acceptodds
Under review as a conference paper at ICLR 2027

Time-Conditioned Neural Quantum States with Residual-Based Fidelity Bounds

Abstract

Learning quantum dynamics by minimizing the Schrödinger residual raises a basic question: what does the residual imply about state accuracy? We introduce Abel-tNQS, a time-conditioned autoregressive neural quantum state with an exact initial-state constraint, and relate its Hilbert residual to time-averaged fidelity. The complex conditional-amplitude construction preserves normalization and direct sampling, provided the local normalization vectors remain nonzero. A linear Abel bound supplies the remaining-time weight for a separate training surrogate; a cumulative residual form gives a tighter post-training fidelity bound. Full-basis evaluations on small Ising chains yield numerical lower-bound estimates between and , without certified numerical error control. In controlled full-gradient ablations with ten seeds per setting, linear weighting reduces final mean magnetization and nearest-neighbor correlation errors by approximately % and % relative to uniform weighting. After optimizer updates, the hard-linear setting also has lower mean errors in both observables than all three tested soft-penalty settings. Observable benchmarks cover chains of up to spins, an open lattice, segmented continuation, and time-dependent transverse fields.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
neural quantum states, real-time quantum dynamics, autoregressive models, residual-based error bounds, fidelity bounds

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_RJFROpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This manuscript introduces a NQS net called Abel-tNQS. The model is a time-conditioned autoregressive network for representing a quantum-state trajectory over a finite time interval. The initial state is encoded in the complex conditional amplitudes, and the residual loss weights earlier times more heavily. The authors also derive bounds on the time-averaged infidelity. They test the numerical bound estimates on four- to six-spin chains, compare observables on chains up to 20 spins and a 4×44\times4 lattice, and run a ten-seed ablation on the weighting and initial-state constraint.

Critical strengths

In theory, the bounds are explained clearly, including the assumptions needed for them to hold. The ten-spin weighting ablation, using ten seeds per setting, keeps the architecture fixed and matches the equal temporal averages for the linear and uniform weights. Under this setup, the improvement is substantial. Besides, the implementation details make the results easier to assess. For example, the authors specify the gradient convention and state that the larger benchmarks use single realizations.

Critical weaknesses

1. Many ingredients are already in the closest work

Van de Walle et al. already use time conditioning, shared parameters over a time interval, an autoregressive representation, architectural initialization, and segmented continuation. Sinibaldi et al. already derive residual-based bounds on state and observable errors. Both are cited. That leaves the particular conditional-amplitude gate, the T−tT-t weight, and the fidelity formulation as the main additions. The cumulative bound uses unitary propagation and a standard state-distance argument. The factor-of-two improvement in Appendix A.1 is also relative to the specific linear state-distance derivation given there. I would not read it as a general improvement over earlier residual bounds. Table 2 mostly tells me how the designs differ. It does not show whether those differences lead to better training or a more useful error estimate, which is what I would need to judge their significance.

2. No direct comparison with an existing method

The 85% and 94% reductions in observable errors are a good result for the weighting ablation. Both are measured against the authors' own uniform-weight variant, though. I still cannot tell whether someone already using t-NQS would gain much by switching. The soft-penalty runs do not answer this either, since t-NQS already has an architectural initialization layer.

The benchmarks leave the same question open. The nearest-neighbor one-dimensional TFIM remains quadratic in fermions when the transverse field depends on time. For the product-xx initial state, efficient Gaussian reference evolution is available. The two-dimensional example has 16 spins and a Krylov reference. These are useful checks, but the earlier t-NQS paper already reports an 8×88\times8 TFIM and a driven Heisenberg example. The protocols differ, so I would not infer an accuracy ranking from this. Still, the present tests do not demonstrate greater computational reach.

3. The training loss and update rule need a closer check

The bounds use the Hilbert residual norm, while Eq. 13 trains a configuration-mean absolute finite-difference residual. The two can rank nonzero residuals differently. So the derivation gives a reason for the time weight, but it does not tell us how well the actual loss tracks the bound. I would like to know how much it matters in practice.

4. The diagnostic is only validated on four- to six-spin systems

The appeal of the fidelity diagnostic is that it could tell us about state accuracy without the exact trajectory. But the validation uses full-basis sums on four-, five-, and six-spin chains. For the larger systems, the paper reports selected observables. Agreement there does not establish state fidelity, so I still do not know how useful the diagnostic is at those sizes.

