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Paper summary
This paper looks at how to split a finite shot budget across inference iterations in quantum deep equilibrium models (QDEQs). The authors first use Proposition 1 to show that Broyden's secant differences get hard to resolve under finite shots. Then they switch to damped Picard iteration. Under a linearized error-propagation model, they derive the terminal MSE, average the coefficients over a calibration set, and use greedy marginal allocation to compute an integer shot schedule offline, which is then frozen. Experiments cover 11 checkpoints. Compared with uniform allocation, the schedule cuts terminal squared error by 25.2%–33.9%. They also compare Picard against Broyden under shared budget caps.
Critical strengths
- The problem setup is clean and the theory hangs together.
- The linear proxy gives reasonable aggregate predictions.
- The writing is well organized and easy to follow.
Critical weaknesses
- The novelty of the core result gets undercut by the authors' own ablations, so the claimed contribution doesn't match the title and abstract. Section 5.4 and the conclusion both admit that the Dynamics-only and Full schedules are nearly identical, and Full shows no resolvable gain over Dynamics-only.
- All experiments are in idealized finite-shot sampling simulations, yet the motivation and conclusions are about real quantum hardware.
- The linearization assumption isn't properly stress-tested, and calling Theorem 1 "exact" is too strong.
Questions for authors
- What does your method buy you over a simple two-parameter ramp-up heuristic?
- What's the break-even point for the calibration cost? On real hardware, where you can't get J_t exactly, how many extra shots would you need to estimate Φ_{T,t+1}, and is that worth it compared to the online shots you save?
4 comments
Response to cdet (2/2): Ramp comparisons and calibration costs
This response compares terminal-aware allocation with tuned ramp heuristics (Q1) and reports calibration costs and conditional break-even estimates (Q2).
Q1: What does the method buy over a two-parameter ramp?
Our method derives model-specific temporal weights from terminal propagation, computes budget-exact allocations, and supplies a quantitative risk objective; a ramp prescribes a functional shape. We claim task-dependent adaptability, not universal superiority over tuned heuristics.
For , Ramp-Proxy selects among 735 frozen candidates using Full's tuning-split coefficients; Ramp-Validation uses finite-shot tuning MSE over 35 candidates. Neither uses formal-test data. Ramp-Proxy compares function families and is not calibration-free.
In the illustrative case , , with constant covariance, and, for the continuous optimum with inactive shot bounds, . Thus propagation can yield increasing schedules. Across 11 checkpoints, the descriptive fit has – (median 0.9969); this is not a method assumption. Across 55 checkpoint–budget cells, Full minimizes the registered linear proxy, while Ramp-Proxy is close: has mean 0.599%, median 0.351%, and range 0.160%–2.585%. Schedule distance has median 0.0506 (range 0.0306–0.1130). These near-geometric profiles explain the near parity. Specifically, Full has no resolved realized-MSE advantage over the tested ramp on the original benchmarks.
On three independently trained PneumoniaMNIST checkpoints, the calibrated profiles are nonmonotone. Ramp-Proxy selects (Uniform) in all 15 cells. Its proxy gap to Full is 11.2%–23.3%; even the best budget-exact nondecreasing integer schedule retains an 8.7%–23.3% gap. In addition, Full's measured MSE point estimates are lower in all 15 cells. At budgets 6,400, 12,800, 25,600, 51,200 and 102,400, mean reductions are 17.45%, 16.38%, 22.10%, 20.07% and 13.30%, respectively.
External tasks: matched inference-shot budgets.
| Dataset | Full vs. Ramp-Proxy | Full vs. Ramp-Validation |
|---|---|---|
| BloodMNIST | 1.90% [0.92%, 2.89%] | 5.01% [1.47%, 8.54%] |
| OrganAMNIST | 2.17% [0.10%, 4.24%] | 3.90% [0.56%, 7.23%] |
These post-hoc descriptive reductions average five budgets within each checkpoint, then use Student- intervals over four checkpoints, unadjusted for multiple comparisons. We will state the task-dependent conclusion explicitly: propagation explains when a ramp is an accurate compression and when monotonicity is restrictive.
Q2: Hardware calibration cost and conditional break-even
Hardware break-even requires device-level measurements of calibration and execution costs. We therefore report no hardware break-even point and have instead expanded the computational analysis of our calibration strategy. Specifically, our sample-only calibration avoids reconstructing full or . For fixed readout , the damped transition satisfies
.
Terminal impacts use -dimensional directional responses . Joint-bitstring samples estimate pilot trajectories, covariances and normalized two-state probe responses. The schedule is then frozen, requiring no online derivative queries.
With , , and shots/probe state, the total calibration cost in joint shots is .
Against exact calibration on the same eight inputs, sampled calibration gives a mean paired relative terminal-MSE improvement of 0.216% (descriptive 95% Student- CI [−2.243%, 2.675%]; three frozen 4/10-qubit checkpoints, budgets averaged within checkpoint). Neither is resolved as better.
