R0:

Reviewer #1: 1. Title can mention the type of study design 2. Study setting - More granular details can be provided, context about the school health promoting programmes, physical activity related programs and routine , food practices in this area, Residential schools vs day scholar schools 3. Line 86 - Full stop is missing after 'were considered' 4. Sample size is prevalence based, can be better calculated from OpenEpi 5. Pilot testing was done - shows good methodological flow 6. Questionnaires - How each items was scores, How many total items were there, Final composite score for the PA, Internal consistency 7. Exposure misclassification Bias is possible - frequency in a week is considered but not the duration 8. What is the criteria for sedentary behaviour? 9. Statistical analysis - Reference for the Stata Corp 10. Variable selection for multivariable regression analysis for parsimonious model - either a DAG or variable selection criteria with p<0.2 11. Results are represented as sufficient PA and factors, better representation will be Insufficient PA and associated factors 12. Operational definition of education levels 13. Table 1: Column percentage is a better representation than row percentage , Hours spent watching TV and hours playing video games column 5(total) is not represented. 14. Table 2: All the variables represented are not reflected in the methodology, where it is available and what these are - again column percentage would be a better representation than row percentages 15. Line 187 - RISK FACTORS ASSOCIATED WITH SUFFICIENT PA - If sufficient PA its not RISK factors and hence can be changed to insufficient PA and risk factors 16. Limitations - can mention the exposure misclassification bias

Reviewer #2: This manuscript addresses an important and under-researched public health issue in sub-Saharan Africa: physical activity patterns among school-aged children in urban Zambia. The topic is relevant to global NCD prevention agendas. The study includes a reasonably large sample and attempts to explore multilevel determinants of physical activity. However, many associations are inconsistently interpreted. The operationalization of physical activity is unclear, and the regression model appears insufficiently specified. Significant improvements are required before the manuscript can be considered for publication.

Title: The title clearly identifies the study topic, target population and geographic setting. Comments: 1. Title is slightly long and descriptive rather than precise. The phrase “Implications for Health Interventions” is generic and somewhat overstated because the study is cross-sectional and does not evaluate interventions. 2. “Upper Primary School Children” needs contextual clarification. Outside Zambia, readers may not immediately understand the age/grade range. Abstract: The abstract is generally well structured and clearly presents the background, methods, results, and conclusion of the study. Overall, the abstract is informative but requires clearer methodological reporting, more accurate interpretation of statistical findings, and more cautious wording of conclusions Comments: 1. The methods section is unclear regarding how physical activity was measured and classified as “sufficient” or “insufficient,” particularly because the WHO recommendation of 60 minutes of daily activity does not directly match the study’s definition based on weekly frequency. 2. The use of multiple questionnaires is also mentioned without explaining how the tools were combined or validated in the local setting. 3. In the results section, some interpretations are problematic. For example, peer support is described as increasing physical activity even though the confidence interval includes 1, suggesting the association was not statistically significant. 4. Some findings reported as barriers, such as lack of playgrounds or neighbourhood safety concerns, appear to show higher activity levels in the affected groups, which creates confusion and should be clarified. 5. The conclusion appropriately highlights the low physical activity levels among children, but the wording occasionally implies causal relationships despite the cross-sectional design. Introduction The introduction provides a good overview of the importance of physical activity in childhood and appropriately links physical inactivity to the growing burden of non-communicable diseases. The authors also present global and African evidence to establish the public health relevance of the topic. However, the section is largely descriptive and would benefit from stronger critical analysis and theoretical framing. Comments: 1. The research gap is not clearly articulated, particularly regarding why data from Lusaka or Zambia are specifically needed and what unique contribution this study makes to the existing literature. 2. Some statements, such as technological advancement leading children indoors, are broad and require stronger supporting evidence. 3. The introduction could better discuss contextual issues such as urbanization, school physical education policies, transport patterns, and environmental barriers relevant to Zambia. 4. The study objective is stated, but it could be more specific regarding the personal, social, and environmental factors being investigated. Methods The methods section includes several important details regarding study design, sampling, and data collection instruments. The inclusion of both public and private schools and the relatively large sample size are strengths. However, there are major methodological concerns that need clarification. Comments: 1. The sampling procedure is confusing and inconsistently described, particularly regarding the number of schools selected and the use of purposive sampling for private schools, which introduces potential selection bias. 2. The inclusion of children aged 9–18 years within upper primary grades also raises concerns about representativeness and heterogeneity. 3. The description of physical activity measurement is unclear, especially how “sufficient physical activity” was defined and how multiple questionnaires were combined into a single outcome measure. 4. The study relies entirely on self-reported data, which may introduce recall and social desirability bias. 5. Authors do not explain whether the instruments were validated or culturally adapted for the Zambian setting. 6. The statistical analysis section also lacks important details regarding variable selection, handling of missing data, assessment of model assumptions, and whether clustering by school was accounted for in the regression analysis. Results The results section presents the findings in a structured manner and includes descriptive, bivariate, and multivariable analyses. The prevalence estimates and demographic characteristics are clearly reported. However, several findings appear contradictory or counterintuitive and are not adequately explained. The results require more careful interpretation and clearer statistical reporting. Comments: 1. Children reporting unsafe neighbourhoods or lack of playgrounds were found to have higher physical activity levels, which conflicts with the interpretation that these are barriers to activity. 2. Similarly, children with very high video game use appeared more physically active, which is unexpected and may reflect confounding or measurement issues. 3. Some statistically non-significant findings are also interpreted as meaningful associations, particularly regarding peer support. 4. The regression model is insufficiently described, and it is unclear why several significant variables from the bivariate analysis were excluded from the final model. 5. The tables are difficult to interpret due to formatting issues, inconsistent percentage presentation, and inclusion of unnecessary columns such as “AOR percentage.” Discussion The discussion appropriately emphasizes the low levels of physical activity observed in the study population and compares the findings with international literature. The public health relevance of inactivity among children is well highlighted. However, the discussion often overinterprets the findings and occasionally implies causality despite the cross-sectional design. Several unexpected or contradictory findings are either insufficiently discussed or selectively interpreted. Comments: 1. Associations related to neighbourhood safety, playground availability, and peer influence are not critically examined despite conflicting directions in the data. 2. The discussion is heavy on speculative explanations without sufficient supporting evidence. 3. Although the authors mention socioeconomic and environmental influences, the section would benefit from deeper engagement with behavioral and ecological theories of physical activity. 4. Greater attention should also be given to potential biases, residual confounding, and measurement limitations when interpreting the results. Strengths and Limitations The authors appropriately acknowledge several important limitations, including the cross-sectional design, use of self-reported physical activity measures, and limited generalizability beyond Lusaka Urban District. The large sample size and inclusion of both public and private schools are notable strengths. The limitations section is honest but could be more comprehensive regarding methodological weaknesses. Comments: 1. Oter limitations should be discussed more explicitly, particularly the non-random selection of private schools, possible clustering effects within schools, and the lack of validation of the adapted questionnaires in the local setting. 2. The statement that the study represents all 10 zones is somewhat misleading because only six zones were sampled. Conclusion The conclusion summarizes the main findings clearly and reinforces the importance of promoting physical activity among school children. The policy relevance of school-based programs, parental involvement, and improved recreational environments is appropriately highlighted. Comments: 1. Some conclusions are inconsistent with the reported findings, particularly the statement regarding low maternal education, whereas the results actually showed lower activity levels among children of more educated mothers. 2. The conclusion also occasionally implies causal relationships that cannot be established from cross-sectional data. The wording should be made more cautious and aligned more closely with the actual findings of the study. Ethics Approval and Consent There is incorrect terminology regarding assent and consent. Parents or guardians provide consent, while children provide assent.