Questions for authors
  1. What does the conditional-amplitude gate improve over the t-NQS initialization layer? Can the two be compared under the same compute budget?
  2. Does linear weighting still help with semi-gradient updates? How sensitive is the gain to the residual surrogate, and does it carry through to the Hilbert residual and fidelity-bound estimates?
  3. Can the diagnostic be tested beyond six spins, with an available reference and measurements of sampling variability, cost, and tightness?
4 comments
AuthorsOpenReview ↗

Response to RjFR (1/2): contribution, initialization and native-method comparison

Thank you for the detailed review. We performed quantitative comparisons, objective/gradient controls and reference-state calibration at N=20. This first comment addresses W1-W2 and Q1; the second addresses W3-W4 and Q2-Q3.

Contribution relative to prior work (W1). Abel combines normalized complex-conditional initialization with time-averaged fidelity analysis and the resulting training weight and post-training assessment. Wang et al. use an imaginary-time temporal network to generate parameters of a spatial autoregressive Transformer; our MADE uses additive time conditioning with shared weights. The cumulative bound follows a Duhamel/unitarity argument, building on accumulated-residual control in Sinibaldi et al. The coefficient comparison in the appendix is between our direct fidelity derivation and the stated linear state-distance derivation under exact initialization.

Initialization control (Q1). Van de Walle et al. enforce initialization by blending amplitude and phase outputs in Eq. (7). Abel instead interpolates normalized complex conditional vectors before local normalization. Its path is invariant under integer 2π2\pi relabelings of component phases. For equal-amplitude endpoints with relative phases 0 and π\pi, choosing π\pi or −π-\pi gives orthogonal amplitude/phase midpoints; complex-vector interpolation gives the same midpoint. It still requires a nonzero mixed vector. We will add this example to the appendix.

The experiment isolates this interpolation choice on a common MADE: both arms use fresh shared polar heads, paired initialization/time draws, linear gates, the same objective and 3000 updates. The baseline adapts amplitude/phase interpolation to normalized autoregressive conditionals; this replaces the submitted real/imaginary head in both arms. Complex interpolation increases mean averaged fidelity by 0.002677 and terminal fidelity by 0.009151; all three averaged-fidelity pairs improve. The logit/angle arm gives lower mean observable errors. Optimizer steps take 31.5–33.6 minutes for complex and 30.7–33.8 minutes for logit/angle interpolation on shared GPUs, excluding startup and I/O; the largest within-seed timing difference is 4.94%. The native-code experiment below compares the full tNQG method.

Native-method comparison (W2). We compared native-code tNQG and Abel on the N=10 open chain with J=1, h=0.5, +x initial state and Jt in [0,1]. Each native run includes five windows and all window/global refinements. We evaluated its default 20,000 updates/window and a 1000-updates/window configuration with a compressed cosine schedule. For the latter, independent timing calibrations fixed Abel allowances at 2300/3800/2500 updates before inspecting native accuracies. Abel uses AD, full-gradient MAE, 32 uniform times × all 1024 configurations/update, linear weighting, and LR 1e-4 to 1e-5 halfway through each allowance. Common 101-point normalized full-basis evaluation gives mean ± sample SD over three training seeds:

ConfigurationAveraged fidelityMAE(Mx)MAE(Czz(1))MAE(Czz, r≤5)
tNQG, default budget0.999906 ± 3.8e-057.98273e-05 ± 2.4e-050.000205999 ± 4.3e-050.000373875 ± 0.00021
tNQG, 1000/window0.9114 ± 0.0290.0351624 ± 0.0170.0192067 ± 0.0090.0105097 ± 0.0057
Abel, cost-targeted0.987257 ± 0.00430.00913809 ± 0.00340.0137988 ± 0.00380.0109808 ± 0.004

At the reduced-budget work point, Abel improves averaged fidelity and Mx/nearest-neighbor accuracy; tNQG has slightly lower distance-averaged correlation error. Native process times are 1.93/3.54/2.09 hours versus Abel 1.90/3.39/1.92 hours, including refinements, checkpointing and final evaluation. The two timing calibrations add 0.356 hours. The default native budget reaches averaged fidelity 0.999906 at approximately 24 hours/run (one run includes an interrupted-session cost reconstruction). Runs used shared A100 80GB GPUs: native tNQG uses an RBM/time-basis ansatz in FP64/complex128, whereas Abel uses an FP32 MADE.

