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Under review as a conference paper at ICLR 2027

How Noisy Training Reduces Model Discrepancy in Quantum Machine Unlearning

Abstract

Machine unlearning aims to remove the influence of selected training data without retraining from scratch. While calibrated training noise can support unlearning guarantees in classical learning, native noise in quantum neural networks (QNNs) is not designed for this purpose. We study how native quantum noise affects the pre-to-post discrepancy between the original (pre-unlearn) model distribution and its retrained gold-standard reference under the same noise regime, before any unlearning update is applied. We develop a trajectory-level 2-Wasserstein analysis that decomposes this discrepancy into deletion-induced update differences, their subsequent propagation, and finite-shot gradient fluctuations. For exact-expectation readout noise, this analysis yields explicit channel-dependent bounds and identifies conditions under which their geometric envelopes become smaller than the noiseless counterpart. We further construct a fixed-QNN example showing that arbitrarily small Wasserstein discrepancy can coexist with maximal deletion sensitivity. Experiments on a 4-qubit QNN show discrepancy reductions in selected readout and interleaved channel regimes, while finite-shot measurement provides no comparable reduction in the tested settings. A 10-qubit MNIST study additionally shows that selected noise regimes reduce unlearning optimization costs. Together, these findings suggest that native quantum noise can facilitate unlearning in selected regimes, while distinguishing geometric proximity and optimization savings from certified removal of data influence.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
Machine Unlearning, Quantum Neural Network, Quantum Noise

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Paper summary

The paper studies how quantum noise during QNN training changes the gap between two model distributions: the distribution of models trained on the full data, and the distribution of models retrained on the retained data only, under the same noise. The authors call this the pre-to-post discrepancy; it is the deletion sensitivity of the identity unlearning mechanism (Def. 1, Sec. 3.1). The main technical result is a coupled-trajectory 2-Wasserstein recursion (Theorem 1, Eqs. 8-11) that upper-bounds the RMS distance between the full-data iterates and the retrained iterates when both start from the same initialization. The bound has three ingredients: a per-step deletion perturbation, a propagation factor, and a finite-shot variance term. Assuming that all channels share the same contraction factor below one, and that exactly one single-qubit channel sits right before the Pauli-Z readout, Corollary 1 and Table 1 give closed-form per-channel factors. Under these bounds, depolarizing, amplitude damping and bit flip noise (with flip probability below 0.5) tighten the bound, while phase damping leaves it unchanged. Prop. 1 constructs a single-qubit example in which the 2-Wasserstein distance goes to zero while the hockey-stick deletion sensitivity stays at 1, so being close in 2-Wasserstein does not certify unlearning. The experiments are a 4-qubit Iris classifier (1,024 paired initializations, 5 splits) that looks at readout noise, interleaved noise and finite shots, and a 10-qubit MNIST task that forgets digit 0, where five unlearning methods (GA, FT, GA+FT, SalUn, DELETE) are compared using success-conditioned step counts.

