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Wolff-Parkinson-White Detection at 471:1 Class Imbalance: A Leakage-Controlled Study of the Data Bottleneck

Nathael Altman

arXiv:2608.14633v1eess.SPcs.LG

TL;DR

WPW detection is difficult because its ECG signature is subtle and the condition is rare. This leakage-controlled study compares seven signal representations across two public corpora and finds that added diversity and capacity did not raise the ceiling, while the deployed pre-filter achieved 0.595 average precision and 0.950 ROC area on the held-out fold.

  • Problem

    WPW detection is challenging because its ECG signature is subtle and the condition is extremely rare.

  • Method

    A leakage-controlled protocol compares seven signal representations using fixed splits and a held-out test fold contacted exactly once.

  • Results

    Added model diversity and capacity did not raise the ceiling, while the deployed two-member percentile-rank vote achieved 0.595 average precision and 0.950 area under the curve.

  • Takeaways & Limitations

    The system is a screening pre-filter rather than a diagnostic tool, with performance established only in-distribution.

  • Takeaways & Limitations

    The study does not establish comparable behavior on pediatric electrocardiograms, which are too few to support a subgroup claim.

Abstract

from arXiv · show

Wolff-Parkinson-White (WPW) syndrome is a congenital cardiac pre-excitation, clinically important and often missed on the resting 12-lead ECG. Detection is hard: the signature is subtle and the condition rare. We pool two public 12-lead corpora, PTB-XL and Chapman-Shaoxing-Ningbo: 66,951 recordings, 142 of them WPW, a prevalence of 0.21% (about 471:1). Under one pre-specified, leakage-controlled protocol, with a held-out fold contacted exactly once, we compare seven representations of the signal, holding the split and the evaluation fixed. Within these corpora and under a modest compute budget, added diversity and capacity do not raise the ceiling: the most orthogonal detector significantly hurts, a feature-union model matches a two-member vote, a convolutional network reaches the wavelet detector without exceeding it, and self-supervised pretraining fails a pre-specified gate. A leak-free learning curve, re-selecting features at every size, still rises at the full 115 positives for the strongest deployed detector (paired 90-to-100% difference +0.027, 95% CI [0.019, 0.033]), so it is not shown to have saturated. An error analysis tested against independent evidence finds that the missed cases have a narrower QRS, confirmed by an on-machine measurement outside our pipeline after we show the sign of this effect depends on which delineator measures it; that uncertain labels show no enrichment among the misses; and that some apparent false positives are recordings the corpus itself codes as pre-excited, placing part of the label problem in the negative class. We measure the optimism of non-nested selection at 0.11 to 0.13 average precision. The deployed output is a percentile rank in a frozen reference distribution, not a probability. On the held-out fold, on 14 positives, it reaches an average precision of 0.595 and an ROC area of 0.950. It is a screening pre-filter, not a diagnostic tool.

1 Introduction

WPW detection is difficult because its ECG signature can be subtle while the condition is extremely rare, making false positives especially damaging to average precision. This paper therefore presents a leakage-controlled, reproducible study focused on the data bottleneck, error sources, selection optimism, and screening-oriented deployment.

  • Motivation: At a positive-to-negative ratio near 471:1, average precision is highly sensitive to the false-positive tail despite strong positive ranking.This reflects metric sensitivity to imbalance, not a ceiling on detector performance.
  • Study contribution: The study evaluates seven 12-lead signal representations under one fixed protocol, finding that added diversity or capacity does not overcome the data constraint.The split, evaluation, and applicable admission gates and learning algorithm are held fixed, while a leak-free learning curve reruns feature selection at every training size.
  • Study contribution: Independent-evidence error analysis links missed cases to narrower QRS, finds no enrichment of uncertain labels, and identifies corpus-coded pre-excitation among some negatives.The narrower-QRS finding was confirmed by an on-machine measurement outside the pipeline, while morphological error analysis showed delineator-dependent effects.
  • Deployment and reproducibility: Nested re-analysis estimates feature-selection optimism at 0.114 and 0.130 average precision, while deployment uses a percentile rank rather than a calibrated probability for screening pre-filtering.The paper releases the decision log, frozen models, out-of-fold scores, and evaluation code for reproduction.

2 Related Work

Prior ECG machine-learning work has advanced toward expert-level performance, but WPW research largely addresses accessory-pathway localization after diagnosis rather than detection at the corpus base rate. Related methodological work motivates patient-disjoint splitting and attention to imbalance, selection optimism, and label noise.

