Review Reports

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The manuscript investigates whether a multilayer perceptron neural network can distinguish normal walking from a deliberately simulated asymmetrical gait using variables derived from four pelvic markers. Twenty healthy young adults performed normal walking and a simulated hemiplegic pattern. The authors calculated three-dimensional ranges of motion of the centroid of the pelvic markers, together with products described as a moving area and volume. The resulting variables were entered into an SPSS neural-network model, which reportedly achieved approximately 98–99% classification accuracy.
The idea of reducing marker requirements for gait screening is potentially useful, and the within-participant acquisition of two deliberately different gait modes provides a reasonable setting for an initial methodological experiment. However, the present analysis does not establish that the model detects clinically meaningful gait asymmetry. The apparent random trial-level training/test split creates a serious risk of subject leakage, while the simulated gait is intentionally extreme and differs from normal walking in speed, stride length, cadence, stance duration, step width, and pelvic displacement. Consequently, the very high accuracy may reflect recognition of walking speed, task instructions, or participant-specific marker trajectories rather than generalizable detection of asymmetry.
Several biomechanical constructs are also incorrectly named or insufficiently validated. The centroid of four pelvic markers is not the center of pressure and cannot be assumed to represent whole-body center of mass without validation. Similarly, multiplying coordinate ranges produces a bounding-box area or volume, not a validated measure of dynamic stability. The clinical claims concerning stroke, cerebral palsy, fall risk, population screening, and treatment monitoring therefore extend considerably beyond the evidence.

- The neural-network evaluation likely contains substantial subject-level data leakage. The manuscript states that SPSS automatically allocated 70% of observations to training and 30% to testing. Because several trials from every participant were included, trials from the same person could occur in both sets. Pelvic coordinates and derived variables contain subject-specific information related to body dimensions, walking style, marker placement, and habitual speed. A random trial-level split can therefore generate highly optimistic performance, even when the classifier does not generalize to new people. The model must be evaluated using grouped participant-level resampling, such as leave-one-subject-out cross-validation or repeated grouped k-fold cross-validation, with all trials from each participant confined to one fold. Any preprocessing, feature selection, architecture choice, and hyperparameter tuning must be performed within the training folds. The authors should report fold-level sensitivity, specificity, balanced accuracy, F1 score, ROC-AUC with confidence intervals, and a pooled out-of-subject confusion matrix. Given the small cohort, a nested validation procedure or a clearly separated internal validation strategy is needed. Until such an analysis is performed, the reported 97–99% correction rates should not be interpreted as evidence of generalizable classification.

- The experimental task does not validate detection of pathological gait asymmetry.
Healthy participants were instructed to keep one leg straight and swing it laterally after viewing a video. This produces a deliberate and pronounced task condition rather than hemiplegic gait. It does not reproduce paresis, spasticity, impaired selective motor control, sensory loss, weakness, compensatory trunk movement, or the heterogeneous asymmetry observed after stroke or in cerebral palsy. Moreover, the classifier only distinguishes normal from simulated gait and cannot identify the affected side or quantify the degree of bilateral asymmetry. The title, Abstract, Discussion, and Conclusions should therefore describe the work as classification of normal versus experimentally simulated asymmetrical walking in healthy adults. Claims concerning patient screening, mild stroke detection, cerebral palsy, treatment effectiveness, fall-risk warning, and clinical deployment should be removed or explicitly presented as hypotheses requiring external validation. At minimum, the next validation stage would need independent patients spanning different diagnoses, impairment levels, affected sides, walking speeds, and assistive-device use.

- The biomechanical variables and stability interpretation require fundamental correction.
The mean position of the LASI, RASI, LPSI, and RPSI markers is a pelvic-marker centroid. It is not the center of pressure, which is a ground-reaction-force quantity derived from force plates, and it should not be abbreviated as “CoP.” Nor is it necessarily an accurate estimate of whole-body center of mass, particularly during an asymmetric task involving compensatory trunk and limb motion. The manuscript alternates between CoP and CoM as if they were interchangeable. The authors should use a neutral term such as “pelvic marker centroid” unless they validate the estimate against a recognized full-body center-of-mass method. In addition, the products RoM-X × RoM-Y and RoM-X × RoM-Y × RoM-Z represent an axis-aligned bounding-box area and volume. They do not measure the area swept by the trajectory and are not established measures of gait stability or fall risk. A larger mediolateral or vertical range does not necessarily imply lower dynamic stability. The authors should either validate these measures against established stability outcomes—such as margin of stability, extrapolated center of mass, local dynamic stability, step variability, or appropriate force-plate measures—or restrict their interpretation to geometric dispersion of the pelvic-marker centroid.