The integrable chain gives a controlled reference problem for these comparisons. A reach comparison with the previous 8×8 result calls for matched lattice and evolution-window benchmarks.

AuthorsOpenReview ↗

Response to RjFR (2/2): training objective and state assessment beyond six spins

This second comment addresses the remaining questions raised in your review.

Objective, gradients and weighting (W3, Q2). The Hilbert norm in the bound and the mean-absolute training surrogate are related by D,a≤ρ≤Da\sqrt{D}\\,a\leq\rho\leq D a for the same D-component residual, where a is its complete-basis mean absolute component and rho its Hilbert norm. This population relation does not bound the norm using a finite minibatch. The dimension-dependent factors allow different objective rankings, so we evaluate the physical residual alongside state fidelity. Finite-difference training additionally introduces derivative error; semi-gradients omit differentiation through HψH\psi.

We tested MAE/full, MAE/semi and Hilbert-norm/full under uniform and linear weighting, with three paired seeds per setting: 18 runs. These controls use automatic time derivatives, all 1024 configurations, paired initialization/time draws and 3000 updates. Weights 0.5 and 1-t have equal integrals. Hilbert-norm training uses mean⁡σ∣rσ∣2+10−12\sqrt{\operatorname{mean}_{\sigma}|r_{\sigma}|^2+10^{-12}}; assessment uses the unsmoothed physical residual. The common 401-point evaluation gives:

Objective / updateAveraged fidelity, uniform → linearNumerical cumulative lower estimate, uniform → linear
MAE / full0.97715 → 0.988680.93142 → 0.95612
MAE / semi0.95106 → 0.983580.89785 → 0.95804
Hilbert norm / full0.98301 → 0.990710.95374 → 0.96724

Linear weighting improves averaged fidelity and the cumulative numerical lower estimate in all nine pairs, including semi-gradient and Hilbert-norm training. Mean terminal fidelity decreases slightly in both full-gradient settings. At intermediate checkpoints, some surrogate decreases coincide with worse assessed bounds; this explains why the post-training diagnostic is evaluated separately from training loss.

State diagnostic beyond six spins (W4, Q3). We calibrated the sampled diagnostic on a frozen N=10 control and the submitted N=20 checkpoint. Each assessment uses 201 times, 4096 configurations/time and 32 independent evaluation repetitions. The full-support proposal q(σ)=(pBorn(σ)+2−N)/2q(\sigma)=(p_{\mathrm{Born}}(\sigma)+2^{-N})/2 chooses a Born or uniform branch independently for each configuration. Importance weighting estimates the second moment of the physical residual before the square root and cumulative integration.

The cumulative numerical lower estimates are 0.930741 ± 0.000130 at N=10 and 0.881494 ± 0.000347 at N=20 (mean ± evaluation SD). Reference averaged fidelities on the same grid are 0.978066 and 0.954838; N=20 terminal fidelity is 0.726214. The N=10 full-basis diagnostic is 0.930757. At N=20, complete-state reference propagation is cross-checked against an independent propagator and Gaussian-reference observables. Reference states enter the fidelity calibration; the residual diagnostic is computed from the learned trajectory and Hamiltonian.

The 32 repetitions take 2.15/4.54 shared-GPU hours at N=10/N=20. Increasing nested sample prefixes from 256 to 4096 reduces evaluation SD from 0.000586 to 0.000130 and from 0.001124 to 0.000347, respectively. These prefixes reuse the 4096-sample caches. The N=10 grid-refinement change exceeds its sampling SD, identifying time resolution as an additional source of error.

For numerical certification, independent assessment samples and proved bounds on importance-weighted values would give concentration bounds on residual second moments. Upper enclosures would then propagate through the square root and cumulative functional, together with validated differentiation, normalization, initial-state, quadrature and roundoff errors. The present results are numerical estimates: evaluation SD quantifies sampling variability of a fixed checkpoint and excludes these other errors and nonlinear plug-in bias.

We also assessed the three default-budget native trajectories through the physical residual of their normalized, phase-retaining reconstructed wavefunctions. The common 401-point evaluation gives:

Native seedNumerical lower estimateReference averaged fidelity
1010.999645650.99989051
1020.999617320.99987835
1030.999809620.99995023

Analytic derivatives, finite differences and two coefficient propagators agree numerically, and 201-to-401 grid refinement changes the lower estimates by less than 5e-8. The native overlap matrices are ill-conditioned, so validated linear algebra is an additional requirement for certifying these trajectories.