  • General ECG machine learning: End-to-end deep networks approach expert-level performance on several rhythm and morphology tasks using large 12-lead and ambulatory ECG corpora.The PTB-XL release and community benchmarks have helped drive progress in 12-lead ECG machine learning.
  • WPW-specific work: WPW machine-learning studies primarily localize accessory pathways after WPW recognition, rather than detect WPW at the corpus base rate.Classical and deep-learning approaches map delta-wave polarity to ablation sites and report high multi-site localization accuracy on independent cohorts.
  • Evaluation design: Patient-level splitting avoids inflated generalization estimates caused when recordings from the same patient appear in both training and test sets.The study therefore adopts patient-disjoint splitting while disclosing that one corpus lacks patient identifiers in its released metadata.
  • Methodological challenges: Related methodological literatures address extreme class imbalance, patient-stratified validation, confidence intervals, non-nested selection optimism, and label noise in machine-read ECGs.These issues motivate corresponding analyses of evaluation reliability and labels in the study.

3 Data

The study pools two public 12-lead ECG corpora to obtain 142 WPW recordings, while explicitly controlling severe class imbalance, source-corpus batch effects, and split limitations. Data coding is retained conservatively, with descriptive differences and label-vocabulary constraints reported rather than harmonized or silently removed.

  • Dataset composition: 66,951 recordings include 142 WPW cases, yielding 0.21% prevalence and approximately 471:1 class imbalance.PTB-XL contributes 70 WPW cases among 21,799 recordings, while Chapman-Shaoxing-Ningbo contributes 72.
  • Dataset composition: 0.949 cross-validated AUC separates source corpora from non-WPW raw signals, demonstrating a strong acquisition and population batch effect.The corpora differ in hardware, analog filtering, patient populations, and electrode-labeling conventions; pooling therefore trades more positives for measured heterogeneity.
  • Splitting and leakage control: 10-fold splitting distributes positives and corpora across folds, blocks known patient identifiers, and assigns 115 WPW cases to training/out-of-fold selection, 13 to validation, and 14 to the single held-out test set.Chapman-Shaoxing-Ningbo lacks record-level patient identifiers, so each recording is treated as a distinct patient; pairwise similarity testing directly probes possible duplicate WPW recordings.
  • Label definitions: 142 positives are defined by corpus codes: PTB-XL requires WPW likelihood 100, and Chapman-Shaoxing-Ningbo requires SNOMED code 74390002.Questionable labels are retained and flagged; “non-validated label” refers specifically to the corpus metadata field for human confirmation.
  • Descriptive cohort differences: 48 years versus 61 years is the PTB-XL WPW versus non-WPW median age, and 47 years versus 62 years is the corresponding Chapman-Shaoxing-Ningbo comparison.WPW recordings also carry fewer additional abnormalities than surrounding archives, while diagnostic statements describe the ten-second tracing rather than complete clinical histories.
  • Coding limitations: 17.9% versus 4.0% is the Chapman-Shaoxing-Ningbo coding frequency for atrial flutter versus atrial fibrillation, reported as a corpus property rather than clinically harmonized data.The two corpora remain separately reported because SCP-ECG and SNOMED-CT use different vocabularies, and the tables are descriptive only.

4 Methods

The study fixes a leakage-controlled preprocessing, feature-selection, learning, and evaluation protocol across seven signal representations. Methods emphasize filtering without harmonization, clinically motivated and wavelet features, guarded selection, and a fixed small residual network.

