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REVIEW 3 major objections 5 minor 35 references

Response to recent comments on Phys. Rev. B 107, 245423 (2023) and Subsection S4.3 of the Supp. Info. for Nature 638, 651-655 (2025)

T0 review · 3 major / 5 minor · reviewed 2026-08-16 · deepseek-v4-flash

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Pith's one-line read The paper claims that two external critiques fail to identify any flaw in the topological gap protocol's false discovery rate estimate.

desk verdict A competent rebuttal that adds useful robustness checks but overclaims 'no flaws' while leaving the simulation-to-device distributional match untested. read the letter →

arxiv 2504.13240 v1 pith:3QAL3FNP submitted 2025-04-17 cond-mat.mes-hall quant-ph

Morteza Aghaee , Zulfi Alam , Mariusz Andrzejczuk , Andrey E. Antipov , Mikhail Astafev , Amin Barzegar , Bela Bauer , Jonathan Becker
show 122 more authors
Umesh Kumar Bhaskar Alex Bocharov Srini Boddapati David Bohn Jouri Bommer Leo Bourdet Samuel Boutin Benjamin J. Chapman Sohail Chatoor Anna Wulff Christensen Patrick Codd William S. Cole Paul Cooper Fabiano Corsetti Ajuan Cui Andreas Ekefjärd Saeed Fallahi Luca Galletti Geoff Gardner Deshan Govender Flavio Griggio Ruben Grigoryan Sebastian Grijalva Sergei Gronin Jan Gukelberger Marzie Hamdast Esben Bork Hansen Sebastian Heedt Samantha Ho Laurens Holgaard Kevin Van Hoogdalem Jinnapat Indrapiromkul Henrik Ingerslev Lovro Ivancevic Thomas Jensen Jaspreet Jhoja Jeffrey Jones Konstantin V. Kalashnikov Ray Kallaher Rachpon Kalra Farhad Karimi Torsten Karzig Maren Elisabeth Kloster Christina Knapp Jonne Koski Pasi Kostamo Tom Laeven Gijs de Lange Thorvald Larsen Jason Lee Kyunghoon Lee Grant Leum Kongyi Li Tyler Lindemann Matthew Looij Marijn Lucas Roman Lutchyn Morten Hannibal Madsen Nash Madulid Michael Manfra Signe Brynold Markussen Esteban Martinez Marco Mattila Robert McNeil Ryan V. Mishmash Gopakumar Mohandas Christian Mollgaard Michiel de Moor Trevor Morgan George Moussa Chetan Nayak William Hvidtfelt Padk{ae}r Nielsen Jens Hedegaard Nielsen Mike Nystrom Eoin O'Farrell Keita Otani Karl Petersson Luca Petit Dima Pikulin Mohana Rajpalke Alejandro Alcaraz Ramirez Katrine Rasmussen David Razmadze Yuan Ren Ken Reneris Ivan A. Sadovskyy Lauri Sainiemi Juan Carlos Estrada Saldaña Irene Sanlorenzo Emma Schmidgall Cristina Sfiligoj Sarat Sinha Thomas Soerensen Patrick Sohr Tomaš Stankevič Lieuwe Stek Eric Stuppard Henri Suominen Judith Suter Sam Teicher Nivetha Thiyagarajah Raj Tholapi Mason Thomas Emily Toomey Josh Tracy Michelle Turley Shivendra Upadhyay Ivan Urban Dmitrii V. Viazmitinov Dominik Vogel John Watson Alex Webster Joseph Weston Georg W. Winkler David J. Van Woerkom Brian Paquelet Wütz Chung Kai Yang Emrah Yucelen Jesús Herranz Zamorano Roland Zeisel Guoji Zheng Justin Zilke
This is my paper · ORCID
classification cond-mat.mes-hallquant-ph
keywords topologicalgapprotocolfalsediscoveryrateMajoranazeromodesInAs-Alhybriddevicessuperconductivityrebuttaltransportmeasurementsquantumcapacitanceparitymeasurement
verification ladder T0 review T1 audit T2 compute T3 formal

The pith

A machine-rendered reading of the paper's core claim, the machinery that carries it, and where it could break.