Critical strengths
  1. The formal work is careful. Using the noise-matched retraining distribution as the reference (Sec. 3.1), and keeping it separate from the noiseless retraining reference, is the right choice for learning on noisy hardware. I checked the proof of Theorem 1 (App. B.2, Eqs. 35-38), the minibatch extension (Prop. 2), the parameter-shift variance bound (Prop. 3, Eq. 49), the channel adjoint identities (App. C.4), the factors in Table 1 (Eq. 67) and the construction in Prop. 1 (Eqs. 52-56), and I did not find errors. The authors also correctly require conditional unbiasedness with respect to the joint history (Eq. 32), which is easy to get wrong.
  2. The paper is clear about the limits of its own results. It says that the bounds do not rank the actual distances (App. C.1-C.2); that contraction along sampled trajectories does not establish the uniform contraction-below-one condition (App. C.3, E.3); that decay applied only at evaluation time is trivial (App. B.6); and that success-conditioned cost is not the same as an unconditional speedup (Sec. 6, App. F.3). Prop. 1 is included precisely to stop readers from treating a smaller 2-Wasserstein distance as an unlearning guarantee.
  3. The split of the bound into a deletion perturbation and a propagation factor is used to explain a negative result. The bound predicts that amplitude damping should help, but at a damping strength of 0.2 the parameter distance goes up by 13.48% (App. E.1). Table 3 (p. 30) attributes this to a loss of RMS contractivity: as the damping strength goes from 0.05 to 0.4, the percentage of steps on which the RMS update contracts drops from 66.6% to 0% under normal deletion. This shows that a small deletion perturbation alone is not enough.
  4. For a small-scale study, the Iris experiments are well controlled. Initializations are shared across noise settings and deletion scenarios; the empirical 2-Wasserstein distance is computed with an exact optimal matching (Eq. 82); both a clean audit and a noise-matched audit are reported; there is an independent-inference control for finite-shot evaluation (App. D.3, E.1); and there is a variant that deletes mislabeled samples. The audit design also rules out the trivial effect where outputs are simply scaled down by one minus the noise strength (App. B.6).
Critical weaknesses
  1. The channel noise in the experiments is deterministic, so the analogy to DP-style noisy training does not really hold. The introduction (pp. 1-2) cites Sekhari et al. (2021), Ullah et al. (2021) and Chien et al. (2024), where randomness injected into training gives hockey-stick or TV guarantees. In this paper, every channel sweep uses exact expectations (infinite shots; Sec. 4.1, App. D.2). With exact expectations, the channel is just a deterministic change to the loss surface, and the only remaining randomness is the shared initialization. The one genuine source of randomness studied here, finite shots, actually increases the empirical 2-Wasserstein distance (Fig. 4; up 16.06% at 32 shots). What the paper measures is how a deterministic change to the model function affects trajectory separation, and the phrase "noisy training" in the title should reflect that. I suggest stating this distinction explicitly in Sec. 1 and Sec. 3.1, and either dropping the DP analogy or analyzing, in addition to 2-Wasserstein, how shot noise changes the hockey-stick sensitivity (which is where randomness might actually help).
  2. The main readout-noise result has a simple classical explanation that the experiments do not rule out. For readout depolarizing and bit flip noise, the noisy model output is exactly a rescaled copy of the noiseless output (App. C.4). Training under this noise is equivalent to classically training a model whose output is scaled down: the gradients shrink by the same factor, and the parameters move less away from the shared initialization. Table 1 is exactly the chain rule applied to this scaling (Eqs. 61-67), and there is nothing quantum-specific in it. The 14.58% reduction in parameter space at a noise strength of 0.2 (Sec. 4.2) could well come entirely from smaller total movement within the 120-step budget. Please add these noiseless baselines: (i) a learning rate rescaled by the output scale factor or by its square; (ii) a training budget matched by training loss or by the distance of the final parameters from initialization. Then report the ratio of the noisy to the noiseless 2-Wasserstein distance relative to these controls. If the effect survives, the conclusion becomes much more convincing.
  3. The reduction in parameter space barely shows up in function space, and no unlearning-related metric is measured. For readout depolarizing noise at strength 0.2, clean predictions under normal deletion get only 0.65% closer (App. E.1, p. 25). The larger reduction in the noise-matched case comes mostly from decay at evaluation time, which App. B.6 itself admits is uninformative. On MNIST, depolarizing noise increases the clean prediction distance by 3.50% (Sec. 5, Fig. 5). By Prop. 1, the parameter-space 2-Wasserstein distance says nothing about the target quantity set up in Def. 1, the deletion sensitivity, and that quantity is never estimated. I would like to see some empirical proxy for the deletion sensitivity of the identity mechanism or for TV, for example a classifier two-sample test between the noisy full-data and noisy retrained distributions in prediction space, or a membership inference success rate. Without these, the contribution reads more like a result about geometric stability than a result about unlearning.
  4. Theory and experiments are not connected. None of the experiments satisfy the assumptions of Corollary 1. App. C.3 concedes that no bounded region contains the Gaussian initialization with probability 1, and the paper does not claim that its sufficient condition (a regularization strength larger than twice a model-dependent constant) holds for the regularization strength used in the experiments (0.01). Table 3 shows that even without noise, only 63.7% of RMS steps are contractive. The bound is never evaluated numerically, so the reader cannot tell whether it is vacuous (say, orders of magnitude above the empirical 2-Wasserstein distance) or informative. The authors could use the per-step deletion perturbations and RMS propagation factors estimated along the trajectory (Eq. 84) to compute the bound from Eq. 9, and plot it in the same figure as the empirical paired RMS distance and the 2-Wasserstein distance.
  5. The cost results on MNIST are statistically weak and depend on a single method. The parameter 2-Wasserstein ratios are 0.9900 plus or minus 0.0044, 0.9608 plus or minus 0.0142, 1.0096 plus or minus 0.0197, and 1.0227 plus or minus 0.0203 (App. F.3); both amplitude damping increases are within one standard deviation of 1. Each 2-Wasserstein value is computed per split from 8 versus 8 models in 320 dimensions, which is closer to a paired distance than to a distribution-level estimate. The "mean cost reduction" in Table 2 averages percentage changes across methods. GA, GA+FT and DELETE change by at most 0.2 steps on a base of roughly 8 to 13 steps; FT gets worse at a noise strength of 0.05 (from 159.5 to 176.7); and nearly all of the depolarizing gain comes from SalUn (from 306.7 to 218.7). SalUn is also the only method that has failures, so its success-conditioned mean is subject to selection bias. No variance or confidence intervals are given for the step counts. Please report per-method paired differences with CIs over the 40 pairs, medians or survival curves that treat failures as censored, and significance tests, ideally with more initializations.
  6. The experimental scale and noise models are limited relative to how general the conclusions are. Experiment 1 trains a 16-parameter circuit on 60 Iris samples, and the splits overlap (App. D.1). The setting covered by the theory is a single-qubit, parameter-independent channel placed right before readout, where the circuit itself plays no role (Sec. 3.3). Readout noise strengths of 0.2 to 0.8 are far above calibrated real readout error rates. There are no hardware experiments, no composite or device-calibrated noise models (such as combined T1 and T2, coherent over-rotation, crosstalk), and no interleaved circuits deeper than two layers. Adding a device-calibrated noise model (for example a fake-backend model in Qiskit) and at least one larger interleaved setting would help. The wording of the title and abstract ("noisy training reduces ...") should also be toned down to match the mixed evidence.
Questions for authors
  1. Does the 2-Wasserstein reduction under readout depolarizing noise survive when compared to a noiseless baseline whose learning rate is multiplied by one minus the noise strength (or by its square), or a noiseless baseline stopped at matched training loss? In each noise setting, how large is the expected distance of the final parameters from initialization compared with noiseless training?
  2. Can you report the numerical value of the bound in Eq. 9, computed from trajectory estimates of the deletion perturbation and propagation factor, alongside the empirical paired RMS distance and the empirical 2-Wasserstein distance in Figs. 2-3? How loose is the bound?
  3. Have you estimated any event-level quantity between the noisy full-data distribution and the noisy retrained distribution, such as TV, hockey-stick divergence via a classifier two-sample test, or membership-inference advantage? Under depolarizing noise, does it move in the same direction as the 2-Wasserstein distance? Finite-shot training introduces real randomness; it increases the 2-Wasserstein distance, but does it reduce this quantity?
  4. Corollary 1 assumes all channels share the same contraction factor, but under Eq. 73 the curvature bound depends on the channel's scale and offset coefficients. Can you give the bound with a channel-dependent contraction factor (Eq. 68), and say for which channels the ordering in Table 1 still holds?
  5. For Table 2, what are the per-method paired step differences and their confidence intervals over the 40 initialization and split combinations? How many times does SalUn fail in each condition? Does the depolarizing gain survive if SalUn is excluded, or if failures are treated as censored at the maximum budget?
  6. The parameter-space 2-Wasserstein distance is computed on raw angles without periodic wrapping (App. D.3, F.3). Can you quantify the "negligible changes" from removing output-irrelevant parameters? Did you try a wrapped (toroidal) metric, especially on MNIST, where angles may drift over 2,000 SGD steps at a learning rate of 0.5?
6 comments
AuthorsOpenReview ↗

Response to Reviewer JBBd - 1

We sincerely thank the reviewer for the exceptionally detailed and constructive feedback. Your insightful comments and thoughtful suggestions have been invaluable in identifying areas for contribution and have substantially helped us strengthen experimental evaluation of our work.

W1&W6. Thank you for highlighting this distinction. We agree that exact-expectation channel effects should be distinguished from the stochastic perturbations used in DP-style noisy training, and that the title and abstract should reflect the mixed evidence rather than suggest a general discrepancy reduction.

We have revised Sections 1 and 3.1 to make the deterministic-versus-stochastic distinction explicit. In exact-expectation channel setting, fixed quantum channels deterministically modify the model function and loss surface without introducing additional channel-sampling randomness. For full-batch exact-expectation training, the learned-model distributions are induced by randomized initialization, with each trajectory deterministic conditional on its initialization. Section 3.1 also identifies minibatch sampling, when used, and finite-shot measurement outcomes as separate sources of training randomness.

We retain Sekhari et al. (2021) as motivation for examining the relationship between full-data and retrained model distributions before any unlearning update, rather than as evidence that native quantum noise provides the same privacy-preserving mechanism. The revised Introduction explicitly states that native quantum-noise effects differ from the calibrated stochastic perturbations used in DP training. It separately explains that finite-shot measurements introduce stochastic gradient-estimation errors that are not calibrated to satisfy DP. Thus, the connection to the classical literature motivates a research question, not a transfer of its mechanism or guarantees to our setting.

