acceptodds
Under review as a conference paper at ICLR 2027

UTILIZATION OVER QUBITS: RYDBERG REGISTERS IN PHYSICS WORLD MODELS

Abstract

In hybrid classical–quantum models, how many qubits are available matters less than how well they are used. We attach an input-dependent Rydberg-atom co-processor, QUOTA, to world models on ten industry benchmarks (fusion, geothermal, fluid flow and vehicle routing; mostly released state-of-the-art models), under pre-registered rules. With the same 30 qubits, it cuts error by up to 36%, against 7% for the standard design that averages features before the qubits see them. With the classical model fixed, error falls steadily as the budget grows from 0 to 50 qubits, by 13% on shear flow and 6% on convection, following a closed-form hybrid scaling law whose 50-qubit prediction, registered before the runs, held on every seed. The gains come from allocating by signal type: the error of each prediction is split into frequency bands (Fourier octaves and wavelet tiles), the smooth, predictable (analog) bands go to the qubits, the rest (digital) stays with the classical network, and the atom positions, detunings and tethers between atom groups are set anew for every input. Most of this configuration maps onto current neutral-atom processors such as Pasqal's, one device program per input, once the detunings are re-encoded to fit the device's local addressing. For a fixed classical model, the hybrid scaling law reads , the share of error energy removed by qubits, where is the share the qubits can reach, how well they use it and ; it tells how many qubits a task can put to use.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
hybrid quantum-classical machine learning, neutral-atom quantum computing, Rydberg atom arrays, world models, scientific machine learning, neural PDE surrogates, qubit utilization, input-dependent qubit configuration, hybrid scaling laws, frequency-domain routing, fusion energy, digital twins

Reviews

Among:
Shape:
1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_bzYiOpenReview ↗
Rating
1
Confidence
1
Informativeness
1
Presentation
1
Soundness
2
Read review
Paper summary

This work introduces a technique QUOTA for input-dependent Rydberg-atom assignment. The authors demonstrate this technique on real-world physics datasets to reduce error.

Critical strengths

None

Critical weaknesses

The paper is very difficult to read and understand. The lack of exposition, the dense writing, and the poor organization limit the potential impact from the paper. For example, section 3 is difficult to read as it lacks definitions of mathematical terms and other concepts.

Questions for authors

Can you explain the core technique of this paper and how it compares to related work?

What is the error (36% and 7%) referring to in the abstract?

Can you break down the terms and concepts in section 3 such as the 'core'?

2 comments
AuthorsOpenReview ↗

Response to Reviewer bzYi

Thank you for the questions. Each is answered below: where the reviewed PDF states it, and what the revision adds to make it easier to read. Section 3 now opens with a plain-language terms table and one equation, Figure 11 (Appendix A) walks one test window through every step, Table 4 lists every lever with where it is measured, and Algorithm 1 (Appendix H) states the procedure line by line.

Q1 (Core technique and comparison to related work). A pretrained physics simulator predicts a field with some error. The classical part of the hybrid keeps what it predicts well; our goal is to put a small number of qubits to the best possible use on the rest. Prior hybrid models average the features over the grid and add one constant correction everywhere (pooled insertion); we prove in Lean 4 that this can only ever correct the spatial mean, however many qubits are added (Proposition 1). QUOTA instead routes: per input, it decomposes the error into frequency bands and tiles, sends the pieces the simulator gets wrong to groups of 10 interacting Rydberg atoms (configured per input through their laser detunings, 3-D positions and inter-group links; a registered control shows a fixed layout loses nothing, so on hardware only the detunings change per input), reads the atoms, and writes each piece's correction back; the same atoms are reused over up to eight nested passes, each routed to what is left (Algorithm 1). Unlike prior hybrid papers, every row is audited against parameter-matched classical controls under rules fixed before the runs. This comparison is in the reviewed abstract, Figure 1 and contributions 1 and 3.

Q2 (The 36% and 7% in the abstract). The reviewed abstract reads: "With the same 30 qubits, it cuts error by up to 36%, against 7% for the standard design that averages features before the qubits see them." Contribution 1 names the benchmark ("36% on convection against 7% pooled"), Table 3 gives the cell (+36.25%) and §5.5 the sentence. In numbers: on Rayleigh–Bénard convection (30 atoms, three seeds) the released CNextU-net has a mean test error (VRMSE) of 0.640; the pooled design lowers it by 7% (to 0.597); routing the same 30 atoms to the mispredicted modes lowers it by 36% (to 0.408; Figure 5a). Table 1's other numbers changed since the version you read (general comment, part 2); these two did not.

