acceptodds
Under review as a conference paper at ICLR 2027

Beyond Independent Candidates: Joint Quantum Reasoning for Ambiguous Structured Generation

Abstract

Structured generation often requires selecting among multiple plausible interpretations of an underspecified input. Existing ambiguity-aware approaches preserve multiple valid outputs during learning, but typically score candidate structures independently, ignoring how competing interpretations agree or conflict with one another. We introduce a hybrid quantum–classical framework that instead reasons jointly over the candidate set. A classical generator produces multiple structured candidates, which are represented as relational graphs and encoded into a shared candidate-indexed quantum state. Pairwise structural disagreements condition parameterized quantum interactions, allowing the probability assigned to each candidate to depend on its relationships with competing hypotheses. Because several interpretations may be simultaneously valid, we further introduce a quantum multi-valid objective that maximizes measurement probability over the valid-candidate subspace rather than a single reference. We additionally derive finite-shot selection-stability conditions based on probability margins between competing interpretations. Experiments on text-to-SQL and text-to-visualization benchmarks show that the proposed framework outperforms classical graph reasoning, parameter-matched joint reasoning, and candidate-wise quantum baselines, reaching 62.5 and 73.4 exact match on nvBench and Spider, respectively. The gains increase with ambiguity, while finite-shot, circuit-depth, and quantum-noise analyses characterize robustness under quantum execution constraints.

Primary area:
neurosymbolic & hybrid AI systems (physics-informed, logic & formal reasoning, etc.)
Keywords:
Ambiguous Structured Generation, Quantum Reasoning, Multi-Valid Learning, Relational Graphs

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_jBSaOpenReview ↗
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Paper summary

The paper proposes a quantum–classical model for selecting among candidate SQL queries or visualization specifications generated by an LLM. It represents candidates as relational graphs and uses structural differences to drive joint quantum interactions. Training rewards the total probability assigned to valid candidates, although inference returns only one answer. Evaluation on Spider and nvBench includes baseline comparisons, ablations, measurement and noise analyses, and a small hardware study. The contribution is primarily a candidate reranking method rather than a mechanism for clarifying user intent.

Critical strengths
  1. The model explicitly compares structural differences between candidates. This is a useful design choice for SQL and visualization outputs, where plausible candidates may differ in a join, grouping, or filter.

  2. The evaluation goes beyond ideal simulation. Finite-shot, noise, and small-scale hardware experiments examine whether the learned candidate rankings survive execution constraints. These results help assess the gap between the proposed model and its behavior on a physical device.

Critical weaknesses
  1. The formulation does not adequately address ambiguity in user intent. When candidates represent different plausible interpretations, selecting the highest-probability output does not establish what the user intended. The system neither asks for clarification nor explains its chosen interpretation. Benchmark agreement alone therefore provides limited evidence of practical ambiguity resolution. The paper should distinguish equivalent expressions of one intent from genuinely different intents and establish when automatic selection is appropriate.

  2. The practical cost of the proposed approach remains unclear. The paper reports theoretical complexity and logical quantum resources, but not training time, inference latency, or measured resource use relative to classical baselines. Without these measurements or comparisons under equal compute budgets, it is difficult to assess whether the quantum–classical architecture offers a worthwhile practical trade-off.

Questions for authors
  1. When candidates represent different plausible user intents, how does your method avoid returning an answer based on the wrong interpretation, given that it neither asks the user for clarification nor explains the interpretation it selects?

  2. Can you report training time, per-example inference latency, and measured resource use for JointQ-Multi and the classical joint baseline under comparable conditions? Does the performance advantage persist under matched compute budgets?

3 comments
AuthorsOpenReview ↗

Response to Critical Weaknesses

Thank you for recognizing the usefulness of structural disagreement modeling and the finite-shot, noise, and hardware evaluations. We appreciate the concerns regarding user-intent ambiguity and computational costs and have revised the manuscript accordingly.

W1. Distinguishing benchmark equivalence from genuine user-intent ambiguity.

We agree that selecting the highest-probability candidate does not necessarily establish the user's intended interpretation, particularly when multiple semantically distinct interpretations remain plausible. We have clarified this distinction in Sections 3.1, 3.4, and 5.4.

Our framework addresses benchmark-verified candidate selection, rather than interactive user-intent recovery. We distinguish between (i) structurally different expressions with equivalent benchmark-verified semantics and (ii) genuinely different interpretations of an underspecified request. The multi-valid objective avoids penalizing alternative verified outputs but does not independently determine the user's intended meaning. For Spider, verified alternatives must satisfy both canonicalized structural compatibility and execution agreement with the reference SQL query, as detailed in Appendix F.2. These alternatives should therefore not automatically be interpreted as independently verified user intents.

We have clarified that the proposed architecture is a joint candidate-ranking mechanism, not an interactive clarification system. Its selected output represents the highest-ranked candidate under benchmark supervision rather than guaranteed recovery of user intent.

Automatic selection may be appropriate when a single structured output is required and the remaining uncertainty is acceptable. When distinct interpretations could lead to materially different or consequential outcomes, user clarification would be preferable. A probability-margin-based clarification mechanism is a possible extension but is not part of the evaluated system. These revisions clarify the scope and limitations of our contribution without changing the underlying formulation.

AuthorsOpenReview ↗

Response to Critical Weaknesses (CONT.)

