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Under review as a conference paper at ICLR 2027

AN ESTIMAND-SEPARATED AUDIT OF SIMULATED VARIATIONAL QUANTUM FEATURE MAPS ON TABULAR DATA

Abstract

Variational quantum circuits are widely studied as feature maps for classical data, yet benchmark conclusions disagree, in part because they depend on the comparator, the objective, and the resources charged, and because evaluations pool three distinct questions: whether circuit features improve a task model, whether a classical student can reproduce a trained map, and how circuits and classical maps compare when trained directly on the task. We audit the three separately for one angle-encoded circuit family, primarily at q=6 under analytic-statevector simulation, on tabular benchmarks, binding each result to a stated cohort, comparator, and decision rule, and find that for this family and regime the observed gains trace to the classical front end and its nonlinear expansion, with no isolated gate-angle contribution detected. As augmentation, none of 28 circuit-versus-classical transform contrasts clears the benchmark-derived rule, and the one margin over raw features that does is not confirmed on an untouched cohort. Under distillation, four of 28 classical students reproduce a cached trained map, but none remains cheaper once generating and using the teacher's outputs are both charged, so reproduction is not replacement. In head-to-head training behind the same front end, screening rejects seven of 56 contrasts, none placing a circuit above a width-matched classical map. A paired optimizer control isolates the training gain at +1.1 pp, below the 2.0 pp criterion, and training the classical compression alone recovers most of it. The record supports no circuit-free replacement, hardware or end-to-end saving, or practical advantage.

Primary area:
datasets and benchmarks
Keywords:
Variational Quantum Circuits, Quantum Machine Learning, Quantum Feature Maps, Tabular Learning, Feature Learning, Classical-Quantum Comparison, Dequantization, Benchmarking

Reviews

Among:
Shape:
1234this paper, Bottom 27%
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_4ZBhOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper audits three distinct questions in VQC: whether circuit features improve a task model, whether a classical student can reproduce a trained map, and how circuits and classical maps compare when trained directly on the task, separately for one angle-encoded circuit family, primarily at q=6 under analytic-statevector simulation, on tabular benchmarks. The paper binds each result to a stated cohort, comparator, and decision rule, and finds that for this family and regime the observed gains trace to the classical front end and its nonlinear expansion, with no isolated gate-angle contribution detected.

Critical strengths
  1. The paper provides a detailed illustration of the experiments, together with the anonymous code and appendix.

  2. The authors discuss quantum training and inference costs in the paper, which is valuable for a QML paper.

Critical weaknesses
  1. The paper seems to rely heavily on AI during writing, especially with excessive use of dashes (—) and long, complex sentences. This makes the paper difficult to follow.

  2. The experiments lack generality, especially as the circuit configurations are narrow. Although the paper presents extensive analysis, its conclusion is based solely on the tabular data for q=6, making the findings appear unrepresentative.

  3. The structure of the paper seems unreasonable. The main text only consists of analysis, while all tables and experimental details/results are in the appendix. This structure makes the paper difficult to follow, especially with many cross-references across the paper. This makes the paper confusing to read back and forth between sections.

Questions for authors

Overall, the analysis and content of the paper are quite comprehensive. I think it’s just a matter of writing style, so I plan to review the revisions the author makes during the rebuttal period. If the revisions are well done, I’d be happy to accept the paper.

2 comments

Thank you for the review and for the clear statement that the concern is the writing. We have rewritten the main text; the summary of changes is in our comment to all reviewers.

W1. Writing style: dashes and long, complex sentences. We agree that the text was hard to follow. The revised main text and the three statements use shorter sentences, one claim per sentence where we could, and no em-dashes. We also replaced our internal names with standard terms and use one term per concept. Our use of AI tools is disclosed in the AI-use statement; the authors take responsibility for the text.

W2. Generality: narrow circuit configurations, q = 6, tabular data. We agree that the scope is narrow, and Section 7 opens with this. Two things changed.