Q3 (Section 3 terms). Section 3 of the reviewed PDF defined the insertion, the register core (its Hamiltonian) and each control in separate paragraphs; the terms table now gives each in one line. Backbone: the pretrained simulator. Insertion: where the added module reads and writes (pooled grid mean, or routed error modes). Core / register: the small learnable module in that slot; the register is groups of up to 10 interacting Rydberg atoms, one atom per qubit. Detuning, drive, interaction, tether: how the input enters each atom's laser frequency, the global pulse, the r−6r^{-6} coupling between nearby atoms, and the classical link passing one group's readouts to the next. Ceiling UU and utilization: the share of the error energy in the routed modes, and the share of it the correction actually removes (Eq. 1; captured ≤U\le U).

In the supplementary page: #studio (pick a benchmark; the Architecture tab shows the backbone's traced layers, the Register tab the trained 3×10-atom register in 3-D), #passes (the passes over time), #playground (edit atoms live), #scope (terms).

Your review raises presentation only and reports confidence 1. If the first page of Section 3 and Figure 11 now read clearly, we would be grateful if you would consider whether the rating still reflects the revised paper; if a passage is still unclear, naming it would let us fix it before the discussion closes.

AuthorsOpenReview ↗

Follow-up to Reviewer bzYi

We have revised our response above. The quantity you asked about is stated in the reviewed abstract ("With the same 30 qubits, it cuts error by up to 36%, against 7% for the standard design that averages features before the qubits see them") and is now also drawn in Figure 5a; Section 3 opens with a terms table, and Figure 11 walks one example through every step. If a passage is still unclear, naming it would let us fix it before the discussion closes. Thank you for your time.

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

This paper studies how the placement and allocation of a small Rydberg-atom register affect hybrid models for physical prediction, with an additional vehicle-routing study. QUOTA contrasts pooled neck insertions with correctors operating on selected residual modes, and combines the latter with a causal frequency-wise gate between a classical backbone and persistence. It distinguishes the residual energy an allocation covers from the fraction a trained corrector actually captures. The evaluation uses released backbones where available, classical cores with matched or nearby parameter counts, interaction and mean-field ablations, and several allocation strategies. The authors find that routing and classical metric alignment account for most improvements, without establishing a robust quantum-core advantage. They also present a coverage/scaling model and a stochastic-configuration variant evaluated with an energy score.

Critical strengths
  1. The paper systematically investigates the sources of performance improvements through several classical controls, including MLP, GNN, no-interaction, and mean-field models. The authors also transparently report negative findings, including results that fail to replicate and apparent quantum advantages that disappear under stronger baselines. These analyses help distinguish gains from resource allocation and training strategies from those attributable to the quantum core, enhancing the credibility of the study.
  2. The paper provides useful insights by distinguishing residual coverage from residual predictability, showing that high theoretical error coverage does not necessarily translate into substantial prediction improvements. Furthermore, the analysis of frequency gating and persistence reveals a mismatch between the MSE training objective and the mean VRMSE evaluation metric, offering practical guidance for designing correction modules and allocating computational resources.
Critical weaknesses
  1. Proposition 1 establishes that mean pooling and constant write-back operate only on the DC component at the latent insertion site. However, the paper uses the DC share of the final prediction error to explain the limited improvements of neck-inserted modules. Since a constant perturbation in latent space may produce non-DC changes after nonlinear decoding, this theoretical explanation is not fully justified. The authors should clarify the required assumptions or limit the conclusion to direct output-space corrections.
  2. The proposed scaling law provides useful insights into how performance changes with the qubit budget, but its predictive validity remains insufficiently demonstrated. The coverage estimates rely on test residuals, while utilization efficiency is measured empirically and varies with the budget. Therefore, the reported results mainly support conditional extrapolation rather than reliable predictions of performance at unseen qubit budgets. The authors should clarify how the scaling parameters are estimated and provide stronger evidence for the claimed predictive capability.
Questions for authors
  1. What assumptions on the downstream decoder justify applying the DC-mode ceiling from latent space to the final prediction error? Is the error decomposition in Table 5 computed in latent space or output space?
  2. How are the scaling law parameters estimated, and which data splits are used? What additional predictive value does the proposed scaling law provide beyond measured residual coverage and fixed utilization efficiency? Could the authors provide results based only on training and validation data?
  3. In Appendix O, is the normalization factor D in the energy score determined by the target, the input, or fixed training statistics? If D depends on the target, how is the strict propriety of the resulting score guaranteed? Please clarify the normalization and its implications for probabilistic evaluation.
1 comment
AuthorsOpenReview ↗

Response to Reviewer tyrC

Thank you for three precise questions. Each is answered below with a measurement, and none changes a result of the paper.

