and the PSD-Hessian assumption.

The notation the bound depends on is H (the retain-loss Hessian), C-bar (the parameters outside the circuit), and ker(H restricted to the circuit), meaning directions inside the circuit that don't change the retain loss to second order. If a different symbol was meant, happy to clarify further once we've confirmed which one against the review itself. On soundness, we have actually tightened the theorem rather than defend the PSD condition. Under the theorem's own stated conditions, the update is zero outside the circuit and lies in the circuit's Hessian null space inside it, so the second-order term in the Taylor expansion vanishes exactly, as our own appendix proof already showed. No assumption on the sign or convexity of the retain-loss Hessian is needed anywhere, and the revised bound is correspondingly tighter.

Limitations of MANSU.

  • Verified at 8B scale (Llama-3.1-8B, Qwen-3-8B). Six smaller models appear in the appendix, but larger scales are untested.
  • Checkpoint selection uses a threshold-based early stop (not a search that maximizes MMLU) on the same question set later reported on, rather than a disjoint validation split, which bounds but does not remove the selection effect.
  • Circuit-identification examples and forget-evaluation indices are drawn from the same question pool and are not confirmed disjoint. We believe the risk this poses to the headline numbers is limited, since identification only selects which layers are trainable and never touches evaluation labels, but we have not verified disjointness directly, and flag it rather than assume it away, exactly as stated in the paper's own Limitations section.

Limitations of CAD.

  • It reuses the same attribution machinery that selects the circuit, so a high score alone would not rule out attribution instability. Independent linear-probe and activation-patching checks agree with the same circuit (Appendix, independent validation of CAD), though re-attribution after unlearning retains most but not all of the original top layers, consistent with some reorganization rather than a clean dismantling.
  • It is only evaluated on factual-recall MCQ benchmarks. Transfer to open-ended generation is untested.

Figure 2: what each panel shows, and the two label fixes.

Panel 1 (Localize): EAP-IG ranks MLP layers by causal contribution to the forget answers and keeps the top layers as the circuit. Panel 2 (Project): updates restricted to that circuit are masked along a retain-protective Fisher threshold. Panel 3 (Floor): a per-parameter magnitude floor rescales each update so it survives 4-bit rounding. Two label corrections, independent of the panel content, are now reflected in the revised Figure 2. Panel 2's threshold now reads tau = 0.1 times the mean Fisher value (it previously read "99th percentile," which was stale), and Panel 3's guarantee is now scoped to the narrow-bin majority of circuit weights (about 65%), with the remainder empirically confirmed rather than unconditional.

Dear Reviewer WwQr ,

We are writing to ask whether our rebuttal has addressed your concerns. We would be happy to discuss any remaining issues.

Reviewer_NkrYOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
2
Soundness
1
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Paper summary

The paper says unlearning gets undone by 4-bit (NF4) quantization because the weight changes are too small to survive rounding. The method, MANSU, picks a few important MLP layers, unlearns only there, and then forces every small change up to a fixed minimum size so it survives quantization. It also proposes a new metric, CAD.

Critical strengths
  1. NF4 results are reported next to BF16 for every method, which is good practice.
  2. The ablations (random circuit, inverse circuit) ask the right questions.
Critical weaknesses
  1. The main claim does not match the paper's own results. Global GA's changes are 828x below the minimum size, yet it keeps about 90% of its forgetting after quantization (Table 2).
  2. Surviving quantization is built in. With lr 1e-6 for at most 30 steps, almost every change is below the minimum and gets set to the same fixed size. So a negative PTQ gap does not show the knowledge is really gone.
  3. Results are picked on the test sets. The checkpoint is chosen using the same forget questions and MMLU questions that are reported. The headline MMLU of 0.573 appears at only one setting; an independent MMLU check gives 0.47-0.49 (App. J).
  4. Everything is on about 100 questions, so a 0.04 gap is only a few questions. And RMU is not compared.
Questions for authors

Please refer to the weakness section, and specifically "Which numbers are correct where Table 2 and Table 12 disagree?"

2 comments
AuthorsOpenReview ↗

Response to reviewer NkrY

We thank the reviewer for a detailed, technically specific review and address each point below. These corrections will appear in a revised manuscript.

W1: Table 2 vs. Table 12 disagreement (MMLU 0.591 vs. 0.573).

Table 2's WMDP-bio row for MANSU on Llama-3.1-8B-Instruct reports MMLU 0.573, and Table 12, the per-experiment Llama sweep, reports the identical value for the same model/dataset/checkpoint cell. The 0.591 figure is Table 2's MUSE row, a separately trained checkpoint on a different forget dataset, so it is not expected to match the WMDP-bio cell. On MANSU's own rows specifically, Table 2 and Table 12 agree.

W2: Appendix J's independent check (0.47-0.49) vs. Table 2 (0.430/0.573).

Appendix J is not a second run of the same canonical evaluation producing a different answer. That analysis reports forget accuracy of 0.47 to 0.48 and MMLU of 0.47 to 0.49 under a reconstructed evaluation split that follows the same sampling procedure as the paper's frozen indices but is not byte-identical to them, a gap from Table 2 of about 0.05 on forget accuracy and 0.08 to 0.11 on MMLU, reported as such in the appendix. It is a robustness analysis of the released checkpoint, not an exact re-evaluation of the Table 2 checkpoint.