The reading

This paper is a point-by-point rebuttal of two external comments on the topological gap protocol (TGP), a statistical test that decides whether a measured InAs-Al nanowire region is in a topological superconducting phase. The central claim is that neither comment identifies any flaw in the protocol's false discovery rate (FDR), the probability that a region flagged as topological is actually trivial, previously bounded below 8%. The authors argue the critics confuse a statistical tuning tool with a smoking-gun test: the TGP may be sensitive to its thresholds and measurement ranges, but that does not mean it frequently misclassifies trivial regions. Concretely, they show the released code matches the paper's gap-extraction description, that the one-parameter difference between simulated and experimental analysis does not change the FDR, and that cropping the magnetic-field range by half a tesla leaves the FDR low. If correct, the conclusions of the original device papers stand, including the parity-measurement result that underpins the topological qubit program.

What carries the argument

The load-bearing object is the false discovery rate (FDR): the probability that the TGP flags a trivial region as topological, estimated by running the protocol on simulated transport data calibrated to independently measured device disorder (localization length over 1 $\mu$m). The rebuttal's machinery is the transfer argument: because the simulations are drawn from the same distribution as real devices, a low simulated FDR bounds the experimental FDR. The two new tables are the operative mechanism: Table I shows that using the experimental setting `average_over_cutter=True` leaves the FDR statistically unchanged, and Table II shows that cropping $B_{\max}$ to 2.5 T keeps the FDR below 9% — together with a threshold-sensitivity analysis showing that changes in $G_{\mathrm{th}}$ of less than 20% move the FDR by only a few percent.

What would settle it

Re-run the released TGP code on the published simulated datasets with every implementation detail set to the experimental pipeline — cutter averaging on, corrected symmetric bias cropping, and magnetic-field ranges cropped to $B_{\max} \leq 2.5$ T as in Table II — and count false positives under the paper's own topological criterion; if the fraction of false positives among roughly 700 regions of interest exceeds 8%, the central claim fails. The code repository and data paths named in the paper make this check directly executable.

Watch

Extended reading notes

Core claim

On the paper's own terms, the claim to be defended is that no flaw has been shown in the TGP's false discovery rate: re-running the protocol with the experimental setting `average_over_cutter=True` yields at most one false positive in roughly 700 regions of interest (Table I), and cropping the magnetic-field range to $B_{\max} \leq 2.5$ T changes the FDR bound only slightly (Table II). The paper upholds the original claims that a TGP pass indicates a topological region with probability above $1-8\%=92\%$ for the SLG-$\beta$ stack and above $94\%$ for the DLG-$\epsilon$ stack, that measurement-range variations are explained by cooldown-to-cooldown disorder changes and stage-1 cluster sizes, and that the acknowledged bias-cropping bug in the Nature supplement alters extracted gap values by less than 5 $\mu$eV in more than 96% of pixels without changing the parity result. It concludes that the comments attack a 'smoking gun' methodology the papers never used.

Load-bearing premise

Everything rests on the assumption that the simulated datasets used to calibrate the protocol are drawn from the same probability distribution as the real device data; if the simulations overstate how representative the devices are, the claimed FDR bound could be too low.

Editorial extensions

If this is right

  • If the rebuttal is correct, the <8% FDR bound (and <6% for the DLG-$\epsilon$ stack) survives, so regions that pass the TGP remain high-confidence operating points for topological qubit tune-up.
  • The distinction between statistical and smoking-gun tests becomes the operative frame: hyperparameter sensitivity of the TGP is not evidence of bias, and critiques must engage with the FDR itself.
  • The acknowledged bias-cropping bug in the Nature supplement is contained: gap values shift by under 5 $\mu$eV in more than 96% of pixels, and the flux-dependent bimodal random-telegraph-signal parity result is not affected.
  • Measurement-range differences between devices and cooldowns are presented as natural consequences of stage-1 cluster sizes and device drift, with the simulation range distribution in Fig. 2 containing the experimental ranges.