W2. Practical computational cost and performance trade-off.

We thank the reviewer for emphasizing the importance of practical computational efficiency alongside predictive performance. We agree that theoretical complexity and logical quantum-resource estimates alone are insufficient to establish a favorable cost-performance trade-off. We have expanded the resource analysis in Section 5.3 and clarified the computational limitations in Section 5.4.

Our evaluation compares JointQ-Multi with Classical Joint-Set using identical cached candidate pools, graph-input protocols, disagreement features, and validation-based training procedures. JointQ-Multi employs three candidate-register qubits, four feature-register qubits, two reasoning layers, and five disagreement categories. With K=5K=5, this corresponds to seven logical qubits, ten candidate pairs, and 100 logical interaction factors.

Table R1. Performance and computational-resource comparison.

MetricClassical Joint-SetJointQ-Multi
nvBench EM (%)60.1 ± 0.462.5 ± 0.2
Spider EM (%)71.2 ± 0.373.4 ± 0.2
Training time, nvBench (min)48125
Training time, Spider (min)65168
Inference latency (ms/example)9.228.5
Peak GPU memory (GB)2.12.8
Maximum candidates55
Trainable interaction coefficients1010
Candidate-register qubitsN/A3
Feature-register qubitsN/A4
Total logical qubitsN/A7
Candidate pairs (K=5K=5)1010
Logical quantum interaction factorsN/A100
Hardware evaluation shots/exampleN/A1,024

The reported measurements demonstrate an accuracy–cost trade-off. JointQ-Multi improves EM by 2.4/2.2 percentage points on nvBench/Spider but requires approximately 2.6 times longer training. Its inference latency is 28.5 ms/example, compared with 9.2 ms/example for Classical Joint-Set, representing approximately 3.1 times higher latency. Peak GPU memory also increases from 2.1 GB to 2.8 GB. These results indicate that the predictive improvements incur additional computational overhead.

Importantly, the reported training and inference costs reflect the evaluated simulation-based configuration, not end-to-end physical quantum hardware execution. Matching the number of interaction coefficients also does not establish equivalent computational budgets. We therefore make no claim of quantum speedup or superior efficiency under matched compute.

We have clarified these distinctions in Sections 5.3–5.4 and Appendix D. Our contribution concerns the empirical effectiveness of disagreement-conditioned quantum candidate reasoning, while establishing practical hardware-level advantages requires further evaluation under matched resource budgets.

AuthorsOpenReview ↗

Response to Questions

Q1. How does the framework avoid returning a candidate based on the wrong user interpretation without clarification or explanation?

We appreciate this question and agree that distinguishing candidate ranking from user-intent recovery is important. Our framework selects the highest-ranked structured candidate using relational representations and disagreement-conditioned joint interactions. However, the selected candidate is not guaranteed to correspond to the user's intended interpretation when multiple semantically distinct intents are plausible.

As clarified in Sections 3.1 and 3.4, structurally different candidates do not necessarily represent different user intents. Some correspond to alternative SQL or visualization formulations with benchmark-verified equivalent semantics, whereas others may reflect genuinely competing interpretations. The multi-valid objective rewards probability assigned to verified alternatives rather than penalizing all outputs other than a single reference. However, it does not resolve uncertainty about unobserved user preferences. We therefore clarify that our method performs ambiguity-aware candidate selection rather than interactive intent disambiguation. The current implementation neither asks clarification questions nor generates explanations of the selected interpretation.

For applications requiring greater assurance, candidate-probability margins or calibrated uncertainty estimates could help identify cases requiring user clarification. Such mechanisms would require separate evaluation and are not part of the present framework. Accordingly, our results concern candidate selection under benchmark-specific validity criteria, not guaranteed recovery of user intent.

Q2. Can you report training time, inference latency, and measured resource use under comparable conditions? Does the advantage persist under matched compute budgets?

We agree that practical resource comparisons are essential for evaluating deployment trade-offs. We have expanded Section 5.3 and summarized the measurements in Table R1 of our response to W2. JointQ-Multi requires 125/168 minutes of training on nvBench/Spider, compared with 48/65 minutes for Classical Joint-Set. Its inference latency is 28.5 versus 9.2 ms/example, and peak GPU memory is 2.8 versus 2.1 GB.

The default quantum configuration uses seven logical qubits, ten candidate pairs, and 100 logical interaction factors. The physical-device study evaluates 120 examples with 1,024 shots each, totaling 122,880 measurement shots. These hardware measurements are separate from the reported simulation-based inference latency and do not represent end-to-end physical-device execution time.

JointQ-Multi achieves 2.4/2.2 EM-point improvements over Classical Joint-Set on nvBench/Spider under the evaluated conditions. Both methods use identical cached candidate pools, relational input protocols, and validation-based hyperparameter selection. However, these experiments do not establish that the improvements persist under identical training-time or inference-time computational budgets.

We therefore distinguish the controlled accuracy comparison from an equal-compute efficiency claim. A fully matched resource evaluation would additionally account for candidate generation, graph preprocessing, quantum simulation, circuit compilation, hardware execution, and tuning effort. We have clarified these limitations in Sections 5.3–5.4 and Appendix D. Our contribution concerns the empirical effectiveness of disagreement-conditioned quantum candidate reasoning rather than computational speedup.