- The observational units, statistical analysis, and major confounding by walking speed must be clarified and reconsidered.
The manuscript states that each participant contributed three normal trials and six asymmetrical trials, which would yield 60 and 120 trials, respectively, for 20 participants. It later reports 120 normal and 240 asymmetrical trials. The origin of this doubling and the reported construction of twelve neural-network models are not explained. The authors must provide a transparent participant-to-trial flow diagram, describe exclusions and repeated trials, define whether left and right cycles were treated as separate observations, and explain the exact unit used in every analysis. Treating bilateral cycles or repeated trials as independent would constitute pseudoreplication. The paired t-tests applied to twelve model accuracy readings and the ANOVA applied to neural-network importance values are also not sufficiently justified, because these outputs may not be independent statistical observations. More importantly, normal and simulated gait speeds differ dramatically—approximately 1.17 versus 0.45 m/s. RoM-X is the most important feature and is closely related to forward displacement and stride length, making walking speed and task execution likely drivers of classification. The authors should include speed-matched analyses, examine models excluding RoM-X, and compare the neural network against simple interpretable baselines such as logistic regression or a single speed threshold. If comparable performance is obtained from speed alone, the claimed neural-network contribution would require substantial reinterpretation.

- The reporting and reproducibility of the machine-learning analysis need substantial improvement. The manuscript relies on SPSS “default options” and automatic architecture selection, but does not report the final number of hidden units, activation functions, loss function, optimizer, stopping rule, random seeds, class weighting, normalization, or the distribution of observations among training and testing sets for each run. The imbalance between normal and simulated trials also makes overall accuracy potentially misleading. The authors should provide complete model specifications, repeated-run variability, class-specific performance, calibration if clinical screening is discussed, and preferably code plus anonymized derived data or a reproducible analysis workflow. Feature importance from an MLP should be interpreted cautiously and supported with a defined method and uncertainty analysis. The literature review should also distinguish disease classification, gait-mode classification, asymmetry quantification, and patient-independent validation. If the authors expand this context, they may consider citing Trabassi et al., “Machine learning approach to support the detection of Parkinson’s disease in IMU-based gait analysis,” Sensors, 2022, as one example of machine-learning-based neurological gait classification using wearable signals. This would be relevant background but should not be treated as validation of the present marker-based model. Trabassi et al., Sensors, 2024, would only be relevant if the Discussion is expanded specifically to address limited pathological datasets, data imbalance, and advanced augmentation strategies; it is not essential to the present analysis.

Author Response

see attched file

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

The most significant methodological limitation of this study is the use of healthy young individuals to simulate hemiplegic gait (with one leg supporting normally while the other leg remains straight and swings laterally), rather than recruiting actual hemiplegic patients. We would like the authors to further explain the rationale for this design choice. A gait pattern deliberately "acted out" by a healthy individual is fundamentally different from a true pathological gait in terms of kinematics, kinetics, and muscle activation patterns. Consequently, there is no evidence to support whether a neural network model trained on such simulated data can generalize to real clinical populations.

There are currently numerous studies on machine learning in this field, and we encourage the authors to incorporate additional recent research papers appropriately. For example: Zhou H, Xu D, Ugbolue U C, et al. Optimizing knee biomechanical parameters during the stance phase of running using the DFIS system: a pilot study[J]. Measurement, 2026: 120956.

The definition of the “centre of pelvis” (CoP) lacks validation and is further conflated with the “centre of mass” (CoM). In human biomechanics, the CoM is typically calculated through mass-weighted averaging across all body segments (e.g., using anthropometric models), rather than being approximated simply by the geometric centre of four pelvic markers. This approximation may introduce even larger errors in asymmetric gait, yet the authors have not provided any validation data (e.g., comparison with full-body CoM calculations) to support this assumption.