Conditional amortization. For common terminal-error target and baseline ,
,
provided both differences are positive and costs use the same unit. Targets are frozen on tuning data; online shots are estimated only from exact observed matches or unique in-range log-log interpolation.
| Checkpoint | Calibration shots | Shots saved/input vs. Uniform | Break-even inputs |
|---|---|---|---|
| FashionMNIST-4 | 409,600 | 7,849 | 52.2 |
| MNIST-4 | 409,600 | 7,823 | 52.4 |
| MNIST-10 | 716,800 | 7,778 | 92.2 |
These conditional simulator-query estimates imply approximately 53–93 subsequent inputs, assuming equal cost per joint outcome and calibration validity across deployments. This also highlights the limited scalability of statevector-based backends to circuits that are classically intractable to simulate.
Thank the author for the detailed response. I read your response and reviewed your paper.
Overall, the authors put in a lot of extra work, but honestly, only CW3 really got addressed (according to my understanding).
- In CW1, they admit Full is approx. to Dyn-only and reframe the contribution as "downstream propagation". But in their Q1 reply, they also admit Full has no resolved edge over a tuned ramp on the original 3 benchmarks.
- In CW2, basically just acknowledged. They'll add a scope statement to the abstract, but there are no noisy sims at all. Their own bias experiment (in the reply to xfVQ) has bias eating 81–94% of terminal risk, which kinda works against them.
- In Q1, Half-answered. No win over the ramp on the original benchmarks; the only win is on PneumoniaMNIST. But there Ramp-Proxy collapses to Uniform, so that's really Full vs. Uniform again. Also, Ramp-Proxy uses Full's coefficients, so it isn't calibration-free either.
- Q2, No HW break-even. What we got is a sampling-based calibration scheme plus a simulator-level estimate of ~53–93 inputs, and the baseline for that estimate is Uniform, not a cheap heuristic.
Therefore, I'll keep my score.
Thank you for rereading our responses and for acknowledging that CW3 has been addressed. We agree that hardware validation and end-to-end cost advantages remain open. We would like to clarify the additional ramp comparisons and the scope of the noise experiments.
1. CW1/Q1: The external ramp evidence extends beyond PneumoniaMNIST.
We agree that the original benchmarks show no resolved Full advantage over Dynamics-only or Ramp-Proxy. Terminal propagation and the budget-exact allocator are already part of the original formulation (Secs. 3.2 and 4.2), Our ablations and additional comparisons characterize when simpler schedules approximate the derived allocations and when model-derived schedules provide additional benefit.
In addition to PneumoniaMNIST, our Q1 response reports the following reductions in measured terminal MSE at matched online shot budgets (Appendix H.4, Table 13):
| Dataset | Full vs. Ramp-Proxy | Full vs. Ramp-Validation |
|---|---|---|
| BloodMNIST | 1.90% [0.92%, 2.89%] | 5.01% [1.47%, 8.54%] |
| OrganAMNIST | 2.17% [0.10%, 4.24%] | 3.90% [0.56%, 7.23%] |
Effects are averaged over five budgets within each checkpoint; brackets are descriptive, unadjusted 95% Student-t intervals across four checkpoints per dataset. These post-hoc comparisons support modest, task-dependent gains over the tested ramp baselines, without establishing an end-to-end cost advantage.
Ramp-Proxy uses Full’s coefficients to probe the restriction imposed by the ramp family. Ramp-Validation instead selects among 35 candidates using finite-shot tuning MSE without Full’s impact coefficients; its tuning and reference-evaluation costs are not assumed free. On PneumoniaMNIST, Ramp-Proxy does select Uniform, so those measured comparisons numerically coincide. The BloodMNIST/OrganAMNIST comparisons provide additional evidence involving both tested ramp baselines.
2. CW2: Specified readout‑noise simulations and their limitations.
Our added simulations include assignment errors applied to joint measurement outcomes, fixed and iteration‑dependent bias, and cumulative‑shot‑dependent drift (Appendix H.7).
These results identify an error floor that increasing shots alone cannot remove; bias dominance alone does not establish that the allocation is suboptimal. With fixed linear dynamics and allocation‑independent bias and variance coefficients, the bias adds a constant to the risk and leaves the variance‑optimal schedule unchanged. Our separate cumulative‑shot‑dependent drift diagnostic examines when this condition fails and tests total‑risk selection within the same frozen 18‑schedule family. We present it as a known‑channel mechanism test, not hardware validation or evidence of superiority over ramps under drift.
3. Q2: The 53–93-input estimate has a restricted comparator and cost scope.
The 53–93-input figure is a conditional simulator-query amortization estimate against Uniform. It quantifies the inputs needed to recover one schedule-calibration cost, assuming equal cost per joint outcome and continued calibration validity. Target-setting and error–budget characterization costs are excluded.
This estimate does not establish hardware break-even or a cost advantage over cheap heuristics. Appendix H.8 explicitly states the comparator, assumptions, and excluded costs. Its contribution is a concrete accounting of the sampled-calibration procedure under those conditions.
