XSci (AI review)

September 28, 2026

Referee Report

Manuscript: Post-pandemic generalization of a deep-learning ECG biomarker of sudden cardiac death: a pre-registered replication and extension testing convergent electrical remodelling and COVID-19 substrate shift

Recommendation: Major revision required

Summary and Recommendation

This Stage 1 pre-registered protocol asks two questions about a recently described artificial-intelligence electrocardiographic biomarker of sudden cardiac death. The originating study, conducted on a Swedish regional ECG archive closing in 2016, used a generative interpretability procedure to surface a slurred terminal R-wave downstroke in lead aVL and proposed diffuse myocardial remodelling, with interstitial fibrosis as a leading candidate, as the underlying substrate. The authors ask first whether that signature is in fact convergent, arising from several distinct disease processes rather than fibrosis alone, and second whether the post-COVID myocardium shifts its distribution in a way that would matter for a deployed model. Study A operationalises the feature as the mean absolute first and second differences of aVL voltage over the R-peak-to-QRS-offset window and compares diagnostic superclasses in PTB-XL. Study B proposes a retrospective, multi-centre, comorbidity-matched cohort of adults after moderate-to-severe or hospitalised COVID-19 with paired cardiac magnetic resonance, adding repolarisation, imaging, and circulating fibrosis endpoints. Roughly 70 imaging-positive cases and 70 matched controls are targeted for the primary contrast, and the protocol commits explicitly to reporting null results for H2, H4, and H5 as primary findings.

The question is timely and well chosen, and the format is the right one. Interpretability findings from clinical prediction models are routinely reported and then left unexamined; proposing a disciplined, pre-committed programme to test whether one such feature corresponds to a stable biological entity is a genuine service. The outcome-neutral commitment is stated with unusual specificity, the falsification contrast embedded in H3 creates a real opportunity for the study to fail, and the candid explanation of why image-derived open COVID ECG repositories cannot support a sample-to-sample derivative measure demonstrates that the authors understand the measurement physics of their own biomarker. Nevertheless, the protocol in its present form cannot deliver the inferences it promises. The biomarker as defined confounds morphology with amplitude, window length, and acquisition characteristics; the hypothesis set is structured so that the central mechanistic claim is not identified and in one place is internally inconsistent; and the clinical component lacks a temporal contrast, a stated causal estimand, a workable governance model, and any clinical outcome. Major revision is required, but each of these is addressable, and a revised protocol along the lines below would be well worth registering.

Major Concern Category 1: Measurement Validity of the Biomarker

1.1 The operationalisation is an interpretation of the published finding rather than a replication of a published metric, and its correspondence is never tested

The originating description of the biomarker, as the manuscript itself relays in Section 1, is qualitative: a slurred terminal QRS downstroke in lead aVL accompanied by leftward and posterior depolarisation change, emerging from a generative model that perturbed real low-risk traces toward high risk. The authors translate this into two scalar quantities, the mean absolute first and second differences of voltage over a defined window, and this translation is stated clearly and plausibly. It is nevertheless an interpretation whose validity is assumed rather than demonstrated, and everything downstream depends on it. The consequence is that a negative result in either study would be uninterpretable, because a genuine absence of effect could not be distinguished from a failure of the operationalisation to capture the morphology in question. A validation step should be pre-specified: a stratified random sample of records adjudicated by readers blinded to group as slurred or sharp, with the derivative measures evaluated against that reference and a minimum acceptable discrimination fixed in advance. The same reasoning applies to the manuscript's framing more broadly. The protocol nowhere runs the model, obtains its risk score, or assesses its calibration, yet the front matter, Table 2, and Section 7 speak of bounding deployment risk and of miscalibration. Either the design should be extended to include an actual model-output analysis, or the deployment language should be narrowed to what a feature-distribution study can support.

1.2 The derivative measures are confounded with amplitude, window length, and sampling rate

Three properties of the metric as defined in Section 4 undermine the comparisons it will be used to make. It is not amplitude-normalised, and the mean absolute first difference scales linearly with waveform amplitude, so a record with a small terminal excursion in aVL will produce low values for purely geometric reasons; since aVL amplitude varies systematically with frontal-plane axis, and since the protocol's own conceptual figure names left-axis deviation as part of the latent phenotype, this is not a hypothetical concern. It is not invariant to window length, because the R-peak-to-QRS-offset interval is longer in conduction disturbance, hypertrophy, and infarction than in normal records, and a longer window mechanically dilutes the mean absolute difference by including proportionally more of the low-slope terminal segment. The protocol's provision that QRS duration will be "reported to separate a duration effect from a derivative effect" acknowledges the risk without removing it, and since conduction disturbance is by definition a duration phenotype and is one of the four superclasses in which H1 may be declared supported, there is a real prospect that the primary hypothesis is confirmed by an artefact of the window definition. And it is not sampling-rate invariant, a point of particular force given that PTB-XL is distributed at both 100 Hz and 500 Hz and the protocol does not state which is used. A normalised biomarker, a fixed-duration or explicitly modelled window, and a stated resampling and filtering pipeline would each be straightforward to specify, and together would make a positive result attributable to the morphology the authors intend to measure.

1.3 Acquisition heterogeneity will act directly on a high-frequency metric, and no harmonisation plan is offered

The data-source justification rests on a correct measurement argument: image-derived ECGs are rejected because signal recovery introduces timing errors incompatible with sample-to-sample differences. That same sensitivity, however, makes the biomarker vulnerable to variation that persists in fully digital data. Diagnostic devices differ in high-frequency cut-off, in the application of mains notch filtering, and in anti-aliasing filter order and phase, and all of these bear first-order on a second-difference operator. In a multi-centre study pooling digital ECGs from institutions with different device fleets, between-centre variation in the second difference attributable to filter settings could plausibly exceed the moderate biological effect the study is powered to detect, and if centres differ in their case-to-control ratio this becomes confounding rather than noise. Residual baseline wander and high-frequency noise act in the same direction and differ systematically between ambulatory and inpatient acquisition, which maps onto the case-control distinction. A credible plan would fix a single target sampling rate and resampling method, apply one uniform pre-processing filter to all records regardless of source so that effective bandwidth is common, pre-specify a signal-quality screen with exclusion thresholds applied blind to group, and absorb residual device variation through centre-level terms in the Study B model.

