Review Reports - Voice-Based Screening of Depression and Anxiety Using Machine Learning and Deep Learning: A Scoping Review of Methods and Clinical Readiness

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The manuscript entitled "Voice-Based Screening of Depression and Anxiety Using Machine Learning and Deep Learning: A Scoping Review of Methods and Clinical Readiness" addresses a timely and clinically relevant topic. The manuscript is generally well structured, and the attempt to move beyond conventional comparisons of algorithmic performance towards an assessment of clinical readiness represents a potentially valuable contribution. The emphasis on external validation, ecological validity, clinically grounded reference standards, and explainability is particularly relevant for the translation of AI-based voice biomarkers into clinical practice.

However, several methodological aspects require clarification and, in some cases, reconsideration before the conclusions regarding clinical readiness can be considered sufficiently robust.

The proposed framework is central to the novelty of the manuscript and therefore requires stronger methodological justification. Five indicators are introduced (sample size adequacy, external validation, prospective evaluation, real-world evaluation, and model explainability), but the rules used to classify studies as Low, Moderate, or High readiness do not appear to incorporate these dimensions equivalently. For example, an evaluation may reach Moderate readiness solely because the sample size is ≥100, whereas explainability does not contribute directly to qualification for High readiness. The authors should provide a clearer rationale and supporting evidence for the classification logic. Alternatively, consideration could be given to presenting the five readiness dimensions separately in addition to, or instead of, a composite ordinal classification.

The thresholds of <100, 100–1000, and >1000 participants require further justification. Sample-size adequacy in machine-learning studies depends not only on the total number of participants but also on class distribution, model complexity, number and dimensionality of predictors, validation strategy, and the precision required for performance estimates. The manuscript should explain why these specific thresholds are appropriate for determining clinical readiness and acknowledge their limitations more explicitly.

The Methods state that segment-level splitting without subject-level separation at final evaluation was an exclusion criterion. However, Section 3.7 reports five evaluations using segment-level splitting and five using mixed approaches. The authors should reconcile these statements and clarify precisely how the retained evaluations satisfied the eligibility criterion. Given the substantial risk of speaker-dependent data leakage, this issue is particularly important for speech-based classification studies.

The manuscript defines prospective evaluation as prospective data collection with concurrent clinical assessment. However, prospective data acquisition is not necessarily equivalent to prospective evaluation of a prediction model. A dataset may have been collected prospectively while the model itself is subsequently developed and evaluated retrospectively. The authors should distinguish between prospective data collection and prospective model validation/deployment and reconsider the corresponding readiness classification where necessary.

The study-selection sequence should be checked for consistency. The Methods indicate that duplicate removal was performed in Zotero before screening, whereas Figure 1 presents removal of 77 duplicates after title/abstract screening. The text, figure, and numerical flow should describe the same sequence of procedures.

Although the stated scope encompasses both depression and anxiety, the evidence base is overwhelmingly focused on depression, with only one included study specifically addressing anxiety. This imbalance is appropriately acknowledged in the Discussion, but it should also be reflected more explicitly in the interpretation of the overall findings. The authors should ensure that the title, abstract, and conclusions do not inadvertently imply a comparable level of evidence for the two conditions.

The manuscript correctly emphasizes that high classification performance does not necessarily imply clinical readiness. This central argument could be strengthened empirically. If the extracted data permit, the authors are encouraged to provide a descriptive comparison of reported performance according to validation strategy (e.g., internal versus external validation) or readiness category. Such an analysis could help demonstrate whether apparently high AUC/F1 values persist under more rigorous validation conditions.

The definition of external validation should be applied consistently across all included evaluations. Cross-validation, held-out subsets from the same dataset, temporal validation, cross-site validation, and evaluation on a genuinely independent external dataset represent different levels of evidence and should not be conflated. A clearer operational definition would improve reproducibility of the readiness assessment.

The manuscript would benefit from careful proofreading. For example, the heading of Section 4.2 contains a malformed character (“Adoptionâ”), some citation ranges appear duplicated (e.g., the citation sequence associated with the included studies), and the JBI reference should be checked. The expression “a 2025 review published in ScienceDirect” should preferably identify the actual journal rather than the publishing platform. Terminology and formatting of references should also be checked for consistency.

Comments on the Quality of English Language

However, several methodological aspects require clarification and, in some cases, reconsideration before the conclusions regarding clinical readiness can be considered sufficiently robust.

Author Response

Comments 1: The proposed framework is central to the novelty of the manuscript and therefore requires stronger methodological justification. Five indicators are introduced, but the rules used to classify studies as Low, Moderate, or High readiness do not appear to incorporate these dimensions equivalently. For example, an evaluation may reach Moderate readiness solely because the sample size is ≥100, whereas explainability does not contribute directly to qualification for High readiness. The authors should provide a clearer rationale and supporting evidence for the classification logic. Alternatively, consideration could be given to presenting the five readiness dimensions separately in addition to, or instead of, a composite ordinal classification.

