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Paper summary
The paper proposes Matryoshka Machine Unlearning (MMU), which applies unlearning objectives to multiple nested prefixes of a model’s representation. A frozen copy of the original model serves as a teacher. On retained data, the student combines supervised learning with distillation; on forgotten data, it is pushed away from the teacher through a margin-limited KL objective. The authors also extend the approach to diffusion models by applying related objectives to noise predictions at different channel widths. Experiments cover three classification datasets, two backbones, three deletion granularities, and concept suppression in image generation. The strongest results concern class deletion and retained utility, while subclass and instance deletion remain less successful.
Critical strengths
- The paper addresses a meaningful limitation of output-based unlearning with a concrete method. Changing a model’s final prediction does not establish that information is no longer recoverable from its representation. Applying constraints at several nested widths is a reasonable attempt to address this issue. The construction is straightforward, and auxiliary classifiers can be removed after training, making the approach worth investigating further.
- The class-deletion results show a promising balance between suppression and retained utility. In Table 2, MMU achieves zero class-forget accuracy across all six dataset–backbone combinations while maintaining competitive retained accuracy. The paper also evaluates per-example attacks, relearning, and sequential deletion, providing a broader assessment than forget accuracy alone. These findings support MMU as a potentially useful class-deletion method, although they do not establish the broader claims made in the abstract.
Critical weaknesses
- The central representation-level claim is not directly tested, and the contribution of nesting is not isolated. The paper is motivated by the possibility that deleted information remains decodable from short representations after the final prediction changes. However, its objectives constrain predictions through trainable classifiers. In MMU-1, each width has an independent classifier, so the heads could absorb the changes while the encoder remains informative. Figure 3 evaluates the existing readouts rather than newly trained probes; SCRUB also achieves approximately zero forget accuracy at the widths shown. MMU additionally differs from SCRUB in its margin-limited objective, width weighting, and search space. Table 12 lists 96 candidate configurations for MMU versus 24 for SCRUB. The reported controls do not clearly separate these factors. Without a matched single-width hinge baseline and frozen-representation probing against Retrain, I cannot determine whether the main proposed mechanism accounts for the observed improvements.
- Important experimental results are insufficiently reconciled, and the overall claims exceed the evidence. Table 1 reports Retrain forget-set values of 5.21% and 7.65% for random deletion, which the accompanying text interprets as classification accuracy, despite test accuracies of 94.44% and 92.16%. Table 5 instead reports Retrain forget accuracies of 94.27% and 92.58%, with MMU remaining at 100% in both settings. The Table 1 values may reflect an error-rate convention, but the manuscript does not establish this or explain the different MMU outcomes. This ambiguity directly affects the claimed effectiveness of random deletion. Other results also show substantial limitations: MMU’s subclass-deletion U-LiRA AUC remains around 96% on CIFAR-100, and Table 8 reports reappearance of the first deleted condition in 3/16 samples after sequential deletion. Although the conclusion acknowledges some limitations, these findings do not support the abstract’s claim of having no failure mode. The evidence currently supports advantages in particular operating regimes rather than reliable unlearning across deletion granularities.
Questions for authors
These questions concern the interpretation and support of the current claims; their answers could change my assessment.
- Metric and protocol clarification: Does in Table 1 denote accuracy or error rate? Do Tables 1 and 5 use different model variants, training configurations, or selection procedures? Please specify the differences and explain why MMU retains 100% forget-set accuracy in Table 5.
- Attribution of the improvement: What benefit does nesting provide over a single-width method using the same hinge objective, data access, training schedule, and hyperparameter-search budget? Do the existing experiments include a direct comparison that isolates this contribution?
- Evidence for representation-level removal: Have you evaluated newly trained probes on frozen representations at each width, using Retrain as the reference? If not, would you agree that the current evidence supports improved behavior under the evaluated readouts, rather than establishing that the deleted information is no longer decodable?
4 comments
2/2
Q1
Metric. In Table 1, the D_f column reports forget error (100 − accuracy, the "UA" convention of SalUn); Table 5 reports forget accuracy. The manuscript's text wrongly interpreted Table 1 as accuracy. We will use forget accuracy throughout and state the definition in every caption. A consistent conversion leaves the gap to Retrain unchanged: |(100 − a) − (100 − b)| = |a − b|.