AuthorsOpenReview ↗

N20 state-level calibration and objective controls

The revised manuscript incorporates the objective and gradient controls from our first response in Section 7.1 and Appendix A.16. All nine N=10 pairs improve averaged fidelity and the cumulative numerical lower estimate under linear weighting, including the semi-gradient and Hilbert-norm settings. Mean terminal fidelity decreases slightly in both full-gradient settings, and some checkpoint comparisons show that a lower surrogate does not improve the numerical lower estimate.

For W4 and Q3, Appendix A.20 now calibrates the sampled diagnostic on two frozen N=20 checkpoints with different state accuracies. The second is the first completed fresh-control endpoint, added after observing energy drift. Both use the same 201 times, 4096 configurations/time, equal Born/uniform proposal, and 32 independent evaluation repetitions:

Fixed N=20 checkpointCumulative numerical lower estimateReference averaged fidelity
Submitted model0.881494 +/- 0.0003470.954838
Fresh fixed-3000 control0.110748 +/- 0.0001600.153132

The diagnostic itself needs the learned trajectory and Hamiltonian, while complete-state evolution supplies the independent fidelity calibration. The reported SD is evaluation sampling variation; differentiation, quadrature, normalization and roundoff require separate error control. The supplement reconstructs the complete reference and both 201-point model evaluations, extending the original four-to-six-spin validation to state-level assessment at twenty spins.

Appendix A.21 adds the completed three-pair N=20 weighting study. Linear weighting lowers correlation errors in every pair but increases mean full-window magnetization error, showing an observable-dependent effect at this budget.

For W1-W2 and Q1, the prior-work discussion is in Section 2 and Appendix A.6; the native tNQG comparison is in Section 7.2 and Appendix A.17; and the conditional-interpolation experiment is a same-MADE component control in Appendix A.18.

AuthorsOpenReview ↗

Follow-up on our responses and revised manuscript

Dear Reviewer RJFR,

We would like to draw your attention to our November 16 follow-up, “N20 state-level calibration and objective controls,” and the revised manuscript. Together with our first response, these cover the tNQG comparison, initialization-component control, objective and gradient controls, and state-level calibration at N=20.

We would appreciate your feedback on whether this evidence addresses your concerns, and we would be glad to clarify any remaining questions.

Thank you for your time and consideration.

The Authors

Reviewer_L3BDOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper proposes Abel-tNQS, a time-conditioned autoregressive neural quantum state for approximating quantum dynamics by minimizing the Schrödinger residual over a finite time interval. The initial state is enforced through a constraint on normalized complex conditional amplitudes, while the resulting representation retains direct autoregressive sampling.

The authors derive a bound relating the Hilbert residual to time-averaged fidelity and use the resulting remaining-time factor ((T-t)) to motivate a weighted training objective. A tighter cumulative-residual bound is used for post-training fidelity assessment. Experiments on transverse-field Ising systems investigate observable accuracy, residual-based fidelity estimates, temporal weighting, and initial-state enforcement.

