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Under review as a conference paper at ICLR 2027

Parameter-Efficien Data-Free Untraining in Test-Time Adaptation

Abstract

In real-world applications, online adaptation of a source-trained model to contin- ually changing target domains is becoming increasingly common and important. This process is known as test-time adaptation (TTA) and is used in applications such as driving and aerial perception. This inevitably raises data-related risks: continually arriving data may contain corrupted samples or contaminated informa- tion, which can impair model reliability, as well as sensitive information, which can raise privacy risks. This creates an urgent need to remove the knowledge of problematic samples while preserving useful updates and source knowledge during online deployment, without access to historical raw inputs. To the best of our knowledge, existing machine unlearning methods do not address this problem. We first distinguish the two notions of untraining and unlearning, and address this need by proposing a novel untraining setting: Data-Free Untraining in TTA. For this setting, we propose a batch-level untraining method based on a parameter-efficient TTA structure that combines model-state storage, contrastive reconstruction, and selective untraining. We represent the unavailable requested data by reconstructed tokens and remove their knowledge via selective untraining while preserving the retained adaptation and source knowledge. We evaluate our method with differ- ent TTA methods on datasets commonly used in TTA. Our method outperforms all adapted MU baselines and maintains stable performance across successive untraining requests.

Primary area:
transfer learning, meta learning, and lifelong learning
Keywords:
test-time adaptation, continual test-time adaptation, machine untraining, machine unlearning, data-free learning, parameter-efficient adaptation, feature reconstruction, continual learning

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_tUwCOpenReview ↗
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3(+1)
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2
Informativeness
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Paper summary

This paper proposes a setting called Data-Free Untraining in TTA, which aims to retrospectively remove the influence of sensitive or corrupted data contained in specific past batches from a model undergoing continual TTA. A request specifies only batch indices, without access to the original raw inputs, labels, or class information, and the goal is to approximate the Retain-Only Replay model, obtained by re-running TTA from the source model while excluding the requested batches. Following the distinction made by Triantafillou et al. (2026), the authors differentiate untraining, which reverses the influence of a specific set of samples, from unlearning, which removes a class or concept itself, and state that their setting belongs to the former. Built on parameter-efficient TTA methods such as TENT and ViDA, the proposed approach stores per-batch model states and predicted class sets, keeping recent records intact and compressing older ones into averages, and accumulates class-wise Fisher importance scores. When a request arrives, the method reconstructs feature tokens whose class responses are amplified in the stored state of the requested batches relative to a reference state taken before the earliest requested batch, and then optimizes a forget loss that reduces the feature–classifier alignment of these tokens, combined with Fisher-weighted EWC, a feature gradient projection that removes the classifier direction, and an optional retain loss. Experiments with ViT-B/16 on ImageNet-C and CIFAR-100-C streams, into which batches containing FAIR1M aerial images or synthetically perturbed images are injected, report that the proposed method achieves a smaller confidence gap to Replay than existing MU methods adapted to the PEFT parameter space, better preserves same-class accuracy, and remains stable across successive requests.

Critical strengths

The paper raises a novel and practical problem in TTA. To our knowledge, it is the first to formalize the scenario in which the influence of past batches must be retroactively removed from a model under continual TTA. It clearly defines the setup, including batch-level requests aligned with the TTA update unit, a well-defined Retain-Only Replay oracle, and successive request scenarios. In particular, by distinguishing untraining from unlearning, it explicitly establishes an evaluation perspective that requires removing the influence of sensitive samples while preserving recognition of the corresponding classes.

The component design and supplementary analyses are thorough. The idea of reconstructing tokens that capture the traces of the requested batches, by contrasting the stored state of those batches with a reference state that has not seen them, is intuitive. Table 7 shows that using the reconstructed tokens yields results nearly identical to using the actual images (Score 89.85 vs. 90.00), supporting their suitability as substitute inputs. Furthermore, the appendix provides detailed reports on the MIA evaluation protocol, sample-level agreement with Replay, runtime, and memory usage.

