acceptodds
Under review as a conference paper at ICLR 2027

Terminal-Aware Measurement Allocation for Quantum Deep Equilibrium Inference

Abstract

Quantum deep equilibrium models (QDEQs) construct implicit representations through repeated evaluations of a shared parameterized quantum circuit, but finite-shot measurements perturb the numerical information used by equilibrium solvers. We first characterize the measurement precision required to resolve Broyden secant differences at fixed query points, showing that sampling fluctuations can obscure shrinking residual differences near equilibrium. We then study damped Picard inference, which needs no secants, and allocate its shot budget by downstream impact. A locally linearized propagation model combining measurement covariance, readout, and state dynamics assigns each iteration a terminal impact coefficient, and calibration-averaged coefficients yield a shared schedule that is optimized offline, spends the budget exactly, and stays frozen at test time. On image classification benchmarks, the schedule reduces measurement-induced terminal squared error by 25.2%–33.9% relative to uniform allocation at equal budgets; downstream dynamics, rather than full covariance structure, account for most of the gain, and the preferred solver shifts from Picard to tuned Broyden as budgets grow. These results turn the measurement budget of quantum implicit models into an analyzable and controllable resource.

Primary area:
optimization
Keywords:
Quantum deep equilibrium models, Finite-shot inference, Shot scheduling, Stochastic fixed-point methods, Uncertainty propagation

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_cdetOpenReview ↗
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1
Confidence
3
Informativeness
2
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2
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1
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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
  1. The problem setup is clean and the theory hangs together.
  2. The linear proxy gives reasonable aggregate predictions.
  3. The writing is well organized and easy to follow.
Critical weaknesses
  1. 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.
  2. All experiments are in idealized finite-shot sampling simulations, yet the motivation and conclusions are about real quantum hardware.
  3. The linearization assumption isn't properly stress-tested, and calling Theorem 1 "exact" is too strong.
Questions for authors
  1. What does your method buy you over a simple two-parameter ramp-up heuristic?
  2. 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
AuthorsOpenReview ↗

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\Phi_{T,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⁡(μ^t∣Ft)=ΣY(ztS)St\operatorname{Cov}(\widehat{\mu}_t\mid\mathcal F_t)=\frac{\Sigma_Y(z_t^S)}{S_t}.

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\tilde e_{t+1}=J_t\tilde e_t+\alpha\tilde\xi_t, e~0=0\tilde e_0=0. Reference-trajectory Jt,CtJ_t,C_t are deterministic but may vary with tt. Square-integrable martingale differences satisfy

E[ξ~t∣F~t]=0,Cov⁡(ξ~t∣F~t)=Ct/St\mathbb E[\tilde\xi_t\mid\tilde{\mathcal F}_t]=0,\qquad \operatorname{Cov}(\tilde\xi_t\mid\tilde{\mathcal F}_t)=C_t/S_t.

Hence, exactly, QT(x;S)=E[∥e~T∥22]=∑t=0T−1at(x)/StQ_T(x;S)=\mathbb{E}[\lVert\tilde e_T\rVert_2^2]=\sum_{t=0}^{T-1}a_t(x)/S_t. 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 EE be nonlinear terminal MSE averaged over inputs/repeats and QQ the proxy averaged over the same inputs. Across Full cells, median E/Q=0.9986E/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=1.5121E/Q=1.5121) and 41.04%, both on FashionMNIST-4 at T=50,α=0.25T=50,\alpha=0.25, with B=6,400B=6{,}400 and 102,400102{,}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.

AuthorsOpenReview ↗

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 wt=(t+c)γw_t=(t+c)^\gamma, 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 Jt=qIJ_t=qI, 0<q<10<q<1, with constant covariance, at∝q2(T−1−t)a_t\propto q^{2(T-1-t)} and, for the continuous optimum with inactive shot bounds, St⋆∝at∝qT−1−tS_t^\star\propto\sqrt{a_t}\propto q^{T-1-t}. Thus propagation can yield increasing schedules. Across 11 checkpoints, the descriptive fit log⁡aˉt=b+kt\log\sqrt{\bar a_t}=b+kt has R2=0.9217R^2=0.9217–0.99970.9997 (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: [QT(SRamp)−QT(SFull)]/QT(SFull)[Q_T(\mathbf S_{\rm Ramp})-Q_T(\mathbf S_{\rm Full})]/Q_T(\mathbf S_{\rm Full}) has mean 0.599%, median 0.351%, and range 0.160%–2.585%. Schedule distance ∥SFull−SRamp∥1/B\lVert\mathbf S_{\rm Full}-\mathbf S_{\rm Ramp}\rVert_1/B 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 γ=0\gamma=0 (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.