Reviewer_eQxjOpenReview ↗
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Paper summary

The paper treats ambiguity in structured generation as a set-level reasoning problem. A classical generator produces up to five candidate SQL queries or visualization specifications, each is converted into a typed relational graph, and the graph representations are encoded into a joint state over a candidate register and a feature register. Cross-candidate interactions are parameterized by a disagreement vector - typed differences in joins, grouping, aggregation, conditions, values - so the strength of the coupling between two candidates depends on how much their structures differ. A multi-valid objective maximizes the total measurement probability over the verified valid-candidate subspace rather than a single reference, and the candidate with the largest Born-rule probability is selected.

Critical strengths

1.Reframing ambiguity as reasoning over a set, rather than scoring each candidate alone, is the right conceptual move, and the architecture keeps the expensive parts classical. The quantum module only mixes the candidate register, which is a defensible division of labour. 2.The multi-valid objective addresses a real problem: with several valid interpretations, single-reference cross-entropy penalizes correct outputs. The paper is also careful to state that this is an objective-level property and not a generalization claim, which is the honest reading of Proposition 4.2. 3.The ablation ladder is exactly what one wants: candidate-wise, joint without disagreement, joint with shuffled disagreement, joint with single-reference supervision, joint with multi-valid supervision. Each step moves one factor, and the shuffled-disagreement control is the one that tells us the features carry information rather than the extra capacity. 4.The parameter-matched classical joint-set baseline is the control most quantum-ML papers omit, and the reported margin over it is modest and credible rather than spectacular.

Critical weaknesses

1.The quantum module is a small classically simulable mixing layer, and the paper does not say what it buys. Three candidate qubits and four feature qubits with two layers of exp(-i θ d T x P) is a 128-dimensional model. The authors state that they claim no speedup, which is right, but then the contribution reduces to 'this unitary parameterization beats an MLP of matched parameter count by about two points'. Why is not analysed: no inspection of the learned angles, no test of whether a wider MLP or a small attention layer closes the gap, no argument that unitarity or entanglement is doing the work. A single-qubit ablation or an entanglement-capacity sweep would make the claim about the mechanism rather than about the architecture. 2.The standard candidate-selection baselines are missing. Listwise reranking, minimum-Bayes-risk or consensus decoding, execution-guided selection, and self-consistency are the obvious ways to exploit a candidate pool, and none is on the table. The classical joint-set baseline is constructed by the authors, so it is a strawman until a published reranker is compared. Given that valid candidates are identified by execution, 'run all five, keep the executable ones, take the modal result' is a strong, essentially free baseline. 3.Where the valid set comes from is underspecified in the main text. Spider provides one gold query per example, so Svalid has to come from execution equivalence against the gold result. If so, the 'valid subspace' is derived from the gold answer, and the method is closer to execution-guided reranking than to ambiguity modelling. The training and inference asymmetry - validity used only in training - needs the exact procedure in the main paper, not only in Appendix F.4. 4.The theory is elementary and reads more portentously than it is. Lemma 4.1 is a tautology: the objective depends only on the total valid mass, so redistributing within the valid set cannot matter. Proposition 4.2 is algebra. Theorem 4.3 is a first-order product-formula Lipschitz bound, and Theorem 4.4 is Hoeffding plus a union bound. All correct, but the perturbation bound ED sums |θ| times |ξ| over all pairs and layers and is very loose, so the decision-stability condition Δ > 2 ED is unlikely to be checkable on real data. A short appendix would be enough. 5.Statistics and tuning protocol. Three seeds with standard deviations of 0.2-0.4 and a headline gap of 2.4 points is fine on its face, but the candidate pool is shared and cached across methods, so the variance reflects training only and a paired test is the appropriate one; none is reported for the main table. It also matters whether the quantum arm and the classical joint-set arm received the same hyperparameter budget - the paper should state the tuning protocol explicitly.

Questions for authors

1.What happens if a listwise reranker, consensus/self-consistency over executions, or MRR decoding is used as the baseline instead of the authors' classical joint-set model? 2.How exactly is Svalid computed for Spider, and is the gold result used to define it? 3.Can you show that the gain comes from the quantum parameterization rather than extra capacity - for example by widening the classical joint-set MLP or by replacing the unitary with a learned K x K matrix of the same rank? 4.What do the learned angles θr look like, and does the disagreement conditioning survive when the interaction is ablated to a single learned scalar per pair? 5.Were the quantum and classical arms tuned with the same budget? Please report a paired test on the main comparison.

4 comments
AuthorsOpenReview ↗

Response to Critical Weaknesses

First, we thank you for the detailed technical assessment and for recognizing the merits of our set-level formulation, multi-valid supervision, and controlled ablations. We have revised the manuscript to clarify the quantum mechanism, classical comparisons, validity assignment, theoretical scope, and statistical evaluation.

W1. Contribution of the quantum parameterization.

We agree that our seven-qubit, two-layer model is classically simulable and that improvements over an interaction-parameter-matched classical model do not establish a uniquely quantum advantage. Our objective is to investigate disagreement-conditioned unitary mixing for candidate reasoning. The effective interaction angle is aijr(ℓ)=θr(ℓ)dij(r)a_{ijr}^{(\ell)}=\theta_r^{(\ell)}d_{ij}^{(r)}, which couples candidates according to their structural disagreements. We clarified the product-form implementation in Section 3.3 and the ablation definitions in Appendix D.