Critical weaknesses

The advantage over simple control baselines is not convincingly demonstrated. In Table 2, Clean Rollback and Source Reset achieve Scores of 88.50 and 88.43 on ImageNet-C, only modestly below the proposed method (89.85), and 87.98 and 87.43 on CIFAR-100-C, higher than the proposed method (85.05). On CIFAR-100-C, their CF-Gap (0.000 and 0.001) is also clearly lower than that of the proposed method (0.053), and on ImageNet-C they are comparable. In the sequential setting of Table 3, both controls also show a lower CF-Gap than the proposed method at the second request. However, since the bold entries in the tables mark only the best among the adapted MU methods, this is not immediately apparent. This issue is also related to the evaluation design. CF-Gap and MIA-Gap naturally become small simply by reverting to a state that has never seen the requested batches, and since the ImageNet-C stream uses only mild corruptions at severity 1, the adaptation gain from TTA is inherently small. The number of retained batches between the last requested batch and the arrival of the request is also not specified. Moreover, the proposed method already stores the reference state, which is essentially the state that Clean Rollback restores, so rollback is available at no additional cost. The paper reports that the proposed method retains a few more percentage points of SC-Acc and R-Acc than Clean Rollback. However, rollback achieves a lower MIA-Gap on both datasets and a lower CF-Gap and a higher Score on CIFAR-100-C. The paper also does not examine conditions under which rollback should fail, such as many retained batches after the requested ones or stronger corruptions. It therefore remains unclear when the more complex reconstruction and optimization procedure is preferable to simple rollback.

There are inconsistencies between the claims and the actual results regarding storage cost, privacy, and the choice of baselines. Although the paper states that storage does not grow with the stream length when R, L, and H are fixed, Table C.3 shows the persistent state growing from 12.11 GiB to 18.80 GiB, which is dozens of times larger than the ViT-B/16 model itself and is difficult to reconcile with the claims of parameter or storage efficiency. In addition, the fact that tokens carrying the class responses of a requested batch can be reconstructed from its stored state implies that the stored state itself encodes information about the sensitive data, yet the paper describes no procedure for deleting the exact records of the requested batches or their accumulated contributions to the Fisher bank after untraining. Regarding the baselines, the existing MU methods operate only on proxies without stored states, whereas the proposed method relies on per-batch state records, creating a substantial gap in available information. Furthermore, applying the existing methods in a class-conditional manner is likely to degrade same-class accuracy by design. SSD-PEFT produces results identical to No-Untrain on all ImageNet-C metrics, which raises doubts about whether it was applied correctly. Meanwhile, the paper does not compare against Amnesiac ML (Graves et al., 2021), which subtracts the updates of the requested batches and is the most natural baseline when per-batch states are stored.

Questions for authors
  • In each experiment, how many retained batches lie between the last requested batch and the arrival of the request? Can you show that the proposed method clearly outperforms Clean Rollback as this gap and the corruption severity increase, that is, in situations where rollback discards a substantial amount of subsequent adaptation? If not, what is the justification for using this method instead of rollback, given that reference state is already stored?

  • Most SC-Acc and R-Acc values in Tables 2, 3, 5, and C.1 correspond to multiples of 1/16, suggesting that accuracy was measured on about 16 images. Could you provide the actual number of evaluation images for each metric and the per-seed raw values?

2 comments
AuthorsOpenReview ↗

Response to Reviewer tUwC (Part3)

We have completed the experiments described in our previous response and revised the manuscript accordingly.

We first revised the calculation of the overall Score, as updated in the experimental section and in Appendix D.4. The original Score used CF-Gap, which compares the mean requested-image confidence of the evaluated model with Retain-Only Replay. Because it reduces each model’s output to a single averaged confidence value, different changes across classes or samples can cancel one another.

We therefore replace CF-Gap in the Score with JS mean. For every requested image, JS mean computes the Jensen-Shannon divergence between the full softmax probability distributions of the evaluated model and matched Retain-Only Replay, and then averages it across images. A lower value indicates that the corrected model more closely reproduces the oracle model’s complete output behavior, rather than merely matching one confidence statistic. Tables 2, 4, and 5 report results using this revised Score.

Q1: The proposed method does not convincingly outperform Source Reset and Clean Rollback, particularly under mild corruption and short request delays.

A1: We redesigned the ImageNet-C experiment to test the intended correction-retention trade-off more directly. The requested interval uses severity-1 corruptions. During the delay between the end of that interval and the arrival of the untraining request, online adaptation continues on previously unseen severity-3 domains selected from snow, fog, frost, brightness, and contrast.

Table 2 shows that Retain-Only Replay and Ours both obtain an R-Acc of 0.641, whereas Source Reset and Clean Rollback obtain 0.555 and 0.539. Thus, reset and rollback lose 8.6 and 10.2 percentage points of retained-stream accuracy, respectively. Ours also achieves an SC-Acc of 0.867 and a Score of 84.19, compared with 0.782/82.16 for reset and 0.782/81.97 for rollback.

