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Under review as a conference paper at ICLR 2027

Genealogy-Conditioned Quantum Architecture Search with Synthetic Lineage Pretraining

Abstract

Quantum architecture search (QAS) can automate the design of parameterized quantum circuits (PQCs), but testing an architecture typically requires an expensive inner-loop parameter optimization. Surrogate models can screen candidates before this evaluation, yet training the surrogate often requires the same quantum-evaluated architecture labels that it is meant to save. We introduce Genealogy-Conditioned Quantum Architecture Search (GCQAS), which pretrains a reusable offspring-ranking model without executing quantum circuits or collecting expert labels. GCQAS constructs synthetic lineages, assigns each family a different randomized scoring rule, and trains a contextual Transformer to infer how candidate structure, inheritance, and ancestral outcomes jointly determine local rankings. Because the rule differs across lineages, the model cannot memorize one and is forced to learn to infer the active rule from the ancestors' outcomes in its context. During a target search, the model remains frozen and uses the contextual information from candidate circuit's genealogy to predict the performance of each offspring in a genetic algorithm. We evaluate the same surrogate on distribution matching and variational quantum eigensolver under noiseless and noisy simulation, with target circuits of up to 16 qubits despite pretraining only on six-qubit lineages. GCQAS continues to guide search across this change in scale and objective, whereas a genetic algorithm with no surrogate, a genetic algorithm with in-context Bayesian optimization as a surrogate, and an online QAS surrogate do not achieve comparable solutions under the evaluation budget. GCQAS also improves on task-specific adaptive construction in the corresponding benchmark regimes. These results show that synthetic lineage pretraining can learn a transferable search strategy: task-general knowledge is stored in the model, while sparse target-specific evidence is supplied through the evolving context.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
Quantum Architecture Search, Evolutionary Algorithm, Surrogate Models, In-Context Learning

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_WZkMOpenReview ↗
Rating
2
Confidence
4
Informativeness
1
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2
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Paper summary

The authors in the paper introduced GCQAS. Which is a model that pretrains a small contextual transformer on synthetic circuit lineages. Each lineage gets its own random linear scoring rule over 16 candidate and features. During the time of QAS the model is frozen. It ranks 20 offspring per slot inside a genetic algorithm, and only the winner receives full parameter optimization. The same checkpoint is used on 9 distribution matching and 3 VQE tasks. In the following I provide my detailed review:

Critical strengths
  1. I think the method provided in the paper has a potential practical advantage over meta-transfer QAS or predictor-based QAS as no quantum-evaluated labels needed for pretraining. Also that preselection keeps measured fitness as the only source of population fitness is well motivated

  2. The paper provide quite strong empirical results. GCQAS reaches the KL threshold on BAS 3 x 3 by generation 9, while Pool GA is at mean KL 0.7 at generation 20. It also reports lower VQE error than both state of the art TensorRL variants.

Critical weaknesses
  1. I believe the central claim of the paper is not justified. The whole paper argues that typed ancestry is the key ingredient, but there is no ablation that removes inheritance features while holding model and data fixed. The presented PFNs4BO comparison does not isolate ancestry. PFNs4BO also differs in architecture, output head, and pretraining prior, so the gap could come from any of those choices.

  2. The fact that the surrogate sees very little circuit structure seems quite alarming. This is because the inputs are 16 pooled statistics which includes layer, parameter, gate counts with shared, added, removed, and inherited amounts. As it never sees the circuit ctructure the identical counts are indistinguishable. This also makes the claim that "trained on 6 qubits, works on 16" less surprising than it is presented. As count-based features are almost automatically portable across qubit numbers and gate sets.

  3. The synthetic prior seems to be unvalidated. In equation 2 the labels are random linear functions of ancestor features hence nothing shows that real KL or energy landscapes are even approximately of this form. The a through and decisive diagnostic is missing in the current paper.

  4. The abstract and introduction motivate the work by the "cost of inner-loop optimization", but the paper reports no wall-clock time and excludes pretraining and surrogate inference from budget. The one budget comparison for BAS 3 by 3 versus ACLBM, uses a published trajectory, not matched reruns. Moroever, because only the selected offspring are optimized, the saving depends on how many children are evaluated. The paper needs an "evaluations to reach to a specific error" comparison against a GA that evaluates all children and also TensorRL.

  5. I have some concerns about the baseline and comparison proticol. (1) GCQAS and original PFNs4BO use 3 runs, the others use 10, and original PFNs4BO's history covers generations 0–9 versus 0–20. The headline 16-qubit result is therefore not a controlled comparison. (2) There are no learned predictor QAS baselines, no CRLQAS, and no ADAPT-VQE style baseline for VQE, although the paper cites all of them. (3) The run counts are small so there is not confidence interval orstatistical testing.