  • Preprocessing: All signals use a zero-phase fourth-order Butterworth band-pass filter from 0.5 to 40 Hz, which denoises but does not harmonize acquisition environments.Corpus separability falls from 0.949 unfiltered to approximately 0.90 after filtering.
  • Preprocessing: The ablation establishes that filtering helps, but does not establish 0.5 to 40 Hz over the alternative filtered band.The two filtered bands differ by 0.001 on M3, while the convolutional network’s apparent 0.033 preference lies within its ±0.13 seed spread.
  • Representations: M1 uses delineated clinical intervals and morphology, whereas M3 uses shift-invariant multiscale wavelets; M3’s strongest descriptor has standardized mean difference −2.155.The M3 descriptor’s standardized mean difference replicates separately as PTB-XL −2.196 and Chapman-Shaoxing-Ningbo −1.686.
  • Learning algorithms: M7 is a pre-specified one-dimensional residual network with roughly 63,500 parameters trained directly from raw signals, and its smaller architecture reflects a compute constraint.The study explicitly treats M7 as its own learner because it learns its representation rather than using the shared feature-based learning algorithm.
  • Feature selection: Feature admission requires simultaneous effect-size, false-discovery-rate, and redundancy controls because candidate descriptors outnumber the 115 WPW cases.Selection is computed once on pooled development folds 1 through 8, creating selection optimism in those out-of-fold estimates.
  • Learning algorithms: Feature-based detectors use gradient-boosted decision trees with native missing-value handling, while random forest and logistic regression provide same-protocol learner controls.On M2, the forest reaches 0.306 against 0.266 average precision out-of-fold at a fixed feature count, while the frozen M2 configuration reaches 0.299.

5 Results · 5.1 Held-out test performance · 5.2 Why a two-member vote, and why not the convolutional network

The deployed rank-vote system achieves strong held-out ranking and suppresses false alarms at equal sensitivity, while the convolutional network is not selected because its out-of-fold performance is lower. Raw-score fusion scores higher but is rejected as unsafe across acquisition environments.

  • 5.1 Held-out test performance: The deployed system averages equal-weight percentile ranks from the wavelet-localization and median-beat detectors rather than delivering a probability.Percentiles are computed against a frozen reference distribution of out-of-fold training scores; the operating point is user-selected.
  • 5.1 Held-out test performance: 8 true positives, 3 false positives, and 6 false negatives yield 0.571 recall and 0.727 precision at the frozen operating point.Against 6,699 held-out negatives, the false-positive rate is 0.045% and specificity is 99.96%.
  • 5.2 Why a two-member vote, and why not the convolutional network: 0.717 out-of-fold average precision for the vote is statistically indistinguishable from 0.718 for M4 alone, so its justification is error-profile change rather than metric improvement.The vote was chosen before fold 10 was opened using out-of-fold analysis of complementary detector errors.
  • 5.2 Why a two-member vote, and why not the convolutional network: 8 true positives, 3 false positives, and 6 false negatives for the vote versus 8, 10, and 6 for M4 yield equal held-out sensitivity with one-third as many false positives.False-alarm suppression at equal sensitivity is the operative deployment criterion for a screening aid.
  • 5.2 Why a two-member vote, and why not the convolutional network: 0.737 out-of-fold average precision from raw-score averaging exceeds 0.717 for the rank vote and 0.718 for M4, but raw-score fusion is rejected as environmentally unsafe.The same detector’s score scales differ by a factor of 2.7 across the two corpora.
  • 5.2 Why a two-member vote, and why not the convolutional network: 0.651 out-of-fold average precision for M7 is below 0.717 for the vote and 0.718 for M4, despite M7’s numerical lead on the 14-positive held-out fold.Every held-out confidence interval overlaps every other, so the ranking is not resolvable at that positive count.
  • 5.1 Held-out test performance: 0.595 average precision and 0.950 ROC area characterize the deployed ensemble on the 14-positive held-out fold.The precision-recall curve shows a steep precision drop at high recall under the 471:1 base rate.

5.3 The central result: data is the bottleneck

Across five attempts to raise performance through representational diversity or model capacity, added diversity and capacity did not raise the ceiling within the explored model family. The only statistically resolved comparison favored the baseline direction: adding the most orthogonal detector significantly hurt.

  • Comparative result: Five attempts tested added representational diversity or model capacity on development folds containing 115 positives, using paired average-precision differences with bootstrap confidence intervals.The comparisons were made out of fold under a common protocol.
  • Comparative result: Only one comparison was statistically resolved, and it went in the wrong direction: adding the most orthogonal detector significantly hurt.The result was reported as a paired difference in average precision with a bootstrap confidence interval on the difference.
  • Feature-union models: The feature-union models combined selected features from five detectors, with one model additionally including classical intervals, under the identical protocol.The row-2 model is the “Feature-union model” shown in Figure 2.
  • Central result: Within the explored model family, these comparisons showed that added diversity and capacity did not raise the ceiling.The passages caution that this finding alone does not prove data is the binding constraint.