For comparison, in the original experiment without a deliberately inserted domain transition, reset and rollback trailed Replay in R-Acc by only 6.7 and 3.5 percentage points. We moved that original experiment to Appendix C.4, Table C.8. These results support our central claim that selective correction can remove the requested influence while preserving useful adaptation acquired afterward.

We further define delay as the number of retained online-adaptation batches processed between the end of the requested interval and the arrival of the untraining request. Table 5 evaluates delays of 30, 50, and 70:

  • At delay 30, Replay and Ours both obtain 0.602 R-Acc, whereas reset and rollback obtain 0.539 and 0.555. Their deficits are therefore 6.3 and 4.7 percentage points.
  • At delay 50, Replay and Ours both obtain 0.641, whereas reset and rollback obtain 0.555 and 0.539. Their deficits increase to 8.6 and 10.2 percentage points.
  • At delay 70, Replay obtains 0.711 and Ours obtains 0.664, whereas reset and rollback obtain only 0.512 and 0.555. Their deficits further increase to 19.9 and 15.6 percentage points. As delay increases, the model processes more batches from the inserted domains and accumulates more useful adaptation. Source Reset and Clean Rollback restore earlier model states, so they discard an increasingly large fraction of this adaptation. The growing R-Acc deficits therefore directly reveal their limitation under longer request delays.

Ours preserves substantially more of the intervening adaptation, but it is not unaffected by increasing delay. Its Score decreases from 84.75 at delay 30 to 84.19 at delay 50 and 84.14 at delay 70. At delay 70, its R-Acc also falls 4.7 percentage points below Replay, whereas it matches Replay at delays 30 and 50. Nevertheless, its R-Acc of 0.664 remains clearly higher than reset at 0.512 and rollback at 0.555. The results therefore support a qualified conclusion that our method better preserves post-request domain adaptation than restoring an earlier state, although its correction accuracy also gradually degrades under sufficiently long delays.

Q2: Persistent storage grows from 12.11 GiB to 18.80 GiB, which appears inconsistent with the storage-efficiency claim.

A2: We extended the stream to 5,000 batches and report the measurements in Appendix C.3, Table C.7. With 50 exact records and 10 archives per rank, total history storage is 14.56 GiB at batch 100, 18.44 GiB at batches 1,000 and 2,000, and 18.56 GiB from batch 3,000 through batch 5,000. The Fisher class union also remains at 936 classes from batch 3,000 onward.

Thus, storage grows during early class coverage and then reaches a measured plateau. We have corrected the manuscript claim from “does not grow with stream length” to the more precise statement that storage is bounded by the fixed history budget and finite class-wise Fisher bank. We also explicitly acknowledge that the current 18.56 GiB bound remains large and is not yet optimized for edge deployment.

AuthorsOpenReview ↗

Response to Reviewer tUwC (Part4)

Q3: Stored states and the Fisher bank may retain information about the requested data, but the paper does not provide a complete procedure for deleting these auxiliary traces.

A3: We have clarified the scope of the current untraining guarantee in Appendix C.3. The current method corrects the active model’s behavior on the requested data but does not guarantee complete removal of every trace from auxiliary historical states and Fisher statistics.

We also added the auxiliary-state cleanup procedure to Appendix B. Exact state records associated with the requested batches are deleted, archived records overlapping the requested interval are invalidated, and Fisher entries associated with the affected classes can be reset. This conservative cleanup reduces residual auxiliary traces, but resetting class-level Fisher entries may also discard useful retained information. We therefore identify complete and selective auxiliary-state erasure as a limitation of the current framework rather than claiming that active-model correction alone provides complete system-level deletion.

Q4: The adapted machine-unlearning baselines have less historical information, SSD-PEFT matches No-Untrain, and Amnesiac ML is missing.

A4: Tables 2 and 4 now report paired no-history and matched-history versions of SCADA-UL, DELETE, SSD, SalUn, and SCRUB. The history-enabled rows use the same stored-state reconstruction as Ours.

The results show that providing history does enable these baselines to erase the response associated with the target category more aggressively. For example, at the first request, history reduces SCADA’s F-Conf from 0.481 to 0.091 and its SC-Acc from 0.391 to 0.109. For SCRUB, F-Conf decreases from 0.560 to 0.004. These large reductions indicate that the reconstructed historical information successfully identifies the target influence and allows the original class-directed objectives to suppress it more completely.