  6. I think the scope of the experiment is narrow as the noisy VQE run also uses an MPS-derived seed population, so it partly shares TensorRL's advantage and does not test the surrogate in isolation.

  7. Finally, although the authors declare that they use TensorRL codebase but even following the codebase it is hard to implement the algorithm presented section 4.2 and 4,3. Code are promised only "upon acceptance", which limits verification.

Questions for authors
  1. Can you retrain the same model on the same synthetic data with the parent-score and inheritance features removed or shuffled, and report the downstream results on the BAS and VQE tasks?

  2. Which of the 16 features carry the performance and transfer? Please run a feature-group ablation, and test on cases where circuits with identical counts differ structurally.

  3. How well does the frozen surrogate's ranking agree with verified scores on each target task, compared with random ranking and a parent mean fitness-inheritance selector? If possible please also show how robust the results are to replacing the random linear rules with nonlinear ones.

  4. How many full parameter optimizations, optimizer steps, and wall-clock hours does GCQAS need to reach a given KL or energy error, compared with a GA that evaluates all children and with TensorRL?

  5. Can you report confidence intervals or significance tests for on BAS 4 by 4?

  6. Can you add learned-predictor QAS, CRLQAS, and ADAPT-VQE-style baselines, or if resources not permit explain why they are not considered?

  7. How does GCQAS compare with an equally MPS-seeded Pool GA and TensorRL in the noisy H2O setting? Does the surrogate still help when the population is seeded identically?

  8. Can you specify in the paper the exact 16 features, the parent-sampling, crossover and repair procedures in section 4.2, and the training and checkpoint details section 4.3, and wither a pseudocode or an anonymized code during review?

14 comments
AuthorsOpenReview ↗

Thank you for your comments! 1/3

Thank you for the detailed and thoughtful review! We appreciate the time and care you took to examine our method and experiments.

We respond to each question below, with references to the supplementary material for the additional experiments, figures, tables, and methodological details. Thank you again for the constructive feedback and for helping us improve the paper.

Q1 Thank you for your suggestion. We retrained the surrogate on the same synthetic corpus with the same training protocol, removing the inheritance statistics and ancestral outcomes from every node during both pretraining and search. Each node retains only the four circuit statistics: the numbers of layers, gates, two-qubit gates, and parameters. The genealogy still determines which nodes appear in the context (App. H.2).

With this retrained surrogate, the search makes no progress on BAS 3×3: the mean KL divergence remains at approximately 1.6 through generation 15, whereas GCQAS reaches 5.2×10⁻¹⁰ at generation 5 (App. H.3, Fig. 14). On noiseless eight-qubit H₂O, the error remains near the initial population's level of 10⁻⁴–10⁻³ Hartree through generation 15, whereas GCQAS falls below 10⁻¹¹ Hartree (App. H.5, Fig. 17). These results show that circuit statistics alone are insufficient to guide selection in these experiments, even when the surrogate is trained specifically on those inputs. This support the contribution of the parent-related information.

Q2 Thank you for raising these questions. Table 7 defines the 16 inputs as circuit statistics, inheritance statistics, and ancestral outcomes. The ablations show that all three groups contribute, with inheritance and circuit statistics having the largest effect (App. H.3, Fig. 14). Randomizing these groups separately raises the mean KL divergence at generation 5 on BAS 3×3 to 4.9×10⁻¹ and 3.7×10⁻¹, respectively, compared with 5.2×10⁻¹⁰ for GCQAS. Randomizing parent scores has a smaller, later effect: the search follows GCQAS for the first three generations but falls behind by approximately one order of magnitude from generation 4. The same ordering of contributions appears on eight-qubit H₂O (App. H.5, Fig. 17).

This difference is consistent with how candidates are generated. Proposals within a pool are bred from the same population and share many ancestors, so their ancestral outcomes provide less distinction between them than their proposal-specific inheritance and circuit statistics. Nevertheless, ancestral outcomes supply verified information about performance on the target task. They may become more useful as the population converges and proposals become more similar in size and inheritance, helping the surrogate interpret which variations are promising in the current search context. We offer this as a possible explanation, rather than a mechanism established by the ablations.

We agree that structurally different circuits can have identical counts. We examined this directly in App. H.6 (Table 9, Fig. 18), using one BAS 3×3 search with 2,040 fully evaluated proposals across 102 pools. No two proposals within the same pool differed by less than 5% on every one of the 16 inputs; even across proposals of the same generation, only 2 of 345,777 pairs met this criterion. Matching only the four circuit statistics was more common, at approximately 0.2% of pairs, and such circuits could differ substantially in performance. Thus, counts alone do not uniquely describe a circuit, but indistinguishability across all 16 inputs did not arise among the proposals that the surrogate actually compared in this search. These observations supported retaining the compact representation in the present study; they do not rule out a benefit from gate-level or graph encodings on other searches.