Q1 (Latent vs output DC ceiling; the FFT-shell table, now Table 6). The table is computed in output space. Proposition 1 was already stated for "the latent it is attached to"; you are right that it transfers to the output only through a linear, shift-equivariant decoder, so the paper now states that condition, claims no transfer, and reports the output-space decomposition as a measurement of its own: on TRL2D the pooled neck register changes only the k=0k=0 shell (−0.49% ± 0.21%, 3/3 seeds; every other shell within noise; Figure 10h, Table 6). The explanation of the small neck gains therefore needs no decoder assumption. Every utilization ceiling in §5.4–5.6 and Appendix H is taken in an orthonormal output-space basis, where captured ≤U\le U is exact (Eq. 1, Lean 4) and held in all 42 cells.

Q2 (Closed form, splits, train/valid-only checks; coverage vs predictability). U(K)U(K) is the error-energy share of the top-KK modes, computed at 11 budgets with no training; (U∞,K0,a)(U_\infty, K_0, a) are least-squares fits to it, and the efficiency η(K)\eta(K) = captured/U(K)U(K) is measured, never predicted. Fitted on training and validation windows alone, the exponent and scale match the test fit within 95% block-bootstrap intervals (shear flow a=1.96 [1.90,2.03]a=1.96\,[1.90,2.03] VALID vs 1.93 [1.91,1.95]1.93\,[1.91,1.95] TEST; convection 1.88 [1.84,1.91]1.88\,[1.84,1.91] vs 1.89 [1.84,1.96]1.89\,[1.84,1.96]; Figure 10g, Table 25). The predictive evidence is prospective: ranges registered before the runs at 50, 100 and 200 qubits held on all 18 seeds (Table 26 gives the residuals), and a prediction made from validation data alone, hashed before two unseen rows' TEST was downloaded, held for both cores (Appendix N). Figure 8c extends the check to nine benchmarks: the form fitted on validation matches the test ceiling within a median of 6% over the measured range, and fitted on at most 30 qubits it forecasts 300 within a median of 20%, below the measurement at 41 of 54 points, so we present it as a conservative guide (Appendix V). Your distinction between coverage and predictability is now measured directly: the fill factorizes as routing × features × fit (Eq. 1, Headroom.lean, Figure 21). On TRL2D and MHD the router still places 60–80% of the ceiling on the atoms, yet a least-squares head on the register's features explains none of it out of sample at any context halo (Appendix H): coverage without predictability. The abstract no longer states the 0→50-qubit gains (13%, 6%) as a law's prediction; the ceiling's fitted parameters, intervals and residuals replace them (Tables 25–26).

Q3 (Energy score normalization DD). In the submitted Appendix O, DD was the target window's standard deviation, which makes the score observation-weighted rather than strictly proper; thank you for catching it. The registered replacement uses a fixed training-set scale DtrainD_{\mathrm{train}} (strictly proper; Gneiting & Raftery 2007), and the result holds on 3/3 seeds on both rows (Table 27, Figure 10i): drawn configurations beat the deterministic hybrid and a validation-tuned Gaussian dressing on shear flow (0.0063 vs 0.0079 and 0.0069) and convection (0.0228 vs 0.0279 and 0.0235). The abstract's 16–20%, computed under the target-dependent DD, is withdrawn; Table 27 replaces it.

Where: §5.3, Figure 10h, Appendix E Table 6 (Q1); Figure 10g, Appendix V Tables 25–26, Appendix N, Figure 9c, Appendix H (Q2); Figure 10i, Appendix W Table 27 (Q3); page/index.html (#passes, #playground).

Reviewer_c5AYOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper attaches an input-conditioned Rydberg-atom co-processor to pretrained physics world models and asks a deliberately deflationary question: do the qubits do anything a parameter-matched classical core cannot? The error of each prediction is decomposed into Fourier octaves and band-wise POD modes; the smooth, predictable part is routed to 30 atoms whose positions, detunings and tethers are set per input, while the rest stays with a classical head. Controls replace the register with a matched MLP, remove interactions, or use a mean-field decoupling.