We also acknowledge the reviewer's observation about finite-shot training: at 32 shots, the empirical parameter-space W2W_2 is 16.06%16.06\% above the exact-expectation reference in the normal-deletion setting. The revised abstract now explicitly reports that finite-shot training increases empirical parameter-space discrepancy in the tested settings. These results concern W2W_2, not an evaluation of TV or hockey-stick deletion sensitivity.

Finally, we have changed the title to How Quantum Noise Shapes Model Discrepancy in Quantum Machine Unlearning. Replacing ``Noisy Training Reduces'' with "Quantum Noise Shapes'' tones down the directional claim and, together with the explicit distinction in Sections 1 and 3.1, clarifies the meaning of noise in our study. The revised abstract states that channel noise can decrease or increase discrepancy depending on its type, placement, and evaluation space, and explicitly acknowledges the finite-shot finding. It limits the reported optimization-cost benefits to selected noise regimes and distinguishes geometric proximity and optimization savings from certified removal of data influence. We have also revised the empirical-contribution statement in the Introduction and the Conclusion.

AuthorsOpenReview ↗

Response to Reviewer JBBd - 2

W2&Q1. We agree that affine readout noise fν=sf0+bf_\nu=sf_0+b admits a noiseless reformulation. For exact-expectation GD under squared loss and s≠0s\neq0, this requires targets (y−b)/s(y-b)/s, learning rate ηs2\eta s^2, and regularization λ/s2\lambda/s^2. It is therefore generally not equivalent to changing the learning rate alone. Interleaved noise need not admit this affine relation.

To assess adjusted noiseless training, we retain the original targets and select clean (η,λ,K)(\eta,\lambda,K) by minimizing average validation MSE, requiring both full-data and retrained validation accuracies to be within one percentage point of their noisy references. Test data and discrepancies are excluded from selection.

Placement / channelParameter ratioClean-prediction ratio
Readout depolarization (q=0.20q=0.20)0.748±0.2310.748\pm0.2311.024±0.0611.024\pm0.061
Interleaved amplitude damping (γ=0.04\gamma=0.04)0.529±0.1420.529\pm0.1420.853±0.1290.853\pm0.129

Both noise conditions retain mean parameter-discrepancy ratios below one at comparable validation accuracy. Interleaved amplitude damping also retains a mean clean-prediction ratio below one.

For readout depolarization q=0.20q=0.20, we additionally evaluate the two requested learning rates while retaining the original targets and λ=0.01\lambda=0.01. At each learning rate, we compare K=120K=120 with a common full-data/retraining horizon selected solely to match mean displacement from initialization. All ensembles match their noisy references within 0.365%0.365\%.

Noiseless learning rateClean horizon KKParameter ratioClean-prediction ratio
0.12=η(1−q)0.12=\eta(1-q)Fixed: 1201201.055±0.0761.055\pm0.0761.061±0.0391.061\pm0.039
0.120.12Displacement-matched: 130130–1351350.968±0.0530.968\pm0.0531.034±0.0311.034\pm0.031
0.096=η(1−q)20.096=\eta(1-q)^2Fixed: 1201201.281±0.1231.281\pm0.1231.149±0.0591.149\pm0.059
0.0960.096Displacement-matched: 163163–1691690.965±0.0530.965\pm0.0531.033±0.0311.033\pm0.031

After matching displacement, both requested learning-rate controls yield mean parameter-discrepancy ratios below one. The noisy full-data/retrained mean displacements are 1.530/1.5331.530/1.533, versus 1.569/1.5731.569/1.573 for nominal noiseless training. Both tables report the mean ±\pm sample SD of within-partition noisy/clean discrepancy ratios over five Iris normal-deletion partitions. All prediction comparisons use the same channel-free audit.

Together, these results show that the mean parameter-discrepancy reduction under readout depolarization persists under validation-accuracy selection and, separately, displacement matching. This supports studying its effect on model distributions despite the exact affine reformulation. The mean readout clean-prediction ratios remain above one.

The affine reformulation and validation-selected controls are included in Appendix C.5, with a main-text clarification at Line 298.

W3&Q3. We added C2ST and loss-based membership inference (MIA) to compare full-data and retrained models within each training condition, before any unlearning update. Both use clean, exact predictions without evaluation-time noise. C2ST reports balanced accuracy.

On 10-class MNIST, C2ST uses each model’s concatenated predictions on a shared set of 20 held-out test images. Models with the same initialization stay in the same fold, and evaluation uses held-out model pairs. For MIA, we score each deleted example by its negative squared-error loss: full-data models that saw the example are positives, and models retrained without the deletion set are negatives. We compute ROC-AUC on held-out model pairs and average it across deleted examples and data splits.

Here, Wν/W0W_\nu/W_0 denotes the parameter-space W2W_2 ratio relative to noiseless training.

DatasetTraining conditionWν/W0W_\nu/W_0C2STMIA ROC-AUC
IrisNoiseless1.00093.48%0.5957
IrisReadout depolarization (q=0.20q=0.20)0.88490.82%0.5872
IrisReadout amplitude damping (γ=0.20\gamma=0.20)1.06486.91%0.5678
Iris32-shot training1.17989.65%0.5944
MNISTNoiseless1.000100%0.9991
MNISTReadout depolarization (q=0.20q=0.20)0.9570100%0.9993
MNISTReadout amplitude damping (γ=0.08\gamma=0.08)1.0102100%0.9989

Under depolarization, parameter W2W_2 and C2ST both decreased in the point estimates on Iris and MNIST, while MIA changed little. For MNIST, depolarization reduced parameter W2W_2 by 4.3%, yet C2ST remained at 100% and MIA remained near 1. For 32-shot training on Iris, parameter W2W_2 increased by 17.9%, whereas C2ST decreased and MIA remained nearly unchanged.

Thus, parameter-space proximity need not imply lower empirical distinguishability, consistent with Proposition 1. These attack-specific point estimates do not establish statistically reliable improvements or certify reduced deletion sensitivity. The revised paper reflects this discussion on Appendix B.6.

AuthorsOpenReview ↗

Response to Reviewer JBBd - 3

W4&Q2. Following your suggestion, we evaluated the empirical counterpart of Eq. (9) using measured deletion perturbations, including the initial perturbation, and RMS propagation factors, without imposing common contraction. Comparisons with paired RMS and optimal-assignment empirical W2W_2 were added to Figures 2 and 3.