AuthorsOpenReview ↗

Thank you for your comments! 2/3

Q3 Thank you for suggesting this analysis (App. H.2–H.4, Fig. 15). For one BAS 3×3 seed per variant, we optimized all 20 proposals per pool with the same budget. The 19 unselected proposals' scores were used only to assess ranking and did not affect the search.

GCQAS reaches within-pool Spearman correlations of 0.83–0.89 at generations 2–5, showing strong agreement with verified candidate order despite training only on synthetic labels. At generations 1–4, it selects the best proposal in 29–47% of pools (Top-1 accuracy; random: 5%). Figure 15 also reports selection among the best three (Top-3; random: 15%). Later, Top-1 declines while correlation stays high: identifying promising proposals is easier than identifying the single best one.

Online ridge regression uses the same 16 inputs and verified ancestral scores but fits its weights during search. Its correlation is 0.24–0.54 and mean Top-1 accuracy is 10%. At generation 5, mean KL over ten seeds is 1.7×10⁻¹, versus 5.2×10⁻¹⁰ for GCQAS (App. H.3–H.4). We did not average parent performance because this cannot distinguish offspring sharing a parent pair despite different crossover and mutation outcomes.

We could not run this analysis on every benchmark because evaluating all unselected proposals is expensive. Pool GA may offer insight into the surrogate's effect on search performance. It substitutes random selection while keeping the genetic operators, pool size, optimizer, and budget unchanged. Its BAS 3×3 mean KL remains 9.8×10⁻² at generation 15; GCQAS reaches the threshold on every seed. Tables 4–6 extend this comparison across benchmarks.

We agree that quantum objectives are nonlinear. Our aim was pretraining with minimal expert supervision; the surrogate ranks related proposals locally. With nonlinear Gaussian-process labels on unchanged circuits and inputs, none of ten BAS 3×3 seeds reached the threshold (App. I, Fig. 19). Greater expressiveness alone did not help here. We tested one family and one training run; other designs may work better. We thank the reviewer and plan to explore labels informed by an expert system.

Q4 Thank you for question. (App. J). A full circuit optimization includes multiple evaluations. Noiseless genetic-search evaluations return the objective and gradient; TensorRL uses objective evaluations with COBYLA.

On BAS 3×3, the GA that evaluates all children (oracle) optimizes 340 proposals plus 20 population members per generation. GCQAS optimizes only the 20 members. Both also optimize 20 initial circuits. Median generations to KL ≤ 10⁻¹¹ are 6 for GCQAS and 4.5 for the oracle. This implies 140 versus 1,640 full optimization calls, derived from the schedule rather than measured separately (App. H.3, K.2, K.6).

Each optimization allows up to 250 iterations. Median gradient counts to KL ≤ 10⁻¹¹ are 2.91×10⁴ for GCQAS and 2.53×10⁵ for the oracle. Actual iteration totals are not reported separately. At the different target of KL ≤ 8.09×10⁻⁶, both succeed on all ten seeds; mean times are 2.4 h versus 13.3 h (Table 13).

We ran the released TensorRL code with fixed initialization. To reach chemical accuracy (1.6×10⁻³ Hartree) on BeH₂-6, H₂O-8, and H₂O-10, its median evaluation counts are 2.4×10⁵, 2.6×10⁶, and 4.0×10⁶; GCQAS needs 5.7×10³, 1.3×10⁴, and 8.1×10³ gradient calculations (Fig. 20(b)). On H₂O-8, both succeed on all three seeds, averaging 1.4 h for TensorRL and 0.042 h for GCQAS (Table 14). TensorRL optimization-call and iteration totals are not reported separately. The genetic searches share an initial population and reach chemical accuracy by generation 1, so this comparison does not isolate the surrogate's contribution.

Search times exclude preparation: 58 s for corpus generation without quantum simulation and 4.6 h for training on one H100 GPU. All benchmarks reuse the frozen model (Table 11). BAS 3×3 inference takes 81 s per generation (0.5%). The full selection phase takes 545 s versus 10,999 s for the oracle (Fig. 21, Table 12).

Evaluation counts omit circuit-size and gradient-cost differences. GCQAS selects larger circuits. Pool GA reaches the BAS 3×3 target in 42 min but succeeds on only 6/10 seeds (Table 13). Shared-hardware timings are indicative.

AuthorsOpenReview ↗

Thank you for your comments! 3/3

Q5 Sure! The BAS 4×4 results are below (App. G.1, Table 4). Our new runs use three seeds per method; entries show mean KL divergence ± sample standard deviation. Lower is better.