Critical strengths

1.The audit design is the strongest part of the paper and, frankly, better than most of the hybrid-QML literature. Released checkpoints, an identical interface, a parameter-matched MLP, a no-interaction arm, a mean-field arm, a zero-qubit arm, seed-paired gains, and kill rules fixed before the runs. This is what a serious control set looks like. 2.The utilization framing is useful and it is proved in the case that matters: a pooled insertion reads and writes only the DC mode, so its ceiling is the DC share of the error energy. That single observation explains a whole class of null results - including the ones in this paper - and it converts into a design rule that practitioners can apply tomorrow. 3.The allocation study separates the ceiling U from the captured share and then tests the predicted ordering captured ≤ U across 42 row-strategy cells (Spearman ρ = 0.71). That is a test of a stated mechanism, not a post-hoc story. 4.The paper reports its own failed replication - the long-horizon TRL2D edge did not survive a registered fourth seed - and the rows where the register loses to its MLP (shear flow -4.7%, TORAX -19.2%). Very few papers in this area do that.

Critical weaknesses

1.The headline number belongs to the allocation, not to the quantum part. The 36% figure is a routed-versus-pooled comparison, and at that same strategy the register is 0.48% worse than its matched MLP. A reader of the abstract will attribute 36% to the Rydberg co-processor. The abstract should say, in the same sentence, that the matched classical core achieves the same allocation gain, and the title should probably be 'utilization, not qubits'. 2.The published-state-of-the-art column is not on the same scale. Shear flow shows 0.8080 published against 0.0236 for the authors' classical model; convection 0.6566 against 0.0449. The footnote concedes that the released checkpoint does not reproduce the published number under this evaluator. Printing the column as-is invites the conclusion that the hybrid beats the published model by a factor of thirty, which cannot be what is meant. Normalize, re-evaluate both under one metric, or drop the column. 3.Statistical power is low, and the 'tie' conclusion cuts both ways. Three seeds, minimum detectable effects of 53-99% on four audit rows, and a sign test over eight rows with p = 0.69. That is consistent with no effect, but also with a real 10% effect on some rows. The negative claim is as underpowered as a positive one would be, and the paper's rhetorical confidence ('the register ties') is stronger than the statistics support. 4.No hardware, and the compilation cost is not accounted for. Everything is exact statevector simulation of at most thirty atoms in groups of ten. Decoherence, readout error and calibration drift are unmodelled, and the claim that the configuration maps onto current neutral-atom processors is plausible but untested. More importantly, one device program per input means recompilation on every sample; on real hardware that cost may dominate the 18% training overhead reported here. 5.The scaling law is a good fit, not a law. G(K) has four free constants (η, Uinf, K0, a) fitted to points from 0 to 30 qubits, and the prediction at 50 is a modest extrapolation with six seed points behind it. The paper's phrasing 'a law whose 50-qubit prediction held' overstates what has been shown; it should be presented as an empirical fit with one successful extrapolation, and its parameters should be reported with confidence intervals.

Questions for authors

1.Can you state in the abstract that the matched classical core captures the same allocation gain as the register? 2.How should the published column be read for shear flow and convection, where the scale differs by more than an order of magnitude from the authors' models? 3.What is the power calculation behind the 'ties' conclusion, and what effect size could the eight-row sign test have detected? 4.What would the per-input compilation and readout cost be on a real neutral-atom device, relative to the classical forward pass? 5.Please report the fitted parameters of G(K) with confidence intervals, and the residual at 50 qubits.

2 comments
AuthorsOpenReview ↗

Response to Reviewer c5AY

Thank you for the detailed review and for your assessment of the audit design. For each weakness we give what the reviewed PDF already stated, then what the revision adds.