Response 1: We agree that the classification logic required explicit justification. The weighting was intentional but insufficiently explained. External validation and real-world evaluation were treated as primary qualifying criteria because they address generalisability and deployment feasibility, the two conditions without which clinical implementation cannot proceed regardless of other model properties. Explainability was operationalised as a parallel indicator, recorded individually for each evaluation and visible in Supplementary Table S2 (Clinical Readiness Appraisal), rather than as a sequential prerequisite within the composite classification. Sample size was applied as a floor criterion distinguishing evaluations with fundamentally insufficient statistical power. We have added a paragraph to Section 2 (Critical Appraisal and Clinical Readiness Framework) providing this rationale, and direct readers to Supplementary Table S2 (Clinical Readiness Appraisal), which presents all five indicators as individual binary profiles enabling independent assessment of specific readiness gaps.

The following text has been added to Section 2, after the paragraph defining the High/Moderate/Low categories:

"The composite classification was designed to reflect the most consequential translational prerequisites rather than to aggregate all five indicators uniformly, in accordance with established clinical prediction model evaluation standards and AI deployment frameworks. External validation and real-world evaluation were treated as the primary qualifying criteria for higher readiness categories because they directly address generalisability and deployment feasibility, the two conditions without which clinical implementation cannot be considered. Model explainability was operationalised as a parallel indicator: its presence or absence was recorded for each evaluation and is visible in Supplementary Table S2 (Clinical Readiness Appraisal), but it was not incorporated as a sequential prerequisite within the composite classification, given that an unexplainable model lacking external validation cannot be considered deployment-ready regardless of its interpretability. Sample size was applied as a floor criterion distinguishing evaluations with fundamentally insufficient statistical power from those meeting a minimum threshold for reliable performance estimation. The five indicators are presented both as individual binary profiles in Supplementary Table S2 (Clinical Readiness Appraisal) and as a composite classification, enabling readers to identify specific readiness gaps independently of the summary category."

Comments 2: The thresholds of <100, 100–1000, and >1000 participants require further justification. Sample-size adequacy in machine-learning studies depends not only on the total number of participants but also on class distribution, model complexity, number and dimensionality of predictors, validation strategy, and the precision required for performance estimates. The manuscript should explain why these specific thresholds are appropriate for determining clinical readiness and acknowledge their limitations more explicitly.

Response 2: We agree that the thresholds required explicit justification. We have made two additions to the revised manuscript.

First, in Section 2 (Critical Appraisal and Clinical Readiness Framework), immediately after the definition of indicator (1), sample size adequacy, we have added the following text:

"A sample below 100 was considered insufficient for stable performance estimation across most classification architectures regardless of other design features. The threshold of 1,000 identifies evaluations with substantially greater statistical reliability than the field median observed in this review (median N = 118), while the 100–1,000 range represents the majority of the evidence base. These thresholds were selected as pragmatic stratification points broadly consistent with minimum sample size considerations for clinical prediction model development [7], and do not account for class distribution, model complexity, predictor dimensionality, validation strategy, or the precision required for performance estimates; they should be interpreted as approximate stratification criteria rather than absolute adequacy standards."

Second, the following sentence has been added to Section 4.4 (Limitations):

"The sample size thresholds applied in the clinical readiness framework (<100, 100–1,000, >1,000) were defined pragmatically and do not incorporate class imbalance ratios, model parameter counts, predictor dimensionality, validation strategy, or the statistical precision required for reliable performance estimation."

Comments 3: The Methods state that segment-level splitting without subject-level separation at final evaluation was an exclusion criterion. However, Section 3.7 reports five evaluations using segment-level splitting and five using mixed approaches. The authors should reconcile these statements and clarify precisely how the retained evaluations satisfied the eligibility criterion. Given the substantial risk of speaker-dependent data leakage, this issue is particularly important for speech-based classification studies.

Response 3: We thank the reviewer for this observation, which prompted a comprehensive re-examination of data splitting practices across all included evaluations by direct inspection of the original source publications.

We first clarify the distinction between the two categories mentioned in the original Section 3.7. The five evaluations described as using "mixed approaches" combined segment-level training with subject-level majority voting for the final prediction: segment boundaries from the same speaker were used only within the training and segment-scoring stages, while the final classification decision was aggregated at the subject level. These evaluations satisfy inclusion criterion 7, which requires subject-level data separation at model evaluation, not throughout all processing stages. This distinction is clinically meaningful: the risk of speaker-dependent data leakage arises specifically when a speaker's data contribute to both the training set and the held-out evaluation, a condition that subject-level majority voting at the prediction stage prevents. This clarification has been made explicit in the revised Section 3.7.

Regarding the five evaluations originally coded as segment-level, this re-examination revealed two distinct issues. First, four evaluations (Zhang et al. 2024, CMDC dataset; Zhang et al. 2026, MODMA dataset; Wang et al. 2025a, Androids corpus; Wang et al. 2022, CONVERGE corpus) had been incorrectly coded as segment-level or unclear during the initial data charting process. Direct inspection of the source papers confirmed that all four implemented subject-level separation at the point of final evaluation; the original coding represented a data extraction error that has been corrected in the revised charting form and manuscript.