MethodBAS 4×4 KL divergence
GCQAS7.79×10⁻⁷ ± 1.2×10⁻⁶
Pool GA4.14 ± 1.0
PFNs4BO+GA (original)4.31×10⁻¹ ± 2.1×10⁻¹
PFNs4BO+GA (retrained)3.84 ± 3.2
CEO-ADAPT1.59 ± 6.6×10⁻¹
CRLQAS5.08 ± 1.2×10⁻¹
ACLBM7.09×10⁻³ (standard deviation not reported)

GCQAS achieves the lowest mean KL divergence among all compared methods. Every GCQAS seed also outperforms every seed of the other genetic searches (Fig. 9). EDA-QAS is the main-text result with Adam; ACLBM is the published reference. CEO-ADAPT reached its time limit.

We also included standard deviations across seeds for the other benchmarks in the supplementary (App. G, Tables 4–6). Figures 5–13 show individual runs, so reviewers can assess both the mean performance and its variability.

Q6 We considered cited learned-predictor QAS methods, including He et al. (2026), but could not find released code for most. We therefore did not add this comparison and acknowledge the gap.

We initially chose TensorRL as the RL baseline based on its reported improvements over CRLQAS. We have now added CRLQAS (App. F–G). Its KL divergence is higher than GCQAS on the nine- and ten-qubit targets and BAS 4×4 (Table 4).

We also added CEO-ADAPT-VQE as an ADAPT-VQE baseline. It needs the fewest gradient calculations on VQE and achieves lower error on LiH-12, but higher KL divergence on the ten-qubit distribution targets and BAS 4×4 (Tables 4–5). For VQE, it uses a Hartree–Fock reference and expert-designed coupled exchange operators that conserve particle number and spin projection. GCQAS uses generic gates and the same frozen surrogate across objectives (App. G.2). We view it as a general search method, while recognizing the efficiency of chemistry-specific methods on VQE.

Q7 Yes. We added Pool GA on eight-qubit H₂O under shot noise (10⁴ shots), using the same MPS-derived initialization as GCQAS (App. G.3, Table 6). GCQAS records an energy error of 3.03×10⁻⁵ ± 1.9×10⁻⁵ Hartree, versus 6.32×10⁻⁵ ± 3.9×10⁻⁵ for Pool GA (mean ± standard deviation). The surrogate thus improves the mean result even with MPS initialization, although the spreads overlap and we do not claim statistical significance. Table 6 also includes the published TensorRL errors: 1.5×10⁻⁴ Hartree for fixed initialization and 8.7×10⁻⁵ for the trainable variant.

Q8 To support reproducibility, we added detailed pseudocode and experimental settings. Appendix K (Algorithms 1–7) covers the search procedure, genetic operators, parameter inheritance, context construction, and optimization; K.7–K.8 describe synthetic data generation, the surrogate architecture, and training. Appendix H.1 (Table 7) defines all 16 inputs. Appendix F specifies the experimental protocol and baselines, including the parent-selection and optimizer changes from the main text. We are sorry that we cannot release the code at present and we hope these additions help clarify the method and support its reproduction, We appreciate the reviewer's request for these details.

If you have any questions you feel needs to be addressed in order for you to improve our score, please let us know and we'll try out best to address them. Thank you for your help and your insightful comments!

Reviewer_UvhtOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper introduces Genealogy-Conditioned Quantum Architecture Search (GCQAS), which pretrains a reusable offspring-ranking model without executing quantum circuits or collecting expert labels. GCQAS constructs synthetic lineages, assigns each family a different randomized scoring rule, and trains a contextual Transformer to infer how candidate structure, inheritance, and ancestral outcomes jointly determine local rankings. Experiment results show that synthetic lineage pretraining can learn a transferable search strategy: task-general knowledge is stored in the model, while sparse target-specific evidence is supplied through the evolving context.

Critical strengths
  1. The insight is novel. The paper formulates QAS surrogate pretraining as contextual offspring selection and constructs synthetic circuit lineages. This can provide supervision without quantum simulation, quantum hardware, or previously solved target tasks.

  2. The method is carefully designed. The paper frees the model from memorizing rules, instead using a frozen contextual surrogate that combines candidate statistics, parent–child relations, and verified search history to select offspring while leaving final fitness decisions to the task objective.

  3. The generality and evaluation results are good. The method can be extended to circuits with 16 qubits despite pretraining only on six-qubit lineages.

Critical weaknesses
  1. The synthetic equations are just linear combination of rules, this may not represent the complex quantum target.

  2. VQE energy error is reported as the lowest reported entry in each benchmark with only 6-8 qubits. The robustness and stability remain a concern.