However, stronger target-category suppression is not necessarily equivalent to accurate batch-specific untraining. Retain-Only Replay still produces a nonzero response for legitimate retained examples from the same class. History-enabled SCADA therefore increases JS mean from 0.1031 to 0.3519 and reduces Score from 60.59 to 41.65. History-enabled SCRUB similarly increases JS mean from 0.1125 to 0.5401. These results indicate that the baselines often remove not only the requested-batch influence but also useful responses to retained examples from the same class.

The comparison therefore shows that access to historical information improves the ability of these methods to locate and suppress the target category, but their class-level objectives can produce over-forgetting. Effective batch-specific untraining requires both informative historical inputs and a sufficiently selective correction objective. The complete comparison and discussion are provided in Tables 2 and 4 and Appendix C.1.

We also added an Amnesiac-style baseline that subtracts the stored EMA parameter change accumulated over the requested interval. At the first request, it obtains JS mean 0.0100, R-Acc 0.617, and Score 81.97, compared with 0.0080, 0.641, and 84.19 for Ours. Across three requests, its Scores are 81.97, 78.68, and 73.67, whereas Ours obtains 84.19, 84.22, and 79.10. These results are reported in Tables 2 and 4.

Q5: How many evaluation images are used for SC-Acc and R-Acc?

A5: Appendix D.4 now specifies the evaluation-set sizes. Each request uses 128 same-class retained images for SC-Acc and 128 retained-stream images for R-Acc.

Reviewer_ieXrOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary
  • This paper proposes a new problem called Data-Free Untraining in Continual Test-Time Adaptation (TTA), where the goal is to remove the influence of specific past batches without accessing the original data.

  • The proposed method stores model states during parameter-efficient TTA and reconstructs feature tokens using the logit differences between past model states and a reference state. These tokens are then used for selective untraining with a forget loss, Fisher-weighted regularization, and gradient projection.

  • Experiments on ImageNet-C and CIFAR-100-C with TENT and ViDA show better results than several adapted machine unlearning baselines.

Critical strengths
  • Meaningful new problem setting

Removing the influence of previously processed batches without storing raw data is a meaningful problem in online TTA. I think this setting has practical motivation, especially when the model continuously adapts to incoming data. The paper also makes a clear distinction between untraining and unlearning, and introduces Retain-Only Replay as an oracle for evaluation. These are good points of the paper.

  • Well-organized method and experiments

The combination of model-state-based reconstruction and selective untraining is interesting. The authors evaluate the method with different TTA methods and datasets, and provide ablation studies and sequential untraining experiments. In particular, Table 7 shows that reconstructed tokens give similar results to using real images for untraining, which is a useful result.

Critical weaknesses
  • Limited validation of batch-specific influence removal

One important assumption of this paper is that feature tokens reconstructed from the logit differences between past model states and a reference state can represent the influence of the requested batches. However, it is not sufficiently clear how accurately these tokens capture the influence specific to those batches.

Also, the proposed forget loss is a surrogate objective that reduces the alignment between features and classifier weights. It is not clear whether optimizing this loss consistently produces a model close to Retain-Only Replay under different conditions.

The comparison between reconstructed tokens and real images also provides sample-level Replay agreement results. However, these analyses are limited to the first untraining request on ImageNet-C. I think similar evaluations on other requests and datasets would be helpful to support the main claim.

  • Baseline comparison and practical efficiency

The authors adapt several existing MU methods to the proposed setting, which is reasonable. However, the adapted MU baselines mainly use class-conditioned forget proxies, while the proposed method uses model-state history associated with the requested batches. Due to this difference, it is difficult to tell how much improvement comes from the proposed untraining method itself.

In particular, on CIFAR-100-C, the proposed method achieves higher same-class and retained-stream accuracy than Source Reset and Clean Rollback, but has larger CF-Gap and MIA-Gap, resulting in a lower overall score. I think a comparison with simpler state-based correction methods using the same model-state history would be useful.

There is also some concern about practical efficiency. The persistent storage reaches 18.80 GiB, and each untraining request requires considerable computation time. Although the method uses parameter-efficient TTA, it is not clear how efficient the whole framework would be in an actual online deployment. Some discussion on the expected request frequency and acceptable processing delay would be helpful.

  • Minor writing issue : missing Period (.) in Line 39-40.
Questions for authors

N/A

2 comments
AuthorsOpenReview ↗

Response to Reviewer ieXr (Part3)

We have completed the experiments described in our previous response and revised the manuscript accordingly.