Reading between the lines

Editorial extensions of the paper, not claims the author makes directly.

  • One could press further than the paper does: the robustness checks vary one parameter at a time, so a joint worst-case sweep over $G_{\mathrm{th}}$, cutter averaging, bias cropping, and $B_{\max}$ would directly test whether the FDR bound remains below 8% under combined stress.
  • The same calibration logic could be exported to other material platforms: if simulations matched to measured localization length yield a similarly low FDR for other nanowire systems, the protocol would be a general tune-up tool rather than a device-specific one.
  • The debate implicitly raises a question the paper leaves open: the true-positive criterion uses the scattering invariant together with stable zero-bias peaks and gap reopening, but the false-negative rate is explicitly unquantified; a reader wanting to use the TGP for discovery, not just tune-up, would want that number.
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Editorial analysis

A structured set of objections, weighed in public.

Desk editor's note, referee report, and a circularity audit.

Referee Report

3 major / 5 minor

Summary. This manuscript is a point-by-point rebuttal by the Microsoft Quantum collaboration to two comments by H. F. Legg (arXiv:2502.19560 and arXiv:2503.08944) on the topological gap protocol (TGP) as used in Phys. Rev. B 107, 245423 (2023) and in the Supplementary Information of Nature 638, 651-655 (2025). The rebuttal addresses seven points from Ref. 3 and several from Ref. 4, covering the definition of the transport gap, the threshold parameter Gth, the difference between simulated and experimental analysis (average_over_cutter), measurement ranges and their effect on TGP outcomes, the definition of 'topological' via the scattering invariant, and the interpretation of conductance data in the parity-readout devices. The manuscript provides new simulation statistics in Tables I and II, a stability analysis of ROI2s under magnetic-field-range cropping in Fig. 3, and a reproducibility statement with code links. The central claim is that no flaws have been identified in the FDR estimate (below 8%) and that the objections raised in Refs. 3 and 4 are unfounded.

Significance. If the rebuttal is correct, it defends the reliability of the TGP as a statistical tuning tool, preserving the conclusions of two high-profile experimental papers. The manuscript's strengths include the provision of reproducible code and package environment files, new simulation tables showing FDR bounds under changed analysis settings, and a direct stability analysis of individual ROI2s under magnetic-field-range modifications. The point-by-point format is useful for the community. However, the significance is tempered by two load-bearing caveats identified in the manuscript itself: the admitted cropping bug in the published SI for the Nature paper, and the explicitly quoted but not quantitatively tested assumption that simulated data are drawn from the same probability distribution as experimental data. These caveats mean that the strong 'no flaws' claim in the abstract is not fully established as written.