5.4 Cross-corpus transfer and the batch effect

Cross-corpus transfer preserves ranking discrimination but reduces average precision, partly because WPW prevalence differs between corpora. Raw score scales are not portable, motivating percentile-rank deployment rather than thresholding single-corpus scores.

  • Transfer performance: 0.994 to 0.963: M4’s area under the curve holds across corpus transfer while average precision falls from 0.693 to 0.445.The reported comparison is within corpus to across it for area under the curve, and PTB-XL to Chapman-Shaoxing-Ningbo for average precision.
  • Prevalence and lift: 0.160% against 0.321%: Chapman-Shaoxing-Ningbo has half the WPW prevalence of PTB-XL, which roughly halves precision at equal ranking quality.After prevalence normalization, PTB-XL model lift rises from 216 to 278, while Chapman-Shaoxing-Ningbo model lift falls from 568 to 195.
  • Score-scale portability: 2.7-fold: M4’s 99th-percentile raw score is 0.0336 on PTB-XL versus 0.0125 on Chapman-Shaoxing-Ningbo.The differing raw-score scales mean a threshold read from one corpus cannot be assumed to transfer to the other.
  • Deployment implication: Percentile ranks: the deployed system communicates scores this way because ranking transfers whereas absolute raw scales do not.The jointly trained deployed model largely harmonizes its own scale, so its threshold transfers between the two training corpora; the scale problem concerns single-corpus models and future third corpora.

5.5 No detectable leakage · 5.6 External specificity on an unseen corpus · 5.7 Non-learned baselines and the commercial reference

The shuffled-label control collapses feature-detector performance to prevalence, while the frozen rank-vote shows specificity behavior on an unseen corpus. Non-learned references provide distinct baselines, with commercial measurements carrying substantial within-corpus WPW signal but not directly comparable to deployed detectors.

  • 5.5 No detectable leakage: 0.0021 base rate: shuffled-label average precision collapses to 0.002–0.003 across feature-based detectors, preventing reproduced ranking.Original average precision values ranged from 0.198 to 0.718; five shuffles establish collapse but cannot support a p-value below approximately the stated limit.
  • 5.6 External specificity on an unseen corpus: 10,344 recordings were scored without ingestion failures by the frozen M3+M4 rank-vote on the unseen Georgia 12-lead ECG corpus.With only two WPW-labeled recordings, this external check assesses specificity and false-alarm behavior rather than sensitivity.
  • 5.6 External specificity on an unseen corpus: 89.1% of recordings fell within the reported anchored suspicion-level result on the unseen Georgia corpus.The supplied passage reports this percentage but is truncated before completing the associated description.
  • 5.7 Non-learned baselines and the commercial reference: The clinical two-of-three rule achieved sensitivity 0.373 and specificity 0.734 across 66,951 recordings.The evaluated criteria were PR <120 ms, QRS >120 ms, and a delta wave; because no validated automatic delta-wave detector was available, the analysis used the two-of-three rule.
  • 5.7 Non-learned baselines and the commercial reference: 17,751 negatives were flagged to catch 53 positives, yielding precision 0.003 for the clinical rule.This baseline illustrates the substantial false-alarm burden of the textbook criteria in the pooled dataset.
  • 5.7 Non-learned baselines and the commercial reference: 0.583 out-of-fold average precision and 0.969 area under the curve were achieved by M6 on 57 available positives.M6 was trained on 782 on-machine Marquette 12SL measurement columns under the stated protocol and restricted to PTB-XL folds where those measurements existed.
  • 5.7 Non-learned baselines and the commercial reference: The device-derived measurements carried substantial WPW signal, consistent with 12SL QRS duration alone separating detected WPW cleanly.The figure is not directly comparable to deployed detectors because it uses one corpus, 57 positives, and a different feature source.
  • 5.7 Non-learned baselines and the commercial reference: 0.693 median-beat-detector performance on PTB-XL alone was modestly above the commercial reference, making the within-corpus comparison informative.The passage distinguishes this within-corpus comparison from the non-comparable cross-corpus figures.

5.8 Comparison to prior work

The closest published comparison is a WPW discrimination figure of 0.855 from PTB-XL, but it is a hierarchical leaf estimate from eight cases produced by a joint 71-label network rather than a WPW-specific detector. Our held-out area under the curve was 0.950 on 14 positives with a 95% confidence interval of [0.89, 1.00]; both estimates are underpowered, so the figures are reported only for orientation.