1.4 The biomarker depends entirely on automatic fiducial placement in the most delineation-hostile of the limb leads

Every number in the study flows from two automatically determined landmarks, the aVL R peak and the QRS offset, and the protocol treats both as given. Lead aVL is frequently low in amplitude and sometimes near-isoelectric, and the protocol does not say which lead beat detection is performed on or what happens when no R peak can be identified. The QRS offset is the hardest fiducial point in ECG delineation because the J point is a gradual transition, and at 500 Hz an error of a few milliseconds is several samples out of a short terminal window. Most importantly, the error is not random with respect to group: a slurred terminal downstroke, which is the phenotype under study, makes the J point harder to locate and tends to push automatic offset estimates later, so the measurement error is correlated with the exposure and biases rather than merely attenuates. The cited general-purpose toolbox is also being applied at the edge of its validated envelope, since its delineation methods were evaluated on standard databases and typically on higher-amplitude leads. A blinded delineation validation substudy reporting bias and limits of agreement against manual marking, a pre-specified sensitivity analysis using an independent algorithm such as a wavelet-based delineator, and reporting of delineation failure rates by group would put the measurement on a defensible footing.

Major Concern Category 2: Hypothesis Structure and Inferential Framework

2.1 The convergence framework is not falsifiable as specified, and H1's decision rule does not identify it

Table 1 attributes to the originating authors a fibrosis-specific reading in which the feature is a marker of localised scar with a single anti-fibrotic therapeutic implication. That attribution appears stronger than the source supports, since the manuscript's own Section 1 summary describes the originating hypothesis as one about diffuse remodelling and distributed conduction barriers, which is considerably closer to the authors' own position. More consequentially, the Convergent Electrical Remodelling model as drawn in Figure 1 routes six input categories into a single node and therefore accommodates any pattern of results: reduction in four superclasses supports it, reduction in two satisfies the stated rule, reduction in one can be attributed to inadequate representation of the other tributaries, and reduction in none can be attributed to measurement. A framework with this property describes rather than predicts. The decision rule compounds the difficulty, because counting significant superclasses cannot distinguish convergence from a shared confounder. Cardiac ageing alone produces conduction slowing, axis change, and reduced high-frequency QRS content, and the disease superclasses in PTB-XL are substantially older than the normal group, so an age gradient would satisfy H1 without any convergent electrophysiological endpoint existing. Given that the manuscript's own Table 2 identifies a chronological-age signature as an encoded property of the original model, age is the principal rival hypothesis rather than a nuisance covariate, and relegating it to a post hoc sensitivity analysis cannot rescue a primary inference that ignores it. Restricting to single-superclass records introduces a further, unanalysed selection. The remedy is to specify what convergence forbids: that substrate-specific effects become statistically indistinguishable after conditioning on a shared mediator, or that a multivariate ECG representation of the four superclasses collapses onto a single axis aligned with the aVL feature. Either would fail under plausible alternatives; the present rule would not.

2.2 H1 and H3 make incompatible predictions, and H2's direction is never stated

H1 predicts reduced derivatives in two or more superclasses including conduction disturbance, while H3 predicts that bundle-branch morphologies show no such reduction. In the published label aggregation the protocol adopts, the bundle-branch codes are themselves constituents of the conduction-disturbance superclass, so the two hypotheses are compatible only under a construction rule that Section 4 does not state. If flagged records are retained in the superclass, one hypothesis will be contradicted by construction; if they are removed, the residual group is much narrower and its expected size is unreported. Since H3 is described as the study's built-in falsification, its evidential value depends on being a genuinely independent test rather than a subset of a group in which the opposite result is predicted, and the pathophysiological reasoning for why diffuse anisotropic slowing should smooth the terminal downstroke while discrete proximal block should not needs to be articulated rather than assumed. A separate gap concerns H2, which states only that the measures "differ" from controls, while the front matter asserts that "the direction is hypothesised." The hypothesised direction is never written down anywhere in the manuscript, which is precisely the latitude that pre-registration exists to remove.

2.3 The statistical plan leaves substantial analytic latitude, and the null branch has no evidential machinery

Section 6 is titled "Statistical analysis and power" but addresses only one contrast. Study A, the component that will run first and that anchors the mechanistic claim, has no power analysis at all, despite a decision rule involving eight tests under Holm-Bonferroni control across superclasses whose sizes differ by an order of magnitude, so the "two or more superclasses" rule will be driven disproportionately by the larger groups. The Study B calculation is asserted rather than derived; the stated figure is in a plausible region but is conservative relative to standard approximations for the Wilcoxon-Mann-Whitney test at the stated effect size, which suggests an unstated formula or allocation assumption, and the supplementary power curves referenced are not provided. The requirement of seventy imaging-positive cases implies a considerably larger screened cohort, since imaging-positive is one of three strata, and that implied total is never given. The dose-response and concordance hypotheses are unpowered altogether. And the stated plan to handle missing covariates by multiple imputation sits uneasily with rank-based primary tests, since pooling U statistics or Cliff's deltas across imputations is not a solved problem and requires a specified transformation or resampling approach. Beyond these, the outcome-neutral commitment, welcome as an integrity provision, does not by itself make a null result interpretable. Section 7 states that a null would bound the deployment risk of the original model, but a non-significant rank test is equally consistent with a true absence of effect, with an effect below the detectable threshold, with measurement error in the derivatives, and with misclassification of infected controls. Bounding anything requires a smallest effect size of interest specified in advance and tested against, whether by equivalence testing on the effect-size interval or by a Bayes factor. The authors are unusually well placed to set such a margin, since Section 1 already supplies the relevant anchors from the post-COVID ECG literature. The asymmetry of the present plan should also be corrected: checks for confounding and shortcut effects are triggered by a large result but nothing is triggered by a null.

2.4 H5 is phrased so that it cannot fail, and its markers are poorly suited to the inference

H5 predicts that circulating galectin-3 and soluble ST2 and magnetic-resonance extracellular volume correlate with the aVL shift "where fibrosis is the operative tributary." Whether fibrosis is the operative tributary is not measured independently of the hypothesis; it is what the correlation is meant to establish. As written, a positive correlation confirms the hypothesis and a null correlation can be attributed to fibrosis not having been operative, so no observation disconfirms it. The markers themselves compound the problem, since neither galectin-3 nor soluble ST2 is myocardium-specific and both are substantially influenced by renal function, age, and adiposity, with chronic kidney disease among the protocol's own matching variables. Restating H5 unconditionally with a pre-specified minimum correlation magnitude, pre-specifying adjustment for renal function and body-mass index, naming the assay platforms, and stating a minimum subset size and a multiplicity rule would convert the most fragile component of the protocol into its most mechanistically informative one.