W3: Global GA, 828x below the floor yet retains about 90% of its forgetting (Table 2).

This deserves a quantitative answer, not a restatement of the mechanism. We audited Global GA's checkpoint with real NF4 quantization (bitsandbytes), the same method used in Appendix E for MANSU's own crossing claim, across the full model. Of 219,361,023 updated parameters, none exceed the canonical floor of 8.4e-4 (the largest update, 8.25e-5, is itself an order of magnitude below it). Despite this, 3,637 parameters (0.0017% of the updated set) do cross an NF4 bin boundary, consistent with NF4's non-uniform, finer-near-zero bin spacing. This is a confirmatory sanity check rather than independent evidence on its own, since these crossings occur where the mechanism predicts, at weights already near a local boundary, and these updates sit far enough below the floor that the block scale was unlikely to shift regardless. That said, 0.0017% of updated parameters is too small a set to be the primary driver of the roughly 90% of forgetting Global GA retains under NF4, and we do not claim this fully accounts for the +0.050 PTQ gap. Part of Global GA's update lands in embed_tokens and lm_head, which bitsandbytes NF4 leaves in bf16, so that part survives quantization regardless of size. We have not measured how much of the residual it explains, since that requires a revert test (zeroing GA's update in those modules and re-evaluating) that we have not run.

W4: Checkpoint selected and reported on the same question set, small sample size, RMU not compared.

The checkpoint-selection mechanism works like this. The checkpoint we keep is the most recently saved one. Training stops early only when a monitored 400-question MMLU set drops below a fixed threshold, and at that point we revert to the last-saved checkpoint. Forget accuracy plays no role in checkpoint selection. Section 4 and Appendix C.3 state this precisely, consistent with the evaluation-indices discussion elsewhere in the paper.

Separating the two metrics resolves this. Because forget accuracy plays no role in selection, the same-set tautology does not apply to the forget-accuracy figure at all. MMLU is different by design, since a threshold-based early stop decides which checkpoint survives rather than a search that maximizes MMLU, so the selection effect is bounded, not unbounded. Our evaluation-indices discussion already discloses this openly.

The floor is necessary but not sufficient on its own, and that distinction is what answers this. Applying the same floor to a random same-size circuit (Table 3, C(i)), an inverse circuit (C(ii)), a global update (D), or SSD-selected weights (E(ii)) shows that the inverse, global, and SSD variants all turn the PTQ gap positive, while the random circuit, though it keeps a negative gap (-0.024), forgets substantially less (0.500 vs. 0.430) and loses more retain/MMLU (0.471/0.470 vs. 0.523/0.573) than the causal circuit. Only the causally selected circuit combines deep forgetting, a negative gap, and preserved retain accuracy together. This is evidence against a pure selection-artifact explanation, though not a held-out proof. We have not run an RMU comparison and do not promise one for the revision.

Dear Reviewer NkrY ,

We are writing to ask whether our rebuttal has addressed your concerns. We would be happy to discuss any remaining issues.

Reviewer_7vmaOpenReview ↗
Rating
1
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

Motivated by the lack of current forgetting methods that survive quantization, This paper presents a new method, MANSU for unlearning. MANSU identifies a forget circuit, performs restricted updates within that circuit. The authors validate this method on Llama-3.1-8B-instruct, and find that MANSU achieves a lower PTQ gap than existing methods, while also retaining other knowledge better.

Critical strengths

This problem is well motivated and proposes an interesting design.

Critical weaknesses

This work lacks rigorous evidence that MANSU outperforms existing methods, as baseline forgetting algorithms were not tuned and the results for MANSU are cherrypicked. For MANSU, the authors select the best-performing model across different copies of the model, measured via performance on an 100 question dataset. Afterwards, they report the score on that same 100 question dataset --- different datasets should be used for test and validation, and there is also no mention of performing this tuning process (or even any tuning process) for all other forgetting methods.

Additionally, the authors highlight $\Delta $ PTQ as the metric MANSU dominates, but the final metric we should care about is performance after PTQ, in which MANSU is outperformed by many other existing methods. It is unclear why the authors chose to focus on $\Delta $ PTQ instead of performance after PTQ.

Questions for authors

How does tuning the baseline methods/not cherrypicking MANSU change the narrative? Do these results hold for additional datasets?

4 comments
AuthorsOpenReview ↗

Response to reviewer 7vma

We thank the reviewer for the feedback.

Cherry-picking and baseline tuning.

The checkpoint-selection mechanism directly addresses part of this concern. The checkpoint we report for MANSU is selected purely by an MMLU-threshold early stop. Forget accuracy plays no role in selection. This narrows that specific concern to the reported MMLU figure, and our evaluation-indices discussion already discloses it openly. Section 4 and Appendix C.3 have been corrected to state this mechanism precisely. On baseline tuning specifically, the MMLU early-stop rule described above was applied to MANSU's own checkpoint, not to the baselines. Global GA ends at MMLU 0.235 and GU+SimNPO at 0.200 (Table 2), both far below any early-stop threshold, confirming the baselines were run to convergence without the same utility-preserving stop. We have not run an additional hyperparameter-tuning sweep over the baseline methods beyond the values already reported in the appendix, and would rather say so directly than imply otherwise. Claims in the paper that rest on these baselines' utility collapse are being scoped down in the revision accordingly.