Second, one evaluation, Zhou et al. (2026), MODMA dataset, was confirmed to use segment-level splitting without subject-level separation at final evaluation. Table S1: Study Characteristics of the original publication reports 1,202 training segments and 301 test segments drawn from 52 participants, with no subject-level aggregation applied. This evaluation has therefore been excluded from the synthesis post-hoc. The total number of qualifying dataset evaluations is revised from 38 to 37, and all figures, percentages, and readiness classifications in the manuscript have been updated accordingly.

The revised manuscript presents a corrected Section 3.7 reporting 32 evaluations (86%) with subject-level separation throughout, zero evaluations with segment-level splitting, and five evaluations (14%) using mixed approaches with subject-level separation at final prediction.

Changes to the manuscript: Section 3.7 has been revised to reflect the reclassification of four evaluations from segment-level or unclear to subject-level, the post-hoc exclusion of one segment-level evaluation (Zhou et al. 2026, MODMA), and an explicit clarification of how mixed-approach evaluations satisfy the subject-level separation criterion. Section 3.1 has been revised to document that 35 studies contributing 38 evaluations initially met all eligibility criteria; the post-hoc exclusion of one evaluation (Zhou et al. 2026, MODMA) reduces the final synthesis to 34 studies and 37 qualifying dataset evaluations. Figure 1 (PRISMA-ScR flow diagram) has been updated to reflect this as a separate post-hoc exclusion step following the initial inclusion box. The total evaluation count has been updated from 38 to 37 throughout the manuscript (Sections 3.1, 3.3–3.10, 4.1, 4.2, Abstract, and Introduction). All descriptive statistics, frequencies, proportions, and clinical readiness classifications have been recalculated to reflect the revised set of 37 qualifying dataset evaluations. Section 4.2 notes that 32 evaluations were excluded for segment-level splitting, including one excluded post-hoc following re-examination of the source publication.

Comments 4: The manuscript defines prospective evaluation as prospective data collection with concurrent clinical assessment. However, prospective data acquisition is not necessarily equivalent to prospective evaluation of a prediction model. A dataset may have been collected prospectively while the model itself is subsequently developed and evaluated retrospectively. The authors should distinguish between prospective data collection and prospective model validation/deployment and reconsider the corresponding readiness classification where necessary.

Response 4: We thank the reviewer for this important conceptual clarification. The distinction is valid. As operationalised in the pre-specified framework, indicator (3) always measured whether data were collected prospectively with concurrent clinical assessment, not whether the model itself was validated prospectively. The scores applied to this indicator have therefore always reflected the temporal and ecological design of the data-generating study. However, we agree that the label "Prospective evaluation" was ambiguous and could be read as implying prospective model validation in the strict clinical prediction modelling sense: the application of a pre-trained, pre-specified model to prospectively accruing cases with outcomes unknown at the time of prediction [Collins et al., 2015; Adnan et al., 2025]. Under this stricter criterion, no evaluation in the included set would qualify.

To resolve this ambiguity at source, indicator (3) has been renamed from "Prospective evaluation" to "Prospective data collection" and its definition has been revised as follows:

"Prospective data collection: whether speech recordings and clinical assessments were obtained concurrently within a prospectively designed study protocol, rather than derived retrospectively from archival sources. This indicator concerns the design of the data-generating study, not the model pipeline, and is distinct from prospective model validation, the deployment of a pre-specified model to accruing cases prior to outcome ascertainment, which no evaluation in this review achieved."

No readiness classifications have been changed, as the scoring applied to this indicator was always consistent with the above operationalisation. The renaming and revised definition make this explicit without altering the evidence base.

Changes to the manuscript: indicator (3) has been renamed and its definition revised in Section 2. The column header in Table 3 has been updated from "Prospective Evaluation" to "Prospective Data Collection". All descriptive references to this indicator in Sections 3.7, 3.10, 4.1, and 4.4 have been updated accordingly.

Comments 5: The study-selection sequence should be checked for consistency. The Methods indicate that duplicate removal was performed in Zotero before screening, whereas Figure 1 presents removal of 77 duplicates after title/abstract screening. The text, figure, and numerical flow should describe the same sequence of procedures.

Response 5: We thank the reviewer for identifying this inconsistency. The Methods section correctly describes the intended and actual sequence: duplicate removal was performed in Zotero before title and abstract screening commenced. The narrative in Section 3.1 and the PRISMA-ScR flow diagram were inconsistent with this, placing deduplication after title and abstract screening.

The correct record flow is: 2,463 records retrieved; 1,931 remaining after database-level filters; 77 duplicates removed within Zotero (1,854 records entered screening); 1,596 excluded at title and abstract screening; 258 full-text reports sought.

Section 3.1 has been revised to present this sequence explicitly, and Figure 1 has been updated to position deduplication between the database-filter step and title and abstract screening, consistent with the Methods.

Revised Section 3.1 text (changes highlighted):

"The database search retrieved 2,463 records across PubMed (n = 402), Web of Science (n = 1,118), and IEEE Xplore (n = 943). After applying database-level filters for language, publication date, and document type, 1,931 records remained. Duplicate removal was performed within Zotero, eliminating 77 records and yielding 1,854 records for screening. Title and abstract screening excluded a further 1,596 records. The remaining 258 full-text reports were sought for retrieval; 28 could not be retrieved, and 230 were assessed for eligibility."