  • Comparison to prior work: 0.855 is the closest available WPW comparison, traced to the PTB-XL benchmark and cited as a target baseline in a recent single-lead study.Its computation determines how it can be used for comparison.
  • Comparison to prior work: 8 WPW cases underlie the reference estimate, generated by a single network jointly trained on all 71 diagnostic statements with hierarchical score propagation.The reference is a class-specific hierarchical leaf area under the curve, not a WPW-specific detector, and reports no confidence interval.
  • Comparison to prior work: 0.950 is our held-out area under the curve on 14 positives, with a 95% confidence interval of [0.89, 1.00].The reference estimate rests on 8 positives and has no reported interval.
  • Comparison to prior work: Neither estimate supports ranking because both rest on too few positives, so the numerical gap is not interpreted as a comparison.The figures are reported for orientation only.

6 Interpretability

Interpretability analyses linked the feature-based detectors to distinct signal facets and leads, with the strongest-effect descriptor showing a replicated lead-dependent pattern consistent with ventricular pre-excitation. The convolutional network’s saliency was highest around the QRS and its onset, but this was not sufficient evidence of WPW-specific attention.

  • Feature-based detectors: Each feature-based detector emphasized a distinct signal facet and lead, spanning delta-region, QRS morphology, activation-loop, and spectral descriptors.M1 emphasized V1 delta-region information; M3 and M4 emphasized QRS morphology in lateral and precordial leads; M5 emphasized activation-loop geometry; M2 emphasized a spectral distributional summary.
  • Feature-based detectors: −2.155 was the strongest standardized effect, from M3’s signed QRS-onset polarity descriptor, whose lead-dependent sign pattern replicated in both corpora and matched ventricular pre-excitation physiology.The descriptor was strongly negative in leads I and aVL and positive in III and aVR, making a corpus artifact less expected.
  • Feature-based detectors: 0.784 out-of-fold area under the curve and 0.096 average precision were achieved by the strongest-effect descriptor alone, showing discrimination but not a sufficient detector at this base rate.The descriptor’s average precision was far below that of the full detector, so M3 remains a many-feature model.
  • Feature-based detectors: 0.667 was the standardized effect of the V5 Hjorth-complexity descriptor with the highest mean absolute Shapley attribution, showing that effect size and attribution need not coincide.This descriptor differed from M3’s signed QRS-onset polarity descriptor, which had the largest effect size.
  • Convolutional network: Highest saliency on the QRS and its onset and lowest saliency on ST-T were observed for the convolutional network, but this pattern was necessary rather than sufficient evidence of WPW-specific attention.Grad-CAM criteria were registered before map production; the control needed to make the interpretation sufficient was not run.

7 Error Analysis

Error analysis found that missed WPW cases had narrower QRS measurements, but this signal required independent adjudication because delineator-based measurements could reverse direction. Label uncertainty did not explain misses, while several apparent false positives reflected corpus coding gaps or QRS-deforming conditions.

  • Scope: 14 of 35 misses were decomposable; the remaining 21 lacked PTB-XL validation and comorbidity fields, sharply limiting the analysis.The decomposition applies only to PTB-XL cases, not all committee errors.
  • QRS width: 76.5 ms versus 118.0 ms: missed PTB-XL positives had narrower custom-proxy QRS widths than detected positives.The comparison was significant by Mann-Whitney testing (p = 0.0008), but the proxy was independently evaluated because it was unreliable.
  • QRS width: 140.0 ms versus 103.0 ms: an independent acquisition-device measurement confirmed narrower QRS duration in detected versus missed WPW cases.The device measurement was computed from the same recordings but outside the study pipeline.
  • Measurement reliability: Three QRS-width measurements disagreed, showing that a single delineator can produce internally consistent but wrong-sign error explanations.The custom proxy correlated 0.58 with the device, yet returned physiologically impossible widths below 60 ms in 9 of 57 cases.
  • False positives: 6 of 25 apparent false positives involved documented pre-excitation or below-threshold WPW labels, while most genuine remainder cases involved QRS-deforming conditions.These findings identify label-definition gaps without asserting that all six recordings were genuinely pre-excited.

8 Discussion

The discussion argues that the strongest detector remains data-limited rather than saturated, while rare-class screening is best framed as portable ranking rather than calibrated probability. It also bounds the conclusions by emphasizing scarce positives, label and cohort limitations, modest compute, and untested external sensitivity.