Major Concern Category 3: Design, Identification, and Deliverability of the Clinical Component

3.1 The design contains no temporal comparison, so it cannot test the post-pandemic shift its title claims

The manuscript is titled around post-pandemic generalisation, Table 2 is captioned as a temporal contrast, and Section 7 frames the study as bounding deployment risk for a model trained in a window closing in 2016. No temporal comparison exists in either component. PTB-XL is entirely pre-pandemic and its contrasts are between disease superclasses within a single era. Study B compares post-COVID cases with contemporaneous non-COVID controls, which estimates the effect of infection as an exposure rather than a change in the population over time. These estimands differ in their deployment implications: a model can remain perfectly calibrated in a population where infected and uninfected individuals differ, provided the population mixture has not changed, and can miscalibrate badly through changes in age structure, comorbidity prevalence, or acquisition technology even if infection has no electrophysiological effect at all. Two feasible additions would close the gap. A within-archive comparison of ECGs recorded at the contributing centres before and after the pandemic, on the same biomarker, would measure the distributional shift that actually matters for deployment while holding device and population roughly constant. A within-person pre-post analysis in the subset of cases with an archived pre-infection ECG would be stronger still, since each patient serves as their own control and the between-person nuisance factors of axis, habitus, and lead placement are removed. Existing work on de-novo ECG change after COVID-19 in screened athletic populations was possible precisely because baseline recordings existed, and institutional archives spanning several years will contain them for a meaningful fraction of the cohort. Failing either addition, the title and hypotheses should be reframed around exposure rather than temporal shift.

3.2 Selection and matching are specified in ways that work against the study's own aims

Cases are defined by cardiac magnetic resonance "performed for clinical indication," which conditions entry on persistent symptoms, troponin elevation, or an abnormal baseline ECG. Since an abnormal ECG is itself frequently the trigger for imaging referral, the case group is selected partly on a variable adjacent to the one being measured, and the resulting difference from controls will index referral practice as well as substrate. Controls are defined as adults "without documented COVID-19" in a period of high population seroprevalence, which describes testing and documentation behaviour rather than infection status, producing both attenuation from misclassification and a systematic difference in healthcare-seeking propensity. The matching set introduces a further difficulty: it includes heart failure, diabetes, and chronic kidney disease, conditions that the protocol's own principal source on post-acute sequelae identifies as consequences of infection, so matching on them removes part of the effect being estimated and may open selection pathways whose direction of bias is not guaranteed to be conservative. Distinguishing comorbidity ascertained before the infection date from comorbidity arising afterwards, and matching only on the former, would resolve this, and an explicit causal diagram would make the reasoning checkable. The estimand should also be stated, since the protocol combines matching, covariate adjustment, and a crude rank comparison without indicating which quantity is intended, and time zero should be fixed given that infection date, imaging date, and ECG date all differ across a twelve-month eligibility window. Finally, the analysis should respect the matched structure; applying an independent-samples rank test to matched data produces error rates and interval coverage that depart from nominal values, with the discrepancy widening as the selection process strengthens, and the selection process here is strong.

3.3 The governance model is incompatible with the analysis, and the study is not currently deliverable as specified

Section 8 states that for Study B "only de-identified, aggregate results leave each site," while Section 6 specifies cross-site matching on age, sex, and a five-item comorbidity set, multiple imputation of missing covariates, pooled rank tests, a trend test across severity strata, and correlations between the aVL shift and imaging and humoral measures. None of these can be executed on site-level aggregates, and matching in particular is inherently an individual-level operation. The resolution changes the study materially. A genuinely federated design would require local matching at each site, a distributed and version-controlled analysis script, quantified between-site heterogeneity, a minimum per-site cell count, and a power calculation reflecting the efficiency loss; a pooled design would require Section 8 to describe the de-identification standard, transfer mechanism, custodian, and retention plan. Related gaps compound the difficulty. No contributing centres are named, no institutional review board approvals are reported as obtained or pending, no consent or waiver arrangement is described, no accrual window or data-freeze date is set, and no feasibility evidence is offered that the required number of imaging-positive cases is reachable. No specific funding is declared for a multi-centre study involving imaging and biomarker assays, and the author list comprises two investigators from a single health cluster with no named statistician, data manager, or site principal investigators. The authors might reasonably consider seeking in-principle acceptance for Study A now and returning with Study B once at least one data-use agreement and a feasibility count are in hand.

3.4 No clinical outcome is ascertained, so the study cannot speak to sudden cardiac death

The manuscript concerns a biomarker of sudden cardiac death, yet neither component contains an outcome. PTB-XL is a labelled diagnostic dataset without mortality or arrhythmia follow-up, and the Study B endpoint list comprises the derivatives, a repolarisation set, imaging parameters, and circulating markers, with no arrhythmic event, defibrillator therapy, cardiac arrest, or death among them. The strongest possible result would therefore establish only that an ECG morphology tracks myocardial disease, leaving open whether it carries the prognostic information the original model exploits. This matters most for the deployment argument, because a distributional shift without elevated arrhythmic risk implies over-prediction and warrants recalibration, whereas the same shift accompanied by elevated risk means the model is behaving as intended and no recalibration is indicated. The protocol cannot distinguish these opposite conclusions. Since the Study B cohort is retrospective and drawn from institutional systems, follow-up for arrhythmic events, device therapy, and mortality is in principle obtainable from the same records, and even an exploratory assessment of whether the biomarker-to-outcome association differs by exposure group would transform what the study can claim.

Minor Issues

1. The manuscript states 21,799 ECGs while the cited source describes 21,837 records, a difference reflecting dataset versioning. The exact repository version and the sampling rate used should be stated, since both directly scale the derivative metrics and determine the high-frequency content available to the second difference. The collection era of the dataset, which predates current acquisition practice by some decades, should also be acknowledged where generalisability is discussed.

2. The structured abstract heading is present with no content beneath it, and no protocol version, date, or registration identifier is supplied. Both are expected for Stage 1 assessment and for permanent registry deposit, the latter so that subsequent amendments can be tracked against a frozen document. A patient and public involvement statement, now required by many cardiovascular journals for retrospective patient-data studies, is likewise absent.