Critical strengths
  1. The controlled ablation in Section 7 provides reasonably convincing evidence for the benefit of the proposed temporal weighting, with ten seeds per setting and matched optimization protocols. The improvements over uniform weighting are substantial, especially for nearest-neighbor correlations.
  2. I appreciate that the paper distinguishes between the theoretical fidelity bounds and their numerical estimates, rather than presenting the latter as certified guarantees.
  3. By imposing the initial state through normalized complex conditional amplitudes, the method avoids having to balance an initial-condition penalty against the dynamical residual during optimization. This also preserves the autoregressive structure and direct sampling, subject to the non-vanishing condition stated in Section 4.1. The construction seems useful, particularly given the difficulties encountered by some of the soft-penalty settings in Figure 5.
Critical weaknesses
  1. Global-in-time learning of quantum dynamics using autoregressive neural representations has a longer history than the discussion here suggests. Wang et al. [1] already proposed a spacetime neural network in 2021 that represents quantum dynamics jointly across spatial configurations and time, using a self-normalized autoregressive construction. Although that work demonstrates imaginary-time rather than real-time evolution, it is relevant to the architectural motivation of this paper and should be discussed. The more recent approaches of Van de Walle et al. [2] and Sinibaldi et al. [3] are even closer to the current setting, involving explicitly time-dependent NQS and global-in-time residual-based learning and error assessment. I see the differences in the hard initial-state constraint, residual formulation, and temporal weighting, but the overall conceptual contribution feels incremental. It is also difficult to evaluate the improvement over these methods without quantitative comparisons under common benchmark settings.
  2. Eq. 13 minimizes a sampled mean-absolute residual, rather than the Hilbert-residual norm appearing in the fidelity bounds, and the larger observable experiments additionally stop parameter differentiation through the Hamiltonian-action term. While these approximations may be computationally convenient, the derived bounds do not directly characterize the training objective being optimized. This leaves an important gap between the theoretical motivation and the actual learning procedure. In particular, the remaining-time factor is justified through a bound involving one residual quantity, but the experiments apply it to another. It would be useful to know whether the weighted objective remains preferable when directly optimizing the Hilbert residual, and how much the semi-gradient approximation affects the learned trajectory.
  3. The numerical fidelity lower-bound estimates in Section 5 are evaluated on systems containing only 4-6 spins, where the full computational basis is accessible. Although the estimates are quite tight in these experiments, they do not include certified control of differentiation or quadrature errors. For larger systems, evaluating the Hilbert-residual norm accurately becomes a much harder task. I am not sure how the proposed bound would be used in practice when full-basis summation is unavailable, especially if the goal is to assess state fidelity without knowing the exact evolution.
  4. In Figure 5, hard initial-state enforcement performs considerably better than the tested soft-penalty alternatives, but the soft baselines appear quite sensitive to the penalty coefficient and optimization. At λ=100\lambda=100, for example, nine seeds achieve high initial fidelity while one fails badly. This raises the question of whether a separately tuned soft-constraint implementation could close much of the reported gap.
  5. The experiments on larger systems mostly demonstrate agreement with selected observables rather than providing strong evidence of improved efficiency or reliability relative to previous NQS evolution methods. Figure 4 covers N=10N=10 and N=20N=20 chains and a 4×44\times4 lattice, but only one training realization is reported for each setting. The paper includes continuation and driven-field experiments, yet their optimization schedules are substantial and differ across configurations. Since previous global-in-time approaches already avoid the conventional tVMC evolution procedure, it would be particularly useful to compare training cost and achieved accuracy against them. I would also like to see whether the improvements observed in the controlled N=10N=10 ablation consistently carry over to the larger systems. At present, the strongest quantitative evidence for the proposed training choices comes from a relatively small system.
  6. The two-window continuation experiment in Appendix A.9 does not seem sufficient to establish that segmentation itself is advantageous, since the compared configurations differ in more than just the number of windows.

[1] https://arxiv.org/abs/2108.02200

[2] https://iopscience.iop.org/article/10.1088/2632-2153/ae0f39

[3] https://journals.aps.org/prl/abstract/10.1103/kqvx-dl54

Questions for authors
  1. How does Abel-tNQS compare quantitatively with the global-in-time NQS methods in [2] and [3], particularly in terms of accuracy and total training cost? Also, could the authors clarify the architectural distinction from the earlier spacetime autoregressive approach in [1]?
  2. Since the training surrogate in Eq. 13 differs from the Hilbert residual used in the theoretical bounds, is there evidence that minimizing this surrogate reliably reduces the bound itself? A comparison of the objectives on the small systems would help clarify how much of the observed improvement follows from the theoretical argument.
  3. Could the residual-based fidelity assessment be extended to the larger systems without full-basis evaluation, and what would be required to obtain a numerically reliable bound?
3 comments
AuthorsOpenReview ↗

Response to L3BD (1/2): prior work, direct comparison and training objective

Thank you for the detailed review. We performed additional experiments on direct comparison, training objectives, soft-constraint tuning and state assessment. This first comment addresses W1-W2 and Q1-Q2; the second addresses W3-W6 and Q3.

Prior work and direct comparison (W1, Q1). Wang et al. learn an imaginary-time trajectory by using an internal temporal network to supply time-dependent parameters to an external autoregressive Transformer, trained with implicit-midpoint matching. Abel uses a shared-weight MADE with additive time conditioning and an instantaneous Schrödinger-residual surrogate. Building on global trajectory learning and residual assessment in Wang et al., Van de Walle et al. and Sinibaldi et al., our contribution combines normalized complex-conditional initialization, time-averaged fidelity analysis and residual-guided training. We will add Wang et al. to related work. Part 2 reports the initialization component comparison with Van de Walle et al.