DatasetFull vs. Ramp-ProxyFull vs. Ramp-Validation
BloodMNIST1.90% [0.92%, 2.89%]5.01% [1.47%, 8.54%]
OrganAMNIST2.17% [0.10%, 4.24%]3.90% [0.56%, 7.23%]

These post-hoc descriptive reductions average five budgets within each checkpoint, then use Student-tt 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 JtJ_t or ΦT,t+1\Phi_{T,t+1}. For fixed readout F=RμF=R\mu, the damped transition satisfies

JtR=RKt,Kt=(1−α)Im+α(Dzμt)RJ_tR=RK_t,\qquad K_t=(1-\alpha)I_m+\alpha(D_z\mu_t)R.

Terminal impacts use mm-dimensional directional responses (Dzμt)Reℓ(D_z\mu_t)Re_\ell. Joint-bitstring samples estimate pilot trajectories, covariances and normalized two-state probe responses. The schedule is then frozen, requiring no online derivative queries.

With Ncal=8N_{\rm cal}=8, T=25T=25, Ppilot=Pcov=512P_{\rm pilot}=P_{\rm cov}=512 and L=128L=128 shots/probe state, the total calibration cost in joint shots is Ccal=NcalT(Ppilot+Pcov+2mL)C_{\rm cal}=N_{\rm cal}T(P_{\rm pilot}+P_{\rm cov}+2mL).

Against exact calibration on the same eight inputs, sampled calibration gives a mean paired relative terminal-MSE improvement of 0.216% (descriptive 95% Student-tt 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 ε\varepsilon and baseline HH,

Ndeploy⋆=Coff,Full−Coff,HSH(ε)−SFull(ε)N_{\rm deploy}^\star=\frac{C_{\rm off,Full}-C_{\rm off,H}}{S_H(\varepsilon)-S_{\rm Full}(\varepsilon)},

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.

CheckpointCalibration shotsShots saved/input vs. UniformBreak-even inputs
FashionMNIST-4409,6007,84952.2
MNIST-4409,6007,82352.4
MNIST-10716,8007,77892.2

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):

DatasetFull vs. Ramp-ProxyFull vs. Ramp-Validation
BloodMNIST1.90% [0.92%, 2.89%]5.01% [1.47%, 8.54%]
OrganAMNIST2.17% [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.

Reviewer_3cnTOpenReview ↗
Rating
4(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
3
Read review
Paper summary

From the original work of Schleich et al., the budget allocation was left as a future work direction; however, the motivation was clear: continual measurement of quantum states by the fixed-point solver could lead to a great overhead. This work proposes a well-built ablation study on how the measurement allocation budget affects QDEQ models and, from this, an alternative to reduce the measurement budget. It also includes the impact of QDEQ for different datasets, MNIST-4, FashionMNIST-4, and MNIST-10. The authors also considered the effect that different fixed-point solvers have on the overall budget allocation, which presents additional information for scalable QDEQ models.

Critical strengths

The goal is clear: what must change in quantum deep equilibrium models (QDEQs) for them to scale. Beyond the measurement-budget study the authors propose, the work also uses a different solver because of the noisy nature of quantum circuits. The results on the three datasets showcase promising improvements on the original QDEQ architecture.

Critical weaknesses
  1. The study relies on a frozen DQEQ with a fixed, finite iteration horizon.
  2. The original DQEQ paper only reports Top-1 accuracy, but the authors' reported metrics are their construction under a budget profile of zT.
  3. Out-of-the-box dataset validation.
Questions for authors

Numbered according to "Critical Weaknesses".

