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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
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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
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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
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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.
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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.
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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.
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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.
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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.
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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.
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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
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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?
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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.
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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.
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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?
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Can you report confidence intervals or significance tests for on BAS 4 by 4?
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Can you add learned-predictor QAS, CRLQAS, and ADAPT-VQE-style baselines, or if resources not permit explain why they are not considered?
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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?
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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
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.
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.
| Method | BAS 4×4 KL divergence |
|---|---|
| GCQAS | 7.79×10⁻⁷ ± 1.2×10⁻⁶ |
| Pool GA | 4.14 ± 1.0 |
| PFNs4BO+GA (original) | 4.31×10⁻¹ ± 2.1×10⁻¹ |
| PFNs4BO+GA (retrained) | 3.84 ± 3.2 |
| CEO-ADAPT | 1.59 ± 6.6×10⁻¹ |
| CRLQAS | 5.08 ± 1.2×10⁻¹ |
| ACLBM | 7.09×10⁻³ (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!
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.