acceptodds
Under review as a conference paper at ICLR 2027

Blind by Construction: Record-Level Unlearning Audits Miss Retained-Carrier Reconstruction on Frozen Time-Series Features

Abstract

A record-level unlearning audit compares a model that unlearned a deleted record with one that never saw it, so it is blind by construction to what the retained records reveal about the deleted subject. When a deletion covers a subject with many records, a correlated record from another subject stays in the pool; we call such a record a retained carrier. For frozen time-series features with a ridge readout, we derive an exact identity for how much a carrier adds to reconstructing the deleted subject. Measuring this contribution requires finding carriers, and cosine similarity on frozen features fails here: the features share one dominant direction, so it marks almost every retained record as a carrier and inflates the contribution. After de-centering, the artifact disappears: the all-subject median excess is 0.000 on CWRU, PTB-XL and MIMII and +0.046 on Paderborn. Planted carriers with known effects often go undetected, so these zeros state the measurement's detection limit rather than the absence of leakage. Membership inference on the same data remains accurate. The two channels measure different quantities: whether a deleted record is still distinguishable, and how much a retained carrier lets an attacker reconstruct the deleted subject. Unlearning evaluations should report both, each with its measurement range.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
machine unlearning, unlearning audit, time-series foundation models, retained-carrier reconstruction, membership inference

Reviews

Among:
Shape:
1234this paper, Bottom 9%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.50 over 4 reviews, above 9% of the others.
Reviewer_8BaPOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
1
Soundness
1
Read review
Paper summary

The paper argues that record-level unlearning audits cannot detect what retained, correlated records ("retained carriers") reveal about a deleted subject, because the two models such audits compare both keep those records. The paper also indicate the issues of using raw cosine similarity as carrier indicator; therefore, proposing "de-centering" to resolve it. After that, on three datasets, the authors claims no carriers are identified while the membership inference remains accurate. The authors claims both need to be evaluated to assure the model is indeed unlearn.

Critical strengths
  1. It is important to measure the effect of carrier if it still exists after related record is deleted. As it could be infered by the remaining records.
  2. Evaluated over multiple foundation models, diversifying the experiments.
Critical weaknesses
  1. The presentation of paper needs to be improved, many unknown terms used in abstract without proper context; e.g., what is de-centering, and what is median excess? and what does 0.000 mean here? And if the planted carrier can not be detected, how does the paper measure the effect from the carrier?
  2. de-centering technique is a standard approach to fix the dominate direction, and theorem 1 is standard formula for ridge regression.
Questions for authors
  1. Why pre-register an all-subject median that is zero whenever fewer than half the subjects have a detected carrier? Why keep the 0.9 threshold when the detector rarely flags the planted carriers?
  2. Would an exact retrain without the deleted subject show the same excess? If so, why is this an unlearning-audit gap rather than ordinary generalization from similar subjects?
Reviewer_eG5POpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper finds how standard unlearning audits can detect what other, correlated subjects left in the training data still reveal about a subject (for example a patient or a machine) whose records were deleted, in a setting where a frozen time-series foundation model feeds a linear regression head that is refit after each deletion. The authors argue that a record-level audit cannot see this by design, derive an exact formula for how much a given set of correlated records changes the head's prediction error on the deleted subject, and then measure this effect on industrial and clinical benchmark datasets. They find that the usual way of finding correlated records, cosine similarity between frozen features, marks almost every record as correlated and produces large false effects, and that once this is corrected by subtracting the mean feature, the measured effect is zero or close to zero, while membership inference attacks on the same data still succeed. They explain the zeros as a limit of what the measurement can detect rather than as evidence of no leakage, because planted correlated records with known effects were mostly missed and they recommend that unlearning evaluations report membership results and this reconstruction measure side by side, each with the smallest effect it can detect.

Critical strengths
  1. Section 4.1 shows that cosine similarity on frozen time-series features rates nearly every pair of records as near-duplicates, for three encoder families and also for non-learned MiniRocket features (Section 6.3), and that analyses built on it report large effects that are not real. The paper is useful well beyond unlearning, for anyone who uses these embeddings to deduplicate data or to search for similar records.

  2. The reporting is clear and easy to follow. The main statistic and the decision rule were fixed before the experiments, subjects where nothing was detected are reported apart from subjects where an effect was measured and found to be zero, and the failed positive controls are reported instead of omitted (Sections 4.2 and 5.2).