  • Data bottleneck: The strongest detector’s learning curve is still rising at 115 positives, so the deployed system is not shown to have saturated.Median-beat detector M4 rises from 0.317 at twelve positives to 0.715 at 115; the paired 90%-to-100% difference is +0.027, 95% CI [0.019, 0.033].
  • Data bottleneck: M3’s final learning-curve segment is flat, but its saturation evidence is inconclusive and does not cap the committee.Its paired 90%-versus-100% difference is −0.007, 95% CI [−0.023, +0.010].
  • Screening design: At 471:1 prevalence, specificity enables targeted review rather than requiring expert review of an unfiltered archive.The discussion gives operating examples of a 0.045% held-out false-positive rate near 0.57 recall and 0.93 recall while flagging 100 recordings per 1000.
  • Screening design: The deployed output is a portable rank, because screening decisions depend on review capacity and clinical-economic judgment rather than a base-rate-dependent probability.The discussion states that recovering 93% requires reviewing roughly one recording in ten, whereas recovering 70% requires two per thousand and yields three quarters real.
  • Limitations: The evidence remains statistically limited: 142 WPW cases and 14 held-out positives leave confidence intervals wide and model rankings unresolved.Patient-disjointness is available where identifiers exist, but the Chapman-Shaoxing-Ningbo release lacks identifiers; the positive near-duplicate check found no duplication or held-out twin.
  • Limitations: Claims about model sophistication are scoped to two-corpus training, while label ambiguity, residual batch effects, hospital-archive prevalence, and external sensitivity remain important limitations.The study used a single laptop CPU, did not test externally pretrained ECG foundation models, and the Georgia check contains only two WPW-labeled recordings, one apparently mislabeled.

9 Conclusion

This leakage-controlled study finds no higher performance ceiling from added representation diversity or model capacity under its fixed, modest-compute protocol, while the learning curve remains rising. The deployed percentile-rank vote achieved held-out screening performance, but remains an in-distribution pre-filter rather than a diagnostic tool.

  • Conclusion: Seven signal representations compared under one leakage-controlled protocol did not show a higher ceiling from added model diversity or capacity, while the leak-free learning curve still rises.The held-out test fold was contacted exactly once, and models were trained or pretrained only on the two pooled corpora at modest compute.
  • Conclusion: Narrower QRS characterized missed cases in the corpus with an independent measurement, while the conclusion’s sign depended on which delineator measured it.This was the only error-analysis finding to survive multiplicity correction across its full family of twelve tests; 21 misses in the other corpus remained uncharacterized.
  • Conclusion: The system is a screening pre-filter, not a diagnostic tool, with sensitivity established only in-distribution.Its consequential use is enabling a larger, better-labeled corpus that could raise its own ceiling.
  • Conclusion: All models, out-of-fold scores, evaluation code, and the complete decision log are released for reproducibility and checking.The release supports independent reproduction of the reported results.

Reproducibility and Code Availability

The complete implementation, artifacts, evaluation outputs, and fold assignments are publicly released for exact reproducibility. An interactive demonstration is available, but it is explicitly not a medical device or substitute for clinical interpretation.

  • Implementation: The project repository releases the implementation, frozen artifacts, evaluation outputs, interpretability results, decision log, and per-recording fold assignments.The released pipeline reproduces the reported numbers.
  • Demonstration: The interactive demonstration scores uploaded 12-lead recordings and returns suspicion levels with feature attributions, but is not cleared for clinical use.The demonstration is a research system, not a medical device or substitute for qualified clinician interpretation.
  • Data availability: PTB-XL, Chapman-Shaoxing-Ningbo, and Georgia are publicly available, while proprietary commercial on-machine measurements are not redistributed.The corpora are available through their stated public licensing or PhysioNet channels.

Ethics, Funding, and Competing Interests

The study used only public, de-identified research corpora, required no new participant involvement or ethics approval, received no funding, and was conducted on personal equipment. The author disclosed treatment for the studied condition and a public fundraiser connection.

  • Ethics: No new recordings or participants were involved, and institutional ethics approval was not required because the study used publicly released, de-identified research corpora.The corpora’s stated purpose was research use.
  • Funding: The study received no funding and was performed on personal equipment.
  • Competing interests: The author disclosed treatment for the studied condition at Montreal Children’s Hospital and presenting the work alongside a fundraiser for its Foundation.
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