  • Appendix V reports five preregistered follow-up screens that vary the design within the same family: data re-uploading over all features, one qubit per feature with up to 12 qubits, training sets of 64 to 512 rows, a readout of all 2^q − 1 probabilities, and amplitude encoding. In none does the circuit outperform classical feature maps with the same output dimension on the same input often enough to meet the preregistered rule. These screens are exploratory (mostly one seed), and the paper still makes no claim about other circuit families, larger circuits, or hardware.
  • The paper now says what we think is useful beyond this one family, which is the evaluation design. On fixed data, the same circuit looks 45.7 pp better than the best baseline or 3.5 pp worse, depending only on which baselines are included (Figure 1a). The ablation in Table 4, which trains the classical compression layer and the variational parameters separately, can be applied to any circuit pipeline with classical preprocessing. The conclusion ends with four recommendations for benchmarks.

W3. Structure: analysis in the main text, tables and results in the appendix. We agree. The main results are now in the main text: Table 1 (the three questions and their answers), Table 2 (definitions of the methods), Table 3 (all ten methods and the comparisons), Table 4 (ablation), Table 5 (what the circuit adds to the compressed coordinates), Table 6 (surrogates and cost), and Figures 1 and 3. Sections 4 and 5 can be read with their own tables and Section 6 with Figure 3 (the full list of its 56 comparisons is in Appendix Q), and the results sections follow the order of the three questions. The appendix remains as the full experimental record, with a table at its start that maps its working names to the terms of the main text.

We hope the revision addresses your concerns, and we are glad to make further changes.

Thank you for the revisions and clarifications. I appreciate the efforts to improve the presentation and clarify the scope. However, the additional experiments, mostly conducted with a single seed within the same circuit family, only partially address my concern about the narrow empirical scope. This remains a concern for my assessment, so I will maintain my rating of 2 and leave the final decision to the AC.

Reviewer_vHnxOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary

The paper audits one family of angle-encoded variational circuits as feature maps for tabular data, mostly at q = 6 under analytic statevector simulation, and separates three questions that are usually pooled. The first is whether circuit features add anything to a linear estimator that already sees the original features. The second is whether a classical student fitted to cached outputs of a trained circuit can reproduce that map at lower cost. The third is how circuits and width-matched classical transforms compare when both train on the task behind the same frozen target-informed front end. Results are bound to a stated cohort, comparator, and decision rule. The reported outcomes are null or negative. No circuit-versus-transform contrast clears a benchmark-derived 2pp joint rule, four of 28 distillation arms reproduce a cached map but none stays cheaper once teacher output generation is charged, screening rejects seven of 56 contrasts and none places a circuit above a width-matched classical arm, and a paired optimizer control isolates the gate-angle contribution at +0.05pp.

Critical strengths
  1. Insisting on three estimands instead of one is the right methodological move, and the ledger format, where every row carries a cohort, a comparator, a rule, and the inference it permits, blocks the usual slide from "a circuit was used" to "a practical advantage exists". The 49pp comparator-pool shift in Section 5 is the clearest demonstration I have seen of why that slide happens.

  2. Section 5 reports the one-shot untouched confirmation as a failure, with the mechanism, one dataset where every mapped arm collapses under an unbounded R2, and both the failed mean and the passing median. That is more informative than a cleaned-up positive result would have been.

Critical weaknesses
  1. The regime answers the question in advance. Six qubits, at most 100 training steps, an analytic simulator, a target-informed mutual-information and PCA front end that is never co-trained, and 23 outputs on tabular data. Under those constraints a width-matched classical map should win, and prior benchmarks already report it. The audit then concludes that the gain traces to the front end and its nonlinear expansion.

  2. The prose makes the record hard to use and hard to check. Sentences carry two or three nested qualifications, and the abstract alone introduces cohorts, comparators, rules, arms, lanes, and ledger status before any result appears. A reader cannot tell whether a contrast cleared a rule or was excluded from that rule's family without holding the appendix open.