At 120 updates, the normal-deletion readout results are:

ConditionEmpirical W2W_2Paired RMSEmpirical envelope
Clean0.2054±0.04130.2054\pm0.04130.2056±0.04140.2056\pm0.04140.3141±0.08240.3141\pm0.0824
Depolarization (q=0.20q=0.20)0.1799±0.04500.1799\pm0.04500.1799±0.04500.1799\pm0.04500.2580±0.08210.2580\pm0.0821

Values are means and sample SDs across five partitions, each with 1,024 paired initializations. The within-partition envelope-to-W2W_2 ratios average 1.514±0.1061.514\pm0.106 and 1.415±0.1031.415\pm0.103, respectively. Thus, the envelope is approximately 1.4–1.5 times the observed distance, and both decrease under depolarization.

Additional regularized experiments (λ=0.1\lambda=0.1, η=0.1\eta=0.1; Figure 5) show c^k<1\widehat c_k<1 at all evaluated steps with nonzero paired separation, with observed maxima of 0.9990.999 for readout and 0.9960.996 for interleaved placement. Discrepancy reductions persist relative to the corresponding regularized noiseless reference: interleaved amplitude damping at γ=0.16\gamma=0.16, for example, gives parameter- and clean-prediction-space ratios of 0.629±0.0620.629\pm0.062 and 0.716±0.1070.716\pm0.107. The revision also reports the associated accuracy trade-offs.

These results quantitatively connect the deletion–propagation decomposition to the observed discrepancy. They establish empirical behavior on the evaluated ensembles, not Corollary 1's uniform contraction assumption over a parameter region.

W4&Q4. Yes. Appendix C.2 allows channel-dependent propagation factors. Under Theorem 1's assumptions, for exact-expectation training ν=(N,∞)\nu=(\mathcal N,\infty) and valid bounds 0≤ckN≤cN<10\le c_k^{\mathcal N}\le c^{\mathcal N}<1,

\le a_K^\nu \le B_{\mathcal N} :=2\eta\alpha_FG^{\mathcal N}S_K(c^{\mathcal N}),$$ where $\alpha_F=|F|/|D|$, $S_K(c)=\sum_{t=0}^{K-1}c^t$, and $G^{\mathcal N}$ is the readout data-gradient bound underlying Table 1. Holding the deletion pair, learning rate, horizon, and channel-free gradient bound fixed, $B_{\mathcal N}\le B_{\mathcal I}$ whenever $$\frac{G^{\mathcal N}}{G^{\mathcal I}} S_K(c^{\mathcal N}) \le S_K(c^{\mathcal I}).$$ Thus, $c^{\mathcal N}\le c^{\mathcal I}$ is sufficient for depolarization, amplitude damping, and bit flip to give bounds no larger than the clean bound. For monotonicity with increasing noise strength, non-increasing propagation bounds preserve the decreasing trends for depolarization, amplitude damping, and bit flip on $p\le1/2$; non-decreasing propagation bounds preserve bit flip's increasing branch on $p\ge1/2$. Readout phase damping leaves the prediction and update maps unchanged, so the same propagation factor and bound apply. **W5&Q5**. We address these points in our common rebuttal, together with related concerns raised by other reviewers. **W6**. Thank you for raising concerns about circuit size and the realism of the noise models. We added deeper interleaved circuits and simulated joint relaxation and dephasing using a historical IBM Manila $T_1/T_2$ calibration snapshot and a layer-duration approximation. We also tested coherent $ZX$ overrotations and spectator $ZZ$ crosstalk. | Noise model | Circuit | Parameter $W_\nu/W_0$ | Clean-prediction $W_\nu/W_0$ | |---|---|---:|---:| | IBM Manila | 4 qubits, 4 layers | $0.914 \pm 0.047$ | $1.002 \pm 0.063$ | | IBM Manila | 4 qubits, 8 layers | $0.925 \pm 0.145$ | $1.008 \pm 0.236$ | | IBM Manila | 5 qubits, 4 layers | $0.875 \pm 0.067$ | $1.005 \pm 0.081$ | | $ZX$ overrotation | 4 qubits, 8 layers | $1.000 \pm 0.016$ | $1.008 \pm 0.019$ | | $ZX$ overrotation | 5 qubits, 4 layers | $1.008 \pm 0.009$ | $1.017 \pm 0.027$ | | Spectator $ZZ$ crosstalk | 4 qubits, 8 layers | $1.029 \pm 0.052$ | $1.011 \pm 0.021$ | | Spectator $ZZ$ crosstalk | 5 qubits, 4 layers | $1.065 \pm 0.047$ | $1.052 \pm 0.052$ | Values are mean $\pm$ SD across five partitions. For $ZX$ overrotation and spectator $ZZ$ crosstalk, we first average the ratios over the six signed angles ($\pm 0.005$, $\pm 0.020$, and $\pm 0.050$ rad) within each partition. Under the IBM Manila calibration-informed noise model, the mean parameter-space discrepancy was lower than the noiseless baseline in all three circuits, while the mean clean-prediction ratios remained close to one. These results show that the effect depends on the noise mechanism and the space in which discrepancy is measured. Following your suggestion, we revise our paper to emphasize how different noise regimes can shape model discrepancy.
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Paper summary

The paper investigates how native quantum noise affects the discrepancy between quantum neural networks trained on full data and those retrained after data deletion under the same noise conditions. It develops a trajectory-level Wasserstein stability bound separating deletion-induced update differences, their propagation, and finite-shot gradient errors, and derives channel-specific bounds under a common contraction assumption. It also constructs a counterexample showing that arbitrarily small geometric discrepancy does not imply certified unlearning. Experiments using a four-qubit QNN on Iris and a ten-qubit QNN on MNIST show that selected noise configurations reduce parameter-distribution discrepancy and, for some methods, success-conditioned unlearning update counts. These benefits depend on the noise channel, placement, and algorithm; finite-shot measurement provides no comparable improvement, and reduced parameter discrepancy does not consistently translate into closer predictions.

Critical strengths

The paper investigates how native quantum noise affects quantum machine unlearning and identifies conditions under which noise may facilitate the task. Its theoretical framework separates deletion-induced update differences, their propagation through training, and finite-shot gradient fluctuations, providing a structured account of how different noise sources affect the discrepancy between original and retrained models. Together with the experiments, this offers evidence that selected noise configurations may reduce the optimization effort required by some unlearning methods. The work contributes to the emerging study of quantum machine unlearning and motivates further investigation into data removal in quantum learning systems.

Critical weaknesses

However, the practical strength of the theoretical improvement remains unclear. The channel-specific bounds in Table 1 rely on a common Lipschitz constant (c<1) for the retained-data update maps. Although Theorem 1 itself allows noncontractive dynamics, this stronger assumption is essential to the table’s conclusions and is not established for the experimental models. Contraction of a physical quantum channel does not automatically imply contraction of the parameter-space optimization updates. Moreover, when the remaining constants are held fixed, most channel-dependent factors improve the bound only linearly in a small noise rate. For example, 1% depolarizing noise reduces the stated bound by approximately 1.5%, while readout phase damping leaves it unchanged. Such improvements may be modest in noise regimes chosen to preserve predictive utility, particularly if the underlying bound is loose. Numerical evaluation of valid constants and comparison with measured discrepancies would help establish the bounds’ practical relevance.