  1. Can the authors comment on the possible generalizability of their findings to other similar tasks without the need for a teacher model?
  2. The ultimate goal is the classification of data/images. Authors may want to consider also how Top-1 and Macro-F1 metrics are affected by their proposed measurement allocation framework.
  3. If possible can the authors run their findings on the MedMNIST simply to validate if the budget savings translate to similar tasks.
  4. Beyond classification tasks. The authors' work, for comparative reasons, is based on classification tasks, but classical DQE models have also been used for regression tasks. How well
2 comments
AuthorsOpenReview ↗

Response to 3cnT (1/2): Generalization and classification performance

Thank you for your constructive comments. We appreciate your careful assessment of our work. This response addresses finite-horizon robustness and generalization without a separate teacher model, including schedule transfer (CW1/Q1), as well as end-task classification performance measured by Top-1 and Macro-F1 (CW2/Q2).

CW1/Q1: Finite horizon and teacher-free generalization

The frozen checkpoint and fixed TT adopted in our main experiments represent a deliberate and controlled intervention. This design isolates the error propagation and budget scheduling mechanism. We have not tested adaptive stopping, training-time allocation, or the infinite-horizon equilibrium. To test whether allocation gains hold across finite-horizon settings, we examine a supplementary sweep over T∈{10,25,50}T\in\{10,25,50\}, α∈{0.05,0.10,0.25}\alpha\in\{0.05,0.10,0.25\}, and three budgets, where Full achieves lower terminal MSE than Uniform in 78/81 conditions (mean cell-wise reduction: 37.41%).

We evaluate temporal schedule transfer for generalizability.

Terminal-risk analysis yields a transferable length-25 schedule, applied to an unchanged target QDEQ excluded from its construction, with fresh shots on 128 test images for four-class targets and 200 for MNIST-10 targets, using five repeats. We test four transfer settings: within-task cross-checkpoint transfer, bidirectional MNIST-4 ↔\leftrightarrow FashionMNIST-4 transfer, bidirectional MNIST-4 ↔\leftrightarrow MNIST-10 transfer, and leave-one-checkpoint-out (LOCO) transfer. Transferred schedules still cut terminal MSE by 27–31% versus Uniform in all 20 conditions. For LOCO, the mean point-estimate gap to target-calibrated Full is 0.30%. This descriptive observation does not establish statistical equivalence. It suggests that temporal allocation schedules calibrated on other checkpoints can retain much of the non-uniform allocation benefits when deployed on a target QDEQ.

No separate teacher model is required: calibration references come from the same frozen QDEQ, while transfer uses only a source-derived schedule and no target-model teacher. A new task still requires a compatible trained QDEQ and, for target-calibrated Full, non-test calibration data. Schedule transfer avoids target calibration but inherits source-calibration cost and may lose target specificity.

CW2/Q2: Classification metrics (Top-1, Macro-F1)

Metrics use the same rollouts (11 frozen checkpoints; MNIST-4, FashionMNIST-4, MNIST-10; T=25T=25, α=0.1\alpha=0.1, budgets 6,4006{,}400–102,400102{,}400 and 5 repeats), averaged within checkpoint, with descriptive, unadjusted 95% Student-tt intervals for paired effects (n=11n=11).

MetricUniformFullDiff, 95% CI
Top-180.890%81.192%+0.301 pp [-0.128, 0.731]
Macro-F180.472%80.814%+0.342 pp [-0.105, 0.789]
Exact-prediction flip rate6.122%5.264%-0.858 pp [-1.675, -0.041]

A flip denotes disagreement with the checkpoint's exact Picard-25 prediction, not a label error. Full also cuts terminal latent MSE by 30.78% (95% CI [28.30%,33.26%]), so the larger gain is representational and predictive fidelity, while Top-1 and Macro-F1 gains stay small with intervals including zero.

AuthorsOpenReview ↗

Response to 3cnT (2/2): MedMNIST validation and regression extension

This response addresses external validation on MedMNIST (CW3/Q3) and the extension of terminal-aware allocation to synthetic regression beyond classification (Q4).

CW3/Q3: External validation on MedMNIST

MedMNIST confirms equal-budget improvements in terminal representation fidelity, but it does not establish task-accuracy-level shot savings. We extended evaluation to PneumoniaMNIST, BloodMNIST and OrganAMNIST. Full has lower terminal MSE in all 40 main-budget checkpoint cells across BloodMNIST and OrganAMNIST (20 per dataset) and cuts dataset-level MSE by 13.30%–22.10% across PneumoniaMNIST budgets; matched-error analysis implies ~21% fewer online shots (10/15 scenarios with in-range interpolation) at equal terminal fidelity, with only small, unresolved changes in Top-1 and Macro-F1 and heterogeneous flip-rate shifts. For BloodMNIST and OrganAMNIST, the reported effects are post-hoc descriptive averages over the five main budgets within checkpoint (n=4n=4, unadjusted).