Key details of the neural network modelling are missing. In addition, we would like the authors to further explain why the training and testing data were derived from the same participants.

 

Author Response

see attched file

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

I thank the authors for their careful revision of the manuscript. The revised version has improved substantially, and several of the principal concerns raised during the previous review have been addressed. In particular, the authors now distinguish the pelvic-marker centroid from the center of pressure, provide a participant-level training/testing analysis in addition to the trial-level analysis, report recall, precision, and F1 scores, acknowledge that the experimental condition represents simulated asymmetrical gait in healthy adults, and moderate some of the clinical claims.
The newly added subject-level evaluation is especially important because it reduces the risk that repeated trials from the same participant occur in both the training and testing sets. The revised results suggest that the classification remains strong when participants are separated. Nevertheless, several limited issues should be addressed before publication. These primarily concern the continued prominence of the potentially optimistic trial-level analysis, incomplete description of the participant-level resampling procedure, the interpretation of the proposed “stability” measure, remaining clinical overstatements, and language and reporting clarity. These matters appear suitable for minor revision.

Minor points:

- The participant-level analysis should be treated as the primary validation. The manuscript continues to present the random 70/30 trial-level split prominently, including the approximately 99.5% and 97.7% values emphasized in the Abstract and Conclusion. Because different trials from the same participant can occur in both subsets, this analysis remains vulnerable to participant-specific information leakage and should not be the principal evidence of generalization. Please identify the subject-level analysis clearly as the primary validation and report its held-out testing performance in the Abstract and Conclusion. The trial-level results may be retained as a secondary analysis, provided their potential optimism is explicitly acknowledged.

- Please clarify the repeated subject-level splitting procedure. The revised Methods state that ten models were created, each using 14 participants for training and six for testing. Please explain how these ten splits were generated, whether they were mutually independent, whether every participant appeared in a test set, how often each participant was tested, and whether sex and gait-condition balance were maintained across splits. If the ten models arose from repeated random holdout validation, this should be named explicitly. The manuscript should also clarify whether preprocessing and model architecture selection were repeated using training participants only. Reporting the subject-level distribution of test performance, rather than only averages across model runs, would improve transparency.

- The dataset counts and observational units require one final clarification. The manuscript states that every participant completed three normal and six asymmetrical gait trials. For 20 participants, this would ordinarily correspond to 60 normal and 120 asymmetrical trials, whereas the manuscript reports 120 and 240. If measurements from the two sides or separate gait cycles were counted independently, these should be described as side-specific observations or gait cycles rather than additional trials. Please reconcile these numbers and state exactly what constitutes one input observation in the neural-network analysis.

- The proposed stability variable should be interpreted more cautiously. The change from “CoP” to “CPL” resolves an important terminology problem. However, the ratio between the rectangular area formed by pelvic ranges of motion and the product of stride length and step width is a study-specific geometric index; it is not an established measure of dynamic gait stability. In addition, increased pelvic excursion during the deliberately simulated gait does not by itself demonstrate reduced stability or increased fall risk. Please refer to this outcome as a proposed or exploratory pelvic-motion index, provide a clear dimensionless formula, and avoid concluding that larger values necessarily demonstrate poorer stability. Statements in the Results, Discussion, and Conclusion should distinguish geometric pelvic excursion from validated dynamic-stability measures.

- The remaining clinical claims and language should be revised. The manuscript still suggests that the model could determine improvement after treatment, provide early warnings, and guide intervention. Because the study includes only healthy adults performing a deliberately simulated and relatively pronounced gait alteration, these applications have not yet been validated. Please present them strictly as possibilities for future clinical research. The manuscript also requires another careful English-language edit. Examples include “a NN model was bulti,” “neurol network,” “trails” instead of “trials,” “stork” instead of “stroke,” double-negative sentences, and several unclear definitions of performance measures. The newly added citation to Trabassi et al., 2022 is relevant to machine-learning-supported neurological gait classification, but its sentence should be integrated more naturally into the literature review and should clarify that the cited study used IMU-based gait data rather than pelvic-marker coordinates.

Author Response

see attched

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

none

Author Response

thanks