We compared native-code tNQG and Abel on the N=10 open chain with J=1, h=0.5, +x initial state and Jt in [0,1]. Each native run includes five windows and all window/global refinements. We evaluated its default 20,000 updates/window and a 1000-updates/window configuration with a compressed cosine schedule. For the latter, independent timing calibrations fixed Abel allowances at 2300/3800/2500 updates before inspecting native accuracies. Abel uses AD, full-gradient MAE, 32 uniform times × all 1024 configurations/update, linear weighting, and LR 1e-4 to 1e-5 halfway through each allowance. Common 101-point normalized full-basis evaluation gives mean ± sample SD over three training seeds:

ConfigurationAveraged fidelityMAE(Mx)MAE(Czz(1))MAE(Czz, r≤5)
tNQG, default budget0.999906 ± 3.8e-057.98273e-05 ± 2.4e-050.000205999 ± 4.3e-050.000373875 ± 0.00021
tNQG, 1000/window0.9114 ± 0.0290.0351624 ± 0.0170.0192067 ± 0.0090.0105097 ± 0.0057
Abel, cost-targeted0.987257 ± 0.00430.00913809 ± 0.00340.0137988 ± 0.00380.0109808 ± 0.004

At the reduced-budget work point, Abel improves averaged fidelity and Mx/nearest-neighbor accuracy; tNQG has slightly lower distance-averaged correlation error. Native process times are 1.93/3.54/2.09 hours versus Abel 1.90/3.39/1.92 hours, including refinements, checkpointing and final evaluation. The two timing calibrations add 0.356 hours. The default native budget reaches averaged fidelity 0.999906 at approximately 24 hours/run (one run includes an interrupted-session cost reconstruction). Runs used shared A100 80GB GPUs: native tNQG uses an RBM/time-basis ansatz in FP64/complex128, whereas Abel uses an FP32 MADE.

Training objective and weighting (W2, Q2). The Hilbert norm in the bound and the mean-absolute training surrogate are related by D,a≤ρ≤Da\sqrt{D}\\,a\leq\rho\leq D a for the same D-component residual, where a is its complete-basis mean absolute component and rho its Hilbert norm. This population relation does not bound the norm using a finite minibatch. The dimension-dependent factors allow different objective rankings, so we evaluate the physical residual alongside state fidelity. Finite-difference training additionally introduces derivative error; semi-gradients omit differentiation through HψH\psi.

We tested MAE/full, MAE/semi and Hilbert-norm/full under uniform and linear weighting, with three paired seeds per setting: 18 runs. These controls use automatic time derivatives, all 1024 configurations, paired initialization/time draws and 3000 updates. Weights 0.5 and 1-t have equal integrals. Hilbert-norm training uses mean⁡σ∣rσ∣2+10−12\sqrt{\operatorname{mean}_{\sigma}|r_{\sigma}|^2+10^{-12}}; assessment uses the unsmoothed physical residual. The common 401-point evaluation gives:

Objective / updateAveraged fidelity, uniform → linearNumerical cumulative lower estimate, uniform → linear
MAE / full0.97715 → 0.988680.93142 → 0.95612
MAE / semi0.95106 → 0.983580.89785 → 0.95804
Hilbert norm / full0.98301 → 0.990710.95374 → 0.96724

Linear weighting improves averaged fidelity and the cumulative numerical lower estimate in all nine pairs, including semi-gradient and Hilbert-norm training. Mean terminal fidelity decreases slightly in both full-gradient settings. At intermediate checkpoints, some surrogate decreases coincide with worse assessed bounds; this explains why the post-training diagnostic is evaluated separately from training loss.

AuthorsOpenReview ↗

Response to L3BD (2/2): state assessment, tuned soft constraints and larger systems

This second comment addresses the remaining questions raised in your review.

State assessment beyond six spins (W3, Q3). We calibrated the sampled diagnostic on a frozen N=10 control and the submitted N=20 checkpoint. Each assessment uses 201 times, 4096 configurations/time and 32 independent evaluation repetitions. The full-support proposal q(σ)=(pBorn(σ)+2−N)/2q(\sigma)=(p_{\mathrm{Born}}(\sigma)+2^{-N})/2 chooses a Born or uniform branch independently for each configuration. Importance weighting estimates the second moment of the physical residual before the square root and cumulative integration.