Comment 6: Although the stated scope encompasses both depression and anxiety, the evidence base is overwhelmingly focused on depression, with only one included study specifically addressing anxiety. This imbalance is appropriately acknowledged in the Discussion, but it should also be reflected more explicitly in the interpretation of the overall findings. The authors should ensure that the title, abstract, and conclusions do not inadvertently imply a comparable level of evidence for the two conditions.

Response 6: We agree. The Discussion (Sections 4.1 and 4.3) characterises the near-absence of an anxiety evidence base, but the aggregate readiness statistics in the abstract and the opening interpretation in Section 4.1 were presented without a qualifier that would signal their essentially depression-exclusive scope.

The title has been retained. As a scoping review, declaring both conditions within scope is methodologically appropriate, identifying the near-absence of anxiety evidence is itself a primary finding that would be suppressed by restricting the title to depression.

Two targeted revisions have been made:

Abstract: The following sentence has been added after the clinical readiness statistics: "These findings apply primarily to voice-based depression screening; 36 of 37 evaluations targeted depression, and the evidence base for anxiety disorders is limited to a single evaluation, precluding comparable characterisation for that condition."

Section 4.1: The following sentence has been added at the end of the first paragraph, immediately after the clinical readiness interpretation: "These readiness characterisations apply specifically to voice-based depression screening; 36 of 37 included evaluations targeted depression, and the single anxiety-focused evaluation (Ciampelli et al., 2025) precludes any parallel readiness conclusions for that condition."

Comment 7: The definition of external validation should be applied consistently across all included evaluations. Cross-validation, held-out subsets from the same dataset, temporal validation, cross-site validation, and evaluation on a genuinely independent external dataset represent different levels of evidence and should not be conflated. A clearer operational definition would improve reproducibility of the readiness assessment.

Response 7: We agree that the binary "present/absent" coding risks conflating materially different validation designs. The operational definition of indicator (2) in Section 2 has been revised to make the criterion explicit:

"External validation: whether a model trained on one dataset was evaluated on a second, independently collected dataset with no overlap in participants, collection site, or collection period (present/absent), reflecting generalisability beyond the training context. Cross-validation partitions and held-out subsets from the same dataset do not satisfy this criterion."

The following sentence has been added to Section 3.7, after reporting the proportion of evaluations with external validation present: "The strength of evidence within this category was not uniform: three evaluations — Lin et al. (2022), Xu et al. (2024), and Li et al. (2026) — applied a pre-specified model to a prospectively collected, fully independent clinical cohort, representing the most rigorous form of external validation; the remaining nine evaluations involved transfer of a fixed trained model to a second independently collected corpus, which provides a weaker basis for generalisability claims."

The following sentence has been added to Section 4.4: "The binary coding of external validation does not distinguish between evaluation designs that range from assessment in a prospectively collected independent clinical cohort to transfer of a fixed trained model across independently collected benchmarks; this heterogeneity limits the strength of conclusions attributable to the 'present' category."

Comment 8: The manuscript would benefit from careful proofreading. For example, the heading of Section 4.2 contains a malformed character (“Adoptionâ”), some citation ranges appear duplicated (e.g., the citation sequence associated with the included studies), and the JBI reference should be checked. The expression “a 2025 review published in ScienceDirect” should preferably identify the actual journal rather than the publishing platform. Terminology and formatting of references should also be checked for consistency.

Response 8: We thank the reviewer for the careful proofreading. All identified issues have been corrected:

The malformed character in the Section 4.2 heading ("Adoptionâ") has been removed; the heading now reads "Methodological Limitations and Barriers to Clinical Adoption."

The citation in the Data Charting Process section referencing the included studies has been corrected from [16,48] to [16–47], reflecting the correct range of included study references.

Reference 12 has been corrected from "BI Manual for Evidence Synthesis" to "JBI Manual for Evidence Synthesis."

The phrase "a 2025 review published in ScienceDirect" in the Introduction has been replaced with "a 2025 review published in the Journal of Voice" (Briganti and Lechien, 2025 [6]).

References 27 and 45, which used an inconsistent author-name format (semicolon-separated initials-first), have been reformatted to conform to the MDPI author citation style used throughout the reference list.

A general proofreading pass has been conducted across the manuscript to check for further typographic and formatting inconsistencies.

Additional changes not requested by reviewer

Table 3, previously referenced in the manuscript body, has been relocated to the supplementary materials and redesignated as Supplementary Table S2 (Clinical Readiness Appraisal). All in-text references have been updated accordingly. Supplementary Table S1 (Study Characteristics, full) remains unchanged. The reference to Figure S1 in the Supplementary Materials section has been removed, as the PRISMA-ScR flow diagram is presented in the main text as Figure 1.