Protocol: the two tables are different experiments.
| Table 1 | Table 5 | |
|---|---|---|
| Trials | 10 (seeds 2–11), each with its own source and Retrain | 1 (seed 2) |
| Hyperparameters | selected on pilot seed 1 using validation metrics | fixed, no search |
| MMU variant | nested MMU, as in the submission | a full-width, two-teacher variant (no nesting; a retain-fine-tuned teacher supplies attraction targets; lr 1e-3, T = 1, margin 0.002) |
| Metric | forget error | forget accuracy |
The Retrain values therefore differ for two reasons: the metric, and averaging. Table 1's 5.21% error is the 10-trial mean (94.79% accuracy), while Table 5's 94.27% is the seed-2 trial alone (5.73% error). At 50% forgetting, the corresponding figures are 92.35% (mean) and 92.58% (seed 2). Labelling the Table 5 variant "MMU" was misleading; the revision will name it separately.
The MMU row of Table 1 is wrong. The reported means and gaps do not match our logs, and we found no run that produced them. The logged ten-trial values are:
| Random deletion | Reported (error) | Logged forget accuracy | Logged error | Gap to Retrain | D_r | Test (gap) |
|---|---|---|---|---|---|---|
| 10% | 4.19 ± 0.00 | 100.00 ± 0.00 | 0.00 ± 0.00 | 5.21 | 100.00 ± 0.00 | 95.02 ± 0.19 (0.58) |
| 50% | 4.39 ± 0.53 | 99.61 ± 0.53 | 0.39 ± 0.53 | 7.26 | 99.82 ± 0.31 | 93.81 ± 0.81 (1.64) |
Why MMU stays at 100% forget accuracy, and why the standard deviation is zero. Both MMU variants leave the predictions on the forgotten examples unchanged. The source model fits its training set perfectly. Randomly deleted examples follow the same distribution as retained ones, and MMU's preservation term keeps them at the teacher's prediction. At 10% forgetting this happened in all ten trials, so the forget error is exactly 0.00 each time; the zero standard deviation is real. GA, BE and BS behave the same way, which is why they also show 0.00 ± 0.00. High forget accuracy is not by itself a failure in random deletion, because Retrain still classifies 94.79% of the forgotten examples correctly. But MMU's forget accuracy stays 5.21 points above Retrain's, which is the same as leaving the model untouched.
Consequence. With the corrected values, MMU has no advantage in random forgetting. Its gaps (5.21 and 7.26) are among the largest in Table 1. ℓ1-sparse comes closest to Retrain at both ratios (gaps 3.25 and 0.08), followed by SalUn at 10% (4.59) and RL at 50% (2.00). We will correct Table 1, remove the "MMU best (4x)" summary and the related claims, and state that MMU is not effective for random instance deletion.
Q2
We performed the requested controlled comparison with identical data, training schedule, hinge objective, and 96-configuration search budget.
Nesting reduces class-deletion gaps from 49.9→0.1, 30.7→0.0, and 67.3→0.0 in the three configurations where full width fails. It also improves all four subclass configurations by 2.7–9.7 points, with retain-accuracy differences within ±1.2 points.
Margin-sensitivity and hyperparameter-grid analyses further confirm that these improvements are not confined to a single selected configuration. This directly isolates the effect of nested supervision under the bounded objective.
Q3
Yes. We trained linear probes on frozen width-m representations using held-out non-member data, then evaluated them on forgotten examples against the corresponding Retrain probes.
For RTI/ResNet-18 class deletion:
| Method | Full-width probe excess over Retrain |
|---|---|
| Original | 40.4 pts |
| MMU | 40.6 pts |
| SCRUB (96) | 39.9 pts |
| Bad Teacher | 41.2 pts |
Deleted-class information remains linearly recoverable. We therefore agree that the evidence supports forgetting under trained predictive readouts, not complete removal of recoverable information from the representation.
Revisions. We will adopt Eq. 6 with independent per-width heads, add controlled nesting and head ablations, report matched-budget SCRUB, include fresh probes, correct the random-forgetting inconsistencies, and narrow the unsupported claims.
We thank you again for your feedback. We believe these experiments directly address the reviewer's questions and provide stronger evidence for MMU's nested optimization. We would be grateful if the reviewer would reconsider their score.