Table R1. Cross-candidate reasoning ablation (EM, %).

VariantnvBenchSpider
Candidate-wise Quantum59.4 ± 0.370.8 ± 0.3
JointQ + Unconditioned Interactions60.0 ± 0.471.2 ± 0.3
JointQ + Shuffled Disagreement59.7 ± 0.471.0 ± 0.4
Joint Quantum + Single61.2 ± 0.372.0 ± 0.3
JointQ-Multi (Ours)62.5 ± 0.273.4 ± 0.2

The unconditioned variant preserves interactions without pair-specific disagreement, while shuffling disrupts structural correspondence. Both reduce performance relative to JointQ-Multi. Stronger classical comparisons further include Wider Classical Joint-Set (60.9/71.8 EM) and Set Transformer (61.4/72.4 EM). These results support the effectiveness of the proposed parameterization but do not isolate entanglement or unitarity as the source of improvement. Additional mechanism-specific controls remain necessary.

W2. Missing standard candidate-selection baselines.

We agree that comparisons with listwise reranking, minimum-Bayes-risk decoding, consensus/self-consistency, and execution-guided selection are important for evaluating joint candidate reasoning.

We have expanded Table 7 in Section 5.3 to include Wider Classical Joint-Set, Deep Sets, Set Transformer, listwise neural reranking, minimum-Bayes-risk decoding, and self-consistency/consensus. These shared-pool comparisons use identical cached candidates, while recent SQL-selection approaches, including CHASE-SQL, DPC, R³-SQL, MAP-SQL, and JudgeSQL, are reported separately because their evaluation protocols and metrics differ.

Under the reported shared-pool comparisons, JointQ-Multi achieves 62.5/73.4 EM on nvBench/Spider, compared with 60.1/71.2 for Classical Joint-Set, 61.4/72.4 for Set Transformer, and 54.7/66.8 for Candidate + LLM Rerank. These results provide broader classical comparisons without establishing superiority under matched computational budgets.

We also clarify that SQL executability does not guarantee semantic correctness and that gold-reference information is unavailable during inference. Finally, our earlier ambiguity-stratified results require recomputation to reconcile subgroup accuracy with overall performance and coverage; we withdraw those numerical subgroup claims pending verification. These clarifications are reflected in the revised discussion of comparison scope and limitations.

AuthorsOpenReview ↗

Response to Critical Weaknesses (cont.)

W3. Construction of the valid-candidate set.

We appreciate this observation and agree that the supervision protocol should appear in the main manuscript rather than exclusively in the appendix. We have expanded Section 3.4 to explain the construction of Svalid(x)=S(x)∩Yver(x)\mathcal S_{\mathrm{valid}}(x)=\mathcal S(x)\cap\mathcal Y_{\mathrm{ver}}(x).

For nvBench, verified outputs are determined using canonicalized, benchmark-supported visualization specifications. For Spider, which provides a single gold SQL query, a generated candidate is accepted as a verified alternative only when it satisfies both canonicalized structural compatibility and execution-result agreement with the reference query. Execution agreement alone is insufficient. Further details are provided in Appendix F.2.

Crucially, neither the gold SQL query nor validity indicators are supplied to the model during inference. The model receives the input, candidate graphs, and pairwise disagreement features to predict candidate probabilities. We also clarify that benchmark-verified equivalent outputs do not necessarily represent distinct user intents. Our method addresses ambiguity-aware candidate selection rather than interactive recovery of unobserved user intent.

W4. Theoretical analysis and presentation.

We agree that the algebraic properties of the multi-valid objective should not be presented as novel generalization guarantees. We have shortened Section 4 and retained the detailed theoretical statements and proofs in Appendix A. The main paper now emphasizes the interpretation and limitations of these results. In particular, the disagreement-perturbation quantity

ED=∑ℓ,i<j,r∣θr(ℓ)∣∣ξij(r)∣E_D=\sum_{\ell,i<j,r}|\theta_r^{(\ell)}||\xi_{ij}^{(r)}|

provides a conservative worst-case bound. The condition Δ>2ED\Delta>2E_D is sufficient for selection stability but is not claimed to be tight or routinely certifiable in practice. We have also clarified that the implemented quantum evolution uses a fixed-order first-order product of interaction unitaries rather than the exact Hamiltonian exponential (Section 3.3 and Appendix B). These revisions distinguish mathematical properties of the proposed formulation from empirical performance improvements.

W5. Statistical significance and hyperparameter tuning.

We agree that statistical testing and fair tuning are important given the modest accuracy differences. We have expanded Section 5.1 to report the optimization protocol: Adam, batch size 16, maximum 30 epochs, early-stopping patience 5, seeds {13,42,2026}\{13,42,2026\}, learning rates {5×10−4,10−3,2×10−3}\{5\times10^{-4},10^{-3},2\times10^{-3}\}, and applicable reasoning depths {1,2,3,4}\{1,2,3,4\}. Hyperparameters are selected using validation data.

We additionally report an approximate independent-sample Welch analysis in Section 5.3. Based on rounded three-seed summary statistics, the two-sided pp-values are approximately 0.0029 and 0.0009 for nvBench and Spider, with 95% confidence intervals of [1.57, 3.23] and [1.59, 2.81] EM points, respectively.