Questions for authors
  1. The gate-angle isolate is +0.05pp with a 6-6-1 record, and you state that this is below the 1.3pp repeatability floor measured in Appendix L. Under your own policy, does the paired design license any attribution here, or only a null?

  2. Both tuned-head sensitivities on raw Original clear the joint rule, at +5.77/+2.77 and +6.74/+3.99pp (Table 1). Does that not indicate that the rule is sensitive to head tuning rather than to circuit value?

  3. The untouched confirmation fails its mean clause at 21.95pp, driven by one dataset where the circuit scores minus 464.4 and raw scores minus 28.3 under an unbounded metric. Was a mean rule over an unbounded R2 the right prespecified summary, and would a rank-based or clipped summary have been chosen in advance?

  4. Eight of the twelve design settings were selected using the benchmark, and none of the 37 datasets is untouched confirmation material. What inference survives beyond this roster?

  5. You state that the estimand separation is an instrument for this one family and is not offered for reuse. If the framing is not claimed and the empirical result is a null at q = 6, what is the contribution you would want a reader to carry away?

  6. Would one controlled run at q = 12 to 16 on a single dataset, with the same front end and a matched classical map, change your conclusion more than the 17-dataset sweep at q = 6?

3 comments
AuthorsOpenReview ↗

Reply to Reviewer vHnx (part 1 of 3)

Thank you for the detailed review and for the six questions. The summary of changes is in our comment to all reviewers. Your Section 5 is now Section 4.

One clarification on the summary. Counting the generation of the circuit's outputs alone leaves all four surrogates cheaper (50 to 117 times). They stop being cheaper only when the circuit is also treated as already trained. Table 6 shows the three ways of counting side by side.

W1. The regime answers the question in advance. We agree about the direction, and Section 7 says so in its first paragraph. Three points on the details.

The preprocessing is co-trained in one of the three experiments. In the feature-augmentation experiment (Q1), the compression layer is trained jointly with the circuit, for at most 100 steps. That is what makes the ablation possible: it trains the compression layer and the variational parameters separately. In the surrogate and head-to-head experiments (Q2, Q3) the compression is a frozen PCA. The old text did not make this distinction clear; Section 3 and Table 2 now do.

The head-to-head comparison has its own budget. Circuits and trainable classical feature maps are trained with the same objective (CKA with the labels), the same optimizer, and 300 steps, on the same six coordinates and with the same 23 outputs.

What the paper adds to prior benchmarks. Prior benchmarks do not say which number a benchmark would report for one circuit. On the 13-dataset subset, this circuit is +5.05 pp better than raw features and better than none of seven classical feature maps. On the 17 development datasets, its lead over the best baseline changes by 49 pp when four standard baselines are added (Figure 1a). The contribution is this decomposition, together with an ablation that locates the training gain in the classical compression layer.

We also now report five preregistered follow-up screens that leave this regime in one direction each (Appendix V): no PCA, one qubit per feature with up to 12 qubits, training sets of 64 to 512 rows, a readout of all 2^q − 1 probabilities, and amplitude encoding. None met its rule for continuing. They are exploratory and mostly one seed, and the paper says so.

W2. The prose. We agree. We rewrote the main text and the three statements: one claim per sentence, one term per concept, results in tables in the main text. Whether a comparison met the criterion is now a column of Table 3. The abstract no longer uses any of the words you list.

AuthorsOpenReview ↗

Reply to Reviewer vHnx (part 2 of 3)

Q1. Does the paired design license attribution below the 1.3 pp repeatability level, or only a null? Only a null, and the text now says exactly that (Section 4). The 1.3 pp figure is the largest difference we measured between separately executed runs of one configuration. In the ablation, all runs start from initializations that we verified to be identical by hash, so that variation cancels. What the ablation supports is a bounded null: an isolated effect of the variational parameters outside roughly ±0.5 pp is not present on these 13 datasets (95% CI [−0.26, +0.38]; [−0.51, +0.26] with matched optimizer steps). It supports no positive claim about the quantum gates. Table 5 adds a separate experiment with Ridge: trained instead of random circuit parameters give a directional +1.00 pp (13 wins, 4 losses, adjusted p = 0.09), which is not significant.