The cumulative numerical lower estimates are 0.930741 ± 0.000130 at N=10 and 0.881494 ± 0.000347 at N=20 (mean ± evaluation SD). Reference averaged fidelities on the same grid are 0.978066 and 0.954838; N=20 terminal fidelity is 0.726214. The N=10 full-basis diagnostic is 0.930757. At N=20, complete-state reference propagation is cross-checked against an independent propagator and Gaussian-reference observables. Reference states enter the fidelity calibration; the residual diagnostic is computed from the learned trajectory and Hamiltonian.

The 32 repetitions take 2.15/4.54 shared-GPU hours at N=10/N=20. Increasing nested sample prefixes from 256 to 4096 reduces evaluation SD from 0.000586 to 0.000130 and from 0.001124 to 0.000347, respectively. These prefixes reuse the 4096-sample caches. The N=10 grid-refinement change exceeds its sampling SD, identifying time resolution as an additional source of error.

For numerical certification, independent assessment samples and proved bounds on importance-weighted values would give concentration bounds on residual second moments. Upper enclosures would then propagate through the square root and cumulative functional, together with validated differentiation, normalization, initial-state, quadrature and roundoff errors. The present results are numerical estimates: evaluation SD quantifies sampling variability of a fixed checkpoint and excludes these other errors and nonlinear plug-in bias.

The assessment also applies to three native tNQG N=10 trajectories: cumulative numerical lower estimates are 0.999617–0.999810, compared with reference averaged fidelities 0.999878–0.999950. Analytic/finite-difference derivatives and two propagators provide independent numerical checks.

Initialization comparison with t-NQS (W1, Q1). On a common MADE with shared fresh polar heads, we compared complex-vector interpolation with a normalized autoregressive adaptation of Van de Walle et al.'s amplitude/phase interpolation: three paired seeds and 3000 updates. Complex interpolation increases mean averaged/terminal fidelity by 0.002677/0.009151; the amplitude/phase arm gives lower mean observable errors. This tests the interpolation component; the native full-method baseline in part 1 is tNQG.

Independently tuned N=10 soft constraints (W4). Independent penalty/rate tuning retains the advantage of hard initialization. A four-setting search with two tuning seeds each selected penalty 100 and initial LR 1e-4 by a normalized physical-residual-plus-initial-distance score. The choice was frozen before three fresh seeds per arm. Both arms share initial tensors and time/configuration streams, use the same MADE, FD full gradients (step 0.001), 128 uniform times × 64 uniform configurations × accumulation 2, and 3000 updates; LR changes to 1e-5 after update 1500. Common 101-point full-basis evaluation gives mean ± sample SD:

SettingAveraged fidelityMAE(Mx)MAE(Czz(1))MAE(Czz, r≤5)
Hard0.984472 ± 0.00340.009416 ± 0.00310.011643 ± 0.00110.006225 ± 0.0016
Independently tuned soft0.771836 ± 0.0130.020736 ± 0.00450.150439 ± 0.0330.049172 ± 0.015

Hard initialization improves averaged fidelity and every reported observable error in all three fresh pairs. All soft initial fidelities exceed 0.9966. The soft arm additionally incurs 33.37 process hours for tuning, including replayed work.

Larger systems and continuation (W5, W6). The N=20 calibration above evaluates state accuracy beyond the observable benchmarks. To test transfer of the weighting benefit, a fresh N=20 uniform/linear study uses three paired training seeds with shared initialization and time/configuration streams at fixed 3000-update endpoints. This study is running; we will add all six endpoints and paired differences in a follow-up. The submitted continuation example evaluates a combined protocol with changes to architecture, optimization and windowing. Separating the effect of segmentation requires a control that holds the other choices fixed.