Author Response File: Author Response.docx

Reviewer 2 Report

Comments and Suggestions for Authors

life-4460764-peer-review-v1 Voice-Based Screening of Depression and Anxiety Using Machine Learning and Deep Learning A Scoping Review of Methods and Clinical Readiness

Review

A brief summary

This scoping review synthesizes 35 studies (38 dataset evaluations) on voice-based ML/DL screening for depression and anxiety, applying a five-indicator clinical readiness framework — sample size, external validation, prospective design, real-world evaluation, and explainability — that adds valuable structure beyond prior performance-focused reviews of this fast-moving field. The manuscript is generally well organized, with an internally consistent PRISMA-ScR flow (record counts and exclusion totals in Figure 1 reconcile correctly), and the readiness appraisal is well supported by the data presented. The concerns raised below are primarily clarifications and corrections rather than fundamental design flaws, and should be addressed before publication.

Major Comments

Deduplication sequencing. The Methods/Results state that duplicates (n = 77) were removed after title/abstract screening (335 → 258), rather than before it, which is atypical for PRISMA-ScR workflows and could affect the reported screening burden. Please clarify whether deduplication genuinely occurred at this stage or whether this reflects a reporting/ordering issue in the flow diagram.
Database and language coverage. Only three databases were searched (PubMed, Web of Science, IEEE Xplore), with no Scopus, no grey literature/preprint servers, and no backward/forward citation snowballing. Given that much ML/DL work in this space appears in venues indexed variably across these sources (e.g., arXiv-hosted conference work), this may understate methodological diversity. This is noted as a limitation but could be stated more concretely (e.g., estimated proportion of relevant venues not covered). English-language restriction interacts with the dataset finding. The review reports that 63% of evaluations used Chinese-language datasets, yet also restricted eligibility to English-language publications. It would strengthen the paper to note whether this restriction plausibly excluded additional Chinese-authored studies (published in Chinese-language journals) that might have altered the linguistic-concentration finding, or whether the 63% figure is likely robust regardless.
Overlap between "Moderate" and "High" readiness criteria. As defined, "Moderate" readiness requires at least one of external validation / adequate sample / real-world evaluation, while "High" requires external validation plus one of large sample/prospective/real-world evaluation. It is not fully clear how an evaluation with external validation alone (but no large sample, no prospective design, no real-world testing) would be classified — this sits at the boundary of both categories as written. Please clarify the decision rule or provide a worked example to resolve the ambiguity.
Inter-rater reliability not reported. Two reviewers independently conducted screening and data charting, with disagreements "resolved by discussion." No agreement statistic (e.g., Cohen's kappa) is reported for either screening decisions or the more subjective readiness-indicator classifications. Given that several indicators (e.g., "real-world evaluation," "prospective design") require judgment calls, reporting inter-rater agreement would strengthen confidence in the appraisal.
Tables referenced but not visible in the reviewed file. Table 3 (readiness appraisal) and any summary tables of study characteristics are referenced in-text but do not appear to be included in the version reviewed here — please add those tables or remove the corresponding references.

Minor Comments

Citation range error in study count. Line 303–304 lists included studies as "[16–19,19–24,24–26,26–47]," with overlapping boundary numbers (19, 24, 26 each appear twice). This is very likely a reference-formatting artifact rather than an intentional list and should be corrected to a clean, non-overlapping citation range.
Section 4.2 heading contains a stray encoding character ("Barriers to Clinical Adoptionâ").
Consider adding a brief sentence on publication bias risk, even though formal risk-of-bias assessment is appropriately out of scope for a scoping review.
The abstract and Results section report identical readiness percentages (26/63/11%) — good internal consistency, no action needed, noted as a strength.

Comments for author File: Comments.pdf

Author Response

Comments 1: Deduplication sequencing. The Methods/Results state that duplicates (n = 77) were removed after title/abstract screening (335 → 258), rather than before it, which is atypical for PRISMA-ScR workflows and could affect the reported screening burden. Please clarify whether deduplication genuinely occurred at this stage or whether this reflects a reporting/ordering issue in the flow diagram.

Response 1: We thank the reviewer for this observation. The deduplication genuinely occurred before title and abstract screening, as performed in Zotero and described in the Methods section. The placement of the deduplication step after title and abstract screening in the original Figure 1 and Section 3.1 reflected a reporting and ordering error, not the actual sequence of procedures. The revised manuscript corrects this throughout. The accurate record flow is as follows: 2,463 records retrieved across three databases → 1,931 remaining after database-level filters → 77 duplicates removed in Zotero, yielding 1,854 records entering screening → 1,596 excluded at title and abstract screening → 258 full-text reports sought for retrieval. Section 3.1 and Figure 1 have been updated to present this sequence consistently.

Comments 2: Database and language coverage. Only three databases were searched (PubMed, Web of Science, IEEE Xplore), with no Scopus, no grey literature/preprint servers, and no backward/forward citation snowballing. Given that much ML/DL work in this space appears in venues indexed variably across these sources (e.g., arXiv-hosted conference work), this may understate methodological diversity. This is noted as a limitation but could be stated more concretely (e.g., estimated proportion of relevant venues not covered).