These estimates characterize training-seed variability under the Welch-test assumptions. Because candidate pools are shared, a paired example-level test would provide more directly relevant evidence but cannot be reconstructed from aggregate statistics. We also clarify that comparable optimization protocols do not establish identical computational tuning budgets.

AuthorsOpenReview ↗

Response to Questions

Q1. What happens when listwise reranking, consensus/self-consistency, or minimum-risk decoding is used instead of Classical Joint-Set?

We appreciate this suggestion and agree that comparisons with established candidate-selection strategies are important. We have expanded Table 7 in Section 5.3 to include Wider Classical Joint-Set, Deep Sets, Set Transformer, listwise neural reranking, minimum-Bayes-risk (MBR) decoding, and self-consistency/consensus. Recent SQL-selection approaches, including CHASE-SQL, DPC, R³-SQL, MAP-SQL, and JudgeSQL, are presented separately because their metrics and evaluation protocols differ.

Under the reported shared-pool comparisons, JointQ-Multi achieves 62.5/73.4 EM on nvBench/Spider, compared with 60.1/71.2 for Classical Joint-Set, 61.4/72.4 for Set Transformer, 61.1/72.0 for listwise reranking, 60.5/71.7 for MBR decoding, and 59.6/71.3 for consensus. These results broaden the classical comparison while retaining identical candidate pools. We also clarify that SQL executability does not guarantee semantic correctness and that gold-reference information is unavailable during inference. Differences in evaluation protocols prevent direct ranking against published SQL-generation pipelines.

Q2. How is the valid-candidate set computed for Spider? Is the gold result used?

Yes. We thank the reviewer for identifying the need to clarify this distinction. We have incorporated the essential validity-assignment procedure into Section 3.4, with additional details in Appendix F.2. The verified valid-candidate set is defined as

Svalid(x)=S(x)∩Yver(x).\mathcal S_{\mathrm{valid}}(x)=\mathcal S(x)\cap\mathcal Y_{\mathrm{ver}}(x).

Spider provides a single gold SQL query per example, which is parsed and canonicalized during training and evaluation. A generated candidate is accepted as a verified alternative only when it satisfies both:

  1. Structural compatibility: Canonicalized structural compatibility with the gold SQL query.
  2. Execution agreement: The same execution result as the gold query on the corresponding database.

Execution agreement alone is insufficient because different SQL queries may produce identical results on a particular database instance. The resulting validity indicators determine the multi-valid supervision targets. Examples without verified valid candidates are excluded from the candidate-selection training loss but remain included in coverage and end-to-end evaluations.

Training versus inference. Gold queries, reference execution results, and validity indicators are used only for supervision and evaluation. They are not provided to the model during inference, which uses the natural-language input, generated candidates, relational graphs, and pairwise disagreement features. We also clarify that benchmark-verified alternatives do not necessarily represent distinct user intents.

Q3. Does the improvement arise from quantum parameterization rather than additional classical capacity?

We agree that this distinction is essential. Our controlled comparison uses identical cached candidate pools, relational graph encoders, projected feature dimensions, disagreement vectors, and multi-valid supervision. For L=2L=2 reasoning layers and R=5R=5 disagreement categories, both interaction modules contain

Pinteraction=LR=10P_{\mathrm{interaction}}=LR=10

trainable disagreement-interaction coefficients. Classical Joint-Set achieves 60.1/71.2 EM, compared with 62.5/73.4 EM for JointQ-Multi on nvBench/Spider. We additionally report Wider Classical Joint-Set (60.9/71.8) and Set Transformer (61.4/72.4) to examine stronger classical alternatives.

However, matching interaction coefficients does not imply equal total model capacity or computational cost. These comparisons support the empirical effectiveness of the proposed parameterization but do not establish that entanglement or unitarity causes the improvements. A learned K×KK\times K candidate-mixing operator and additional mechanism-specific ablations remain relevant future controls. We have clarified these limitations in Sections 5.3–5.4.

AuthorsOpenReview ↗

Response to Questions (cont.)

Q4. What do the learned angles look like, and does disagreement conditioning remain beneficial with scalar-per-pair interactions?

The proposed model uses trainable relation-specific quantum interaction angles. For relation type rr, candidate pair (i,j)(i,j), and reasoning layer ℓ\ell, the effective angle is aijr(ℓ)=θr(ℓ)dij(r)a_{ijr}^{(\ell)}=\theta_r^{(\ell)}d_{ij}^{(r)}, where θr(ℓ)\theta_r^{(\ell)} is trainable and dij(r)d_{ij}^{(r)} represents structural disagreement. Thus, interactions depend on both the learned parameters and the type and magnitude of disagreement between candidates.

The controlled ablations in Table 5 examine the importance of structural conditioning:

VariantnvBench EMSpider EM
JointQ + Unconditioned Interactions60.0 ± 0.471.2 ± 0.3
JointQ + Shuffled Disagreement59.7 ± 0.471.0 ± 0.4
Joint Quantum + Single61.2 ± 0.372.0 ± 0.3
JointQ-Multi62.5 ± 0.273.4 ± 0.2

The unconditioned variant preserves cross-candidate interactions while replacing pair-specific disagreements with constants, reducing performance by 2.5/2.2 EM points. Shuffling disagreement vectors reduces performance by 2.8/2.4 points on nvBench/Spider. These findings support the importance of meaningful structural conditioning.