The experimental results in Table 2 also provide limited evidence that noise improves the quality of unlearning. Both noiseless and noisy models achieve low accuracy on the forgotten digit, although this is partly expected because the reported unlearning results include only runs that satisfy the prescribed forgetting threshold. The parameter-discrepancy ratios remain relatively close to one; importantly, these ratios compare the original and retrained models before unlearning, rather than evaluating the final unlearned models against the retrained reference. The clearer benefit is a reduction in update counts for certain methods, particularly SalUn, but this benefit is method-dependent and can accompany lower retained-class accuracy. Comparisons at matched retained utility, together with success rates, uncertainty estimates, and post-unlearning distances to the retrained reference, would provide stronger evidence that noise improves the overall unlearning trade-off.

Questions for authors

What's the relation of Figure 5 and Table 2? Are they describing the same experiment?

4 comments
AuthorsOpenReview ↗

Response to Reviewer zx2N

Thanks for the reviewer's insightful comments. We address the specific concerns below.

W1. Contraction of a physical quantum channel does not necessarily imply contraction of parameter-space updates. The common contraction assumption in Corollary 1 and Table 1 is an additional condition, whereas Theorem 1 allows noncontractive propagation.

Moreover, a small-noise reduction in the channel coefficient alone does not establish a practically meaningful improvement. To assess its practical relevance, we evaluated Theorem 1, Eq. (9), using measured deletion perturbations and observed propagation factors without assuming common contraction. We added estimated-bound curves to Figures 2 and 3, enabling direct comparisons with the observed discrepancies.

We further examined whether consistently contractive RMS propagation is empirically attainable while assessing the associated predictive-accuracy trade-off. After screening regularization and learning-rate combinations, we selected λ=0.1\lambda=0.1 and η=0.1\eta=0.1, retaining the other Experiment 1 settings. Across the evaluated readout and interleaved sweeps through noise strengths 0.40.4 and 0.160.16, respectively, all defined RMS propagation factors are below one. Their observed maxima are 0.9990.999 and 0.9960.996.

Figure 5 presents these results. Discrepancy reductions persist under regularized training relative to its own noiseless reference:

Regularized training conditionParameter Wν/W0W_\nu/W_0Clean prediction (ϕ0)(\phi_0)Noise-matched prediction (ϕν)(\phi_\nu)
Readout depolarization (q=0.20q=0.20)0.870±0.0320.870\pm0.0320.908±0.0490.908\pm0.0490.727±0.0390.727\pm0.039
Interleaved amplitude damping (γ=0.16\gamma=0.16)0.629±0.0620.629\pm0.0620.716±0.1070.716\pm0.1070.450±0.0560.450\pm0.056

Under depolarization, the mean within-partition ratio of the estimated bound is approximately 1.111.11, providing a numerical comparison beyond the channel coefficient alone.

These results connect the observed reductions to the deletion–propagation decomposition and demonstrate that contractive propagation can be empirically attained under suitable training settings, while making the predictive-accuracy trade-off explicit.

To reflect the discussion, we revised our paper: Figures 2, 3, and 5; Lines 354 and 424.

W2. We address these points in our common rebuttal, together with related concerns raised by other reviewers.

Q1. Figure 5 (now Figure 6) and Table 2 use the same MNIST training and retraining ensembles but describe different stages. That figure measures original-versus-retrained discrepancies before unlearning, whereas Table 2 reports unlearning updates and forget/retain accuracies. The Wν/W0W_\nu/W_0 row in Table 2 also refers to the pre-to-post discrepancy. We have strengthened the corresponding paragraph to make this relationship explicit and avoid confusion.

Dear Reviewer zx2N,

Thank you very much for your time and thoughtful feedback throughout the review process. As the ICLR discussion period is approaching its end, we would be happy to address any remaining questions or concerns you may have. We sincerely appreciate the time and effort you have devoted to reviewing our work.

Best regards,
The Authors

I thank the reviewers to address my concerns. The revision gives me a better understanding.

Dear Reviewer zx2N,

Thank you for your positive follow-up. We are glad to hear that our revisions and additional analyses have helped clarify our work.

We hope that these updates have also alleviated your main concerns regarding the theoretical assumptions and empirical relevance of our findings. If you feel that your concerns have been sufficiently addressed, we would sincerely appreciate it if you could consider revisiting your overall rating in light of the revisions.

Thank you again for your thoughtful feedback and consideration.

Best regards,
Authors

Reviewer_57swOpenReview ↗
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2
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Paper summary

This paper studies how quantum channel noise and finite-shot measurements affect the discrepancy between QNNs trained on the full dataset and models retrained on the retained dataset, before any unlearning update. It develops a coupled-trajectory Wasserstein bound separating deletion-induced update differences, their propagation, and finite-shot gradient errors. Under a common contraction assumption, the analysis gives explicit bounds for several final-readout channels. A single-qubit counterexample demonstrates that arbitrarily small Wasserstein discrepancy can coexist with maximal deletion sensitivity. Experiments on a 4-qubit Iris classifier compare parameter and prediction discrepancies across noise regimes. A 10-qubit MNIST experiment evaluates five unlearning methods and reports method-dependent reductions in success-conditioned optimization steps under selected depolarizing-noise settings.

Critical strengths
  1. A precise distinction between geometric proximity and unlearning guarantees. Proposition 1 constructs a fixed QNN and training setup whose full-data and retrained distributions become arbitrarily close in Wasserstein distance while remaining perfectly distinguishable for every (q<1). This makes the limitation concrete within the paper’s own model and helps prevent geometric improvements from being interpreted as removal of data influence.

  2. Useful experimental controls and attention to noise placement. The experiments distinguish parameter-space discrepancy, clean-prediction discrepancy, and noise-matched prediction discrepancy. The clean audit removes direct evaluation-time attenuation, while paired initializations and full-assignment computation of empirical Wasserstein distances strengthen the comparisons. The interleaved-channel experiments are particularly interesting because they exhibit effects absent from the final-readout setting, including changes under phase damping. Reporting regimes where noise increases discrepancy also helps establish the limits of the observations.

