Dear authors,

Thank you for the opportunity to review this paper. The manuscript addresses a timely problem: physician acceptance of artificial intelligence within telemedicine, integrating initial trust and perceived professional substitution into a technology acceptance framework. The physician-focused sample, ethics approval, open-data statement, and reporting of loadings, reliability, HTMT, VIF, R squared, effect sizes, path coefficients, and IPMA are strengths. However, fundamental construct, design, reporting, and inferential problems prevent endorsement as scientifically sound. Below you can find some issues that can support the improvement of your work and future submission.

1) The title and central claim refer to “service utilization,” but the study measures only Behavioral Intention and Intention to Use. Neither is observed utilization. The manuscript describes Intention to Use as “actual desire,” confirming that the endpoint remains hypothetical. This matters because intention frequently does not translate into deployment or sustained use. The title, abstract, conclusions, and discussion must be restricted to intentions, or actual use should be measured through platform logs, verified case counts, or prospective follow-up. Recent multinational physician evidence demonstrates a substantial awareness-to-use gap and shows that training and institutional access are stronger correlates of real use than favorable attitudes alone.

2) “AI-driven telemedicine” is insufficiently specified. Symptom assessment, chatbots, decision support, generative systems, predictive models, and agentic systems have different risks, workflows, and accountability requirements. The authors must define the technology, clinical function, care setting, autonomy, intended user, patient population, data inputs, outputs, human oversight, and whether respondents evaluated a real system, vignette, or generic concept. Otherwise, respondents may have evaluated different exposures.

3) The Methods omit recruitment dates, channels, geographic distribution, institutions, number approached, response rate, incomplete responses, and participant characteristics. Purposive sampling is stated, but the sampling frame is absent, and no demographic table is provided. Age, sex, specialty, career stage, sector, region, telemedicine experience, AI training, and institutional AI availability are essential for judging selection bias and transportability. A participant flow and full characteristics table are required, and conclusions must be limited to the sampled physicians.

4) Eligibility combines physicians with experience, knowledge, or merely exposure to information about AI telemedicine. These groups are not equivalent. “Initial trust” may apply before use, whereas experienced users express learned trust. The authors should define minimum exposure, report proportions with direct clinical use, and perform prespecified stratified analyses. A stronger design would distinguish preuse expectations, first-use trust, calibrated reliance after observing performance, and sustained use.

5) Instrument development is not reproducible. The article gives no item wording, source-scale mapping, translation process, expert-panel composition, content-validity indices, cognitive interviews, pilot sample, or amendments. The complete questionnaire and scoring rules must be supplied. This is critical for Perceived Substitution Crisis, which appears novel. It requires qualitative concept elicitation, expert validation, exploratory factor analysis in one sample, confirmatory assessment in another, test–retest reliability, and convergent, discriminant, and criterion validity.

6) Behavioral Intention and Intention to Use appear conceptually redundant. Their HTMT is 0.853, direct path 0.763, and effect size 1.393. This may reflect tautology rather than prediction. The authors must provide the items, justify the distinction, test a one-factor alternative, compare models, and consider removing one construct. If Intention to Use represents implementation readiness, it needs indicators beyond restated willingness.

7) Discriminant validity has not been established as claimed. Table 2 reports HTMT of 0.927 between Effort Expectancy and Performance Expectancy, exceeding the stated 0.90 criterion. Calling this “approaching” the limit is incorrect. The authors should report bootstrapped HTMT confidence intervals, inspect item semantics, and reestimate a more parsimonious measurement model.

8) The PLS-SEM justification is formulaic. The model is largely confirmatory, the sample is 203, and the constructs appear reflective. Complexity, flexibility, and nonnormality do not alone justify PLS. The authors should state whether the objective is explanation or prediction, report distributional diagnostics, justify composite specification, and conduct a covariance-based SEM sensitivity analysis. If prediction is the objective, they should add PLSpredict and a cross-validated predictive ability test rather than infer prediction from R squared. Current reproducible workflows also support bias-corrected bootstrapping, measurement invariance, multigroup analysis, and Gaussian-copula robustness testing.