Response2: We thank the reviewer for this observation. We agree that the limitations statement was insufficiently specific regarding database coverage. The revised manuscript enumerates the sources not covered: Scopus, ACM Digital Library, arXiv (cs.SD, eess.AS, cs.LG), and the ISCA archive, which indexes INTERSPEECH proceedings comprehensively. Grey literature, preprint servers, and backward/forward citation snowballing were also outside the scope of this review. These omissions are acknowledged as a concrete limitation that may have resulted in underrepresentation of ML/DL conference work indexed variably across the three databases searched. The limitations section (Section 4.4) has been revised accordingly.

Comments 3: English-language restriction interacts with the dataset finding. The review reports that 63% of evaluations used Chinese-language datasets, yet also restricted eligibility to English-language publications. It would strengthen the paper to note whether this restriction plausibly excluded additional Chinese-authored studies (published in Chinese-language journals) that might have altered the linguistic-concentration finding, or whether the 63% figure is likely robust regardless.

Response 3: We thank the reviewer for raising this interaction. The datasets underlying the 63% linguistic concentration figure, MODMA, CMDC, CONVERGE, and the Androids corpus, are publicly available corpora documented in English and constitute the standard reference base of the field internationally. Whether inclusion of Chinese-language publications would have altered this proportion cannot be determined without additional searches in Chinese-language databases such as CNKI or Wanfang, which falls outside the scope of this review. This interaction has been acknowledged explicitly as an unresolved limitation in the revised manuscript (Section 4.4).

Comments 4: Overlap between "Moderate" and "High" readiness criteria. As defined, "Moderate" readiness requires at least one of external validation / adequate sample / real-world evaluation, while "High" requires external validation plus one of large sample/prospective/real-world evaluation. It is not fully clear how an evaluation with external validation alone (but no large sample, no prospective design, no real-world testing) would be classified — this sits at the boundary of both categories as written. Please clarify the decision rule or provide a worked example to resolve the ambiguity.

Response 4: We thank the reviewer for identifying this ambiguity. The categories are mutually exclusive and hierarchically ordered: High readiness requires external validation plus at least one additional criterion (sample >1,000, prospective data collection, or real-world evaluation), whereas Moderate readiness requires at least one of external validation, adequate sample size, or real-world evaluation without the additional threshold. An evaluation with external validation alone, but no large sample, no prospective design, and no real-world testing, is therefore classified as Moderate. A clarifying sentence and worked example have been added to Section 2 to make this decision rule explicit.

Comments 5: Inter-rater reliability not reported. Two reviewers independently conducted screening and data charting, with disagreements "resolved by discussion." No agreement statistic (e.g., Cohen's kappa) is reported for either screening decisions or the more subjective readiness-indicator classifications. Given that several indicators (e.g., "real-world evaluation," "prospective design") require judgment calls, reporting inter-rater agreement would strengthen confidence in the appraisal.

Response 5: We thank the reviewer for this observation. No inter-rater agreement statistic was calculated during the screening or data charting process, and the individual pre-reconciliation forms are no longer available, precluding retrospective calculation. We acknowledge this as a limitation. While formal reporting of Cohen's kappa is not mandated by scoping review methodology, we recognise that the absence of a quantified agreement statistic reduces transparency, particularly for the more judgment-dependent readiness indicators such as "real-world evaluation" and "prospective data collection." This limitation has been added explicitly to Section 4.4.

Comments 6: Table 3 (readiness appraisal) and the study characteristics table have been included in the revised manuscript as Supplementary Table S2 (Clinical Readiness Appraisal) and Supplementary Table S1 (Study Characteristics), respectively. All in-text references have been updated accordingly. These tables were absent from the version submitted for initial review.

Response 6: Table 3 (readiness appraisal) and the study characteristics table have been included in the revised manuscript as Supplementary Table S2 (Clinical Readiness Appraisal) and Supplementary Table S1 (Study Characteristics), respectively. All in-text references have been updated accordingly. These tables were absent from the version submitted for initial review.

Minor comments:

Citation range error in study count. Line 303–304 lists included studies as "[16–19,19–24,24–26,26–47]," with overlapping boundary numbers (19, 24, 26 each appear twice). This is very likely a reference-formatting artifact rather than an intentional list and should be corrected to a clean, non-overlapping citation range.

Section 4.2 heading contains a stray encoding character ("Barriers to Clinical Adoptionâ").

Consider adding a brief sentence on publication bias risk, even though formal risk-of-bias assessment is appropriately out of scope for a scoping review.

The abstract and Results section report identical readiness percentages (26/63/11%) — good internal consistency, no action needed, noted as a strength.

Response to minor comments: We thank the reviewer for these observations. Regarding the citation range error at Line 303–304, the overlapping boundary numbers were a reference-formatting artifact; the citation has been corrected to a clean, non-overlapping range [16–47] in the revised manuscript, now Line 234. The malformed encoding character in the Section 4.2 heading ("Adoptionâ") has been removed; the heading now reads "Methodological Limitations and Barriers to Clinical Adoption." A sentence acknowledging publication bias risk has been added to Section 4.4. The internal consistency of readiness percentages across the abstract and Results section is noted with appreciation.

Author Response File: Author Response.docx

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The revised manuscript has been substantially improved, and the authors have addressed most of the concerns raised in the previous review. In particular, the rationale and limitations of the clinical-readiness framework are now described more clearly, the pragmatic nature of the sample-size thresholds is appropriately acknowledged, the distinction between prospective data collection and prospective model validation has been clarified, the definition of external validation has been strengthened, and the limited evidence base for anxiety disorders is now appropriately reflected in the interpretation of the findings.