The additional experiments support task-dependent improvements in measured terminal MSE under matched online budgets. We would appreciate consideration of the BloodMNIST and OrganAMNIST comparisons when assessing CW1/Q1.
Response to cdet (1/2): Contribution, hardware relevance, and theorem scope
Thank you for your constructive comments. This response addresses the terminal-aware contribution (CW1), hardware relevance and simulation scope (CW2), and Theorem 1 with nonlinear stress tests (CW3).
CW1: Terminal-aware allocation
We agree that Full and Dynamics-only are nearly tied; this finding refines rather than negates the terminal-aware contribution. Near-matching Full and Dynamics-only performance is consistent with our title and abstract: both use downstream propagation ΦT,t+1, the terminal-risk objective and exact budget allocator. Across 15 task-budget cells, median MSE reductions versus Uniform are 31.81%, 31.51% and 0.04% for Full, Dynamics-only and Uncertainty-only (without propagation; Sec. 5.4). Downstream propagation thus dominates observed allocation gains; this is not a universal dynamics/covariance hierarchy.
Full provides the covariance-aware linearized risk model. Covariance can change absolute risk without changing allocation: common positive scaling of temporal coefficients leaves the optimal schedule unchanged (Sec. 3.3; App. E.3) . Full's measured/predicted MSE ratios are 0.981–1.009 across 15 task-budget means (Sec. 5.2, Fig. 2). In a matched audit, Full lowers prediction error versus uncalibrated Dynamics-only by 5.17% (checkpoint-level 95% CI [2.07%, 8.27%]); checkpoint-specific scalar calibration leaves 0.66% (95% CI [−0.01%, 1.33%]). Covariance primarily calibrates absolute risk here, without establishing an irreplaceable directional advantage. Full provides a reference for testing this simplification. We will clarify risk prediction versus allocation benefit in Sec. 5.4 and the conclusion.
CW2: Hardware relevance and simulation scope
Finite-shot measurement uncertainty is an intrinsic constraint on real quantum hardware, which motivates our study of temporal shot budgeting for QDEQ inference. Finite-shot uncertainty persists for nonzero-variance observables even with ideal hardware. Our main evidence is ideal finite-shot simulation: gate noise, state-preparation error, assignment bias and drift are excluded (App. G.5; Conclusion). App. G.5 also reports the offline trajectory/Jacobian cost. We will state the simulation scope in the Abstract.
Each iteration draws fresh joint bitstrings from the Born distribution at the current noisy state (Sec. 2.1), giving
Cov(μt∣Ft)=StΣY(ztS).
This preserves state-dependent variance and cross-observable correlations, without heuristic Gaussian noise. More shots reduce sampling variance; device bias need not vanish. Synthetic assignment-error stress tests show error floors under fixed or iteration-indexed bias, while cumulative-shot-dependent drift can require bias-aware replanning; these are not device measurements.
Offline calibration uses moments and directional sensitivities; the frozen schedule requires no online Jacobians. Equal joint-shot-budget terminal-error gains are demonstrated in simulation. Device performance, hardware calibration scalability and measured hardware break-even remain open.
CW3: Theorem 1 and nonlinear stress test
Theorem scope. For fixed input and schedule, Eqs. 15–17 concern the linear proxy e~t+1=Jte~t+αξ~t, e~0=0. Reference-trajectory Jt,Ct are deterministic but may vary with t. Square-integrable martingale differences satisfy
E[ξ~t∣F~t]=0,Cov(ξ~t∣F~t)=Ct/St.
Hence, exactly, QT(x;S)=E[∥e~T∥22]=∑t=0T−1at(x)/St. Cross-time second moments vanish; neither Gaussianity nor independence across iterations is required. Nonlinear rollouts contain Taylor remainders and random-trajectory covariance; Appendix E.2 analyzes both discrepancies. This scope is already stated in Theorem 1.
Nonlinear stress test. We evaluate T ∈ {10, 25, 50}, α ∈ {0.05, 0.10, 0.25}, and B ∈ {6,400, 25,600, 102,400}: 81 cells across three frozen checkpoints (one per original task; 72 new cells, nine historical anchors), with five measurement repeats and matched reference endpoints/impact coefficients. Let E be nonlinear terminal MSE averaged over inputs/repeats and Q the proxy averaged over the same inputs. Across Full cells, median E/Q=0.9986, median $\delta_Q=|E-Q|/Q=2.04$%, and 77/81 have $\delta_Q\le10$%. The largest discrepancies are 51.21% (E/Q=1.5121) and 41.04%, both on FashionMNIST-4 at T=50,α=0.25, with B=6,400 and 102,400, respectively. Separately, Full has lower measured terminal MSE than Uniform in 78/81 cells, with 37.41% unweighted mean cellwise relative MSE reduction. Prediction accuracy and allocation utility are distinct. These are descriptive results from three checkpoints; we will report the full sweep, including unfavorable outcomes.