PTQ gap versus absolute post-PTQ accuracy.

This is a fair challenge to our framing. The PTQ gap is a within-method comparison, measuring whether a method's own forgetting survives its own deployment step, rather than a standalone ranking criterion on its own. We report it alongside retain accuracy and MMLU because a method can reach a better absolute post-PTQ forget accuracy than MANSU while damaging retain performance substantially more to get there. This is visible directly in Table 2, where Global GA and GU+SimNPO reach lower absolute forget accuracy than MANSU on several cells at the cost of MMLU collapsing toward chance. The Discussion section states this explicitly, reporting the PTQ gap jointly with retain accuracy and MMLU precisely because the gap in isolation, without that joint reading, overstates what it shows.

Baseline tuning, checkpoint reliance, and generalization across datasets.

The cross-domain ablation in Section 6.3 (chemistry and cyber domains) and the multi-model sweep in Appendices K through N (Gemma, Llama, and Qwen families) already extend beyond the single WMDP-bio/Llama cell discussed in the main text. On whether MANSU's own checkpoint is cherry-picked, as clarified above, MANSU's checkpoint is fixed by an MMLU early-stopping rule, not selected after the fact per dataset. That same rule was not applied to the baselines, as noted above.

Dear Reviewer 7vma ,

We are writing to ask whether our rebuttal has addressed your concerns. We would be happy to discuss any remaining issues.

Thank you for your response. However, my original concerns still remain; I maintain my score.

AuthorsOpenReview ↗

regarding your response

Dear Reviewer 7vma,

Thank you for confirming that you have gone through our response. Since you mention that your original concerns remain, could you please specify which ones?

Our response addressed three specific points you raised: (1) the checkpoint-selection mechanism, which we clarified uses an MMLU-threshold early stop with no role for forget accuracy, narrowing the cherry-picking concern specifically to the reported MMLU figure; (2) why we report the PTQ gap jointly with retain accuracy and MMLU rather than as a standalone ranking criterion; and (3) cross-domain and cross-model evidence (Section 6.3, Appendices K-N) beyond the single WMDP-bio/Llama cell you focused on.

Could you tell us which of these remain unresolved? Alternatively, if there’s a concern we haven’t addressed at all, we’d like to know so we can address it at the earliest.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General Comment to the Committee Members

We thank the AC and all three reviewers for their time. Beyond our point-by-point responses, this comment summarizes how the paper has strengthened since submission. Every change below is marked in blue in the revised manuscript.

Precise checkpoint-selection mechanism (bears on NkrY W4 and 7vma). We clarified, in both the main text and appendix, exactly how the reported checkpoint is selected. A monitored MMLU set triggers an early stop at a fixed threshold, and forget accuracy plays no role in selection at all. This sharpens the same-set-selection discussion considerably, narrowing it to the reported MMLU figure specifically, since forget accuracy was never part of selection to begin with.

Refined Figure 2 for full internal consistency. We audited Figure 2 against the main-text circuit equation and tightened the Stage 1 panel so the displayed circuit and its layer ordering match exactly.

New quantitative audit of a baseline's floor margin (Reviewer NkrY, W3). We ran a real NF4 quantization audit of Global GA's full checkpoint (219,361,023 updated parameters), extending to a baseline the same method already used to verify MANSU's own crossing claim. The audit finds 3,637 parameters crossing an NF4 bin boundary at positions consistent with the floor mechanism, a confirmatory sanity check rather than independent evidence on its own, and in any case too small a count to be the primary driver of Global GA's residual forgetting. This is an honest, quantitative scoping of the claim rather than a restatement of it. This audit is now included in the appendix.

New confirmatory check: sampling stability across disjoint question halves. We split the canonical forget-set evaluation into two disjoint random halves and evaluated separately. The two halves agree to within 6 points of each other. We treat forget-accuracy differences smaller than this as noise rather than as evidence of instability.

Sharper statement of Proposition 1's 380x figure (Reviewers NkrY and WwQr). We added a passage distinguishing the theoretical, equal-allocation prediction from the measured 47-828x range on actual baselines, and connected it to the ablation evidence (Table 3) showing the magnitude floor is necessary but not sufficient on its own, since circuit identity is what makes permanence and retained utility coincide.

Restructured Discussion section. We added a subsection explaining why we report the PTQ gap jointly with retain accuracy and MMLU rather than as a standalone ranking criterion (answers 7vma), and organized the limitations discussion into two clear, itemized lists, one for MANSU and one for CAD, for easy reference (answers WwQr).

As instructed, the revised manuscript marks every change made since the submitted version in blue. We will flatten this to ordinary black text in the final revision we upload at the end of the rebuttal window.

We are happy to run any further checks the AC or reviewers would find useful in the time remaining.

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

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