DatasetCkptsExact Top-1MSE cutTop-1 diff
PneumoniaMNIST389.58%13.30%–22.10% (range)+0.036 pp [-0.172, 0.244]
BloodMNIST485.80%2.30% [1.41%, 3.19%]+0.031 pp [-0.032, 0.094]
OrganAMNIST481.35%4.90% [0.90%, 8.90%]+0.005 pp [-0.018, 0.028]

Brackets are descriptive, unadjusted 95% Student-tt intervals across checkpoints; the PneumoniaMNIST MSE entry is a budget range. Classification boundaries resist small latent changes, so lower MSE yields modest Macro-F1 gains. Appendix contains per-budget results, 1,600/3,200-shot runs, and OrganAMNIST’s 13.02 pp validation-test Top-1 gap.

Q4: Extension to regression beyond classification

The solver-aligned regression experiment shows that terminal-aware allocation can improve fidelity to the exact Picard-25 output. In the original-gate-eligible and supplementary all-seed groups, the ground-truth MSE point improvements are 1.00% and 1.75%. We therefore interpret this as an output-fidelity result, not established regression-accuracy improvement.

We add a synthetic scalar-regression benchmark: a QDEQ scalar head learns y=sin⁡(πx1x2)+0.3x32−0.2x4y=\sin(\pi x_1x_2)+0.3x_3^2-0.2x_4, x∼Uniform([−1,1]4)x\sim\mathrm{Uniform}([-1,1]^4), following the Picard-25 (α=0.1\alpha=0.1) protocol. Gate-eligible checkpoints reach R2=0.9812/0.9896R^2=0.9812/0.9896. Across gate-eligible (n=2n=2) and all-seed (n=3n=3) groups, Full reduces terminal latent error by 5.64% / 5.62% and exact matched output error by 2.68% / 3.89%. Thus, the experiment supports improved latent and exact-output fidelity for a continuous head.

In summary, the new experiments establish task-level evaluation of the proposed mechanism: it reduces measurement-induced representation and prediction deviations, with smaller, task-dependent effects on ground-truth performance. Temporal schedules transfer across QDEQ checkpoints without a teacher model. Separately, the classification, MedMNIST, and synthetic-regression experiments show latent-fidelity gains in the reported point estimates.

Reviewer_xfVQOpenReview ↗
Rating
4(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

Quantum Deep Equilibrium Models (QDEQs) is an extension of DEQs with the benefits of a fixed point iterative solver, done in quantum, so that a shallow and small quantum network can be exploited on quantum neural networks. However, finite-shot quantum measurement introduces sampling noise at every step, which affects the classical solver, secant-based solvers via Proposition 1. The authors proposed to damped Picard iteration and Terminal-Aware Shot (TAS) allocation schedule. By unrolling a locally linearized error proxy, they compute temporal weights based on downstream state Jacobians and single-shot covariance. This yields an exact, offline-calibrated discrete allocation problem that distributes a fixed joint-shot budget across iterations. Empirically, TAS reduces terminal representation squared error by 25.2%–33.9% across 11 checkpoints relative to uniform allocation, while ablation studies reveal that downstream dynamical sensitivity, rather than complex quantum covariance, drives the optimization gains.

Critical strengths

I like the author provided Proposition 1. Although it is a proposition, it provides a formal justification for quasi-Newton solver failures during quantum measurements.

Also the models works under finite-shot projection noise than the transient physical gate noise, so that it would be still useful for the upcoming FTQC era. Logical expectation queries will be more expensive.

Critical weaknesses

I have a concern on computational scalability. The offline calibration requires exact classical state vector simulation of Jacobians (∼32\sim 32 GPU-hours for small 4- to 10-qubit circuits). This approach will not scale to classically intractable circuits (e.g., >50>50 qubits) where exact state Jacobians cannot be cheaply computed. Maybe Tensor Network based approximation might be mandatory.