We first revised the calculation of the overall Score, as updated in the experimental section and in Appendix D.4. The original Score used CF-Gap, which compares the mean requested-image confidence of the evaluated model with Retain-Only Replay. Because it reduces each model’s output to a single averaged confidence value, different changes across classes or samples can cancel one another.

For every requested image, JS mean computes the Jensen-Shannon divergence between the full softmax probability distributions of the evaluated model and matched Retain-Only Replay, and then averages it across images. A lower value indicates that the corrected model more closely reproduces the oracle model’s complete output behavior, rather than merely matching one confidence statistic.

Q1: It is unclear how accurately the reconstructed tokens capture the influence specific to the requested batches, and the existing validation is limited to the first ImageNet-C request.

A1: We extended the reconstructed-token versus real-image comparison from the first request to all three requests. The results are reported in Table 9. Under the same correction procedure, update budget, and loss weights, reconstructed tokens and real requested images obtain JS means of 0.0080/0.0060, 0.0060/0.0030, and 0.0330/0.0450 across the three requests. Their corresponding Scores are 84.19/80.30, 84.22/85.37, and 79.10/81.62.

These results show that reconstructed tokens and real requested images do not produce identical models, but both consistently move the corrected model close to Retain-Only Replay across successive requests. Reconstructed tokens perform slightly better on some metrics and slightly worse on others, which is expected because they are feature-space correction proxies rather than reconstructions of the original images.

We further report sample-level output-distribution analysis in Appendix C.2, Table C.5. Relative to No-Untrain, Ours reduces JS mean from 0.1214 to 0.0721, the 95th-percentile JS divergence from 0.3626 to 0.1449, and confidence MAE from 0.2751 to 0.1016. These results provide additional evidence that reconstructed-token correction moves the requested-image outputs toward the behavior of the oracle model.

Q2: The forget loss is a surrogate objective, and it is unclear whether optimizing it consistently produces a model close to Retain-Only Replay.

A2: Table 4 now evaluates the method over three successive untraining requests using matched Retain-Only Replay as the reference. Ours obtains JS means of 0.0080, 0.0060, and 0.0330 across the three requests, compared with 0 for Replay. Its corresponding Scores are 84.19, 84.22, and 79.10, whereas Replay obtains 87.90, 89.05, and 86.15.

The low JS mean at all three requests shows that the corrected output distributions remain close to Replay. However, the larger JS mean and Score gap at the third request also show that the approximation becomes less accurate as the number of accumulated requests and subsequent updates increases.

Q3: The adapted machine-unlearning baselines use class-conditioned proxies, whereas the proposed method has access to model-state history.

A3: Tables 2 and 4 now report paired no-history and matched-history versions of SCADA-UL, DELETE, SSD, SalUn, and SCRUB. The history-enabled rows use the same stored-state reconstruction as Ours.

The results show that providing history does enable these baselines to erase the response associated with the target category more aggressively. For example, at the first request, history reduces SCADA’s F-Conf from 0.481 to 0.091 and its SC-Acc from 0.391 to 0.109. For SCRUB, F-Conf decreases from 0.560 to 0.004. These large reductions indicate that the reconstructed historical information successfully identifies the target influence and allows the original class-directed objectives to suppress it more completely.

However, stronger target-category suppression is not necessarily equivalent to accurate batch-specific untraining. Retain-Only Replay still produces a nonzero response for legitimate retained examples from the same class. History-enabled SCADA therefore increases JS mean from 0.1031 to 0.3519 and reduces Score from 60.59 to 41.65. History-enabled SCRUB similarly increases JS mean from 0.1125 to 0.5401. These results indicate that the baselines often remove not only the requested-batch influence but also useful responses to retained examples from the same class.

The comparison therefore shows that access to historical information improves the ability of these methods to locate and suppress the target category, but their class-level objectives can produce over-forgetting. Effective batch-specific untraining requires both informative historical inputs and a sufficiently selective correction objective. The complete comparison and discussion are provided in Tables 2 and 4 and Appendix C.1.

AuthorsOpenReview ↗

Response to Reviewer ieXr (Part4)

Q4: The comparison with simple controls is insufficient, and a natural state-subtraction baseline is missing.

A4: We added an Amnesiac-style baseline that subtracts the stored EMA parameter change accumulated over the requested interval. At the first request, it obtains JS mean 0.0100, R-Acc 0.617, and Score 81.97, compared with 0.0080, 0.641, and 84.19 for Ours. Across three requests, its Scores are 81.97, 78.68, and 73.67, whereas Ours obtains 84.19, 84.22, and 79.10. These results are reported in Tables 2 and 4.