Nevertheless, one important methodological issue remains insufficiently resolved, together with several internal inconsistencies that should be corrected before the manuscript can be considered for acceptance.

Subject-level separation and potential speaker-dependent data leakage

Section 3.7 states that five evaluations used “mixed approaches that combined segment-level training with subject-level majority voting for the final prediction” and that these evaluations were retained because subject-level separation was applied at the point of final prediction.

This clarification is not sufficient to demonstrate that speaker-dependent data leakage was avoided. Subject-level majority voting at the final prediction stage is not equivalent to subject-independent partitioning during model development. If speech segments from the same participant were present in both training and evaluation partitions, aggregation of segment-level predictions into a subject-level decision would not eliminate the resulting leakage.

For each of these five evaluations, the authors should therefore verify and explicitly state whether all segments belonging to an individual participant were assigned exclusively to one training/validation/test partition before model fitting. If this condition was satisfied, the terminology in Section 3.7 should be revised to make the procedure unambiguous. If it was not satisfied, the relevant evaluations should be reconsidered against the stated eligibility criterion.

This issue is particularly important in speech-based classification because speaker-specific characteristics can be strongly represented in acoustic features and learned embeddings and may artificially increase apparent classification performance.

The numerical sequence in Section 3.1 should be checked again. The manuscript states that 230 reports were assessed for eligibility and that 196 were excluded, followed by 35 studies initially meeting the inclusion criteria. However, 230 − 196 = 34. Figure 1 appears instead to indicate 195 exclusions at the initial full-text stage, followed by one post-hoc exclusion, resulting in 34 studies in the final synthesis.

The text, Figure 1, and all associated counts should report exactly the same sequence.

The Methods state that data were charted for all included studies cited as references [16–47]. However, this citation range contains 32 references, whereas the final synthesis is reported to include 34 studies. The authors should verify whether references to two included studies are missing, whether the citation range is incorrect, or whether the reported number of included studies needs adjustment. This should also be checked against the supplementary tables.

Overall, the revised manuscript is considerably stronger than the previous version, and most of the original concerns have been addressed appropriately. Resolution of the remaining subject-level separation issue is essential because it directly affects the methodological validity of the included evaluations and potentially the resulting clinical-readiness appraisal. The remaining numerical and bibliographic inconsistencies should also be corrected throughout the manuscript and supplementary material.

Comments on the Quality of English Language

However, several methodological aspects require clarification and, in some cases, reconsideration before the conclusions regarding clinical readiness can be considered sufficiently robust.

Second Review

Subject-level separation and potential speaker-dependent data leakage

The text, Figure 1, and all associated counts should report exactly the same sequence.

Author Response

We thank the reviewer for their careful and constructive evaluation of our manuscript. Below we provide a point-by-point response to each comment raised in the review report

Comments 1: Subject-level separation and potential speaker-dependent data leakage.

Response 1: We thank the reviewer for identifying this ambiguity. In response, we re-examined the training and evaluation procedures reported in each of the five source publications underlying the "mixed" data-split category described in Section 3.7. This re-examination confirmed that in all five evaluations, all speech segments belonging to a given participant were assigned exclusively to a single training, validation, or test partition prior to model fitting. Segment-level units were used only as the granularity of model input and inference within an already subject-exclusive partition; majority voting was applied strictly as a post-hoc step to aggregate segment-level predictions into a single subject-level classification at evaluation. No participant contributed data to both the training and evaluation sets in any of these five evaluations. Speaker-dependent data leakage of the kind described by the reviewer was therefore not present, and all five evaluations satisfy inclusion criterion 7.

We have revised Section 3.7 to state this explicitly and to remove the ambiguity between partition-level separation and prediction-level aggregation. No other evaluation counts, study counts, or readiness classifications required revision as a result of this verification.

Revised Section 3.7: “Subject-level partitioning, ensuring that no participant's data appeared in more than one training, validation, or test partition, was applied in all 37 qualifying evaluations. In 32 evaluations (86%), this partitioning was also the unit of model training and inference: models were trained and evaluated directly on subject-exclusive partitions. In the remaining five evaluations (14%), speech segments, rather than whole-subject recordings, were used as the input unit for model training and inference within each subject-exclusive partition, and segment-level predictions were subsequently aggregated by majority voting into a single subject-level classification for evaluation. In these five evaluations, subject-exclusivity was enforced at the partitioning stage, prior to model fitting, and majority voting served solely as a prediction-aggregation step rather than as a substitute for partition-level separation; accordingly, no participant's data contributed to both model training and evaluation, and these evaluations satisfied inclusion criterion 7 without risk of speaker-dependent data leakage.”

Comment 2: The numerical sequence in Section 3.1 should be checked again. The manuscript states that 230 reports were assessed for eligibility and that 196 were excluded, followed by 35 studies initially meeting the inclusion criteria. However, 230 − 196 = 34. Figure 1 appears instead to indicate 195 exclusions at the initial full-text stage, followed by one post-hoc exclusion, resulting in 34 studies in the final synthesis.