Critical weaknesses
  1. The corrected detector is never shown to find correlated records that are actually present, so the near-zero results carry little information. The main statistic is a median over all deleted subjects in which a subject with no detected correlated record counts as zero, so it equals zero whenever fewer than half of the subjects have a detection, whatever the size of the real effect (Appendix B.5). This is the situation on all three datasets that read zero. At the same time, none of the five planted records passes the authors own pre-set criterion of being detected in at least half of the runs with an effect above their threshold for a meaningful effect (Section 5.2). The planted record built to have an effect well above that threshold is detected in 1 of 72 runs, and when it is forced into the analysis the estimate recovers about one ninth of its known effect (Appendix B.4). Appendix F.3 adds that in 137 of 186 subject and seed combinations the remaining data already predicts the deleted subject as well as its noise allows, so no retained record, not even an exact copy, could improve the prediction. Subtracting the mean removes false detections, but the paper does not show that it keeps true ones, and a detector that flags nothing would produce the same tables. Since Section 9 and Box 1 ask practitioners to adopt this detector, I do not think the evidence supports that recommendation yet. I also note that where records are detected, several subjects on MIMII, Paderborn and the larger PTB-XL pool show effects above the paper's threshold, and the all-subject median hides exactly these cases.

  2. The formal results add little that is new, and the privacy harm being measured is not established. Proposition 1 holds by definition: under exact unlearning the two compared models are identical, so a record-level audit detects nothing at all, not only nothing about correlated records. That deleting a record gives no protection against inference from correlated data that remains is already known from work the paper cites [1], [2]. Theorem 1 is the standard low-rank (Woodbury) update for ridge regression, and the mean subtraction is the post-processing step proposed in [3]. On the threat side, "reconstruction" here means how well a linear head forecasts the next value of the deleted subject's signal, and three of the four datasets contain no personal data. The harms used as motivation in Section 1, re-identifying a patient or revealing a machine's operating state, are not tested. Section 8 also states that a positive reading neither shows a deletion failure nor justifies removing other subjects' data, which leaves open what an auditor should do when the measure is positive.

Minor issues:

  • The main text depends heavily on a very large appendix and uses many terms of its own (for example "predicted floor", "admissible pairs", "abstention band" and "window-clustered relabeling") without defining them where they first appear. Sections 5.2, 6.4 and 6.5 were hard to follow even after several readings.

  • Section 8 refers to a certificate from Appendix E that the main text never introduces, and Appendix E.5 says it covers no leak measured in the study. It should either be explained in the main text or dropped.

  • Related work in the main text (Section 7) is a single paragraph, and the actual positioning against prior work is left to Appendix D.

  • In the natural-data experiments the three seeds change only the random control and the planted records (Appendix F.1), so they are not repeated measurements of the effect. Section 4.2 reports a three-seed mean and should say this.

References

[1] R. Chourasia and N. Shah. Forget unlearning: Towards true data-deletion in machine learning. In Proceedings of the 40th International Conference on Machine Learning (ICML), 2023.

[2] M. Humbert, B. Trubert, and K. Huguenin. A survey on interdependent privacy. ACM Computing Surveys, 52(6), 2020.

[3] J. Mu and P. Viswanath. All-but-the-top: Simple and effective postprocessing for word representations. In International Conference on Learning Representations (ICLR), 2018.

Questions for authors
  1. Who are the members and non-members in the LiRA and RMIA experiments, and which model is attacked? By the same reasoning as Proposition 1, an attack on the deleted subject should have no advantage against the model deployed after exact unlearning. If the attacks instead target subjects in a model that was trained on them, the result says nothing about deletion. How does this experiment support the claim that membership and reconstruction measure different things?

  2. Why does the forced estimate recover only about one ninth of the planted record's known effect? If Theorem 1 is exact once the correlated records are given, the gap must come from how the score is normalized, how windows are built, or how the true value was computed. If the estimator itself is biased toward zero, the resolution reported in Section 5.1 is too optimistic.

  3. In the raw-cosine experiments, what effect does the control that removes the same number of randomly chosen subjects show? If removing 48 to 52 random series out of 59 gives a similar effect, the inflation comes from shrinking the training set, which would make the argument simpler.

  4. Could you report, for each encoder and dataset, the estimated strength of the shared feature direction relative to the remaining variation (Remark A.2)? The explanation in Section 4.1 depends on this being large and the appendix does not confirm it for the features actually used.

  5. The evaluator keeps the deleted subject's raw data after the deletion has been carried out. How is this reconciled with the deletion request and can the measurement be made without it?

Reviewer_iLGbOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
3
Read review
Paper summary

The authors proposed an audit mechanism for leakage of deleted subject information when the retained pool act as a carrier. The paper very clearly explains that existing audit mechanisms can leave the correlation factor of retained with deleted data. Further, authors explains reconstruction excess, measured by removing retained carriers from evaluation. Decentring method for finding such carrier has been discussed in the paper.