  3. The paper should provide training statistics to compare with baselines, e.g., training time, GPU usage.

  4. Parent-child relations and ancestral outcomes are at the core of the proposed method, which may not extend well to RL-QAS, QuantumDARTS, etc.

Questions for authors

See Weaknesses.

2 comments
AuthorsOpenReview ↗

Thank you for your comments!

Thank you for the insightful review! We feel your questions raise good points that help us further improve our paper.

The following responses have references to the supplementary material, which can be checked for more details.

W1 We agree that random linear scoring rules may not capture the complexity of quantum objectives. Our aim was to examine how far synthetic pretraining can go with as little expert supervision as possible, so we used these simple rules. Designing nonlinear labeling functions that better reflect quantum objectives is an interesting direction beyond the scope of the present study.

To explore this possibility, we trained a surrogate on nonlinear labels drawn from a Gaussian process, using the same circuits as in the linear-label corpus (App. I, Fig. 19). This alternative performed worse: no seed of the BAS 3×3 search reached the stopping threshold. Although we tested only one nonlinear family, this result suggests that greater expressiveness alone does not ensure better transfer; without careful design, nonlinear labels can make the surrogate less effective. We are looking into labeling functions informed by an expert system as future work. We thank the reviewer for highlighting this direction.

W2 Thank you for raising this concern. Our experiments used multiple independent seeds, up to 10 seeds per benchmark, and we have expanded the reporting to make their robustness clearer. The tables report the mean ± standard deviation over seeds, and the figures show every seed (App. G, Tables 4–6, Figs. 5–13). We also added two larger VQE benchmarks, ten-qubit H₂O and twelve-qubit LiH. GCQAS reaches chemical accuracy (1.6×10⁻³ Hartree) on every seed of all four molecular benchmarks, spanning six to twelve qubits.

The distribution-matching results also show consistent performance across runs: GCQAS reaches the stopping threshold on every seed of the nine- and ten-qubit targets (App. G.1, Table 4, Figs. 5–8). These results support the stability of the method across the tested objectives and circuit sizes.

W3 Thank you for this suggestion. We report training and computational costs (App. J, Tables 11–14). Pretraining takes 4.6 h once on one NVIDIA H100 GPU, using 12 GB of GPU memory, and the same frozen surrogate is reused across all benchmarks. Generating the synthetic corpus takes 58 s on a CPU without quantum simulation. During search, surrogate inference accounts for 0.5% of the wall-clock time of a generation on BAS 3×3.

For comparison with the baselines:

  • ACLBM on BAS 3×3: GCQAS reaches the published ACLBM KL divergence on every seed with a lower median evaluation budget, including operator-pool screening in the ACLBM count (App. J.1, Fig. 20).

These search times exclude the one-time pretraining cost reported above.

W4 Thank you for raising this important point. We agree that the use of parent–child relations and ancestral outcomes may limit the applicability of the current method to other search frameworks. Our interest was in whether contextual information from previously evaluated circuits could help select new candidates. Genetic algorithms offered a natural starting point for validating this idea because crossover and mutation produce candidates that share structure and inherited parameters with their parents, providing explicit relationships through which context can be identified and structured.

Our experiments verify the usefulness of this context within genetic search. We have not verified whether the approach extends to RL-QAS, QuantumDARTS, or other non-genetic methods; identifying and structuring suitable context in those settings was beyond the scope of this study. We appreciate the reviewer highlighting this limitation and will clarify the scope of our claims accordingly.

If you have any questions, please let us know and we'll try out best to address them. Thank you for your help and your insightful comments!

I thank the authors for the detailed response. I will keep my score to accept the paper.

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

The paper proposes GCQAS, a surrogate-assisted quantum architecture search method that pretrains a Transformer on synthetic circuit genealogies without quantum evaluations. The frozen model uses ancestral information and previously evaluated circuit scores to rank candidate offspring. Results are reported for distribution matching and VQE, with circuits up to 16 qubits.

Critical strengths
  • Synthetic genealogy-based pretraining offers an alternative to training QAS surrogates on expensive quantum-evaluated datasets.
  • A single frozen surrogate is applied across different circuit sizes, objectives, and gate sets.
  • GCQAS achieves strong KL divergence results and lower reported VQE energy errors than the considered TensorRL variants.
  • The paper includes Pool GA, EDA-QAS, PFNs4BO, ACLBM, and TensorRL.
Critical weaknesses
  1. The main novelty appears to be genealogy-conditioned synthetic pretraining instead of surrogate-assisted QAS itself. The paper discusses related work, including pretrained QAS predictors, zero-shot QAS, and in-context optimization. However, it remains unclear how much additional benefit comes specifically from genealogy information.