We have clarified the interaction formulation in Section 3.3 and the ablation definitions in Appendix D. However, the reported results do not include learned-angle distributions or a scalar-per-pair replacement experiment. Therefore, the ablations support the contribution of typed disagreement conditioning within our architecture but do not establish that simpler scalar interactions or alternative classical mixing mechanisms would perform worse.

Q5. Were the quantum and classical models tuned under the same budget? Can you report a paired statistical test?

We thank the reviewer for emphasizing statistical rigor and tuning fairness. We have expanded Section 5.1 and Appendix D.4 to clarify the training protocol. Both controlled models use identical cached candidate pools, graph-encoder architectures, projected feature dimensions, optimizer families, and validation-based model selection. The documented settings are:

  • Optimizer: Adam; batch size: 16.
  • Maximum epochs: 30; early-stopping patience: 5.
  • Weight decay: 10−510^{-5}; gradient clipping: 1.0.
  • Random seeds: {13,42,2026}\{13,42,2026\}.
  • Learning rates: {5×10−4,10−3,2×10−3}\{5\times10^{-4},10^{-3},2\times10^{-3}\}.
  • Reasoning depths: {1,2,3,4}\{1,2,3,4\}, where applicable.

The default configuration uses learning rate 10−310^{-3} and reasoning depth L=2L=2, selected using validation performance.

We additionally report an approximate two-sided Welch tt-test using the three-seed summary statistics.

Table R3. Seed-level statistical comparison with Classical Joint-Set.

DatasetClassical Joint-SetJointQ-MultiEM GainApprox. pp95% CI
nvBench60.1 ± 0.462.5 ± 0.2+2.40.0029[1.57, 3.23]
Spider71.2 ± 0.373.4 ± 0.2+2.20.0009[1.59, 2.81]

Both comparisons yield approximately p<0.01p<0.01, with confidence intervals excluding zero under the Welch-test assumptions. These estimates use rounded statistics from three training runs per method and quantify training-seed uncertainty rather than paired example-level uncertainty. A paired bootstrap or McNemar test would be more directly responsive to the reviewer's concern but requires matched per-example predictions, which cannot be reconstructed from aggregate statistics.

Finally, a common training protocol does not establish identical wall-clock tuning costs or equal numbers of completed trials. We have clarified this limitation in the revised manuscript and do not claim superiority under matched computational budgets.

Reviewer_HchMOpenReview ↗
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Paper summary

The paper reframes ambiguity-aware structured generation as joint hypothesis-set reasoning rather than independent candidate scoring. Candidate structured outputs (SQL queries or visualization specifications) are converted into relational graphs, jointly encoded in a candidate-indexed quantum state, and coupled by parameterized quantum interactions conditioned on typed structural disagreements. A quantum multi-valid objective maximizes total measurement probability over the verified valid-candidate subspace rather than a single reference. The authors provide stability analyses for disagreement perturbations and finite-shot measurement, and evaluate on nvBench (text-to-visualization) and Spider (text-to-SQL) with LLaMA-2-13B, comparing against deterministic generation, candidate reranking, independent graph reasoning, an interaction-parameter-matched classical joint-set, and candidate-wise quantum baselines.

Critical strengths
  1. The paper redefines ambiguity-aware structured generation as a set-level reasoning problem, moving beyond independent candidate scoring. By introducing a candidate-indexed quantum state with disagreement-conditioned transitions, it provides a principled mechanism for one interpretation's probability to depend on its structural relationships with competing hypotheses.
  2. The paper proposes a multi-valid objective that maximizes the aggregate probability over the verified valid-candidate subspace, avoiding the penalty on legitimate alternatives in single-reference training. Theoretical guarantees, including valid-subspace invariance and lower-bound properties, further ensure its soundness for multi-answer tasks.
Critical weaknesses
  1. Unsubstantiated quantum advantage: The gain over the parameter-matched classical joint model is marginal (2.4/2.2 EM). Without a strong classical baseline (e.g., a Set Transformer ingesting the same disagreement features), the specific value of the quantum mechanism remains unconvincing.
  2. Pipeline bottleneck: Candidate coverage failure is the dominant end-to-end error source (21.4% on nvBench, 13.9% on Spider). When the upstream LLM fails to generate a valid candidate, the joint reasoning module cannot recover it, severely limiting the practical impact of the proposed quantum framework.
Questions for authors
  1. Can you compare against a stronger classical baseline (e.g., a Set Transformer with identical disagreement features)? Without it, how can the marginal 2.4/2.2 EM gain be attributed to the quantum mechanism rather than architectural differences?
  2. Are the marginal EM improvements over the classical baseline statistically significant?
  3. Since candidate coverage failure is the dominant error source (21.4%/13.9%), how does the quantum module's relative benefit persist if evaluated with stronger generators or larger k_max?
3 comments
AuthorsOpenReview ↗

Response to Critical Weaknesses

First, we would like to thank you for recognizing the contributions of joint hypothesis-set reasoning and multi-valid supervision. We appreciate the constructive concerns regarding classical comparisons and candidate-coverage limitations.

W1. Quantum mechanism and stronger classical comparisons.

We agree that the improvements over our interaction-parameter-matched Classical Joint-Set baseline (2.4/2.2 EM points on nvBench/Spider) do not, by themselves, establish computational quantum advantage or isolate a uniquely quantum mechanism. Our contribution instead concerns the empirical effectiveness of disagreement-conditioned quantum interactions as a parameterization for jointly ranking structured candidates. The proposed seven-qubit model remains classically simulable, and matching the number of trainable interaction coefficients does not imply equal total model capacity or computational cost.