3. Two references carry "[DOI to be confirmed at submission]" placeholders and one is described as a conference abstract. One of these supplies both the discrimination figures quoted in the background and the rationale for the entire secondary repolarisation endpoint set, so its full bibliographic details, design, sample size, and peer-review status should be resolved before registration. The acknowledgement of AI assistance would benefit from naming the tool, version, and the verification procedure applied to the reference list.

4. Figure numbering collides: two different captions are numbered Figure 1, and the second object is then also captioned Figure 3. Table 2 is split across two tables, the second appearing without column headers. Table 1's therapeutic-implication row lies outside anything either study can adjudicate, and Figure 1's caption claims the convergence model is what Study A "tests directly," which overstates what a superclass comparison establishes. The same figure lists autonomic dysfunction and inherited channelopathy as tributaries, neither of which is tested anywhere in the design.

5. The title describes the work as a "replication," but neither component repeats the originating analysis, reuses its data, or re-estimates its model. "External test and extension" would describe the study accurately and would avoid setting an expectation the protocol cannot meet.

6. Several signal-processing choices are left open. The lead on which the R peak is detected is unspecified, which changes the analysis window. The beat-averaging method is not stated, nor is the handling of ectopic and post-extrasystolic beats, whose morphology is systematically altered. The three-beat minimum is asserted without supporting reliability evidence for a noise-sensitive metric and should be set empirically. No rule is given for handling records that fail delineation or for extreme values, and failure rates should be compared across groups since differential exclusion is itself a bias pathway.

7. Table 2 reports a mean case age of 69.2 years and characterises the training and deployment settings, but carries no page- or table-level citation to the source. These are the only hard numbers in the framing section and should be attributable.

8. The sample-size statement describes the assumed effect as "Cliff's delta 0.33, equivalent to a rank-biserial correlation near 0.33," although for two independent groups these are the same quantity, so the phrasing implies two anchors where there is one. Expressing the assumption as a probability of superiority would be clearer clinically. The referenced supplementary power curves are not provided and are material to assessment.

9. The multiplicity structure is ambiguous. "Holm control across the primary and secondary endpoint families" admits both a single combined family and two separate families with independent alpha, and these have different operating characteristics; the ordering of endpoints within each family is also unstated. The dose-response trend test assumes independent ordered groups, which a matched cohort does not supply, and the role of controls within the trend is not specified.

10. The imaging strata are defined qualitatively, as magnetic-resonance evidence of myocarditis or fibrosis and as elevated extracellular volume, without numerical thresholds. Since native T1 and extracellular volume thresholds are vendor-, sequence-, and field-strength-specific, a multi-centre protocol requires either site-specific reference ranges or a harmonisation rule fixed in advance. Assay platforms and reference ranges for the circulating markers require the same treatment.

11. Study B eligibility contains several unresolved points. Cases are defined as moderate-to-severe or hospitalised, yet the severity strata for the dose-response hypothesis include a non-hospitalised group. Vaccination status and infecting variant are not recorded despite both modifying cardiac involvement across the 2021 to 2022 period. Rhythm is not addressed in the exclusions, which cover only bundle-branch block and pacing, although atrial fibrillation, frequent ectopy, and rate-related aberrancy all affect QRS morphology. No rule is given for selecting among multiple qualifying ECGs per patient, and repeated records from the same patient are not addressed in either study. The one-to-twelve-month window is wide and unstratified despite evidence that post-COVID myocardial abnormalities evolve substantially across it, and time since infection should be modelled or used for stratification. The correction formulae for the repolarisation endpoints should be named, since the choice materially changes those measures.

12. Three provisions would strengthen the study's transparency at negligible cost. No blinding is specified between imaging stratification and biomarker computation, although the stratum is the primary grouping variable. No outcome-neutral positive control is specified to demonstrate that the pipeline can recover a known effect, such as the established QRS-duration difference between conduction disturbance and normal records; without one, null derivative results cannot be interpreted. And the commitment to deposit analysis code does not state that the code will be frozen before analysis, nor does the data-availability statement cover the record-level derived features from Study A, which are non-identifying scalars drawn entirely from open data and could be deposited to make the mechanistic claim fully reanalysable. Relatedly, the protocol permits Study A, which anchors the mechanistic claim, to be analysed before registration, since registration is promised only before Study B analysis begins; the commitment should apply to both components.

13. The endpoint set and the hypotheses are not fully aligned. The chemokine CCL7 appears among the Study B endpoints but not in H5 as stated, and should either be added to the hypothesis or labelled exploratory. Bundle-branch block is excluded from Study B yet said to be "analysed separately for H3," which is framed elsewhere as a Study A falsification test; if a second, separately powered falsification analysis is intended, it should be specified.

Missing and Inadequately Integrated Literature

Cited but Inadequately Integrated

The originating study is cited four times but engaged with only at the level of its headline finding. The features of that work most relevant here are never discussed: the counterfactual-generation procedure that produced the aVL description, which should govern how the feature is operationalised; the reported validation in independent health-system and registry cohorts, which speaks directly to the generalisation question this protocol asks; and the reported relationship between the identified high-risk group and defibrillator benefit, which is the clinical anchor the present design lacks. The specific figures and tables from which Table 2's left-hand column is drawn should be cited.

Kotecha and colleagues (2021) appear in the reference list but are not cited anywhere in the text. Their documentation of heterogeneous injury patterns in recovered troponin-positive patients, including coexisting myocarditis-like and infarct-pattern phenotypes, bears directly on the protocol's three-way imaging stratification, which makes no provision for dual pathology. Chudzik and colleagues are cited for a roughly seventeen percent prevalence of fragmented QRS in non-hospitalised patients, but this finding is a substantive challenge rather than background support: fragmentation is conceptually the opposite of the smooth slur the protocol measures, so if post-COVID ECGs tend toward fragmentation, the derivative measures should rise rather than fall, and the tension should be confronted explicitly in H2's directional reasoning. Bhatia and colleagues are cited for the low rate of de-novo ECG change in athletes, but what made that study possible was the availability of pre-infection baseline recordings, a design feature the present protocol does not consider; the same source also implies that the assumed moderate effect requires justification rather than assertion.