Thank you for the additional experiments and clarifications. The matched single-width ablation provides useful evidence that nested supervision improves class-deletion performance, and I appreciate the authors' efforts to correct the experimental results and narrow their claims.
However, the new linear-probing results show that forgotten-class information remains highly recoverable from MMU's frozen representations, with performance nearly identical to the original model. This leaves my main concern about representation-level forgetting unresolved. Moreover, the limitations in subclass, instance, and random deletion remain.
Overall, the rebuttal improves the empirical support for the method but does not sufficiently address my fundamental concerns about its core motivation and contribution.
Follow-up: Representation-Level Forgetting
We conducted an additional experiment to determine whether MMU can reduce recoverable forgotten-class information, rather than only changing predictions under its trained readouts.
Method. We augment MMU (Eq. 6) with a probe-adversarial objective. At each nested width, a linear probe is periodically refitted using data available to the unlearner ( and 10% of ). The encoder is penalized when the probe assigns the deleted class a probability above a threshold . Retrain is not used in this loss. We select and using validation data.
We compare three variants: the original MMU, MMU with the adversary applied only at full width, and MMU with the adversary applied at every width. We evaluate frozen representations using fresh linear and two-hidden-layer MLP probes, fitted on validation data and evaluated on deleted training examples and deleted-class test images. Experiments cover four class-deletion settings and three seeds.
Probe excess over Retrain on deleted examples (accuracy difference in percentage points, averaged across widths; linear / MLP; lower is better):
| Setting | MMU | Adv. full width | Adv. every width |
|---|---|---|---|
| RTI · ResNet-18 | 48.3 / 45.4 | 41.6 / 37.6 | 39.5 / 35.6 |
| RTI · CNN | 48.7 / 42.9 | 35.1 / 30.6 | 32.9 / 29.4 |
| CIFAR-100 · ResNet-18 | 40.6 / 38.7 | 34.9 / 32.3 | 32.1 / 27.7 |
| CIFAR-100 · CNN | 33.1 / 32.2 | 26.2 / 23.7 | 24.5 / 22.4 |
1. Representation-level recoverability decreases, but remains substantial.
Compared with the original MMU, the per-width adversary reduces probe excess in all 12 seed–setting pairs, for both linear and MLP probes. Average reductions are 10.4 and 11.0 points on deleted examples, respectively. The corresponding reductions on deleted-class test images are 8.6 and 7.6 points.
The improvement extends beyond linear probing, but does not establish information removal. Probe excess remains substantial relative to Retrain, and stronger probes could recover additional information.
2. Nested adversarial supervision provides a small additional benefit.
Applying the adversary at every width outperforms applying it only at full width in 11/12 paired comparisons on deleted examples, for both probe families. Average improvements are approximately 2.2–2.3 points, increasing to 3.6–4.1 points at the narrowest width.
This provides evidence that per-width supervision can improve representation-level probe resistance. However, the improvement is small relative to seed variability, and we do not claim a statistically established advantage.
3. Most of the reduction comes from the adversarial objective itself.
On CIFAR-100 CNN, a full-width hinge model equipped with the same adversary achieves nearly identical probe excess to MMU-adv (24.4 / 22.3 versus 24.5 / 22.4). However, its deployed class-forgetting gap is 63.7 points, compared with 0.0 for MMU-adv.
Thus, the adversarial objective accounts for much of the reduction in recoverability, while the nested formulation retains its advantage in achieving class forgetting under the deployed readouts.
4. Utility and limitations.
MMU-adv maintains a 0.0-point deployed class-forgetting gap across all four settings. Relative to Retrain, test accuracy decreases by 1.9 and 2.5 points on RTI ResNet-18 and CNN, respectively, and by 0.2 and 0.4 points on CIFAR-100. The RTI CNN result exceeds our 2-point utility tolerance on the test set.
These are exploratory three-seed experiments using a limited eight-configuration adversarial grid. We have not established complete representation-level removal. The earlier limitations concerning subclass, instance, and random deletion also remain; these experiments do not resolve them.
Implications for our contribution.
We agree with the reviewer that the original MMU objective should not be presented as removing forgotten information from the representation. Our evidence now supports a more precise distinction:
- Nested optimization: The matched single-width ablation establishes that nesting improves the effectiveness of the bounded forgetting objective under deployed predictive readouts.