  1. The 36% and the claim. We agree that the 36% is an allocation gain: that is the paper's claim, not a gap in it. The reviewed PDF said so in its title (Utilization over Qubits), in the abstract's first sentence, in §1 ("We separate two claims. Utilization, not qubit count, governs the gain") and in contribution 4 ("the gains belong to allocation"). The revised abstract defines utilization and states that it is measured for the register and for matched classical controls behind the same router. We do not compress the core comparison into one abstract sentence because it differs by row, and each number is printed where it is measured: on shear flow the register is ahead of its tuned MLP (+10.5%, 3/3, paired p=0.04p=0.04; depth chosen by a registered validation screen after the MLP's own search, the MLP not re-tuned); on convection it is behind (−1.6%; in Table 3 the register removes 36.25% and the MLP 0.48% more); reused over nested passes it captures 96% more than a classical refit on the same tiles (3/3). Both deficits you named are resolved. TORAX: one register seed had failed to train; under one restart rule for every arm (of two initializations the one with lower training error is kept; no validation or test data) the register is ahead of the MLP by +8.4% and of the classical model by +13.1% on 3/3 seeds. Table 1 now shows this row; the first run (−15.5%, 2/3) is kept in Appendix C. Shear flow: the −4.7% is the pooled neck insertion, the design the paper argues against, inside its 115% detectable effect (Table 5); routed, the register is ahead of its MLP by +10.5% (3/3).
  2. Published column. The reviewed PDF flagged the scale in the table footnote and in its appendix on published numbers, which listed each released checkpoint under our evaluator next to persistence, and §5.1 said that most of the margin comes from the classical part; a 30× gain was never claimed. The gap is an artifact of per-window VRMSE on low-variance windows, where persistence already scores 0.0646 (shear flow) and 0.2024 (convection). Table 1 now lists PDE-FM (0.0345 and 0.0415) on the same scale; the classical cells you quoted (0.0236, 0.0449) read 0.0228 and 0.0436 after the equal-budget tuning and full-split scoring listed in the general comment; under a pooled energy-weighted nRMSE the routed correction still lowers shear flow (0.0246 → 0.0172 register, 0.0178 MLP; Figure 10a,b).
  3. Power. The reviewed PDF reported the detectable effect per row and said in §5.1 and §6 that four rows are underpowered; the 53–99% and p=0.69p=0.69 you cite are its own numbers. We agree that a real 10% effect on some rows was not excluded, and after equal-budget tuning the revision measures one: +10.5% on the routed shear-flow row (3/3, p=0.04p=0.04). "Ties" now reads "no detectable difference"; per-row detectable effects are 0.2–6.1% on four rows and 28–115% on the other four, the 8-row sign test has 17% power at a win rate of 0.8 and 43% at 0.9 (Figure 10c,d, Appendix C), the random-effects pool gives +0.81% [−0.14,+1.76]+0.81\%\,[-0.14,+1.76], and no equivalence is claimed.
  4. Hardware and cost. The reviewed PDF stated the simulation limit in §6 and reported a finite-shot readout test and the shots per input in its hardware appendix. The revision adds: 3 basis settings × 1,000 shots at 4 s/shot on Pasqal Orion Alpha, 3.3 QPU-hours per pass, ≥105×\ge 10^5\times the classical forward pass; a fixed trap layout suffices, so only detuning waveforms change per input; device-noise emulation keeps 92–96% of the gain; on hardware (IQM, 54 qubits, gate-compiled) 98% on held-out windows, with the readout scale calibrated on other windows (Appendix U); heads calibrated on device readouts keep 87–98% at 100 shots and 73–85% at 10 (Figure 19c). Reusing a small register (10 atoms × 3 passes match 30) and allocating executions across inputs (+19–25%) lower the cost; we cite Provazza et al., who replace the device with a classical surrogate, and we measured that route on our benchmarks too (Appendices H, M, U).
  5. Scaling. The 50-qubit ranges were registered before the runs and all six seeds fell inside them (reviewed Appendix N). The revision extends this to 100 and 200 qubits (all 18 seeds inside), renames the curve a closed-form coverage ceiling, and reports 95% block-bootstrap intervals on VALID and TEST (shear flow TEST U∞=0.754 [0.740,0.768]U_\infty=0.754\,[0.740,0.768], K0=5.2 [5.0,5.6]K_0=5.2\,[5.0,5.6], a=1.93 [1.91,1.95]a=1.93\,[1.91,1.95]; Table 25) and the residuals you asked for (at 50 qubits +0.0105 shear flow, +0.0017 convection; Table 26).

Your review rated soundness as "minor or fixable concerns". We believe each is now fixed with a measurement, and we would be grateful if you would consider whether the rating still reflects the revised paper.