Critical weaknesses
  1. The readout-training effects admit an exact noiseless reformulation, which limits their interpretation. Equation 60 gives the affine relation fθN(x)=sfθI(x)+bf_\theta^{\mathcal N}(x)=s f_\theta^I(x)+b. Combining this with the regularized squared-loss objective in Equation 80, for s≠0s\neq0, gives s2LZI(θ;y−bs,λs2).s^2 L_Z^I\left(\theta;\frac{y-b}{s},\frac{\lambda}{s^2}\right). Here, the target transformation applies to every training example. Consequently, exact-expectation GD or plain minibatch SGD reproduces noiseless training with learning rate ηs2\eta s^2, targets (y−b)/s(y-b)/s, and regularization weight λ/s2\lambda/s^2, given the same initialization and batches. For example, at q=0.2q=0.2, the equivalent Iris training uses learning rate 0.0960.096, targets 1.25y1.25y, and regularization weight 0.0156250.015625. This is an equivalence to a modified-target noiseless objective, not merely a smaller learning rate. It concerns training and retraining and does not establish the same learning-rate equivalence for Adam-based unlearning. The paper includes paired noiseless baselines with the same nominal optimization settings. However, it does not assess whether noiseless training with the original targets and tuned learning rates, regularization, and training horizons achieves comparable discrepancy at matched predictive utility. The clean audit removes evaluation-only attenuation but does not control for these training changes. Although the equivalence does not invalidate the observed effects of native noise, it shows that the readout-training effects can be reproduced through adjustments to a noiseless objective and optimization procedure. Additional comparisons would clarify their practical significance. Furthermore, the channel comparisons in Corollary 1 and Table 1 assume a common contraction factor that is not established for the experimental settings, as the authors acknowledge. This limits their quantitative explanatory role without invalidating Theorem 1, which does not require contraction. The general framework accommodates interleaved noise, but explicit channel-specific bounds for that placement remain undeveloped.

  2. The evidence linking reduced discrepancy to robust unlearning savings remains limited. If I didn't miss anything, the paper provides no quantitative connection between Wasserstein discrepancy and unlearning effort. Parameter-space and clean-prediction discrepancies can also move in opposite directions: in MNIST at (q=0.2), the former decreases by 3.92% while the latter increases by 3.50%. The reported average step reductions of 3.18% and 4.50% are driven mainly by SalUn; GA, GA+FT, and DELETE remain nearly unchanged, while FT worsens at (q=0.05). SalUn is also the only method with unsuccessful runs, yet its failure counts and maximum unlearning-step budget are not reported. Because the averages condition on success and can compare different subsets of runs, they do not establish an unconditional or statistically reliable paired improvement. Uncertainty estimates for the step differences are also missing. Moreover, noise remains active during unlearning, so the experiment changes both the starting models and subsequent update dynamics; it does not isolate whether smaller initial discrepancy causes the savings. Success additionally requires low forget-set accuracy without a retain-accuracy constraint. These limitations, several of which the authors acknowledge, weaken the practical interpretation of the reported conditional savings.

Questions for authors
  1. Do the authors agree with the exact noiseless-training equivalence above? What do the readout results establish beyond this equivalence? At matched clean predictive accuracy, do the discrepancy reductions—particularly under interleaved noise—persist against noiseless baselines with tuned learning rates, regularization, and training horizons?

  2. Can the authors provide absolute Wasserstein distances and numerical values of the theoretical bounds for representative experimental settings? Is there a tested regime where a useful common contraction bound can be justified, or where the general propagation factors in Theorem 1 quantitatively explain the observed reductions?

  3. How many SalUn runs fail under each condition, and what is the maximum update budget? Please provide paired step differences with uncertainty estimates, account for unsuccessful runs, and assess whether the benefits persist at comparable retained-data accuracy.

  4. What evidence separates the effect of the starting-model discrepancy from changes to the unlearning dynamics caused by retaining the channel during unlearning?

3 comments
AuthorsOpenReview ↗

Response to Reviewer 57sw - 1

We sincerely thank the reviewer for the thoughtful and constructive feedback. We address your feedback in detail as follows.

W1&Q1. We agree with the exact noiseless reformulation of affine readout noise under squared loss. Our motivation is to understand training under the residual noise present in quantum execution. Residual device noise may remain after control and mitigation, so ideal noiseless execution is not a freely available alternative. The noiseless reformulation clarifies the interpretation of the readout effects, while our analysis characterizes how the physical channels present during execution affect the full-data/retrained discrepancy.

To assess whether the observed reductions persist against adjusted noiseless training, we additionally compare with original-target clean baselines whose learning rate, regularization, and training horizon are selected using validation data only. For both full-data and retrained ensembles, validation accuracy is evaluated using the same channel-free readout and must be within one percentage point of the corresponding noisy-trained reference. Among eligible candidates, we select the setting with the lowest validation MSE, averaged across the full-data and retrained models.

Placement / channelParameter Wν/W0′W_\nu/W_{0'}Clean-prediction Wν/W0′W_\nu/W_{0'}
Readout depolarization 0.20.748±0.2310.748\pm0.2311.024±0.0611.024\pm0.061
Interleaved amplitude damping 0.040.529±0.1420.529\pm0.1420.853±0.1290.853\pm0.129

Here, W0′W_{0'} denotes the validation-selected noiseless reference for condition ν\nu, in the corresponding parameter or prediction space. It differs from the fixed noiseless reference W0W_0 in the original experiments. Thus, relative to the validation-selected noiseless controls within the specified clean-validation-accuracy window, the parameter space discrepancy reductions persist on average in parameter space for both tested settings.

To reflect the discussion, we revised our paper: Line 298 and Appendix C.5.

AuthorsOpenReview ↗

Response to Reviewer 57sw - 2

W1&Q2. We evaluated the measured-update counterpart of the recursive envelope in Theorem 1, Eq. (9), without imposing a common contraction factor, and added estimated-envelope comparisons to Figures 2 and 3. The calculation uses measured deletion-induced update perturbations and the RMS propagation factors obtained by applying the same retained-data update to both members of each trajectory pair. Thus, it accounts for both newly introduced deletion perturbations and their subsequent propagation, rather than using only the channel-dependent factors in Table 1.

For a concrete numerical comparison, the normal-deletion readout evaluation covers nine configurations across five partitions, with 1,024 paired initializations per partition. Under the original Experiment 1 optimization settings, the following parameter-space values are obtained after 120 updates:

Readout conditionEmpirical W2W_2Paired RMSEmpirical envelope
Clean0.2054±0.04130.2054\pm0.04130.2056±0.04140.2056\pm0.04140.3141±0.08240.3141\pm0.0824
Depolarization (q=0.20q=0.20)0.1799±0.04500.1799\pm0.04500.1799±0.04500.1799\pm0.04500.2580±0.08210.2580\pm0.0821

The envelope-to-W2W_2 ratios, computed within each partition before averaging, are 1.514±0.1061.514\pm0.106 and 1.415±0.1031.415\pm0.103, respectively. Throughout this response, ±\pm denotes the sample standard deviation across the five partitions. In these representative settings, the empirical envelope is therefore approximately 1.4–1.5 times the observed distance, rather than orders of magnitude larger, and both decrease under depolarization.