AuthorsOpenReview ↗

Completed N20 weighting study and state-level calibration

To test transfer beyond ten spins (W5), we completed three paired N=20 runs per weighting at the prespecified endpoint of 3000 updates. Initial model tensors and time/configuration streams are shared within each pair; Section 7.1 and Appendix A.21 report the complete comparison. Both arms use 32 uniform times x 1024 uniform configurations per update, full-gradient mean-absolute residual training, finite-difference step 0.001, and learning rate 1e-4 through update 1500 and 1e-5 thereafter. The weights 0.5 and 1-t have equal integrals. Common 101-time normalized full-basis evaluation gives the following means +/- training-seed sample SD:

Observable MAEUniformLinearPairs with lower linear error
Mx0.064013 +/- 0.0071670.108395 +/- 0.0381261/3
Czz(r=1)0.300047 +/- 0.0096350.174183 +/- 0.0396803/3
Czz, r=1..50.507312 +/- 0.0098610.304000 +/- 0.1736583/3

Linear weighting reduces both correlation errors in all three pairs, but its mean full-window magnetization error is higher. Absolute correlation errors remain substantial. The weighting effect therefore depends on the observable at this training budget; Appendix A.21 gives the trajectories and training losses. The submitted N=20 benchmark uses staged semi-gradient training, whereas this fresh control uses the fixed full-gradient protocol above.

We also extended the state-assessment calibration in Appendix A.20 to the first completed fresh-control endpoint, selected for this diagnostic after observing energy drift. With the same 201 times, 4096 configurations/time, equal Born/uniform mixture, and 32 independent evaluation repetitions:

Fixed N=20 checkpointCumulative numerical lower estimateReference averaged fidelity
Submitted model0.881494 +/- 0.0003470.954838
Fresh fixed-3000 control0.110748 +/- 0.0001600.153132

The diagnostic uses the learned trajectory and Hamiltonian; independently propagated reference states provide calibration at the two accuracy levels. SD measures evaluation sampling variation, with differentiation, quadrature, normalization, and roundoff errors requiring separate control. The supplement reconstructs both complete 201-point model/reference comparisons.

The revised manuscript also incorporates the native tNQG comparison (A.17), common-MADE initialization control (A.18), and independently tuned hard/soft comparison (A.19) from our first response. Appendix A.9 now presents continuation as a combined protocol, since the existing comparison changes architecture and optimization as well as windowing.

Reviewer_SwymOpenReview ↗
Rating
3
Confidence
1
Informativeness
1
Presentation
1
Soundness
3
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Paper summary

The paper presents an autoregressive method for quantum modeling.

Critical strengths

The paper is well written and organized, although completely over my head. The math is rigorously presented. I am unable to judge the usefulness of the paper based on the experiments presented.

Critical weaknesses

None

Questions for authors

None

1 comment
AuthorsOpenReview ↗

Response to Swym: practical use of the residual diagnostic

Thank you for your assessment. The practical question is how to assess a learned quantum trajectory when an exact evolved state is unavailable. The Schrödinger residual measures deviation from the evolution equation; for a normalized trajectory with the correct initial state, our analysis relates its accumulation to time-averaged fidelity. This provides a post-training state diagnostic computed from the model and Hamiltonian.

We have now calibrated it beyond the original four-to-six-spin tests. At N=20, the sampled cumulative numerical lower estimate is 0.881494 ± 0.000347 (mean ± evaluation SD), compared with reference averaged fidelity 0.954838. The reference validates the diagnostic; evaluation SD measures sampling variability, while numerical certification also requires control of differentiation, normalization, quadrature and roundoff errors.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Revised manuscript: guide to the additional evidence

The revised manuscript consolidates the additional evidence discussed in our responses and the completed N=20 temporal-weight study. The following locations provide a direct route from the review questions to the results:

  • Section 2 and Appendix A.6: relation to Wang et al., Van de Walle et al., and Sinibaldi et al.
  • Section 7.2 and Appendices A.17-A.18: native-code tNQG comparisons at two budgets and a separate common-MADE initialization-component control.
  • Section 7.1 and Appendices A.16 and A.19: objective/gradient controls and independently tuned soft constraints.
  • Section 5 and Appendix A.20: sampled state assessment beyond six spins, including complete-state reference calibration at N=20, evaluation variability, and cost.
  • Section 7.1 and Appendix A.21: all six fixed endpoints of the three-seed N=20 temporal-weight comparison, with observable and training-loss curves.

The N=20 training comparison has mixed outcomes: linear weighting lowers both reported correlation errors in every pair, while full-window magnetization error is higher on average. Appendix A.9 describes the changes in windowing, architecture, and optimization used in the continuation experiment.

The updated anonymous supplement provides the fixed-endpoint weights, evaluation arrays, and reproduction commands for these controls and state assessments.

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

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