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Paper summary
The paper has a useful premise, especially the observation that noise can increase interaction variance by breaking cancellations. The hardware reach experiment is also a strength. However, several claims need tighter support.
Critical strengths
The problem is well motivated, and the separation of identification, architecture, and noise is a clean way to organize the analysis. The hardware experiment is pre-registered and reports interval-level results rather than only point estimates. The identification result is classical and that their claims of quantum advantage are limited. The grid-reconstruction checks and the global-depolarizing control are useful sanity checks.
Critical weaknesses
- Theorem 1 counts conditional mean evaluations, but computing these from circuit queries has a cost. Appendix A reconstructs the full coefficient tensor. The claimed polynomial cost needs an explicit procedure and access assumptions.
- Standardizing against an initialization ensemble does not establish that the remaining interactions are learned from data. The modest gains over sampled nulls warrant a narrower interpretation.
- Eq. 3 assumes a power law that is not guaranteed by Theorem 3. Cancellation can undermine this model. Report failure cases and compare correction methods at matched total shot budgets.
- The device experiment validates interaction reach, while attenuation and correction remain simulation results. The 30 to 35% discrepancy from the calibrated prediction further limits conclusions about correction on hardware.
- Tab. 3 compares methods targeting different interaction definitions, so agreement with Sobol variances alone does not establish superiority. The product law assumption also limits deployment claims for correlated inputs.
Questions for authors
- For the re-uploading circuits used in the main experiments, do you have an a priori criterion that predicts when the sign condition holds? If not, what fraction of the interactions that drive the completeness residual R_k satisfy it?
- In Tab. 2, do the fitted exponents remain monotone for m=2 and m=3 across all five seeds and all twelve datasets? If not, does the downward bias in R_2 still hold in those cases?
- Is there a version of Theorem 3 that covers amplitude damping, or is the amplitude-damping support purely empirical?
- In Tab. 9, under realistic calibration error, for example δ_q = 0.01, does the two-point estimator still outperform zero-noise extrapolation? Figure 3 suggests that it does not at δ_q above roughly 0.02 for the noise levels where it is preferred, so please report the crossover explicitly for the calibration error expected on ibm_fez.
6 comments
Reply to Reviewer dUMg (part 2)
Request 4.
"The device experiment validates interaction reach, while attenuation and correction remain simulation results. The 30 to 35% discrepancy from the calibrated prediction further limits conclusions about correction on hardware."
We have now measured both attenuation and correction on ibm_fez. The test had to fit within the 10 minutes of IBM's free plan, as we do not have paid hardware access. Three models (, , , seeds 0, 1 and 2, with no selection) ran on all 81 grid nodes of a four-qubit chain with gate twirling. Each circuit was interleaved with its folded copy , which raises the noise, and the hypotheses were fixed before any of these jobs ran.
on ibm_fez.
| Seed | Exact | Measured, | Folded, | Extrapolated |
|---|---|---|---|---|
| 0 | 0.1717 | 0.1566 | 0.1350 | 0.1683 |
| 1 | 0.1263 | 0.1114 | 0.1006 | 0.1173 |
| 2 | 0.1446 | 0.1350 | 0.1235 | 0.1412 |
Folding shrank the higher interaction orders more in all three models and lowered by a factor of 0.893 (95% interval ), and extrapolating from the two noise levels moved towards its exact value in every model. The test is in Appendix H (Table 6) and Section 6.3 of the revised paper, and Section 4.1 corrects the gap to the calibrated prediction to 21% to 36%.
Request 5.
"Tab. 3 compares methods targeting different interaction definitions, so agreement with Sobol variances alone does not establish superiority. The product law assumption also limits deployment claims for correlated inputs."
Because real datasets have no ground truth, Table 3 measures agreement with . To compare the estimators independently of their definitions, we use top- recovery of a planted pair.
Planted-pair recovery (mean standard deviation over five seeds).
| Model | Raw | Shapley interaction | Faith-Shap | |
|---|---|---|---|---|
With one encoding, matches both interaction indices, and with re-uploading it recovers the planted pair more often. For correlated inputs, the residual under each dataset's empirical joint distribution still decreases under device noise in all 60 runs. These results are in Section 6.2, Table 3 and Appendix I (Table 8) of the revised paper.
Request 6.
"For the re-uploading circuits used in the main experiments, do you have an a priori criterion that predicts when the sign condition holds? If not, what fraction of the interactions that drive the completeness residual satisfy it?"
Such a criterion is not needed, because parts (a), (b) and (d) of Theorem 3 and Corollary 4 do not depend on the sign condition. The condition can also be checked directly from the Pauli decomposition of a trained model, and it is rare in practice. On our 60 trained models, the subsets that satisfy it carry on average 0.3% of the variance above order two. Section 5 of the revised paper states this after Theorem 3, and Appendix D reports the fraction.
Reply to Reviewer dUMg (part 3)
Request 7.