I also have a concern for the confounding effects of the read out structure. The empirical finding that cross-observable covariance does not impact the optimal schedule might be heavily influenced by the specific repeated readout structure used ( R=In⊗1kR = I_n \otimes \mathbf{1}_k ), which structurally cancels out raw off-diagonal correlations at the final step.

Questions for authors
  • Why does a ∼\sim 30% reduction in latent MSE fail to improve classification accuracy? Is the network heavily overconfident, or does the measurement noise tend to scatter representations parallel to the decision boundary rather than across it?

  • The linear proxy relies heavily on the martingale difference property (zero-mean errors). If unmitigated systematic hardware bias is present (i.e., non-zero mean noise), does the presence of an accumulating bias term fundamentally alter the optimal shot schedule?

  • If the readout matrix RR is replaced by a dense, non-orthogonal weight matrix W∈Rd×nW \in \mathbb{R}^{d \times n}, does the contribution of the cross-observable covariance ΣY\Sigma_Y remain negligible, or does directional coupling amplify the importance of measuring covariance?

3 comments
AuthorsOpenReview ↗

Title: Response to xfVQ (1/2): Calibration scalability and covariance effects

Thank you for your careful assessment and constructive comments. This response addresses calibration scalability (CW1) and the role of readout structure and cross-covariance (CW2/Q3).

CW1: Calibration scalability

Our current evidence does not establish calibration scalability for classically intractable circuits. We derived a readout-space recursion that avoids explicit construction of the full latent Jacobian and evaluated a calibration procedure based on sampled measurement outcomes. These results establish feasibility on the tested small models; scalability to classically intractable circuits remains unverified. Tensor-network calibration remains a conditional future direction.

We derived an m×mm\times m readout-space recursion that avoids the full d×dd\times d latent Jacobian, and tested sample-only calibration. For fixed RR and F=RμF=R\mu, JtR=RKtJ_tR=RK_t, where Kt=(1−α)Im+α(Dzμt)RK_t=(1-\alpha)I_m+\alpha(D_z\mu_t)R. Only readout moments and directional responses are needed.

Sampled-calibration evaluation. We evaluated this procedure on three frozen checkpoints with 4 or 10 qubits, comparing it with exact calibration on the same eight calibration inputs. The estimated relative terminal-MSE reduction from sampled calibration is 0.216%, with a descriptive 95% Student-tt interval of [−2.243%, 2.675%]. Budgets are averaged within each checkpoint before aggregation across the three checkpoints. This comparison does not resolve a performance difference between the two calibration procedures.

Calibration uses 409,600 simulator shots for each four-qubit checkpoint and 716,800 for the ten-qubit checkpoint. These costs are separate from the online inference budget. We also clarify that the previously reported 32.13 GPU-hours combines calibration, tuning, and test diagnostics across 11 checkpoints; it is not a measurement of Full-only calibration cost.

Remaining scalability limitation. The sampled-access interface does not eliminate state-preparation costs, sampling requirements, or the statevector complexity of the simulator used in these experiments. We therefore make no claim of demonstrated calibration scalability for classically intractable circuits.

MPS or other tensor-network methods could provide the required moments and directional responses when the relevant reference and probe states remain efficiently representable. Their usefulness would also require sufficiently accurate response estimates and controlled approximation errors. We will discuss this as a conditional future direction.

CW2/Q3: Readout structure and cross-covariance

The dense-readout experiments distinguish the contribution of cross-covariance to risk prediction from its incremental contribution to temporal allocation.

We replaced the repeated readout with fixed dense non-orthogonal matrices and recomputed matched trajectories, Jacobians, covariances and terminal-impact coefficients. Labels 0.15/0.35 are mixing strengths in Wλ=R(I+λM)/∥I+λM∥2W_\lambda=R(I+\lambda M)/\lVert I+\lambda M\rVert_2, where MM is a fixed symmetric, zero-diagonal mixing matrix normalized to unit spectral norm. At the final query, the propagation operator is the identity and the relevant Gram matrix is Wλ⊤WλW_\lambda^\top W_\lambda. Its non-diagonal structure removes the algebraic cancellation of raw cross-covariance terms present under the original repeated readout.

We compare Full with Raw-diagonal, which retains the measured diagonal variances but removes off-diagonal covariance terms when constructing the allocation coefficients.

Full versus Raw-diagonal. Positive values indicate lower error for Full.