We also redesigned the ImageNet-C experiment to test the correction-retention trade-off more directly. The requested interval uses severity-1 corruptions, while online adaptation during the delay continues on previously unseen severity-3 domains. At delay 50, Retain-Only Replay and Ours both obtain an R-Acc of 0.641, whereas Source Reset and Clean Rollback obtain 0.555 and 0.539.

For comparison, in the original experiment without a deliberately inserted domain transition, reset and rollback trailed Replay by only 6.7 and 3.5 percentage points. We moved that original experiment to Appendix C.4, Table C.8. The revised setting shows that simple restoration controls discard useful adaptation acquired after the requested interval.

On CIFAR-100-C, Ours obtains higher SC-Acc and R-Acc than rollback, 0.782/0.781 versus 0.768/0.751, but larger CF and MIA gaps. We now present this explicitly as a limitation rather than claiming consistent superiority on every dataset.

Q5: The persistent storage and computation costs raise concerns about practical efficiency.

A5: We extended the stream to 5,000 batches and report the measurements in Appendix C.3, Table C.7. With 50 exact records and 10 archives per rank, total history storage is 14.56 GiB at batch 100, 18.44 GiB at batches 1,000 and 2,000, and 18.56 GiB from batch 3,000 through batch 5,000. The Fisher class union also remains at 936 classes from batch 3,000 onward.

Thus, storage grows during early class coverage and then reaches a measured plateau. We have corrected the manuscript claim from “does not grow with stream length” to the more precise statement that storage is bounded by the fixed history budget and finite class-wise Fisher bank.

Reviewer_n7ALOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
1
Soundness
2(+1)
Read review
Paper summary

The paper solves data-free untraining in continual TTA. A request names the past target batches whose influence needs to be removed. No raw data is available in this setting and the reference in Retain-only Replay oracle. The method builds on parameter-efficient TTA (LayerNorm parameters or ViDA adapters). It keeps a bounded history of model states and predicted class sets, plus a per-class bank of squared gradient scores. After receiving a request it reconstructs feature tokens foreach stored record and class using a margin loss and the logit gpa between the stored state and reference state, pushes the adapted features of these tokens away from classifier and protects other knowledge with importance weighted EWC.

Critical strengths
  1. This is new well-posed problem with high practicality with the paper separating untraining and unlearning while giving a useful and clear problem definition. Removing specific data from a model which keeps adapting after deployment is a real need.

  2. As shown by table 7, reconstructed tokens seems to be working well as a stand in for missing data which is a useful check that the data-free part of the pipeline works.

Critical weaknesses
  1. The method doesnt clearly beat simple used of history it already stores and is very expensive thus being impractical
  • The paper's own controls beat the method as seen with source reset and clean rollback on Cifar-100-C.
  • A natural baseline is missing from the analysis, since the method stores the model state after every batch, it allows a simple data-free baseline which is to take the current state and subtract the change accumulated over the requested batches.
  • The paper doesnt report how many batches separate the requested ones from the request which decides the distance between rollback and replay
  • The adapted unlearning baselines are very weak as references. SSD-PEFT seems to reproduce the no-untrain numbers rendering the comparison useless. DELETE and SalUn-PEFT push the SC accuracy on cifar to near zero but dont say anything about untraining.
  • The paper claims it to be storage-efficient and that the storage doesnt grow with stream length but the Appendix C.3 shows that the state storage grows from 12.1 to 18.8 GiB mostly from the per-class importance bank. This is hard to match with the claims of edge deployment in driving and aerial systems
  1. The evaluation is too small to resolve the reported differences and the reported variances dont look consistent.
  • Source Reset throws away all adaptation and still scores 88.43 and 87.43, because its confidence and membership gaps to replay are near zero. CF-Gap compares only a single average confidence, which simple shrinkage can match.
  • The tuning protocol is unclear. Loss weights are fixed “at first-request values”. The first request is also where the method reaches its CF-Gap of .003. If the weights were tuned on the evaluation request itself, the headline result is optimistic.
Questions for authors
  • How many images are used for SC-Acc and R-Acc in each seed on ImageNet-C and how were the stds in Tables 2 and C.1 computed?
  • How many batches separate the end of the requested interval from the arrival of the request in each experiment?
  • How does the method compare with subtracting the stored state change over the requested interval? How does it compare with rolling back and then reapplying the stored state changes from after the interval?
  • Can you reconcile the claim that storage does not grow with stream length with Appendix C.3?

