- Rating
- 2(−1)
- Confidence
- 2
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 2
Read review
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
- 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.
- 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.
- 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.
- 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
- 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).
- 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.
- 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.
- 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.
- 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.
- 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
- 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?
- 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?
- 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?
- 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?
- 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?
- 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
Response to Reviewer JBBd - 2
W2&Q1. We agree that affine readout noise admits a noiseless reformulation. For exact-expectation GD under squared loss and , this requires targets , learning rate , and regularization . 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 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 / channel | Parameter ratio | Clean-prediction ratio |
|---|---|---|
| Readout depolarization () | ||
| Interleaved amplitude damping () |
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 , we additionally evaluate the two requested learning rates while retaining the original targets and . At each learning rate, we compare with a common full-data/retraining horizon selected solely to match mean displacement from initialization. All ensembles match their noisy references within .
| Noiseless learning rate | Clean horizon | Parameter ratio | Clean-prediction ratio |
|---|---|---|---|
| Fixed: | |||
| Displacement-matched: – | |||
| Fixed: | |||
| Displacement-matched: – |
After matching displacement, both requested learning-rate controls yield mean parameter-discrepancy ratios below one. The noisy full-data/retrained mean displacements are , versus for nominal noiseless training. Both tables report the mean 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, denotes the parameter-space ratio relative to noiseless training.
| Dataset | Training condition | C2ST | MIA ROC-AUC | |
|---|---|---|---|---|
| Iris | Noiseless | 1.000 | 93.48% | 0.5957 |
| Iris | Readout depolarization () | 0.884 | 90.82% | 0.5872 |
| Iris | Readout amplitude damping () | 1.064 | 86.91% | 0.5678 |
| Iris | 32-shot training | 1.179 | 89.65% | 0.5944 |
| MNIST | Noiseless | 1.000 | 100% | 0.9991 |
| MNIST | Readout depolarization () | 0.9570 | 100% | 0.9993 |
| MNIST | Readout amplitude damping () | 1.0102 | 100% | 0.9989 |
Under depolarization, parameter and C2ST both decreased in the point estimates on Iris and MNIST, while MIA changed little. For MNIST, depolarization reduced parameter by 4.3%, yet C2ST remained at 100% and MIA remained near 1. For 32-shot training on Iris, parameter 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.
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 were added to Figures 2 and 3.
At 120 updates, the normal-deletion readout results are:
| Condition | Empirical | Paired RMS | Empirical envelope |
|---|---|---|---|
| Clean | |||
| Depolarization () |
Values are means and sample SDs across five partitions, each with 1,024 paired initializations. The within-partition envelope-to- ratios average and , respectively. Thus, the envelope is approximately 1.4–1.5 times the observed distance, and both decrease under depolarization.
Additional regularized experiments (, ; Figure 5) show at all evaluated steps with nonzero paired separation, with observed maxima of for readout and for interleaved placement. Discrepancy reductions persist relative to the corresponding regularized noiseless reference: interleaved amplitude damping at , for example, gives parameter- and clean-prediction-space ratios of and . 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 and valid bounds ,
\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.
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 W2 is 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 W2, 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.