"In Tab. 2, do the fitted exponents remain monotone for m=2 and m=3 across all five seeds and all twelve datasets? If not, does the downward bias in still hold in those cases?"
We thank the reviewer for this question. The exponents are not monotone in every model, but the downward bias still holds in most of the exceptions.
Models (out of 60) with , and the non-monotone cases in which still falls at .
| Channel | falls where not monotone | ||
|---|---|---|---|
| Depolarizing | 60 | 60 | no exceptions |
| Amplitude damping | 56 | 51 | 12 of 13 |
| Dephasing | 39 | 43 | 31 of 38 |
Under the calibrated device model, with noise on every gate, decreased in all 120 runs with re-uploading. The main exception is dephasing, which leaves unchanged, as the Limitations paragraph already notes, and these results are in Appendix J (Table 11) of the revised paper.
Request 8.
"Is there a version of Theorem 3 that covers amplitude damping, or is the amplitude-damping support purely empirical?"
Yes, the amplitude-damping case is now proved as Theorem 3(e). For amplitude damping with parameter (, , and a shift along ), the noisy Pauli coefficients are exactly , where is its Pauli transfer matrix, and
which is the bound of Theorem 3(b) with a outside contributing instead of zero.
On 60 trained models, the exact law agrees with simulation to and the bound is never violated. The ordering across interaction orders remains empirical, and it holds in 59 of 60 models at . Theorem 3(e) is in Section 5 of the revised paper, and its proof is in Appendix D.
Request 9.
"In Tab. 9, under realistic calibration error, for example , does the two-point estimator still outperform zero-noise extrapolation? Figure 3 suggests that it does not at above roughly 0.02 for the noise levels where it is preferred, so please report the crossover explicitly for the calibration error expected on ibm_fez."
Thank you for asking for this comparison. At , the two-point estimator outperforms zero-noise extrapolation only from (error 0.0011 against 0.0027), and only when is over-estimated.
Lowest in at which the two-point estimator has the lower error, for a shared over-estimate (exact expectations, five seeds).
| 0 | 0.002 | 0.005 | 0.01 | 0.02 | 0.05 | |
|---|---|---|---|---|---|---|
| Lowest | 0.07 | 0.05 | 0.07 | 0.10 | 0.15 | none |
Judged by the bias it produces, the calibrated ibm_fez model lies below , where the estimator never leads, so on this device we use no correction or two-level exponential extrapolation, neither of which needs . The crossover is in Appendix K (Table 14) of the revised paper.
Thank you again for your close reading. We hope these answers support a positive reassessment.
Reply to Reviewer dUMg (part 1)
We thank the reviewer for the detailed and specific review. We answer each point below.
Request 1.
Both the procedure and the access assumptions are now stated in Appendix A of the revised paper. We assume that we can choose the inputs and that each execution returns one shot of every Zq, combined into Y=b+∑qvqzq with ∣Y∣≤B. At a grid node of S, the other coordinates are drawn from their product law, so E[Y] is the conditional mean at that node, and no coefficient tensor is reconstructed. By Hoeffding's inequality, N≥2B2log(2K/δ)/ε2 shots at each of the K nodes of Theorem 1 give
∣D^S−DS∣≤2Bεcm∣S∣for all ∣S∣≤k, with probability at least 1−δ,
where cm=0.78, 1.57 and 2.46 for m=1, 2 and 3. The total cost KN is therefore polynomial in n for fixed k and m, and at fixed depth Theorem 1(b) also gives the residual itself exactly, at a cost at most linear in n.
Request 2.
Thank you for this comment. We now describe zS only as the excess over the untrained ansatz. Whether the remaining interactions are learned from data is tested separately, by retraining on shuffled labels. The null ratio, the largest interaction of a shuffled-label model divided by that of the trained model, has a mean between 0.04 and 0.70 across datasets, so on every dataset the trained models carry larger interactions (Table 7, formerly Tab. 6). Section 4 of the revised paper states this narrower reading.
Request 3.
Thank you for this suggestion. Eq. 3 is a modelling assumption that Theorem 3 does not imply, and Section 5.1 of the revised paper now states this. We apply it to the order sums Dk with an exponent fitted per model, and at that level it fits closely, with a lowest fit R2 of 0.9967 for depolarizing noise and 0.9857 for dephasing. Failures appear only for individual subsets, as the first table below shows.
Subsets (m=1, order at most three) where DS grows under noise or the power law fits poorly, with their share of variance in parentheses.
The subsets where DS grows are the cancellation case, and they carry little variance except under dephasing. The second table compares the correction methods at matched total shots.
Mean absolute error of R2 at matched total shots per grid node, at device error (calibrated device model, 60 models).
Two-level exponential extrapolation is more accurate than three-level Richardson extrapolation at every budget, and at device error, correction pays off only above about 16,384 shots per node. The failure cases are in Appendix J, and the matched-budget comparison is in Appendix K (Table 13) of the revised paper.