We also investigated whether discrepancy reductions persist in a setting with consistently contractive empirical RMS propagation. Table 4 motivates this distinction: stronger readout amplitude damping reduces the fraction of RMS-contractive steps, illustrating how weaker propagation control can offset a smaller deletion perturbation.

We screened regularization and learning-rate combinations using validation accuracy and measured RMS propagation on a subset of the existing initialization cohort. We then evaluated the selected setting, λ=0.1\lambda=0.1 and η=0.1\eta=0.1, using all 1,024 paired initializations per partition and retaining the other Experiment 1 settings. The additional depolarization and amplitude-damping sweeps cover strengths up to 0.40.4 for readout placement and 0.160.16 for interleaved placement. Across all evaluated partitions, noise settings, and steps with nonzero paired separation, c^k<1\widehat c_k<1, with observed maxima of 0.9990.999 for readout and 0.9960.996 for interleaved placement.

Discrepancy reductions persist relative to the noiseless reference trained with the same λ=0.1\lambda=0.1 and η=0.1\eta=0.1:

Regularized conditionParameterClean prediction (Φ0\Phi_0)Noise-matched prediction (Φν\Phi_\nu)
Readout depolarization (q=0.20q=0.20)0.870±0.0320.870\pm0.0320.908±0.0490.908\pm0.0490.727±0.0390.727\pm0.039
Interleaved amplitude damping (γ=0.16\gamma=0.16)0.629±0.0620.629\pm0.0620.716±0.1070.716\pm0.1070.450±0.0560.450\pm0.056

Each entry is the within-partition ratio Wν/W0\mathcal W_\nu/\mathcal W_0 in the indicated space, averaged across partitions. In particular, the interleaved reductions occur in both parameter and clean-prediction spaces, so they are not solely due to evaluation-time attenuation.

The additional regularization entails an accuracy trade-off. At readout depolarization q=0.20q=0.20, mean full-data test accuracy changes from 79.37%79.37\% under the original optimization settings to 75.88%75.88\% under the regularized settings. At interleaved depolarization q=0.16q=0.16, it changes from 78.88%78.88\% to 74.69%74.69\%. These comparisons hold the noise condition fixed while changing the optimization settings.

Together, these results provide a numerical connection between the deletion–propagation decomposition and the observed discrepancy, and identify tested settings where discrepancy reductions coexist with consistently contractive empirical RMS propagation. These finite-ensemble measurements are distinct from establishing Corollary 1's uniform contraction assumption over a parameter region. The revised paper presents the estimated-envelope comparisons in Figures 2 and 3 and the additional regularized experiments in Figure 5 and the accompanying paragraph in Appendix E.3. And we provide absolute Wasserstein distances and numerical values of the theoretical bounds for Experiment 1 in Appendix E.4.

W2, Q3&Q4. We address these points in our common rebuttal, together with related concerns raised by other reviewers.

Dear Reviewer 57sw,

Thank you very much for your time and thoughtful feedback throughout the review process. As the ICLR discussion period is approaching its end, we would be happy to address any remaining questions or concerns you may have. We sincerely appreciate the time and effort you have devoted to reviewing our work.

Best regards,
The Authors

Comments on the paper

3 comments
AuthorsOpenReview ↗

Common Rebuttal on Section 5 - 2

3. Updated findings for both depolarization and amplitude damping.

The following table summarizes all four evaluated noise settings. The initial parameter-space discrepancy ratio compares full-data/retrained distributions under each training condition with their noiseless counterpart. Cost reduction is the equally weighted mean of the five methods' relative reductions in mean first-hit update counts; positive values indicate fewer updates. Brackets give the reported nominal 95% bootstrap confidence intervals.

Training noiseInitial parameter-space W2W_2 ratioCost reduction: noiseless unlearningCost reduction: noise-matched unlearning
Depolarization, q=0.05q=0.050.9895 [0.9858, 0.9932]1.93% [−1.41, 5.13]2.90% [−0.27, 5.84]
Depolarization, q=0.20q=0.200.9622 [0.9539, 0.9711]4.35% [−0.76, 9.26]6.55% [1.55, 11.25]
Amplitude damping, γ=0.02\gamma=0.021.0135 [0.9998, 1.0274]2.40% [−2.82, 6.74]0.72% [−5.04, 5.55]
Amplitude damping, γ=0.08\gamma=0.081.0045 [0.9800, 1.0278]11.66% [8.36, 14.64]−1.94% [−9.25, 4.59]

Depolarization: smaller initial discrepancy and lower mean update counts. Mean update counts are lower for all five methods under both unlearning regimes. The updated result is also not solely driven by SalUn. Under noise-matched unlearning at q=0.20q=0.20, FT decreases from 201.35 to 161.66 mean updates, while SalUn decreases from 50.01 to 44.65. GA, GA+FT, and DELETE exhibit smaller absolute changes.

Amplitude damping: cost savings depend on the subsequent unlearning regime. At both tested strengths, the confidence interval for the initial parameter-space discrepancy ratio includes one. Nevertheless, at γ=0.08\gamma=0.08, noiseless unlearning yields an aggregate cost reduction of 11.66%, with an interval of [8.36, 14.64]%. Under noise-matched unlearning, the estimate is −1.94%, with an interval of [−9.25, 4.59]%, which remains compatible with either savings or increases. Thus, amplitude damping provides evidence of optimization savings in one regime without clear evidence of a reduction in initial parameter-space discrepancy, rather than a regime-independent benefit.

Together, the two channels provide complementary findings. Depolarization exhibits a more consistent joint pattern of smaller initial parameter-space discrepancy and lower mean update counts, whereas amplitude damping shows that cost savings can occur without evidence of a discrepancy reduction and can change with the unlearning dynamics. These observations motivate studying starting discrepancy jointly with method-specific update dynamics. In light of these observations, we have revised the paper's title and refined the presentation of our contributions to more clearly communicate the scope and key findings of our work.

AuthorsOpenReview ↗

Common Rebuttal on Section 5 - 1

We sincerely thank all reviewers for their time and thoughtful, constructive feedback. Each review has provided valuable suggestions for strengthening our work, and we have made every effort to address them through additional analyses, expanded experiments, and revisions to both the main text and the appendix. All changes in the revised manuscript are marked in blue for ease of reference. We welcome further questions and suggestions during the remainder of the rebuttal period and would be glad to consider them carefully as we continue to clarify our findings and improve the manuscript.

Several reviewers raised related concerns about Experiment 2, particularly the effect of retaining noise during unlearning, the success-conditioned SalUn results, and the uncertainty of the reported cost reductions. We address these shared concerns below and summarize the corresponding revisions to Section 5 and its accompanying appendix.