  2. The method combines parent scores, inheritance statistics, synthetic pretraining, and a contextual Transformer. The authors should isolate the importance of each component, particularly by comparing against the same surrogate without genealogy information and against a simpler parent-score predictor.

  3. The synthetic labels are generated from randomized linear scoring rules, whereas real quantum objectives involve nonlinear circuit dynamics and parameter optimization. What explains the transfer between these synthetic rules and physical quantum objectives? An analysis of offspring-ranking accuracy on actual quantum tasks would support this claim.

  4. The authors acknowledge that some comparisons are not compute-matched. BAS 4×4 uses different run counts and search horizons, while the VQE results are compared with published TensorRL results. A comparison using matched objective-evaluation budgets and computational costs is needed to establish efficiency improvements.

  5. Most distribution-matching experiments use exact statevector probabilities, while the noisy VQE experiment considers simulated shot noise instead of hardware noise.

Questions for authors
  1. What is the specific advantage of genealogy-conditioned pretraining over existing surrogate-assisted QAS and in-context optimization methods? Can the authors isolate the benefit of genealogical information?

  2. How does performance change when ancestry information, parent scores, or inheritance statistics are removed?

  3. The synthetic scoring rules are randomized linear functions, whereas quantum objectives are generally nonlinear. What explains the observed transfer, and how well do surrogate predictions correlate with actual offspring performance?

  4. Can the authors provide comparisons under matched quantum-objective evaluation budgets, including parameter optimization and surrogate inference costs? against ACLBM and TensorRL?

  5. How robust are the reported improvements across independent runs?

  6. How does ranking accuracy change with increasing circuit width and depth? Does the surrogate remain effective under realistic gate noise, readout errors, and finite measurement budgets?

  7. Since the surrogate is ultimately used to rank offspring instead of predict absolute fitness, have the authors considered a pairwise ranking loss instead of MSE? Would this improve transfer across different quantum objectives?

6 comments
AuthorsOpenReview ↗

Thank you for your Comments! 1/2

Thank you for the constructive review! We feel your questions raise good points that help us further improve our paper.

The following responses have references to the supplementary material, which can be checked for more details.

Q1 and Q2. We compared two alternatives in the same genetic search on BAS 3×3 with ten seeds (App. H.3, Fig. 14). Online ridge regression is a simpler surrogate, fitted during the search on the same inputs and verified scores. PFNs4BO is a different in-context optimization method, which conditions on an unordered set of observations. Both are clearly weaker. At generation 5, the mean KL divergence is 1.7×10⁻¹ for ridge regression and 5.2×10⁻¹⁰ for GCQAS. PFNs4BO+GA (original) ends at 6.3×10⁻³, whereas every GCQAS seed reaches the stopping threshold of 10⁻¹¹.

The ablations explain the benefit more directly. In order of impact:

  • Inheritance statistics have the largest impact. When they are randomized, the search stays near random selection (4.9×10⁻¹ at generation 5; circuit statistics: 3.7×10⁻¹). They are specific to each proposal, so they separate the proposals of one slot.
  • Parent scores have a smaller and later impact. When they are randomized, the search is unchanged for three generations and falls behind by about one order of magnitude from generation 4. The proposals of a slot share many ancestors, so parent scores separate them little at first. They are, however, the only inputs that carry verified information about the target, which may be why they matter later.
  • Ancestry is a sufficient context. Replacing it with all prior circuits, or with the previous generation, brings no gain, although these hold more information, possibly because the added circuits are less relevant to the proposal.

The order of the input groups is the same on eight-qubit H₂O (App. H.5, Fig. 17).

Q3. We agree that quantum objectives are generally nonlinear. Our aim was to see how far pretraining can go with as little expert supervision as possible, so we kept to random linear rules. Our reasoning is that the surrogate only makes a local prediction. It compares the proposals of one slot, which are bred from the same population and are therefore similar circuits. It only has to follow the local trend among them, not model the objective.

The measured ranking supports this. In one BAS 3×3 search in which every proposal was evaluated, the within-slot Spearman correlation of the prediction with the verified score is 0.83–0.89 at generations 2–5. The selected offspring is the best of its 20 proposals in 29–47% of the slots at generations 1–4 (random: 5%) (App. H.4, Fig. 15). We also tested nonlinear labels, drawn from a Gaussian process without domain knowledge. They were worse than the linear rules: no seed reached the stopping threshold (App. I, Fig. 19). Nonlinear labeling functions informed by an expert system are a direction for our future work, and we thank the reviewer for this insightful comment.