The text, Figure 1, and all associated counts should report exactly the same sequence.

Response 2: We thank the reviewer for catching this discrepancy. The correct figure is 195, consistent with Figure 1: 230 reports were assessed for eligibility, 195 were excluded at full-text review (48 multimodal, 44 non-clinical/insufficiently defined population, 31 unclear evaluation separation, 30 insufficient sample size, 21 target condition mismatch, 8 no quantitative performance metrics, 6 text-only analysis, 4 no eligible ML/DL model, 3 non-original research), yielding 35 studies initially included, subsequently reduced to 34 studies (37 dataset evaluations) after the post-hoc exclusion described in Section 3.7. The figure "196" in Section 3.1 was a transcription error and has been corrected to "195". We have re-checked this sequence throughout the manuscript and confirmed that Figure 1 and all downstream counts (35 studies initially included, 38 initial dataset evaluations, 34 studies and 37 evaluations in the final synthesis) were already internally consistent; only the single value in the running text required correction.

Comment 3: The Methods state that data were charted for all included studies cited as references [16–47]. However, this citation range contains 32 references, whereas the final synthesis is reported to include 34 studies. The authors should verify whether references to two included studies are missing, whether the citation range is incorrect, or whether the reported number of included studies needs adjustment. This should also be checked against the supplementary tables.

Response 3: We thank the reviewer for identifying this discrepancy. We cross-checked the citation range against the full study characteristics table (Supplementary Table S1) and found that the gap was in fact three references, not two: of the 32 references in the original [16–47] range, one (reference 17, Zhou et al., "Gaborformer") corresponds to the study excluded post-hoc in Section 3.1 (Zhou et al., MODMA dataset) rather than to one of the 34 studies retained in the final synthesis. This left only 31 references for the 34 included studies, meaning three included studies had not been assigned a reference: Wang et al. (Biomedical Signal Processing and Control, 2026), Guo et al. (2024 IEEE International Conference on Bioinformatics and Biomedicine), and Zhang et al. (IEEE Transactions on Affective Computing, in press). We have added these as new references 48–50 and updated the citation in Section 2 ("Data Charting Process") from [16–47] to [16–50]. No other numerical results were affected, as data extraction for all three studies had already been completed and correctly reflected in the charting form and downstream synthesis; only the reference-list citation was incomplete.

Author Response File: Author Response.docx

Round 3

Reviewer 1 Report

Comments and Suggestions for Authors

The revised manuscript has been substantially improved, and the main methodological concerns raised in the previous review have been satisfactorily addressed. In particular, subject-level separation is now clearly described, the PRISMA flow has been reconciled, and the distinction between prospective data collection and prospective model validation is clearer.

Only minor consistency corrections remain: the citation range [16–50] should be adjusted following the post-hoc exclusion of one study, the contradictory statements regarding the single anxiety-focused study in Section 3.2 should be corrected, and the term “prospective evaluation” should be replaced where appropriate with “prospective data collection” for consistency.

Overall, the manuscript is now considerably stronger and suitable for publication after these minor revisions.

Comments on the Quality of English Language

However, several methodological aspects require clarification and, in some cases, reconsideration before the conclusions regarding clinical readiness can be considered sufficiently robust.

Second Review

Subject-level separation and potential speaker-dependent data leakage

The text, Figure 1, and all associated counts should report exactly the same sequence.

Author Response

We thank the reviewer for the positive assessment and for identifying these remaining points, which we have addressed as follows.

Comment: The revised manuscript has been substantially improved, and the main methodological concerns raised in the previous review have been satisfactorily addressed. In particular, subject-level separation is now clearly described, the PRISMA flow has been reconciled, and the distinction between prospective data collection and prospective model validation is clearer.

Only minor consistency corrections remain: the citation range [16–50] should be adjusted following the post-hoc exclusion of one study, the contradictory statements regarding the single anxiety-focused study in Section 3.2 should be corrected, and the term "prospective evaluation" should be replaced where appropriate with "prospective data collection" for consistency.

Overall, the manuscript is now considerably stronger and suitable for publication after these minor revisions.

Response:

Citation range: We have corrected the citation in Section 2 to read [16, 18–50], explicitly excluding reference 17, which corresponds to the study excluded post-hoc from the final synthesis (Section 3.1). This range now correctly corresponds to the 34 references for the 34 studies retained in the final synthesis.

Anxiety-focused study: We have removed the erroneous sentence in Section 3.2 (No study focused solely on anxiety without a depression component as a primary target), which directly contradicted the preceding statement that one study (TRAILS cohort, Netherlands) exclusively examined anxiety. The section is now consistent with the characterization of this study elsewhere in the manuscript (Abstract, Sections 4.1 and 4.2).

Terminology: We have replaced "prospective evaluation" with "prospective data collection" in the two instances identified, in Section 2 ("Data Items") and in Section 3.10, ensuring consistent use of this term throughout the manuscript, as distinct from "prospective model validation" as defined in the clinical readiness framework (Section 2).

Author Response File: Author Response.docx