Xie and colleagues are used to justify the dose-response hypothesis, but the gradient documented there is between acute care setting and subsequent clinical cardiovascular outcomes, not any electrocardiographic measure, and importing it across outcome domains is an assumption worth stating. The same work's dual contemporary-and-historical control architecture is directly applicable to the control-definition problem in Study B, and its documentation of incident heart failure and metabolic disease after infection bears on the matching set. The systematic review of temporal dataset shift is invoked only as a trigger for post hoc checks, whereas its taxonomy distinguishing covariate shift from concept drift would sharpen H2 considerably, since a shift in the biomarker distribution and a change in the biomarker-to-outcome relationship carry different deployment implications and the present design can detect only the former. The review of myocardial interstitial fibrosis is cited to support the biomarker pairing in H5, but its assessment of how weakly circulating markers track histologically verified fibrosis, and its distinction between reactive interstitial and replacement fibrosis, are not carried into the design. The signal-processing toolbox is cited once without naming the delineation method or version or reporting its published agreement statistics for QRS offset, and the PTB-XL source is cited for label aggregation while its signal-quality annotations, dual sampling rates, multiple-records-per-patient structure, and recommended folds go unused.

Truly Missing Papers

Das and Zipes (2009) is not cited and should be. Their review establishes fragmented QRS as a depolarisation marker of myocardial scar associated with mortality and sudden cardiac death, and documents that it is not disease-specific. This is the closest existing precedent for the claim that a terminal-QRS morphology indexes a shared remodelling endpoint, and the finding that fragmentation rather than smoothing marks scar is the principal empirical challenge to the biomarker's assumed direction. Engaging with it is essential to both H1 and H3. De Bakker and colleagues (1993) is likewise absent; their demonstration of zigzag activation through surviving bundles in infarcted human myocardium is the foundational mechanistic account of how structural remodelling produces slow anisotropic conduction, and it supplies exactly the electrophysiological grounding the convergence model currently asserts rather than derives.

On measurement, Martínez and colleagues (2004) provides the standard wavelet-based delineator evaluated against manually annotated databases with explicit reporting of QRS-offset error, serving both as a benchmark and as a ready alternative algorithm for the sensitivity analysis recommended above. Luo and Johnston (2010) reviews how bandwidth, notch filtering, and baseline removal distort QRS morphology and high-frequency content, and is the natural foundation for the harmonisation plan the protocol lacks. Strodthoff and colleagues (2021) is the standard benchmark for PTB-XL, establishing the conventional superclass task definitions and folds and analysing hidden stratification within those superclasses, all of which bear on the group-definition concerns raised here.

On design and inference, Hernán and Robins (2016) offers the target-trial framework for stating eligibility, exposure, time zero, and the causal contrast, which would immediately expose the ambiguity between an exposure effect and a temporal shift. Austin (2011) demonstrates through simulation that independent-sample inference applied to matched observational data yields error rates and interval coverage departing from nominal values, supporting the recommendation that the Study B analysis respect the matched structure. Lakens (2017) provides the accessible treatment of equivalence testing and the specification of a smallest effect size of interest, which is the machinery the outcome-neutral framework currently lacks. Finally, Finlayson and colleagues (2021) gives the clinical framework for reasoning about dataset shift in deployed systems and would place the deployment argument on firmer conceptual ground than a single citation currently allows.

Austin, P. C. 2011. Comparing paired vs non-paired statistical methods of
    analyses when making inferences about absolute risk reductions in
    propensity-score matched samples. Statistics in Medicine 30:1292-1301.
Das, M. K., and D. P. Zipes. 2009. Fragmented QRS: a predictor of mortality and
    sudden cardiac death. Heart Rhythm 6(3 Suppl):S8-S14.
de Bakker, J. M. T., F. J. L. van Capelle, M. J. Janse, et al. 1993. Slow
    conduction in the infarcted human heart: zigzag course of activation.
    Circulation 88:915-926.
Finlayson, S. G., A. Subbaswamy, K. Singh, et al. 2021. The clinician and dataset
    shift in artificial intelligence. New England Journal of Medicine 385:283-286.
Hernan, M. A., and J. M. Robins. 2016. Using big data to emulate a target trial
    when a randomized trial is not available. American Journal of Epidemiology
    183:758-764.
Lakens, D. 2017. Equivalence tests: a practical primer for t tests, correlations,
    and meta-analyses. Social Psychological and Personality Science 8:355-362.
Luo, S., and P. Johnston. 2010. A review of electrocardiogram filtering. Journal
    of Electrocardiology 43:486-496.
Martinez, J. P., R. Almeida, S. Olmos, A. P. Rocha, and P. Laguna. 2004. A
    wavelet-based ECG delineator: evaluation on standard databases. IEEE
    Transactions on Biomedical Engineering 51:570-581.
Strodthoff, N., P. Wagner, T. Schaeffter, and W. Samek. 2021. Deep learning for
    ECG analysis: benchmarks and insights from PTB-XL. IEEE Journal of Biomedical
    and Health Informatics 25:1519-1528.

Conclusion and Path Forward

The authors have taken an interpretability finding that most readers would treat as an intriguing footnote and asked whether it survives contact with independent data and with a population whose cardiac substrate may have changed. That is exactly the kind of external scrutiny the clinical artificial-intelligence literature needs and rarely receives, and the decision to pursue it through a pre-registered, outcome-neutral protocol places this work in a small and creditable category. The measurement candour, the falsification contrast, and the open-data anchoring of the mechanistic component are real strengths that should be preserved through revision.

The revisions required are nonetheless substantial and fall into three groups. The biomarker needs to be placed on a defensible measurement footing: normalised for amplitude and window length, fixed with respect to sampling rate and acquisition bandwidth, validated against adjudicated morphology, and supported by a blinded delineation reliability substudy with an independent algorithm as sensitivity analysis. The hypothesis set needs to be restructured so that the central claim can fail: convergence should be reformulated as a prediction that forbids something, the conduction-disturbance and bundle-branch groups should be constructed so that H1 and H3 are not in conflict, H2's direction should be stated, the power analysis should cover every hypothesis, and the null branch should be equipped with a pre-specified smallest effect size of interest. And the clinical component needs a coherent design: a genuine temporal contrast or a reframed title, a stated estimand with a defined time zero and a causal diagram, matching restricted to pre-infection comorbidity with analysis respecting the matched structure, a governance model reconciled with the analysis plan, at least one documented data source with a feasibility count, and some form of outcome ascertainment. The authors might reasonably seek in-principle acceptance for the open-data component now and return with the clinical component once these elements are in place. The question is worth the effort, and a protocol revised along these lines would be worth registering and worth running.