Q4. Yes. We now compare GCQAS with ACLBM and TensorRL on a common budget: the number of objective evaluations that return a gradient. It includes all parameter optimization and, for ACLBM, the screening of its operator pool (App. J.1, Fig. 20). The surrogate adds no such evaluations. Its inference takes 0.5% of the wall-clock time of a generation, and its pretraining takes 4.6 h once on one GPU for all benchmarks (App. J.2).

  • ACLBM: GCQAS reaches the published ACLBM KL divergence on every seed of BAS 3×3, the three ten-qubit targets, and BAS 4×4, each with a median budget below that of the published ACLBM run.
  • TensorRL: we ran the released code. To reach chemical accuracy on BeH₂-6, H₂O-8, and H₂O-10, TensorRL needs a median of 2.4×10⁵, 2.6×10⁶, and 4.0×10⁶ objective evaluations; GCQAS needs 5.7×10³, 1.3×10⁴, and 8.1×10³. On H₂O-8, this is 1.4 h against 2.5 min per seed (Table 14).

Q5. Thank you for this question. Yes, the results are robust across independent runs. The tables report the mean ± standard deviation over seeds, and the figures show every seed (App. G, Tables 4–6, Figs. 5–13). GCQAS reaches the stopping threshold on all seeds of the nine- and ten-qubit targets and chemical accuracy on every seed of the four molecules. It achieves the best result of the compared methods on multiple benchmarks.

AuthorsOpenReview ↗

Thank you for your Comments! 2/2

Q6. With respect to circuit depth and depth : Thank you for this question; we added Fig. 16 (App. H.4) specifically to answer it. The ranking accuracy remains relatively stable with circuit width and depth. Between generations 2 and 5 of a BAS 3×3 search, the mean depth of the proposals grows from 20 to 61 layers and the mean width from 4.3 to 5.1 gates per layer, while the within-slot rank correlation stays at 0.86–0.89. It decreases moderately only for the deepest proposals, above about 70 layers. The accuracy depends more on the generation: the correlation is 0.41 in generation 1, when a proposal has only its two parents as context, and 0.86–0.89 from generation 2 on. This suggests that the surrogate is more sensitive to how much context it can use than to the size of the circuits.

With respect to noise : Our surrogate model also achieves chemical accuracy under shot noise with a measurement budget of 10^4 shots (see Table 6). Under depolarizing noise, the evolved circuits exhibit stable energy convergence, but their energies remain near the Hartree–Fock expectation value. This behavior may reflect the strongly single-reference character of the molecular benchmarks. For example, the Hartree–Fock state |11110000> accounts for approximately 99.9% of the probability weight of the H2O ground state. Under accumulated noise at the error rates considered in TensorRL-QAS, the solution circuits produce measurement statistics similar to those of the Hartree–Fock state, suggesting that they do not resolve the smaller components associated with electron correlation. These observations highlight the challenge of automatically finding noise-robust circuit architectures and motivate incorporating additional information into the objective function beyond energy alone.

Q7. Thank you for the suggestion. We tested it (App. I, Fig. 19). With a pairwise ranking loss, the BAS 3×3 search still converges, but about two generations later, and 8 of 10 seeds reach the stopping threshold. It therefore did not improve on the squared error in this experiment. A possible reason is that a pairwise loss keeps only the order of two records, whereas the squared error also uses how far apart their labels are, which gives the surrogate more signal from the same synthetic corpus. We have not tested this explanation. Ranking-based losses, and their effect on transfer across objectives, are a direction that we are looking into for future work.

If you have any questions you feel needs to be addressed in order for you to improve our score, please let us know and we'll try out best to address them. Thank you for your help and your insightful comments!

Reviewer_ycsQOpenReview ↗

Comment

Thank you for the responses and additional experiments. The new comparisons and ranking analysis address several of my concerns. My main remaining concern is interpreting the noise results. Stable convergence near the Hartree-Fock energy does not establish that the circuits recover the correlation energy or that the surrogate can reliably rank candidates under gate noise. Could you clarify whether its rankings remain consistent with the evaluated noisy energies, and whether readout errors were considered?

The width analysis also appears to concern gates per layer. It would help to clarify how ranking accuracy changes with the number of qubits and whether the behavior observed on BAS also holds for the molecular tasks.

Comments on the paper

2 comments
AuthorsOpenReview ↗

On the Supplementary PDF

We thank all three reviewers for their time and for their careful, constructive reviews!

Many of the questions asked for ablation studies, additional baselines, statistics over independent runs, cost measurements, and a complete specification of the method. We have therefore uploaded a supplementary PDF that contains all additional experiments and details.

Our response to each reviewer answers each question directly and names the section of the supplementary material that holds the full evidence.

We are grateful for the reviewers' suggestions! The additional experiments they suggested helped us explain the evidence for this work more clearly.

If you have any questions or comments, please feel free to let us know!