I would suggest the authors to evlaute on larger held-out sets per metric and also report all the results against the reset and rollback controls and baselines. The authors would also need to justify the score weighting since source reset scores at the near top.

Update: Based on the clarifications and updates from authors I have increased my rating

Comments on the paper

2 comments
AuthorsOpenReview ↗

Response to Reviewer n7AL

Thank you for waiting for the additional experiments. We have completed the experiments described in our previous response and revised the manuscript accordingly. Thanks for the constructive suggestions.

We first revised the calculation of the overall Score, as updated in the experimental section and in Appendix D.4. The original Score used CF-Gap, which compares the mean requested-image confidence of the evaluated model with Retain-Only Replay. Because it reduces each model’s output to a single averaged confidence value, different changes across classes or samples can cancel one another.

We therefore replace CF-Gap in the Score with JS mean. For every requested image, JS mean computes the Jensen-Shannon divergence between the full softmax probability distributions of the evaluated model and matched Retain-Only Replay, and then averages it across images. A lower value indicates that the corrected model more closely reproduces the oracle model’s complete output behavior, rather than merely matching one confidence statistic.Tables 2, 4, and 5 report results using this revised Score.

Q1: The proposed method does not clearly outperform Source Reset and Clean Rollback.

A1: We redesigned the ImageNet-C experiment to test the intended correction-retention trade-off more directly. The requested interval uses severity-1 corruptions. During the delay between the end of that interval and the arrival of the untraining request, online adaptation continues on previously unseen severity-3 domains selected from snow, fog, frost, brightness, and contrast.

Table 2 shows that Retain-Only Replay and Ours both obtain an R-Acc of 0.641, whereas Source Reset and Clean Rollback obtain 0.555 and 0.539. Thus, reset and rollback lose 8.6 and 10.2 percentage points of retained-stream accuracy, respectively. Ours also achieves an SC-Acc of 0.867 and a Score of 84.19, compared with 0.782/82.16 for reset and 0.782/81.97 for rollback.

For comparison, in the original experiment without a deliberately inserted domain transition, reset and rollback trailed Replay in R-Acc by only 6.7 and 3.5 percentage points. We moved that original experiment to Appendix C.4, Table C.8. These results support our central claim that selective correction can remove the requested influence while preserving useful adaptation acquired afterward.

Q2: A natural state-subtraction baseline is missing.

A2: We added an Amnesiac-style baseline that subtracts the stored EMA parameter change accumulated over the requested interval. At the first request, it obtains JS mean 0.0100, R-Acc 0.617, and Score 81.97, compared with 0.0080, 0.641, and 84.19 for Ours. Across three requests, its Scores are 81.97, 78.68, and 73.67, whereas Ours obtains 84.19, 84.22, and 79.10. These results are reported in Tables 2 and 4.

Q3: How many batches separate the requested data from the request, and how does delay affect the comparison?

A3: We define delay as the number of retained online-adaptation batches processed between the end of the requested interval and the arrival of the untraining request. We evaluate delays of 30, 50, and 70 in Table 5.

The R-Acc results and their deficits relative to Retain-Only Replay are:

  • At delay 30, Replay and Ours both obtain 0.602 R-Acc, whereas reset and rollback obtain 0.539 and 0.555. Their deficits are therefore 6.3 and 4.7 percentage points.
  • At delay 50, Replay and Ours both obtain 0.641, whereas reset and rollback obtain 0.555 and 0.539. Their deficits increase to 8.6 and 10.2 percentage points.
  • At delay 70, Replay obtains 0.711 and Ours obtains 0.664, whereas reset and rollback obtain only 0.512 and 0.555. Their deficits further increase to 19.9 and 15.6 percentage points. As delay increases, the model processes more batches from the inserted domains and accumulates more useful adaptation. Source Reset and Clean Rollback restore earlier model states, so they discard an increasingly large fraction of this adaptation. The growing R-Acc deficits therefore directly reveal their limitation under longer request delays.

Ours preserves substantially more of the intervening adaptation, but it is not unaffected by increasing delay. Its Score decreases from 84.75 at delay 30 to 84.19 at delay 50 and 84.14 at delay 70. At delay 70, its R-Acc also falls 4.7 percentage points below Replay, whereas it matches Replay at delays 30 and 50. This indicates that separating the requested influence from a longer sequence of subsequent updates becomes more difficult as the delay grows. Nevertheless, at delay 70, Ours retains an R-Acc of 0.664, which remains clearly higher than reset at 0.512 and rollback at 0.555. The results therefore support a conclusion: our method better preserves post-request domain adaptation than restoring an earlier state, although its correction accuracy also gradually degrades under sufficiently long delays.