Q2. Do the tuned results on raw features show that the criterion is sensitive to tuning rather than to circuit value? They show the opposite, and we agree the old text did not make this clear. With a tuned penalty, the margin over raw features stays (+5.77/+2.77 and +6.74/+3.99 pp), and the comparisons against the seven classical feature maps still fail (0 of 14). So the pattern "better than raw features, not better than classical feature maps" is not caused by the fixed penalty. It says that the value lies in having a nonlinear feature expansion at all, and a classical feature map can supply one. In Table 5, a separate experiment, a degree-2 polynomial of the same coordinates matches the circuit (−0.10 pp); the circuit is ahead of an MLP and RFF there (+1.24 and +0.81 pp).

Q3. Was a mean criterion over an unbounded R² the right prespecified summary? In hindsight, no, and the revised text says so. We kept the criterion of the development benchmark unchanged because the purpose of the held-out evaluation was to test that criterion, not a more favorable one. The preregistration anticipated the unbounded score and specified a summary with R² clipped at zero as a secondary analysis. That summary meets all three conditions (+14.38/+4.67 pp, 10 wins, 1 loss, 1 tie), and the median and the win-loss record of the primary analysis also pass. We still report the primary result as a failed confirmation, and the recommendations at the end of the paper now say that a rank-based criterion is the better choice in advance.

Q4. What inference survives beyond these datasets? None at the level of a population of tasks, and the paper claims none. Eight of twelve design choices were tuned on the development datasets, so results on them may favor the circuit. The only evidence from outside is the 12 held-out datasets. Our confidence intervals describe resampling of the observed datasets only. Sections 3 and 7 state this.

AuthorsOpenReview ↗

Reply to Reviewer vHnx (part 3 of 3)

Q5. If the framing is not offered for reuse and the result is a null at q = 6, what is the contribution? You are right that the sentence undersold the work, and we removed it. We would like a reader to take away three things.

1, A worked example showing that pooling the three questions changes the reported conclusion by tens of percentage points on fixed data. 2. An ablation design that separates the classical compression layer from the variational parameters, from identical initializations and with matched optimizer steps. It can be run on any circuit pipeline with classical preprocessing, and it is the part of the design we do offer for reuse. The conclusion now lists it among four recommendations for benchmarks. 3. The released result logs, preregistrations, and analysis code.

Q6. Would one controlled run at q = 12 to 16 change the conclusion more than the sweep at q = 6? It would test a different claim, namely scaling, and we agree it is the natural next experiment. We can report part of it. In a preregistered screen (Appendix V, screen 2) the circuit has one qubit per feature and no PCA, with 6 to 10 qubits under the preregistered rule and up to 12 in descriptive runs. It is compared with classical feature maps that have the same output dimension and receive the same features. On the 13 datasets that were run, at one seed, this circuit scores above the 6-qubit circuit on 11, so the compression to six coordinates does cost the circuit information. It outperforms the best classical feature map on 1 of the 9 regression datasets under the rule, against a preregistered threshold of 5. This is one seed, the preprocessing differs from the main experiments because PCA is removed, and we did not run more than 12 qubits, where one circuit already takes 3.1 to 4.3 hours to train in simulation. We therefore present it as exploratory. Section 1 states that the paper makes no claim about more qubits, and Section 7 that nothing was run with more than 12.

Reviewer_GcK5OpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary

Summary: The authors carried out a large, diverse benchmark of tabular datasets for 20 classification and 17 regression tasks. This work aims to identify the possible performance gains when tabular data is encoded through quantum variational circuits, as opposed to purely classical workflows.