λPrediction MAE reduction25-step MSE reduction (95% CI)
0.15+10.47%−0.43% [−1.14%, 0.29%]
0.35+28.46%−0.88% [−3.85%, 2.09%]

The prediction results evaluate both predictors against the same sampled last-query errors. The allocation results evaluate complete 25-step finite-shot inference. Their intervals are descriptive 95% intervals across three selected checkpoints, with five budgets averaged within each checkpoint. Negative point estimates indicate that Full has slightly higher MSE; both intervals include zero.

The allocation objective is Q^(S)=∑taˉt/St\widehat Q(\mathbf S)=\sum_t \bar a_t/S_t, where coefficients are averaged over calibration inputs. A common positive rescaling of all aˉt\bar a_t changes the predicted risk while leaving the minimizing allocation unchanged. Consequently, better risk prediction need not produce a different or better temporal schedule.

These results show a readout-dependent contribution of cross-covariance to quantitative risk prediction. Removing the final-query cancellation does not establish an independently resolved covariance allocation gain in these models, and it does not establish universal covariance irrelevance. Changing the readout also changes the underlying map and its dynamics, so we interpret this as a readout-structure study.

AuthorsOpenReview ↗

Response to xfVQ (2/2): Prediction flips and systematic bias

This response addresses the relationship between representation error and classification behavior (Q1), followed by the effect of systematic bias on shot allocation (Q2).

Q1: Overconfidence or tangential noise?

The observed behaviour arises because Full reduces perturbation magnitude and overall prediction flips, not from blanket overconfidence or a dedicated tangential-noise mechanism; the small net Top-1 gain comes from simultaneous reductions of harmful and beneficial flips.

Accuracy and flip decomposition. Exact/Uniform/Full Top-1 is 82.659%、80.890%、81.192%. Full−Uniform is +0.301 pp (95% CI [−0.128, 0.731]), so no gain is resolved. Full reduces prediction flips by 0.858 pp (CI [−1.675, −0.041]): harmful correct→wrong flips fall 0.442 pp, but beneficial wrong→correct flips also fall 0.141 pp, yielding the +0.301 pp net change. Wrong→wrong flips affect flip rate but not Top-1.

Direction and boundary-crossing controls. For the audited ReLU–linear head, a boundary-crossing analysis using all competing-class margins reproduces the recorded label flips. We additionally compare the actual perturbations with random directions of the same norm within col⁡(R)\operatorname{col}(R):

ScheduleActual noiseRandom control
Full5.264%5.272%
Uniform6.122%6.237%

Here, “Random control” denotes the same-norm random-direction flip rate. The observed rates are close. This control provides no clear evidence that Full gains from a special alignment that preferentially avoids decision boundaries. Its scope is the tested models, perturbation norms, and readout subspace.

Confidence calibration. Before temperature scaling, mean confidence minus accuracy is −1.93 percentage points for Exact, −0.20 for Uniform, and −0.55 for Full. Mean confidence is therefore below accuracy in all three cases. This aggregate diagnostic does not support blanket overconfidence, although it does not exclude miscalibration within subsets of inputs.

Positive scalar temperatures fitted on the tuning set leave argmax predictions—and therefore these label-flip statistics—unchanged. All confidence intervals reported in this Q1 analysis are descriptive intervals across 11 checkpoints.

Q2: Systematic bias

Under fixed linear dynamics and allocation-independent bias and noise coefficients, bias adds an irreducible floor without changing the variance-optimal schedule; allocation-dependent bias can change the schedule.

From e~t+1=Jte~t+α(bt+ηt)\tilde e_{t+1}=J_t\tilde e_t+\alpha(b_t+\eta_t), we obtain

E[∥e~T∥22]=∥α∑tΦT,t+1bt∥22+∑tat/St\mathbb{E}[\lVert\tilde e_T\rVert_2^2]=\lVert\alpha\sum_t\Phi_{T,t+1}b_t\rVert_2^2+\sum_t a_t/S_t.

The squared-bias term is independent of S\mathbf S. Adding it therefore leaves the minimizing allocation unchanged for these fixed variance coefficients. A nonzero accumulated bias cannot be removed by reallocating shots within this model.

We examine two complementary simulation settings.