Critical strengths
  • The discussed problem is interesting and gives and open direction for time series models unlearning when data used for training is correlated.
  • The observation of not using cosine similarity directly and how it can give false measure of similarity is very practical and describes that the method has been properly tested.
  • The idea of measuring reconstruction excess is really something that can help understanding privacy and leakage properly in case of unlearning.
Critical weaknesses
  • I am a bit unconvinced that the idea is novel enough. Earlier research has independently focused on privacy based on correlation between forget retain set and their dependance. Decentralisation of embedding similarity has also been explored. The idea of applying this to time-series data is interesting and can advance the field but on its own has limited novelty.
  • One way to increase novelty is using such measurement to develop a model initial training objective in a way that such correlated data points are well separated or such information that is shared amongst subjects can be well handled before. This can be further help in practical application of the idea.
  • I am concerned about message main empirical results are trying to deliver. if fewer subjects act as carrier the result is mostly zero. The no leakage claim is much more confusing with undetectable leakage. thus practical understanding of these measurements is unclear.
  • The choice of corrected way of selecting the carriers and detection part is not properly validated against exactly what data point act as carriers.
  • The exact unlearning is used only for evaluation. What about the approximate unlearning technique and how the carriers detection is affected. The measurement must change as the embedding representation is varied when retain set is explicitly protected using unlearning method.
  • The theory applies to any frozen encoder with a ridge head, but experiments cover only time-series encoders, so generality is untested.
  • The fine-tuning results are not consistent with the exact unlearning method.
  • Pools are small (mostly 10–60 subjects, at most 1000 PTB-XL patients), and no compute or runtime costs are reported. when the data is increased how much time it takes to compute the similarities.
  • Reconstruction term is used but its not properly measured, forecasting error is measured but after unlearning/deleting how is that error reflect on actual reconstruction, like attribution?
  • Key understanding are placed in the appendices: the failed controls, and that 137 of 186 subject-seed points are already predicted within noise.
Questions for authors

For rebuttal, some experiments are:

  • validation on detector like use at least one carrier family whose positive control passes, plus detection ROC curves against planted ground truth across thresholds and anisotropy corrections. In the paper’s own tests, the method failed to catch leaks the authors planted on purpose. The authors should show at least one case where it catches a known leak.
  • The paper reports only the median, which comes out as zero whenever fewer than half the subjects have a look-alike. The authors should also report the average, and how many subjects leak above the threshold.
  • Test on bigger datasets and unlearning pool and report the cost.
  • The authors measures leakage as in a way that the model predicts the deleted subject’s signal. It never shows that this lets anyone identify the person or learn something private about them. A real attack would show the leakage actually matters.
  • test on some other modalities.
Reviewer_gpM5OpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

The paper states that unlearning audits miss leakage due to correlated records and shows that cosine detectors fail by flagging pretty much every record as correlated due to the time series nature of the data. The authors then propose a de-centering approach to overcome the detector failure.

Critical strengths

Privacy problems due to correlation are very interesting and relevant. Looking at it in a machine unlearning + time series setting is a valuable to the community and for practice.

Critical weaknesses

Contribution 1:

  • Proposition 1 is true by definition of exact unlearning and the appendix states "This paper claims no discovery that correlated records leak”. I fail to see the novelty of this contribution.

Contribution 2:

  • This is a standard Woodbury update for adding rows to ridge regression (App. A.1) the authors take from prior unlearning papers (App. D.3).
  • The formula and experiments match by construction “this checks the implementation and is not a prediction” (App. B.3)
  • The predictive extensions fail: “rejected in 9 of 9 pre-registered fits” (App. C.1), and “no separation over baseline error” (App. F.2).

Contribution 3:

  • De-centering is simply mean removal taken from the literature “inherit … from this literature” (App. D.4).
  • The detector misses known leaks, and reported zeros follow from that. A planted carrier with a known effect of +0.63 is flagged “in 1 of 72 subject-seed rows” (App. B.4), and “no control reached its pass state” (App. B.5). Undetected is recorded as 0 leakage, so on CWRU, PTB-XL and MIMII the median is 0 “even at readings of +10 or −10” (App. B.5). The zeros show the detector rarely fired, not that leakage is absent.
Questions for authors

Can you please restate the contributions of this paper? Proposition 1 holds by definition, Theorem 1 is a Woodbury update, and the de-centered detector fails controls. Much of the limitations and citations of where things come from (sections 2-5 have 0! citations) are in the appendix, so the main text overstates the contributions and does not give proper credit to prior work.

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

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