AuthorsOpenReview ↗

Follow-up to Reviewer c5AY

We have revised our response above so that each of your five points shows what the reviewed PDF already stated and what the revision measures. In short: the allocation claim you ask for is the paper's own (title, abstract, §1, contribution 4); the 10% effect that the audit could not exclude is now measured on the routed shear-flow row (+10.5%, 3/3 seeds, p=0.04p=0.04); the published column is on one scale; hardware cost and device noise are reported, with runs on a 54-qubit processor (98% of the gain kept once the readout scale is calibrated); the ceiling has intervals, residuals and registered bounds met at 50, 100 and 200 qubits. If any answer falls short, a sentence naming it would let us address it before the discussion closes. Thank you for your time.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Summary of the discussion for the Area Chair: where each concern stands

Dear Area Chair, dear reviewers,

Thank you for handling this submission. As the discussion closes, we summarize where each concern stands so that the record is easy to check. Every statement points to the revised PDF or to the PDF as reviewed.

What the paper claims and shows. The claim is qubit utilization: in a hybrid classical–quantum model, how a qubit budget of any size is used for each input (which errors it is routed to, how the atoms are detuned, and how they are reused over nested passes) matters more than its size. Table 4 lists every lever, including positions, tethers, partitions and loops, with where each is measured.

  • Proved (Proposition 1, Lean 4). A register that receives the grid average of the features, the standard hybrid design, adds the same correction at every grid point of its layer. It cannot correct any error that varies across the grid, at any qubit count.
  • Measured, on ten tasks under rules registered before each run. Routing the same 30 qubits to the mispredicted modes cuts the released convection model's test error by 36% (VRMSE 0.640 → 0.408) against 7% for the pooled design, and gives 3.9–7.9× the pooled gain on four of five rows with predictable error (Table 3).
  • Predicted, then confirmed. The coverage ceiling fitted on validation matches the test fit within its intervals, and the ranges registered before the runs at 50, 100 and 200 qubits held on all 18 seeds (Appendix V).
  • Reuse. The same atoms run over nested passes capture 96% more than a classical refit on the same tiles, in every budget cell and on 3/3 seeds (§5.6).
  • On hardware. Compiled to gates and run on a 54-qubit IQM processor (64 test windows), the corrector keeps 98% of the register's gain on held-out windows, with the readout scale calibrated on other windows (Appendix U).
  • The quantum part, drawn. Figure 8 shows the trained program of the best register with its Hamiltonian (the gate statements proved in Lean 4), how its parameters grow with the qubit count (trained at 5 to 200 qubits), and the reachable share on nine benchmarks: fitted on validation at up to 30 qubits, forecast to 300, with the test measurements on top.

Code, weights and an offline interactive page are in the supplementary ZIP; a script recomputes 299 printed numbers from the per-seed result files.

Where each review stands.

  • c5AY (rating 2, confidence 2) lists four strengths, among them that the audit design is "better than most of the hybrid-QML literature" and that the utilization ceiling "is proved in the case that matters". Of the five weaknesses, three were already stated in the reviewed PDF: that the gain belongs to the allocation (the title, the abstract's first sentence, §1 and contribution 4); that four rows are underpowered (§5.1 and §6, the source of the 53–99% the review quotes); and that released checkpoints do not reproduce their published numbers under our evaluator (table footnote and appendix). The revision answers the other two with measurements (device-noise emulation, hardware runs and QPU cost per pass; intervals and residuals for the ceiling) and adds per-row detectable effects and sign-test power. No reply so far.
  • tyrC (rating 2, confidence 3) asked three technical questions. Each has a direct answer (Table 6; Tables 25–26; Table 27) and none changes a result: the output-space measurement supports the explanation without any decoder assumption, the ceiling fitted without test data agrees with the test fit, and the probabilistic result holds on 3/3 seeds under a strictly proper score. The reviewer maintained the score without naming a remaining concern; we have asked which one remains.
  • bzYi (rating 1, confidence 1) reports insufficient expertise and raises presentation only. The quantity asked about (36% against 7%) is defined in the reviewed abstract, contribution 1, Table 3 and §5.5. The revision adds a terms table, one defining equation, a worked example (Figure 11) and Algorithm 1. No reply so far.

Our request. Two points needed a correction, the scope of one explanatory sentence and the scale of the energy score; both are made, and the results they concern hold (Table 6; Table 27, 3/3 seeds). No review questions a proof, a registered rule or a headline result, and all three soundness scores read "minor or fixable concerns". We believe these concerns are now fixed, with evidence, in the revised PDF, and we respectfully ask that the decision weigh the revised paper against them. We remain available for any question before the deadline.

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

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