- Representation-level probing: The original MMU leaves substantial forgotten-class information recoverable, despite successful deployed class forgetting.
- Adversarial extension: Explicit per-width adversarial supervision consistently reduces recoverability under the evaluated probes, but the remaining excess demonstrates incomplete removal.
We will incorporate these findings and revise the motivation and claims accordingly, distinguishing deployed predictive forgetting, membership privacy, and representation-level recoverability. We appreciate the reviewer's insistence on this distinction. The additional experiments do not fully resolve the concern, but they quantify the remaining limitation and clarify what the nested formulation contributes.
Response 1/2
We thank the reviewer for identifying the missing controls. We conducted the requested matched single-width hinge ablation and frozen-representation probing, together with head-sharing, margin-sensitivity, and robustness experiments. Gap = |forget accuracy − Retrain forget accuracy|.
W1: Does nesting itself improve unlearning? We held the hinge objective, data, training schedule, and 96-configuration grid fixed; only the supervised widths differ.
Table 1. Gap to Retrain (percentage points, test split; lower is better).
Nesting reduces the class-deletion gap by 30.7–67.3 points in the three configurations where full width fails and improves all four subclass configurations by 2.7–9.7 points. Retain-accuracy changes remain within ±1.2 points across 12 settings. Instance deletion shows no consistent improvement.
Robustness. For margins δ ∈ {16, 64, 256, 1024}, nesting reaches zero validation class-deletion gap at δ ≥ 256 in all four configurations, versus one for full width. Hyperparameter-grid success rates (class gap ≤ 2 pts, utility within 2 pts) are 28/27/9/5% for nesting versus 4/0/0/0% for full width (RTI ResNet-18/CNN, CIFAR-100 ResNet-18/CNN).
The effect persists on Matryoshka-trained sources whose prefixes receive explicit classification supervision: the three nontrivial class-deletion gaps change from 58.7→0.0, 41.3→0.0, and 67.7→6.3.
Can the auxiliary heads absorb forgetting? We compared independent per-width heads against a single tied head under Eq. 6 on Matryoshka-trained sources.
Table 2. Class-deletion gap to Retrain (percentage points).
These shared-head results are for the tied-head hinge control, not the separately evaluated MMU-2 variant.
Fresh probes. Linear probes trained on held-out non-member data recover forgotten-class information from frozen features. On RTI/ResNet-18, full-width probe-accuracy excess over Retrain is 40.6 pts for MMU, 39.9 for SCRUB, and 40.4 for Original.
W2: Which claims are supported? We agree that the statement of having "no failure mode" exceeds the evidence. We will remove it and distinguish predictive agreement with Retrain, membership privacy, and feature-level information removal.
Class deletion. The nested-hinge formulation attains a 0.0–0.1-point gap to Retrain across RTI and CIFAR-100 with both CNN and ResNet-18, maintaining competitive retained utility. The controlled full-width hinge fails substantially in three configurations.
RTI subclass deletion. Retrain is the appropriate reference, not zero accuracy: a model that never saw a deleted subclass can still recognize it through features learned from retained sibling subclasses.
Table 3. RTI subclass forget accuracy (%) and gap to Retrain (pts).
Gaps are computed per seed before averaging. MMU comes closest to Retrain in both settings, whereas Bad Teacher substantially over-forgets. MMU's membership-inference accuracy is also near Retrain: approximately 50.6–53.4%, versus 49.2–51.1% for Retrain.
CIFAR-100 subclass deletion. The nested hinge still under-forgets, with gaps of approximately 39–43 points and substantial membership leakage (the submitted U-LiRA AUC is near 96%).
Instance deletion. Membership-inference accuracy remains approximately 60–68% for MMU, versus roughly 50% for Retrain. Several baselines also retain membership signals, and nesting provides no consistent improvement for individual-record removal.
Sequential deletion. In the generation experiment, the first removed condition reappears in 3/16 samples after sequential deletion. We agree that this constitutes incomplete removal and will report it as a limitation.
Revised claims. MMU provides strong predictive class-deletion results, improved RTI subclass agreement with Retrain, and a controlled benefit from nested supervision. It does not establish universal success across deletion granularities, membership privacy, or resistance to fresh feature probes.