9) The power calculation is internally inconsistent and likely incorrect. The text states an F test for R squared deviation from zero, seven predictors, effect size 0.15, alpha 0.05, and power 0.95, yet reports 74 participants. Under those parameters, approximately 153 are required, while Figure 1 displays a critical t value, suggesting a different test. The authors must provide the complete settings and output, identify the maximum number of arrows entering an endogenous construct, and preferably perform Monte Carlo power analysis for the latent model.

10) Data-quality procedures are absent. The manuscript should report missingness, imputation or complete-case rules, exclusions, duplicate prevention, rapid completion, straight-lining, careless responding, and distributional inspection. These omissions matter because a long single-source questionnaire is vulnerable to fatigue and low-quality responses.

11) Common-method variance is unaddressed because all predictors and outcomes were collected from the same respondent, questionnaire, and time point. Procedural safeguards, a marker variable, or a latent-method factor should be reported. Full-collinearity diagnostics may be added but should not be treated as proof that common-method bias is absent. Temporal separation or multiple data sources would be stronger.

12) No covariates or heterogeneity analyses are presented. AI literacy, prior use, specialty, seniority, sector, organizational readiness, and training could confound or modify the paths. The authors should prespecify covariates using a causal diagram, assess measurement invariance before subgroup comparisons, and apply multigroup analysis or interactions.

13) Statistical reporting requires correction. Bootstrap resamples; confidence-interval method, sidedness, random seed, and missing-data handling are absent. Values of p equals 0.000 must be reported as p less than 0.001. Coefficients need 95 percent confidence intervals, not only t statistics and p values.

14) Several signs and decisions are inconsistent across Table 7 and the narrative. For H4, H5, and H6, the table image shows negative coefficients, whereas parts of the prose report positive values while describing negative directions. H10 is significant but labelled “Not Supported” because its direction opposes the hypothesis. The authors must reconcile every coefficient with the analysis file, state directional hypotheses before the Results, and distinguish a rejected directional hypothesis from a null association.

15) The IPMA interpretation is too managerial for the evidence. Scores derived from hypothetical intentions do not establish that increasing trust will increase clinical adoption. The authors should describe IPMA computation, scaling, uncertainty, and sensitivity to construct specification, then frame it as exploratory prioritization rather than an intervention recommendation.

16) Causal language is pervasive despite a cross-sectional design. Terms such as “influence,” “driving,” and “increases,” and the serial pathway from trust to behavioral intention to use, imply temporal order not observed. The analysis estimates contemporaneous associations and is vulnerable to reverse causation, confounding, and temporal bias. The authors must rewrite causal claims, treat indirect effects as exploratory associations, and acknowledge that longitudinal mediation cannot be recovered from one wave. Current guidance requires language to match whether the estimand is descriptive, predictive, or causal.

17) The positive association between substitution crisis and behavioral intention is overinterpreted as curiosity and adaptation, neither of which was measured. Alternatives include reverse-scoring errors, professional-survival motivation, suppression, subgroup mixture, common-method effects, and construct misspecification. Recent experimental evidence suggests professional concerns depend on whether AI is framed as a primary decision-maker or verification aid, while recent clinician studies emphasize calibrated trust and appropriate reliance. The next version should consider professional identity threat, role framing, AI literacy, accountability, contestability, and behavioral-reliance tasks.

18) Ethics and reproducibility statements require correction. The Methods state that written informed consent was obtained, whereas the Consent section says “Not applicable.” This must be reconciled and recruitment privacy described. The Figshare statement is positive, but the repository should contain deidentified item-level data, a dictionary, questionnaire, codebook, SmartPLS project or reproducible code, model settings, bootstrap output, and exclusion rules.

This assessment is limited by the manuscript’s omission of the complete instrument, respondent profile, and analytic artefacts. Consequently, item-level construct validity, sample representativeness, and exact computational reproducibility cannot be independently verified from the article alone.

Final message: The manuscript has a potentially useful dataset and clinically relevant question, but its claims exceed what the design and measurement support. A substantially revised version could become valuable if the authors redefine the outcome as intention, document and validate the constructs, repair statistical inconsistencies, reestimate a defensible measurement model, add robustness and predictive analyses, and sharply constrain causal and managerial conclusions.