Critical strengths

Strengths:

  1. Great body of work with a wide diversity of ablation studies.
Critical weaknesses

Main Weakness: Honestly, it is a paper that is hard to read and follow. Most of the body of the work is presented in the Appendix. While I partially disagree with the ICLR statement, reviewers are not required to read the appendix. I partially disagree with this statement as 9 pages limit makes it hard to fit a story of the body of results. However, the authors' work presents no tables or figures in the main body of the paper. Results are summarized in the main paper, while results (figures and tables) are reported in the appendix. Even the conclusion paragraph is hard to understand what the '' take-home message '' is. I'm willing to change my score through the revision process when the body of work its explained in a simplified manner.

Questions for authors

Major Comments:

  1. A great part of the results are related to teacher models, but in Figure 1, which depicts the general pipeline of the benchmark, it's not clear what a teacher model is. Can you please clarify?
  2. The quantum features depend on a classical encoding part, which, according to Figure 1, is generated from a Transformer and a protocol that is specific to each task. How much does this classical part affect the performance/richness of the quantum embeddings?
  3. Compared to classical pipelines, beyond accuracy metrics, what is the overhead from using variational quantum circuits? This should be discussed.
1 comment

Thank you for the review, and for saying what would change your assessment. We have rewritten the main text in a simpler form; the summary of changes is in our comment to all reviewers. Results now appear in the main text (Tables 1 to 6, Figures 1 and 3), and the take-home message is the paragraph headed "Finding" in Section 1 and the first paragraph of the conclusion. In short:

Circuit features outperform raw features but not classical feature maps. A classical surrogate reproduces the trained circuit. The gain from training comes from the classical compression layer, not from the variational parameters of the circuit.

Q1. What is a teacher model? The teacher is the trained circuit itself. In the second experiment we store the 23 outputs of the trained circuit on the training rows. We then fit a small classical model, which we now call a classical surrogate, to predict those outputs from the same inputs. This is knowledge distillation with the circuit as teacher and the surrogate as student. We then ask whether the surrogate can stand in for the circuit downstream. Section 3 defines this in one paragraph, and the rest of the main text uses only the word "surrogate". Figure 2 now shows where the circuit's outputs go in each experiment; in this one they are the target of the classical surrogate.

Q2. The classical encoding "generated from a Transformer": how much does the classical part matter? We apologize for the confusion. There is no Transformer architecture in the pipeline. The box in the figure was a quantile transform, and we corrected the label. The classical preprocessing is: feature selection by mutual information, a quantile transform, a compression layer that reduces the features to 6 coordinates, and a rescaling. Figure 2 now draws the first three steps in one panel, "Classical Preprocessing", and its box labels use the terms of the main text.

How much this classical part matters is the main result of the paper, and two tables now answer it.

Ablation (Table 4, Figure 1b). All runs start from identical initializations and we train one part at a time. Training the whole pipeline gives +1.14 pp over the untrained pipeline; training only the classical compression layer gives +1.03 pp; training only the variational parameters of the circuit gives +0.05 pp (6 wins, 6 losses). The result is the same when all runs use the same number of optimizer steps. What the circuit adds to the compressed coordinates (Table 5). On the same six compressed coordinates, the circuit is +2.61 pp better than using the coordinates directly, so a nonlinear feature map after the compression helps. A degree-2 polynomial of the same coordinates does equally well (−0.10 pp). So almost all of the training gain comes from the classical part, and the nonlinear expansion that the circuit supplies can be supplied classically.

Q3. What is the overhead of variational circuits beyond accuracy? Section 5 and Table 6 report this in the main text. Training one 6-qubit circuit in simulation takes about 165 to 570 seconds per dataset and seed. A classical surrogate takes seconds. Even when the time to generate the circuit's outputs is counted as a cost of the surrogate, the four successful surrogates are 50 to 117 times cheaper to build. With 11 or 12 qubits, one circuit took 3.1 to 4.3 hours to train in simulation, against at most two seconds for the classical feature maps (Appendix V). All of these are classical simulation times. They do not measure the cost on quantum hardware, and Section 7 says so.

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