Our theoretical analysis characterizes how noise changes the discrepancy between full-data and retrained model distributions before any unlearning update. Experiment 2 complements this analysis by examining whether these changes are accompanied by lower unlearning optimization costs. The revised evaluation strengthens this connection while distinguishing the effects of training noise from those of noise during unlearning.

1. Comparing noiseless and noise-matched unlearning from the same pretrained checkpoints.

The original noise-matched setting was motivated by the practical scenario in which training and unlearning take place under the same noise conditions. However, we agree that this setting changes both the starting checkpoint and the subsequent unlearning dynamics.

We therefore now evaluate each pretrained checkpoint under both noiseless unlearning and noise-matched unlearning, with the latter retaining the channel and strength used during training. Both regimes use the same clean forgetting criterion and method-specific optimization settings. This comparison tests whether lower update counts persist when noise is removed during unlearning. It separates dependence on the active channel during unlearning from differences induced by training, although these training-induced differences are not limited to the initial Wasserstein discrepancy.

2. Revising the SalUn update schedule and expanding the paired evaluation.

In our QNN adaptation of SalUn, the number of retained-data updates per cycle is a configurable hyperparameter. The original schedule used 7 forget-set updates with randomized incorrect labels, followed by 57 retained-data updates. We observed that this long retained-data phase could increase forget-set accuracy and counteract the preceding forgetting updates. We therefore shortened the retained-data phase to 14 updates.

The revised schedule is applied uniformly across all evaluated conditions, including the rerun noiseless baseline. Thus, the updated comparisons use the same SalUn configuration across conditions; they do not compare revised noisy runs against the earlier noiseless results.

We also increased the evaluation from 40 to 80 paired runs per condition, using 16 initializations across five data partitions. Comparisons remain paired by partition and initialization. All 80 runs now reach the specified forgetting criterion in every evaluated combination: clean forget-training and forget-validation accuracies must both be at most 3%. Consequently, the updated means include the complete evaluated cohort, without excluding unsuccessful runs or comparing different successful subsets. The revised appendix reports per-method paired step differences with confidence intervals.

AuthorsOpenReview ↗

Summary of Revisions

Summary of Revisions

We thank the reviewers for their constructive feedback. We have refined the claims, added controls, connected theory with experiments, and strengthened unlearning-cost evidence. All revisions are highlighted in blue.

1. Refined Framing and Scope (Title, Sections 1, 3, 6; suggested by Reviewer JBBd)

  • Changed the title from “How Noisy Training Reduces Model Discrepancy in Quantum Machine Unlearning” to “How Quantum Noise Shapes Model Discrepancy in Quantum Machine Unlearning” and related statements. This emphasizes our central contribution: explaining how quantum noise affects discrepancy and identifying conditions for meaningful reductions.

2. New Empirical Distinguishability Probes (Appendix B.6; suggested by Reviewer JBBd)

  • Added classifier two-sample tests (C2ST) and membership-inference (MIA) probes on clean original and retrained predictions, complementing the existing fixed-QNN counterexample.
  • For MNIST at q = 0.20, parameter W2W_2 is reduced (ratio 0.957), yet C2ST remains 100% and MIA ROC-AUC remains near 1. Thus, smaller geometric discrepancy does not imply lower distinguishability or certified unlearning.
  • Clarified that pre-to-post discrepancy is measured before unlearning. Exact-expectation channels deterministically alter training, whereas finite shots add stochastic gradient errors. Native noise does not imply DP guarantees or certified removal.

3. Stronger Noiseless Controls (Appendix C.5; suggested by Reviewers 57sw and JBBd)

  • Added original-target noiseless controls tuned over learning rate, regularization, and training horizon. Full-data and retrained validation accuracies each match their noisy references within 1 percentage point under clean evaluation.
  • At matched accuracy, noisy/adjusted-noiseless parameter-space W2W_2 ratios are 0.748 ±\pm 0.231 (readout depolarization, qq = 0.20) and 0.529 ±\pm 0.142 (interleaved amplitude damping, γ\gamma = 0.04). Corresponding clean-prediction ratios are 1.024 ±\pm 0.061 and 0.853 ±\pm 0.129.
  • We clarify the exact noiseless reformulation of affine readout noise under squared loss. Importantly, the accuracy-matched controls suggest that the observed parameter-space discrepancy reductions can persist at comparable predictive accuracy, although their magnitude depends on the baseline. These findings reinforce the significance of studying how native quantum noise shapes model discrepancy beyond conventional predictive performance.

4. Quantitative Theory and Experiment Connection (Figures 2, 3, 5, Appendices E.3, E.4; suggested by Reviewers 57sw, zx2N, and JBBd)

  • Added trajectory-level estimated envelopes (estimated upper bound) from measured deletion perturbations and RMS propagation. At qq = 0.20, readout empirical W2W_2 decreases from 0.2054 to 0.1799, while its estimated envelope decreases from 0.3141 to 0.2580.
  • Added regularized experiments (λ\lambda = 0.1, η\eta = 0.1) with RMS-contractive propagation at every evaluated nonzero-separation step. For interleaved amplitude damping (γ\gamma = 0.16), parameter and clean-prediction ratios are 0.629 ±\pm 0.062 and 0.716 ±\pm 0.107. We report accuracy trade-offs and distinguish observed contraction from uniform contraction.

5. Extended Circuit and Noise-Model Evaluations (Appendix E.5; suggested by Reviewer JBBd)

  • Added experiments with deeper interleaved circuits and more realistic noise simulations, including calibration-informed relaxation and dephasing based on IBM Manila, coherent ZX overrotation, and spectator ZZ crosstalk.
  • Under calibration-informed noise, parameter-space discrepancy ratios remain below one (0.875 to 0.925) across three circuit configurations, while clean-prediction discrepancies remain near the noiseless reference. Coherent overrotation produces little change, whereas crosstalk tends to increase discrepancy. These results further support our analysis of how different quantum noise mechanisms shape model discrepancy.

6. Stronger Unlearning-Cost Evaluation (Section 5, Appendix F; suggested by Reviewers 57sw, zx2N, and JBBd)

  • Increased MNIST evaluation from 40 to 80 paired runs per condition, uniformly shortened SalUn’s retained-data phase from 57 to 14 updates per cycle, and added paired bootstrap confidence intervals. All 80 runs satisfy the forgetting criterion in every condition (There are no failure cases for SalUn).
  • Under depolarization (qq = 0.20), all five methods require fewer mean updates, with aggregate reductions of 4.35% under noiseless unlearning and 6.55% under noise-matched unlearning.
  • Under amplitude damping (γ\gamma = 0.08), starting parameter W2W_2 is essentially unchanged (ratio 1.0045), yet cost reduction is 11.66% under noiseless unlearning versus −1.94% under noise-matched unlearning. This reveals dependence on subsequent unlearning dynamics.

We appreciate the reviewers’ feedback, which has strengthened our work.

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

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