Reviewer3 (AI review)

September 28, 2026

AI Review (reviewer3.com)

Comments (9)

1. Inconsistent figure numbering in Figure 3 — Editorial

Figure 3. The aVL terminal - QRS biomarker. A normal beat ends in a sharp downstroke with high first and second differences (left); the high - risk phenotype is a smooth slurred downstroke with low differences (right). The shaded

The figure on page 6 is captioned as 'Figure 3. The aVL terminal-QRS biomarker', but the header embedded within the figure graphic itself reads 'Figure 1. The aVL terminal-QRS biomarker: sharp vs slurred downstroke'. This internal label contradicts the figure's actual numbering in the text and caption.

2. Negative value for absolute difference metric — Major

. Over the 15 For lead aVL, beats are detected and the QRS offset delineated with an open pipeline window from the R peak to the QRS offset, F1 is the mean absolute first difference and F2 the

The text defines F1 as the 'mean absolute first difference' of the aVL voltage. Since it is an average of absolute values, F1 must be non-negative. However, Figure 3 (lower right panel) displays 'F1 = -0.038', which is a negative value and mathematically contradicts the definition of F1 as an absolute difference.

3. Potential sample size insufficiency for trend analysis — Minor

and 70 matched controls are required for the primary contrast. Recruiting 120 per arm allows the severity - stratified dose - response analysis with adequate cells. The target is stated in advance; if

The protocol plans to perform a Jonckheere-Terpstra trend test across three ordered strata of acute-illness severity (non-hospitalised, hospitalised, intensive care) using a target sample size of 120 cases. If the cases are unevenly distributed across these strata (for example, very few intensive care patients), the cell sizes will be extremely small, severely limiting the statistical power of the trend test. The authors should specify minimum cell size thresholds or a plan for collapsing strata if recruitment is highly skewed.

4. Confounding of systemic biomarkers by comorbidities — Minor

across severity strata. Concordance (H5) uses Spearman correlation between the aVL shift and extracellular volume and biomarkers. Multiple imputation han

The protocol proposes using simple Spearman correlations to evaluate the relationship between the aVL shift and circulating biomarkers (galectin-3, soluble ST2). However, both galectin-3 and soluble ST2 are systemic biomarkers that are heavily influenced by non-cardiac comorbidities, particularly renal function (eGFR) and systemic inflammation. Performing unadjusted Spearman correlations within the case cohort could yield spurious associations driven by shared comorbidities rather than cardiac-specific fibrogenesis. The authors should use multivariable regression (e.g., partial correlation or linear regression) to adjust for renal function and other systemic confounders when evaluating these associations.

5. Lack of QRS amplitude normalization — Critical

. Over the 15 For lead aVL, beats are detected and the QRS offset delineated with an open pipeline window from the R peak to the QRS offset, F1 is the mean absolute first difference and F2 the

The primary metrics F1 and F2 are defined as the mean absolute first and second differences of the raw aVL voltage. Because derivatives scale linearly with the amplitude of the underlying signal, these metrics are directly proportional to the QRS amplitude in lead aVL. Systematic differences in QRS amplitude across disease states (such as high voltage in hypertrophy, or low voltage in myocardial infarction or myocarditis) will confound the F1 and F2 measurements, making it impossible to distinguish true terminal QRS slurring from simple variations in QRS voltage. The authors must normalize the first and second differences by a measure of QRS amplitude (such as the peak-to-peak amplitude or R-wave amplitude in lead aVL) to isolate the shape of the waveform from its scale.

6. Confounding of F1/F2 by QRS duration — Minor

H3 (falsification). Notched or bundle - branch morphologies do not show the reduced - derivative slur, confirming the metric sep arates a smooth slur from high - frequency fragmentation.

The falsification hypothesis assumes that notched or bundle-branch morphologies will not show reduced F1 or F2 because notches introduce high-frequency changes. However, bundle-branch blocks also severely prolong the QRS duration, which significantly widens the R-to-QRS-offset window. Because F1 and F2 are calculated as the mean absolute differences (sum of differences divided by the number of samples in the window), a longer window containing slow-moving or flat terminal segments will mathematically bias the mean absolute differences downward. This duration-induced reduction in F1/F2 could mask the high-frequency notched effect, leading to a false support of H3. The authors should analyze the sum of absolute differences or control strictly for QRS duration within the bundle-branch group.

7. Confounding by clinical indication in controls — Critical

Controls: comorbidity

In Study B, cases are post-COVID patients who underwent CMR for a clinical indication (suggesting active cardiac symptoms or suspected injury), whereas controls are matched on age, sex, and comorbidities but selected from patients who had a digital ECG in the same period, without requiring a similar clinical indication. This introduces a major selection bias: any observed differences in F1, F2, or repolarisation measures could be driven by the presence of acute/subacute cardiac symptoms or active myocardial injury in the cases, rather than being a specific post-COVID substrate shift. To rule out this alternative explanation, the control group should consist of COVID-negative patients who underwent ECG/CMR for the same clinical indications.

8. Morphological variation in lead aVL — Major

For lead aVL, beats are detected and the QRS offset delineated with an open pipeline window from the R peak to the QRS offset, F1 is the mean absolute first difference and F2 the mean absolute second difference of the aVL voltage, averag ed across beats per record. A reduction indicates the smooth slur; an increase indicates notching. At least three analysable

The protocol defines the biomarker window starting from the R peak to the QRS offset in lead aVL. However, in many patients—especially those with myocardial infarction or axis deviations—lead aVL may exhibit a QS or rS morphology where a distinct R peak is absent or the terminal portion is an upward slope rather than a terminal R-wave downstroke. The protocol does not specify how these alternative QRS morphologies are handled or whether records with absent R waves in lead aVL are excluded. This could lead to misaligned windows and highly distorted F1/F2 values in the disease groups. The authors should specify clear morphological inclusion/exclusion criteria for lead aVL or use a global QRS template to define the window.