To address the concern regarding stronger classical baselines, we expanded Section 5.3 and Table 7 to include wider classical joint reasoning, Deep Sets, Set Transformer, listwise neural reranking, minimum-Bayes-risk (MBR) decoding, and self-consistency/consensus selection. These shared-pool comparisons use the same retained candidate sets, allowing us to examine candidate-selection performance without differences in upstream candidate generation.

Table R1. Shared-pool classical candidate-selection comparison (overall EM, %).

MethodnvBenchSpider
Classical Joint-Set60.1 ± 0.471.2 ± 0.3
Wider Classical Joint-Set60.9 ± 0.371.8 ± 0.4
Deep Sets59.8 ± 0.470.9 ± 0.4
Set Transformer61.4 ± 0.372.4 ± 0.3
Listwise Neural Reranker61.1 ± 0.372.0 ± 0.4
MBR Decoding60.5 ± 0.471.7 ± 0.4
Self-Consistency / Consensus59.6 ± 0.471.3 ± 0.4
JointQ-Multi (Ours)62.5 ± 0.273.4 ± 0.2

In the reported overall comparisons, JointQ-Multi exceeds Set Transformer by 1.1/1.0 EM points and Wider Classical Joint-Set by 1.6/1.6 points on nvBench/Spider, respectively. These results strengthen the empirical comparison against classical candidate-selection alternatives. Nevertheless, they do not establish that quantum operations themselves, rather than differences in model parameterization, account for the improvements.

We additionally include recent SQL-selection approaches, such as CHASE-SQL, DPC, R³-SQL, MAP-SQL, and JudgeSQL, in a separate benchmark-specific panel of Table 7. Because these methods may use different candidate-generation procedures, evaluation protocols, and metrics, their reported results are presented for context rather than as directly comparable controlled EM measurements.

We emphasize that our results support the effectiveness of the evaluated disagreement-conditioned joint-reasoning architecture, without claiming computational quantum advantage, matched-compute superiority, or a uniquely quantum explanation for the observed accuracy improvements.

W2. Candidate coverage and pipeline bottleneck.

We agree that candidate coverage imposes an inherent upper bound on end-to-end performance. However, it is important to distinguish upstream candidate-generation failures from downstream selection errors, since our framework specifically addresses the latter.

Let CC denote candidate coverage and AcondA_{\mathrm{cond}} conditional selection accuracy given at least one verified valid candidate. Then

Aend=CAcond,A_{\mathrm{end}}=C A_{\mathrm{cond}},

and the total error decomposes as

=(1-C)+C(1-A_{\mathrm{cond}}).$$ Using the results in Table 3, we obtain: **Table R3. Candidate coverage and error decomposition (%).** | Metric | nvBench | Spider | |:--|--:|--:| | Coverage@5 | 78.6 | 86.1 | | Coverage failure | 21.4 | 13.9 | | Conditional selection accuracy | 92.4 | 94.7 | | Selection failure across all examples | 6.0 | 4.6 | | End-to-end Multi-EM | 72.6 | 81.5 | Thus, while upstream coverage failures account for most remaining errors, JointQ-Multi selects a verified valid candidate in **92.4%/94.7% of covered cases**. This distinction is essential when evaluating a candidate-selection framework: the generator determines which interpretations are available, whereas the reasoning module determines how effectively those candidates are selected. Furthermore, our candidate-set-size analysis (Table 6) evaluates $k_{\max}\in\{3,5,8\}$ and shows improvements from 60.2/71.4 EM at $k_{\max}=3$ to 62.7/73.6 EM at $k_{\max}=8$ on nvBench/Spider. We have clarified these distinctions in Sections 5.2–5.4 and explicitly acknowledge that improving candidate generation is complementary to the proposed selection mechanism.
AuthorsOpenReview ↗

Response to Questions

We have strengthened the revised manuscript by clarifying the classical comparisons, adding a seed-level statistical significance analysis, and expanding the discussion of ambiguity-dependent performance and candidate-set scaling.

Q1. Can you compare against stronger classical baselines and isolate the contribution of the quantum mechanism?

We appreciate this important question. Our framework is evaluated against deterministic generation, candidate reranking, independent graph reasoning, an interaction-parameter-matched Classical Joint-Set model, and candidate-wise quantum reasoning. To strengthen the classical comparisons, we have expanded Section 5.3 and Table 7 to include a wider Classical Joint-Set model, Deep Sets, Set Transformer, listwise neural reranking, minimum-Bayes-risk (MBR) decoding, and self-consistency/consensus selection. All controlled candidate-based methods use the same cached candidate pools, reducing differences arising from upstream candidate generation.

Table R1. Overall Exact Match (EM, %) on nvBench and Spider.