AuthorsOpenReview ↗

Rebuttal Summary

We sincerely thank the reviewers and Area Chairs for their careful evaluation and constructive feedback.The feedback identified four main issues in the original submission:

Q1: Does the original evaluation adequately measure untraining quality?

We appropriately revised the experimental section and added several experiments. The original Score used CF-Gap, which compares average confidence and can hide changes across classes or samples. We replaced it with mean Jensen–Shannon divergence from matched Retain-Only Replay, comparing output distributions and measuring similarity to oracle behavior. The revised metric and Score are described in the experimental section and Appendix D.4.

We extended the reconstructed-token versus real-image comparison from one to all three requests and added JS mean, 95th-percentile JS divergence, and confidence MAE. Both inputs consistently move the model toward Replay, supporting our premise that reconstruction should recover feature-space directions informative for correction rather than original images. Results are in Table 9 and Appendix C.2, Table C.5.

Q2: Do the experiments convincingly distinguish our method from reset and rollback?

We appropriately revised the experimental section and added several experiments. We redesigned new experiments on ImageNet-C to test the correction-retention trade-off: requested batches use severity-1 corruptions, while unseen severity-3 domains are inserted before the delayed request. At delay 50, Ours matches Replay at 0.641 R-Acc; Source Reset and Clean Rollback obtain 0.555 and 0.539, losing 8.6 and 10.2 points. These results are in Table 2. The original mild setting without an inserted transition was moved to Appendix C.4, Table C.8.

Across delays 30, 50, and 70, reset/rollback deficits relative to Replay grow from 6.3/4.7 to 8.6/10.2 and 19.9/15.6 points. Ours also degrades as longer subsequent updates become harder to separate, but at delay 70 retains 0.664 R-Acc, versus 0.512 for reset and 0.555 for rollback. Results are in Table 5.

With all 15 ImageNet-C corruptions at severity 5, Ours remains within 3.0, 1.3, and 0.0 R-Acc points of Replay across three requests, while reset and rollback show larger deficits. Selective correction therefore better preserves post-request adaptation than restoring an earlier state. Results are in Appendix C.2, Table C.4.

Q3: Are the baseline comparisons strong and information-equivalent?

We appropriately revised the experimental section and added several experiments. We added an Amnesiac-style baseline that subtracts the stored EMA update over the requested interval. Its three-request Scores are 81.97, 78.68, and 73.67, versus 84.19, 84.22, and 79.10 for Ours.

We also added paired no-history and matched-history versions of SCADA-UL, DELETE, SSD, SalUn, and SCRUB. History-enabled variants use the same reconstructed information as Ours and suppress the target category more strongly, confirming that reconstruction identifies the requested influence. However, their class-directed objectives often suppress retained examples, reducing SC-Acc and increasing divergence from Replay. Batch-specific untraining therefore requires both informative history and a selective objective; our method combines both. Results are in Tables 2 and 4 and Appendix C.1.

Q4: Is storage bounded and controllable?

We first added some experiments. We extended the stream to 5,000 batches; storage reaches a plateau and remains unchanged through batch 5,000. Measurements are in Appendix C.3, Table C.7.

We further introduced a global per-class Top-K Fisher retention. Top-30% reduces persistent state from 18.56 to 8.08 GiB (56.5%) with only a 0.32-point Score decrease. Top-10% reduces it to 5.02 GiB (73.0%) with a clearer utility loss, providing a configurable trade-off. Results and implementation details are in Appendix C.4, Table C.9.

We also added conservative cleanup for exact records, overlapping archives, and affected Fisher entries, and distinguish active-model correction from deleting every historical trace. The procedure is in Appendix B; complete auxiliary-state privacy is identified as an open limitation.

Core contribution

We introduce online untraining for continual TTA and, to our knowledge, the first method designed for it.

Some difficulties are intrinsic to this setting.Delayed requests require separating requested influence from later updates, creating trade-offs among correction, storage, latency, and auxiliary-state privacy. We hope that formulating this task and providing its first systematic evaluation will encourage further work on online untraining and unlearning.

Two reviewers joined the follow-up discussion, recognized the revisions, and increased their assessments. One did not participate, but we addressed all reviews in the revision.

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

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