9. Omission of imaging-normal post-COVID controls — Major

The primary Study B contrast compares the imaging - positive case stratum against matched controls for F1 and F2 (Mann - Whitney U, Cliff's delta), with Holm control across the primary and secondary endpoint families. Dose

The protocol stratifies post-COVID cases into myocarditis-pattern, fibrosis/ECV-elevated, and imaging-normal groups, but the primary contrast only compares the imaging-positive cases against matched controls. By omitting the imaging-normal post-COVID cases from the primary comparisons, the study cannot determine whether any observed ECG changes are truly specific to the imaging-confirmed myocardial substrate (myocarditis/fibrosis) or are simply a general systemic post-COVID effect or related to the clinical symptoms that prompted the CMR. The authors should include the imaging-normal post-COVID group as an additional comparator to establish the specificity of the biomarker.

xPeerd (AI review)

September 28, 2026

AI Review (xPeerd — DAReview)

Summary

This manuscript is a pre-registered study protocol, not a completed empirical report. Its core strength is that it states a clear, testable rationale for examining whether a deep-learning ECG biomarker of sudden cardiac death generalizes across disease substrates and shifts in post-COVID myocardial injury. It also commits in advance to outcome-neutral reporting and explicitly treats null findings as informative, which is a meaningful design strength for reproducibility and publication integrity . The two-part design is logically structured: Study A uses PTB-XL open data to test whether reduced aVL derivatives appear across multiple diagnostic superclasses, while Study B proposes a retrospective matched cohort of post-COVID patients with paired cardiac magnetic resonance to test substrate shift directly .

Its main weaknesses are that several central biological and analytical assumptions remain under-justified, Study B is not yet executable as presented without more operational detail, and parts of the literature base are provisional or incomplete. Because this is a protocol, there are no results to assess, so the manuscript’s contribution depends almost entirely on methodological precision, feasibility, and conceptual coherence. At present, the protocol is promising but still vulnerable to ambiguity in endpoint definition, selection bias in the clinical cohort, incomplete handling of confounding, and overextension of mechanistic interpretation from indirect ECG and imaging proxies .

Potential Major Revisions

1. Clarify the manuscript type and calibrate claims accordingly

The document is explicitly labeled “Study protocol” and repeatedly states that it is intended for pre-registration before analysis begins . However, parts of the framing read as if the paper is already positioned to support mechanistic inference rather than only to propose a test. For example, the manuscript states that “Study A tests directly” the “Convergent Electrical Remodelling Model” . That wording is too strong for an observational open-data comparison using diagnostic superclasses. Study A may test consistency with a convergence hypothesis, but it cannot directly establish shared electrical remodeling as a biological mechanism. I recommend revising all causal or mechanistic language to reflect that the protocol evaluates compatibility with the proposed interpretation rather than directly verifying pathophysiology.

2. Strengthen the conceptual bridge between the original biomarker and the new post-COVID application

The manuscript’s central rationale is that the original deep-learning biomarker, described as “a slurred terminal R-wave downstroke in lead aVL with reduced first and second QRS differences,” may reflect a broader “multi-substrate signature” rather than fibrosis alone . This is an interesting hypothesis, but the conceptual leap remains underdeveloped. The text states that “Fibrosis is one tributary rather than the whole story” and proposes a “Convergent Electrical Remodelling Model” . Yet the protocol does not adequately define what evidence would falsify this broader model, beyond reduced derivatives in two or more PTB-XL superclasses and no reduction in a notch group . That may distinguish smooth slurring from notching, but it does not fully discriminate among alternative explanations such as age effects, conduction delay, signal preprocessing artifacts, or broad disease severity. I recommend adding a fuller alternative-model section specifying what competing explanations exist and which observed patterns would support or weaken each one.

3. Improve endpoint reproducibility by operationalizing ECG preprocessing in sufficient detail

The biomarker definition is promising but presently under-specified for high-stakes reproducibility. The manuscript states: “For lead aVL, beats are detected and the QRS offset delineated with an open pipeline. Over the window from the R peak to the QRS offset, F1 is the mean absolute first difference and F2 the mean absolute second difference of the aVL voltage, averaged across beats per record” . This leaves key details unresolved: sampling-rate harmonization, noise filtering, beat exclusion criteria, ectopy handling, baseline wander correction, delineation robustness across abnormal morphologies, and whether amplitude normalization is used. Since the entire study hinges on sample-to-sample derivatives, even small preprocessing differences could materially change F1/F2. This is especially important because the paper itself argues that image-based ECG recovery is unusable due to timing error “of tens of milliseconds” . The protocol should therefore include a precise signal-processing pipeline, ideally with fixed parameter values and a prespecified quality-control workflow.

4. Reconsider whether PTB-XL superclass comparisons are sufficient to support H1

H1 states that reduced aVL derivatives across “myocardial infarction, ST/T change, conduction disturbance, hypertrophy” would support “a convergent rather than fibrosis-specific reading” . This may be directionally suggestive, but PTB-XL diagnostic labels are broad and clinically heterogeneous. A superclass-level association does not show convergence of substrate; it may simply reflect mixed morphology classes sharing QRS smoothing for unrelated reasons. The protocol acknowledges multiple tributaries but then tests them using coarse labels. I recommend either narrowing the disease phenotypes to more specific ECG/pathology-relevant groups or explicitly downgrading the inferential scope of H1. As written, the planned analysis risks overinterpreting a broad pattern as mechanistic convergence.

5. Address selection bias and indication bias in Study B more explicitly

Study B includes “adults (>=18 years) 1 to 12 months after PCR-confirmed moderate-to-severe or hospitalised COVID-19, with cardiac magnetic resonance performed for clinical indication” . This is a major vulnerability. Patients referred for cardiac magnetic resonance are not representative of all post-COVID patients; they are enriched for symptoms, abnormal preliminary testing, or clinician concern. The manuscript does partly acknowledge that measurable shifts are expected in “the moderate-to-severe and imaging-positive subgroup” , but that does not resolve selection bias. The proposed control group also includes individuals “without documented COVID-19” and only “where available” cardiac magnetic resonance , which introduces asymmetry in ascertainment. I recommend a much more explicit bias analysis plan: define referral pathways, specify calendar-time matching, discuss silent prior infection in controls, and explain how differential imaging availability will affect inference.

6. Refine matching and adjustment strategy to avoid residual confounding

The manuscript says that cases and controls are matched on “age, sex, and a pre-specified comorbidity set,” and analyses adjust for “heart rate and QRS duration” while age is also modeled as a covariate because the original model encodes chronological age . This is sensible but likely insufficient. Medication effects, autonomic state, electrolyte abnormalities, prior myocarditis unrelated to COVID-19, obesity, and ECG acquisition differences can all alter repolarization or derivative-based morphology. The protocol should specify whether matching is exact, propensity-based, or nearest-neighbor; whether matching occurs within centers; and whether center is included as a random or fixed effect. Without this, multicenter variability may be misread as substrate shift.