major comments (3)
  1. [Technical Response to Ref. 4, paragraph beginning 'We note that the published version of the TGP data...'] The manuscript admits a data-processing bug in the published Supplementary Information for Ref. 2: the bias range was incorrectly cropped, and correcting it changes TGP outcomes for device B, including the appearance of a new SOI2 for one cutter and an increase in ROI2 size. This admission is difficult to reconcile with the abstract's claim that 'no flaws have been identified in our estimate of the FDR' and that the objections are 'unfounded.' At least one objection (Ref. 4) identified a genuine error in the published data analysis. The rebuttal should explicitly narrow the 'no flaws' claim to the FDR estimate itself and acknowledge that the published SI contained a flaw, or provide a detailed argument for why an error that changes TGP outcomes does not affect the FDR bound. As written, the strong claim overreaches the manuscript's own findings.
  2. [Quotation from Ref. 1 in 'Technical Response to Ref. 3', point 2] The FDR transfer from simulation to experiment relies on the assumption, quoted in the manuscript, that 'the simulated data is drawn from the same probability distribution as the data produced by real devices.' The new robustness analysis in Tables I and II and Fig. 3 varies parameters inside the simulation model (average_over_cutter, magnetic field range) but does not test the distributional match between simulated and experimental conductance features. Independent localization-length measurements (Fig. 5) constrain disorder but do not establish that TGP-relevant features--zero-bias peak statistics, nonlocal gap shapes, Andreev-enhanced subgap conductance, junction asymmetries--are drawn from the same distribution. The rebuttal should either provide a quantitative comparison between simulated and experimental conductance distributions or explicitly state that the FDR bound is conditional on this untested assumption. Without such a test, the claim that 'no flaws have been identified' is not fully supported.
  3. [Technical Response to Ref. 3, point 1 (threshold Gth)] The manuscript states that 'changes in Gth of less than 20% result in only minor variations in the FDR (i.e. a few percent).' This statement is load-bearing for the robustness of the FDR estimate, but no quantitative evidence is provided for this specific claim. Figure 1 shows the presence/absence of ROI2s for a single measurement as Gth varies from 0.04 to 0.06 Gmax, but it does not report FDR values or statistics over the simulation ensemble. If the FDR is to be claimed robust against Gth variations, the manuscript should include a simulation table or plot showing FDR as a function of Gth, or should rephrase the statement to describe the observed stability without assigning a precise few-percent bound.
minor comments (5)
  1. [Abstract] The phrase 'the objections in arXiv:2502.19560 and arXiv:2503.08944 are unfounded' is too broad given the admitted cropping bug in the published SI. Recommend softening to 'the objections do not affect the FDR estimate' or similar.
  2. [Section 'Technical Response to Ref. 4', paragraph on measurement ranges] The text says the experimental stage 2 ranges are 'well within' the simulated distribution shown in Fig. 2, but the figure does not overlay the experimental values. Adding such an overlay would make the claim directly verifiable.
  3. [Table II footnote [15]] The explanation that 'most of the ROI2s are at high fields for the DLG-ε stack' is helpful but could be expanded to state whether this is a property of the simulated model or a consequence of the chosen parameter ranges.
  4. [Section 'Technical Response to Ref. 3', point 4] The discussion of the scattering invariant as a finite-size criterion is clear, but the manuscript refers to 'Fig. 32 in our paper' without a self-contained reproduction; since this is a response, a brief description of the relevant panels would aid readers who do not have Ref. 1 open.
  5. [Throughout] The manuscript is written as a collective reply under 'Microsoft Quantum' with a long author list in a footnote. For reproducibility and transparency, it would help to indicate which authors produced the new simulations and tables.

Circularity Check

0 steps flagged · score 0.0 of 10

No significant circularity: the FDR estimate is calibrated against an external scattering-invariant label and the transfer-to-experiment assumption is explicit, not a hidden input.

full rationale

The paper is a rebuttal rather than a new derivation; its central assertion is that the FDR estimate from Ref. [1] survives the comments in arXiv:2502.19560 and arXiv:2503.08944. The FDR was computed by applying the TGP to simulated conductance data whose ground-truth labels come from the scattering invariant det(r) < 0, an external criterion drawn from the published literature (e.g., Ref. [16] of the paper), not from the TGP output itself. The transfer from simulations to experiment is explicitly conditional: the paper quotes Ref. [1] as stating that the <8% bound holds 'provided that the simulated data is drawn from the same probability distribution as the data produced by real devices.' That is a stated assumption rather than a circularly hidden input. The new robustness checks (Tables I and II, Fig. 3) vary hyperparameters and magnetic-field ranges inside the simulation ensemble, and they do not reuse the conclusion as a premise. Self-citations to Refs. [1,2] point to published papers with a public code repository [14], which the paper explicitly invites readers to use for validation; under the review rules, code-reproduced results count as independent support. The admitted bias-range bug in the Nature Supplementary Information is disclosed and its quantitative effect is assessed rather than used to redefine the outcome. No 'prediction' in the response reduces by construction to a fitted parameter, a renamed input, or a self-citation chain. The main weakness—that the simulation-to-experiment distributional match is not directly tested—is a validity risk, not circularity, and it does not make the derivation self-referential.