MethodnvBench EMSpider EM
Deterministic LLM48.362.5
Candidate + Likelihood52.165.2
Candidate + LLM Rerank54.766.8
Graph + Single57.1 ± 0.468.8 ± 0.3
Graph + Multi-valid58.9 ± 0.370.3 ± 0.4
Classical Joint-Set60.1 ± 0.471.2 ± 0.3
Wider Classical Joint-Set60.9 ± 0.371.8 ± 0.4
Deep Sets59.8 ± 0.470.9 ± 0.4
Set Transformer61.4 ± 0.372.4 ± 0.3
Listwise Neural Reranker61.1 ± 0.372.0 ± 0.4
MBR Decoding60.5 ± 0.471.7 ± 0.4
Self-Consistency / Consensus59.6 ± 0.471.3 ± 0.4
Candidate-wise Quantum59.4 ± 0.370.8 ± 0.3
Joint Quantum + Single61.2 ± 0.372.0 ± 0.3
JointQ-Multi (Ours)62.5 ± 0.273.4 ± 0.2

In the reported comparisons, JointQ-Multi achieves improvements of 2.4/2.2 EM points over Classical Joint-Set, 1.6/1.6 points over Wider Classical Joint-Set, and 1.1/1.0 points over Set Transformer on nvBench/Spider, respectively. These results extend our evaluation beyond the original interaction-parameter-matched control and indicate favorable performance under the evaluated shared-pool settings.

To examine the contribution of structural conditioning, Table 5 additionally compares candidate-wise quantum processing, unconditioned cross-candidate interactions, shuffled disagreement features, and single-reference supervision. The unconditioned-interaction and shuffled-disagreement variants achieve 60.0/71.2 and 59.7/71.0 EM, respectively, compared with 62.5/73.4 for JointQ-Multi. The former removes candidate-specific disagreement conditioning while retaining interactions; the latter disrupts the correspondence between candidate pairs and their structural disagreements. These ablations help distinguish the effects of joint processing, structural conditioning, and multi-valid supervision.


Q2. Are the improvements over the classical baseline statistically significant?

To address this concern quantitatively, we performed an additional seed-level statistical analysis using the reported mean and standard deviation across three training runs per method. Specifically, we applied a two-sided Welch tt-test to the reported summary statistics, allowing unequal variances between the compared methods. The resulting significance estimates are reported below.

Table R3. Statistical analysis of JointQ-Multi versus Classical Joint-Set.

DatasetClassical Joint-SetJointQ-MultiEM GainApprox. pp-value95% CI for Gain
nvBench60.1 ± 0.462.5 ± 0.2+2.40.0029[1.57, 3.23]
Spider71.2 ± 0.373.4 ± 0.2+2.20.0009[1.59, 2.81]

Both comparisons yield p<0.01p<0.01 under the Welch-test assumptions, and the corresponding confidence intervals exclude zero. This provides evidence that the observed differences are not explained solely by variation across the reported training seeds.

We have incorporated this analysis into the revised manuscript. These calculations are based on rounded seed-level summary statistics (n=3n=3 per method) and assume independent, approximately normal run-level observations. Because the candidate pools are shared, paired example-level testing would provide complementary evidence; the reported Welch analysis specifically quantifies uncertainty associated with training-seed variation rather than paired prediction disagreements.

AuthorsOpenReview ↗

Response to Questions (cont.)

Q3. How does the benefit persist with stronger generators or larger candidate sets?

We agree that candidate coverage is an important limitation of selection-based structured generation. Our method targets downstream selection rather than upstream generation, and we have clarified this distinction in the revised paper. The submitted candidate-set-size experiments evaluate kmax⁡∈{3,5,8}k_{\max}\in\{3,5,8\} using LLaMA-2-13B with a consistent generation protocol.

Table R4. Effect of candidate-set size on JointQ-Multi.

kmax⁡k_{\max}nvBench EMSpider EMGain over preceding size (nvBench/Spider)
360.2 ± 0.371.4 ± 0.3—
562.5 ± 0.273.4 ± 0.2+2.3 / +2.0
862.7 ± 0.373.6 ± 0.3+0.2 / +0.2

Increasing kmax⁡k_{\max} from 3 to 5 produces substantial improvements, whereas further increasing it to 8 yields diminishing returns. This motivates our default setting of kmax⁡=5k_{\max}=5, particularly because dense pairwise candidate interactions scale as O(K2)O(K^2).

We additionally distinguish candidate coverage from downstream selection effectiveness.

Table R5. Candidate coverage and conditional selection at kmax⁡=5k_{\max}=5.

MetricnvBenchSpider
Coverage@152.7%66.1%
Coverage@369.8%79.7%
Coverage@578.6%86.1%
Uncovered cases21.4%13.9%
Conditional selection accuracy92.4%94.7%
End-to-end Multi-EM72.6%81.5%

Let CC denote candidate coverage and AcondA_{\mathrm{cond}} denote conditional selection accuracy. Then the end-to-end valid-set accuracy is

Aend=CAcond,A_{\mathrm{end}}=C A_{\mathrm{cond}},

which yields the error decomposition

1−Aend=(1−C)+C(1−Acond).1-A_{\mathrm{end}}=(1-C)+C(1-A_{\mathrm{cond}}).

Using the reported values, the remaining end-to-end errors decompose into approximately 21.4%/13.9% coverage failures and 6.0%/4.6% selection failures on nvBench/Spider.

This confirms that upstream coverage remains the dominant limitation, while the selection module achieves 92.4%/94.7% accuracy on covered examples. The candidate-size experiments establish diminishing returns with larger pools under the evaluated generator; they do not independently establish that the quantum-versus-classical performance gap persists under stronger generators. We have therefore restricted the claim to the evaluated configurations and clarified the complementary roles of upstream candidate generation and downstream joint reasoning.

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