  1. Bias with frozen schedules. We apply classical bit-flip channels to joint-Z measurement outcomes under fixed or iteration-indexed drift, retaining the frozen Full, Dynamics-only, and Uniform schedules. At B=102,400B=102{,}400, systematic squared bias accounts for 81.4% of Full’s terminal risk under fixed bias and 93.5% under drifting bias. These tests quantify the persistent bias contribution; they do not reoptimize the schedules.

  2. Allocation-dependent drift. We additionally study a synthetic channel whose drift depends on cumulative shot count, using one frozen four-qubit checkpoint and B=25,600B=25{,}600. In this setting, changing the allocation changes the channel encountered by subsequent queries.

Total-risk selection among 18 frozen candidate schedules retains the original Full schedule under the unbiased and stationary conditions. Under increasing and decreasing cumulative-shot drift, it selects different schedules, with estimated MSE reductions of 15.54% and 24.52% relative to the original Full schedule.

Confirmation uses 32 inputs disjoint from calibration. Paired 95% intervals for the corresponding absolute MSE differences, computed over 32 paired repeat means, exclude zero. These intervals describe sampling uncertainty for this frozen checkpoint.

Under decreasing drift, the original Full schedule performs worse than Uniform, and the selected schedule has no statistically resolved improvement over Uniform. The experiment therefore demonstrates that an allocation-dependent channel can make a previously calibrated schedule unsuitable and that total-risk selection can improve upon that schedule within the tested candidate family. It establishes neither hardware performance nor global optimality.

I appreciate the comprehensive rebuttal efforts, including the readout-space sampled calibration, dense non-orthogonal readout tests, flip decomposition, bias/drift studies, and external MedMNIST/regression validations. While end-task accuracy gains remain modest and hardware scalability is still bounded by simulation, it addressed my main technical concerns and the scope and trade-offs of terminal-aware shot allocation. I'll raise my score.

Comments on the paper

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AuthorsOpenReview ↗

Summary of Contributions, Additional Evidence, and Scope — Paper 51498

Dear Area Chairs, Senior Area Chairs, and Program Chairs,

Thank you for overseeing the discussion. We would like to highlight the core contribution and the additional evidence presented in our responses.

Our contribution is a terminal-aware framework linking measurement covariance and downstream dynamics to a linearized terminal-risk objective and budget-exact shot allocation. Across the 15 original task–budget cells, Full and Dynamics-only achieve median terminal-MSE reductions of 31.81% and 31.51% versus Uniform, compared with 0.04% for Uncertainty-only (Sec. 5.4). Both Full and Dynamics-only retain downstream propagation: their near tie limits the demonstrated additional allocation benefit of full covariance, while the ablation identifies propagation as the dominant scheduling signal in these tested settings.

The added comparisons clarify when simple ramps approximate the model-derived schedules and when their shape becomes restrictive. On the original benchmarks, Full has no resolved terminal-MSE advantage over Ramp-Proxy. Nonmonotone profiles on PneumoniaMNIST reveal limitations of the tested ramp family, while the BloodMNIST and OrganAMNIST comparisons provide further evidence of task-dependent allocation gains (Appendix F.5). These findings support the framework’s value in explaining and selecting temporal allocations across different model settings.

We have also clarified in our latest response that the external ramp comparisons include BloodMNIST and OrganAMNIST, alongside the limitations of the noise studies and conditional cost estimates.

Separately, a known-channel synthetic drift diagnostic on one frozen checkpoint illustrates how the terminal-risk analysis can incorporate allocation-dependent bias. Within the same 18-candidate family, the total-risk objective selected different schedules and reduced measured MSE by 15.54% and 24.52% under increasing and decreasing drift, respectively, relative to variance-only selection, which retained Full (Appendix H.7).

Theorem 1 is exact for the stated linear proxy. The nonlinear stress tests assess the proxy’s approximation accuracy in nonlinear finite-shot rollouts, while the schedule-transfer experiments examine the reuse of allocation schedules across frozen QDEQ checkpoints (Appendices H.1 and H.3). The empirical evidence supports improved terminal fidelity in simulation, with small or statistically unresolved improvements in task accuracy.

The revised manuscript preserves the core method and theorem, with targeted main-text clarifications and detailed supplementary protocols and results in the appendices.

We would appreciate your consideration of these findings when assessing the paper’s contribution and scope.

Best regards,

The authors of Paper 51498

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

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