Assumptions & free parameters 3 free parameters · 3 assumptions · 0 invented entities

The rebuttal's quantitative claims rest on the TGP hyperparameters (Gth, average_over_cutter, field ranges) and on the domain assumption that simulations reproduce the device distribution. No new physical entities are introduced.

free parameters (3)
  • Gth (conductance threshold for gap extraction) = 0.05 * Gmax (exp(-3))
    Chosen based on expected disorder strengths; the authors claim under 20% changes alter FDR by only a few percent, making it a tunable hyperparameter.
  • average_over_cutter = True for experimental, False for simulated data (original); response says correct value is True
    Binary protocol parameter that affects TGP classification; the response shows it does not change FDR significantly, so it is a free parameter of the protocol.
  • Stage 2 magnetic field range Bmax = ~3 T in simulations, 2.5 T in robustness test
    The measurement range is a choice that affects TGP outcomes; the response demonstrates FDR is weakly dependent on it.
assumptions (3)
  • domain assumption Scattering invariant det(r) < 0 reliably identifies topological phase in finite-sized disordered nanowires
    Used as ground truth for labeling simulations as topological vs trivial; adopted from literature (Refs. 16, 17), but not directly verified in the devices.
  • domain assumption Simulated transport data is drawn from the same probability distribution as experimental data
    This is the condition under which the FDR bound transfers to experiments; quoted from Ref. 1 and implicit in the rebuttal's robustness arguments.
  • standard math Binomial confidence intervals for zero false positives give valid FDR upper bounds
    Used to convert observed false positive counts into FDR upper bounds (e.g., under 6.8%); standard statistics.

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Cite this review

Pith. "Pith review of Response to recent comments on Phys. Rev. B 107, 245423 (2023) and Subsection S4.3 of the Supp. Info. for Nature 638, 651-655 (2025)." pith.science (2026). https://pith.science/paper/3QAL3FNP

@misc{pith2026250413240,
  author       = {Pith},
  title        = {Pith review of: Response to recent comments on Phys. Rev. B 107, 245423 (2023) and Subsection S4.3 of the Supp. Info. for Nature 638, 651-655 (2025)},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/3QAL3FNP}},
  note         = {Machine review of arXiv:2504.13240}
}
read the original abstract

The topological gap protocol (TGP) is a statistical test designed to identify a topological phase with high confidence and without human bias. It is used to determine a promising parameter regime for operating topological qubits. The protocol's key metric is the probability of incorrectly identifying a trivial region as topological, referred to as the false discovery rate (FDR). Two recent manuscripts [arXiv:2502.19560, arXiv:2503.08944] engage with the topological gap protocol and its use in Phys. Rev. B 107, 245423 (2023) and Subsection S4.3 of the Supplementary Information for Nature 638, 651-655 (2025), although they do not explicitly dispute the main results of either one. We demonstrate that the objections in arXiv:2502.19560 and arXiv:2503.08944 are unfounded, and we uphold the conclusions of Phys. Rev. B 107, 245423 (2023) and Nature 638, 651-655 (2025). Specifically, we show that no flaws have been identified in our estimate of the false discovery rate (FDR). We provide a point-by-point rebuttal of the comments in arXiv:2502.19560 and arXiv:2503.08944.

Figures

Figures reproduced from arXiv: 2504.13240 by the authors.

Figure 1
Figure 1. FIG. 1 [PITH_FULL_IMAGE:figures/full_fig_p003_1.png] view at source ↗
Figure 2
Figure 2. FIG. 2 [PITH_FULL_IMAGE:figures/full_fig_p005_2.png] view at source ↗
Figure 3
Figure 3. FIG. 3 [PITH_FULL_IMAGE:figures/full_fig_p006_3.png] view at source ↗
Figures from the paper (2 more)
Figure 4
Figure 4. Figure 4: FIG. 4 [PITH_FULL_IMAGE:figures/full_fig_p006_4.png]
Figure 5
Figure 5. Figure 5: FIG. 5 [PITH_FULL_IMAGE:figures/full_fig_p009_5.png]

Discussion (0). Continue with ORCID to comment.

Reference graph

Works this paper leans on

35 extracted references · 24 canonical work pages

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    2022

Pith tools

Reviewed August 16, 2026 · model on record in the stance chip above.