AuthorsOpenReview ↗

Thank you for your comments & Summary

We sincerely thank the Area Chair and Reviewers ycsQ, Uvht, and WZkM for their careful and constructive reviews, which we believe strengthened the paper!

1. Our work GCQAS pretrains a contextual Transformer on synthetic circuit lineages labeled by randomized scoring rules, with no circuit execution, quantum-evaluated labels, or previously solved tasks. In a genetic search, the frozen surrogate ranks the 20 offspring proposals of each slot from the verified scores of their ancestors. Only the selected offspring receives a full task evaluation, and verified scores remain the only source of population fitness. The same checkpoint, pretrained on six-qubit lineages, is used unchanged on 14 benchmark settings (distribution matching and VQE, 3–16 qubits).

2. What the reviewers appreciated

  • Pretraining that needs no quantum-evaluated labels (all three).
  • A novel insight and a carefully designed method (Uvht), with well-motivated preselection (WZkM).
  • A single frozen surrogate across circuit sizes, objectives, and gate sets, up to 16 qubits (ycsQ, Uvht), with strong empirical results (all three).

After the discussion, ycsQ raised their score and Uvht maintained acceptance. WZkM wrote that we "addressed nearly all of my specific methodological and reporting requests" and that the revisions "substantially improve the clarity of the paper."

3. Questions and our responses

  • What drives the gain? (ycsQ, WZkM) In ten-seed ablations on BAS 3×3, the model with untrained weights fails, a surrogate pretrained with the circuit statistics alone does not guide the search, online ridge regression on the same inputs is clearly weaker, and the ancestry of a candidate is a sufficient context. With the ablation WZkM proposed, we refined our claims: the parent-related inputs matter collectively, and the 16-qubit result is the transfer of a statistics-based selection rule.
  • Do random linear scoring rules transfer? (all three) Trained only on synthetic labels, the frozen surrogate reaches a within-slot Spearman correlation with the verified scores of 0.70–0.89 on BAS 3×3 and the ten-qubit targets at generations 2–4, where a parent-mean rule is no better than random selection. Its mean is positive on every benchmark from 8 to 16 qubits (0.82 on BAS 4×4; 0.30–0.41 on the noiseless molecular benchmarks). The suggested nonlinear labels and pairwise ranking loss did not improve on the linear rules and squared error; we state this label sensitivity as a limitation.
  • Cost (all three). Pretraining takes 4.6 h once on one GPU; surrogate inference takes 0.5% of a generation. At a common target on BAS 3×3, GCQAS needs about 12× fewer full parameter optimizations, 9× fewer gradient calculations, and 3× less wall-clock time than the oracle, which optimizes every proposal.
  • Robustness and baselines (all three). With mean ± SD and every seed reported, GCQAS reaches the stopping threshold (10⁻¹¹) on all 40 seeds of the nine- and ten-qubit targets and chemical accuracy on every seed of the four molecular benchmarks (6–12 qubits; H₂O-10 and LiH-12 are new). On BAS 4×4, every GCQAS seed is below every seed of every method that we ran; with three seeds we claim no statistical significance, as WZkM advised. We added CRLQAS, CEO-ADAPT, and the learned-predictor baseline BQAS-SSL.
  • Noise (ycsQ, WZkM). Under shot noise, we added a Pool GA with the same MPS-derived initialization and the exact errors of the final circuits. GCQAS has the lowest mean recorded and exact errors of the methods that we ran; we agree that this is suggestive and does not demonstrate noise-robust architectures.
  • Reproducibility (WZkM). Algorithms 1–7 and all 16 inputs are specified; WZkM found this response satisfying.
  • Cost across qubit counts (WZkM's remaining question). Our last response reports wall-clock time, circuit-training memory, and success rates on eight benchmarks (8–16 qubits). GCQAS meets the success target on every seed of all eight (LiH-12 is now complete). It reaches each baseline's attained performance in 0.06–0.48× the time of both PFNs4BO+GA variants on all eight, in under 0.08× that of CRLQAS and TensorRL (where run), and faster than Pool GA on five of eight. Its memory is within about 9% of the surrogate-free Pool GA. These results are specific to our implementations and shared hardware.

4. Scope and future work Following the reviewers' advice, we position GCQAS as a problem-agnostic search, not a replacement for constructions specialized for chemistry such as CEO-ADAPT. We state as future work: synthetic labels informed by domain knowledge, gate noise and readout errors with validation on quantum hardware, non-genetic search frameworks (Uvht), further learned-predictor baselines, and a controlled scaling study on larger circuits. We have uploaded an updated manuscript that incorporates the discussion; our last response to WZkM, whose reply we await, will be in the later version.

Thank you for your time and guidance!

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

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