7. Clarify multiplicity, hierarchy, and decision rules across hypotheses

The statistical plan specifies Holm control “across the primary and secondary endpoint families” for the primary Study B contrast, and Holm-Bonferroni control across eight primary tests in Study A . However, the full hierarchy across H1-H5 remains unclear. The manuscript includes primary, falsification, dose-response, and concordance hypotheses , but does not fully define whether failure of H1 affects interpretation of H2, or whether H4/H5 are contingent on H2. That matters because the paper’s narrative coherence depends on the two studies reinforcing one another. I recommend a transparent inferential hierarchy showing which conclusions are confirmatory, which are exploratory, and which require prior support from another hypothesis.

8. Temper statements implying biological separability that the design cannot fully deliver

The manuscript claims that the paired modalities allow the “relative contributions of localized scar, active interstitial inflammation, and stable collagen to the aVL derivatives” to “be separated rather than assumed” . This is overstated. Native T1, T2, extracellular volume, late gadolinium enhancement, galectin-3, ST2, and CCL7 are all informative but indirect and partly overlapping proxies. In a retrospective matched cohort, they do not cleanly decompose distinct biological components. I recommend changing this to a more modest claim, such as triangulating associations with plausible tissue states rather than separating causal contributions.

9. Reassess literature support and citation stability

The reference list includes items with unresolved bibliographic status, including “Int J Cardiol 2024. [DOI to be confirmed at submission]” and “Europace 2023 (abstract). [DOI to be confirmed at submission]” . For a protocol whose rationale depends heavily on a focused emerging literature, reliance on incomplete or abstract-only citations weakens evidentiary stability. More importantly, the first reference is “Nature (2026)” for the Obermeyer biomarker paper . Given the protocol’s framing around a very recent anchor study, the authors should explicitly distinguish established findings from still-new evidence and avoid giving the impression that the mechanistic interpretation is settled.

10. Fraud/paper-mill screen: low concern, but some stylistic features require caution

I do not see strong paper-mill traits such as incoherent topic switching, fabricated numerical tables, or meaningless jargon chains. On the contrary, the protocol is internally organized, hypothesis-driven, and unusually explicit about null results and preregistration . Still, some features warrant caution: highly polished rhetorical phrasing, repeated emphasis on integrity provisions, and the acknowledgment that “The authors used an AI assistant for helping in literature retrieval, protocol drafting, and language editing” . This is not evidence of misconduct, but it increases the importance of verifying that every citation, claim, and operational detail has been independently checked by the authors. The epistemic risk here is not obvious fabrication, but overconfident conceptual stitching aided by fluent drafting.

Potential Minor Revisions

1. Typographic and formatting issues

There are visible formatting artifacts throughout the extracted text, including broken spacing and line-flow disruptions, for example “slur￾versus-notch falsification” in the abstract/methods region , “de￾identified” in the ethics/data section , and “T peak￾to-end” in the endpoints section . These appear to be PDF encoding or hyphenation artifacts, but they should be corrected in the manuscript source before circulation or submission.

2. Inconsistent page-text presentation

Several sections show intrusive footer/header text such as “This preprint research paper has not been peer reviewed” and “Electronic copy available at: https://ssrn.com/abstract=7030178,” inserted mid-flow in the extracted text . While this may be a conversion issue, the final version should ensure that page headers do not visually interrupt sentence continuity.

3. Minor wording improvements

The phrase “The honest expectation is therefore a measurable shift” is rhetorically vivid but not ideal for a protocol; “the prespecified expectation” or “based on prior evidence, the expected pattern” would be more neutral . Likewise, “stated honestly” as a subsection cue is stylistically unusual for formal biomedical writing and may be better replaced with “limitations of public data sources” or similar .

4. Abbreviation discipline

The manuscript introduces the “Convergent Electrical Remodelling Model” and its acronym CERM in Figure/Table context . The authors should ensure that abbreviations are introduced in the main text before figure-dependent usage and used consistently thereafter.

5. Citation presentation

Some references are complete with DOI, while others are incomplete or marked “to be confirmed” . The reference list should be standardized before submission. If certain citations remain abstract-only, that status should be transparent in the text where claims derived from them are discussed.

6. AI content analysis

Estimated percentage of AI-generated content: moderate-to-high in prose style, approximately 35-55%.

This estimate is based on stylistic indicators rather than proof. The manuscript’s prose is consistently fluent, structurally uniform, rhetorically balanced, and unusually polished for a technical protocol, especially in lines such as “This is the core integrity provision” and “The honest expectation is therefore a measurable shift” . The acknowledgment confirms AI assistance in “literature retrieval, protocol drafting, and language editing” , so AI involvement is already disclosed.

Highlighted likely AI-shaped sections:

• The structured abstract and rationale, where the language is highly compressed and symmetrical in formulation .
• The explanatory conceptual framing around the CERM model and “tributary” metaphor, which reads more rhetorically synthesized than conventionally biomedical .
• The outcome-neutral commitment section, which is strongly polished and repetitive in assurance language .

Assessed epistemic impact: limited if the protocol details, citations, and statistical plan are accurate; more serious if fluent AI-assisted drafting has obscured unresolved methodological gaps. Here, the main risk is not plagiarism-like surface generation but the possibility that polished wording overstates operational readiness and mechanistic clarity.

Recommendations

1. Reframe the manuscript more explicitly as a protocol that tests associations consistent with a convergence hypothesis, not as a study that can directly establish shared remodeling biology.

2. Expand the methods with a fully reproducible ECG signal-processing appendix covering preprocessing, beat selection, delineation, sampling-rate handling, artifact control, and quality assurance thresholds.

3. Add a dedicated limitations/bias section for Study B focused on referral bias, survivor bias, undocumented prior COVID in controls, multicenter heterogeneity, and asymmetrical access to cardiac magnetic resonance.

4. Predefine a stricter inferential hierarchy across H1-H5 so that readers can distinguish confirmatory from exploratory conclusions.

5. Narrow the biological claims attached to imaging and circulating biomarkers; present them as triangulating correlates rather than separable tissue-state estimators.

6. Update and verify all citations, especially those with missing DOI information or abstract-only status, and ensure that the rationale does not lean too heavily on unstable or incomplete references.

7. Standardize tone and remove rhetorically charged expressions that, while readable, may reduce perceived scientific neutrality in a protocol manuscript.

8. Before submission, conduct a line-by-line author verification of every AI-assisted section to ensure that polished prose has not outpaced methodological specificity.

Overall, I judge the manuscript to be coherent, scientifically plausible, and not overtly suggestive of fabrication, but still in need of substantial methodological sharpening before it would function as a strong autonomous protocol for later peer-reviewed publication