R0:

Reviewer #1: Recommendation 1: The modeling approach is fundamentally sound and relevant to TB control (a major public health issue), but the manuscript needs to address transparency (data sources, parameter justification) and clarify some methodological assumptions (e.g. definition of Reproduction number) before it can be accepted.

Recommendation 2: The sensitivity analysis methods (Pearson, PRCC) are suitable but need more rigor in reporting (sample details, uncertainty). The data-fitting procedure requires complete description (data source, fitting algorithm, goodness-of-fit). The authors should include more quantitative statistical assessment of their model fit and uncertainty in parameter effects.

Recommendation 3: The authors should provide a Data Availability Statement with actual access information (URL, DOI, or supplementary files) for the epidemiological data and any other material used. At the end of the file, an editorial link points to the Bangladesh NTP Annual Report 2022, which presumably provided TB case counts, but this is not an open dataset citation. Without accessible data, readers cannot reproduce or verify the results.

Recommendation 4: The writing requires major language editing. Grammatical issues and awkward phrasing occur repeatedly. Several citations are incomplete (marked as “[?]”). These issues hinder readability. The manuscript would benefit from careful editing by a fluent English speaker. With editing, the intellectual content is conveyable, but in its current state the language detracts from clarity.

Reviewer #2: This manuscript presents a mathematical modeling study on tuberculosis transmission using an SEITR framework incorporating distancing and treatment control strategies. The authors apply optimal control theory, stability analysis, sensitivity analysis, and data fitting to assess the impact of interventions. The topic is relevant to public health and epidemiological modeling, and the integration of control theory with real data is a valuable contribution. Overall, the study demonstrates potential scientific merit; however, several important issues should be addressed to improve the quality, clarity, and reliability of the work.

Major Strengths

The manuscript develops a structured SEITR model that includes exposed and treated compartments, allowing for a more realistic representation of tuberculosis dynamics.

The application of Pontryagin’s Maximum Principle to determine optimal intervention strategies is appropriate and well motivated.

The use of sensitivity analysis, including Pearson correlation and PRCC, strengthens the interpretation of key parameters.

Incorporation of real tuberculosis data from Bangladesh and curve fitting enhances the practical relevance of the study.

The findings highlight the importance of combined distancing and treatment strategies, which is relevant for policy planning.

Major Concerns

Language and Presentation The manuscript contains numerous grammatical errors, awkward phrasing, and unclear sentences that affect readability. Several sections require substantial English language editing. Professional proofreading is strongly recommended to improve clarity and coherence.

Incomplete and Missing Citations Many references in the text are marked with “[?]”, indicating missing citations. These must be replaced with appropriate and verifiable references. Failure to do so weakens the scientific credibility of the manuscript.

Reference Quality and Formatting Several references appear incomplete, inconsistently formatted, or potentially inaccurate. All references should be verified and formatted according to journal guidelines. The authors should ensure that all cited sources are reliable and accessible.

Mathematical Notation and Consistency Some notations are used ambiguously, particularly the symbol λ, which represents both the force of infection and adjoint variables. This may confuse readers. The notation should be revised for clarity. In addition, some derivations in the optimal control section are not sufficiently detailed and require clearer explanation.

Data Availability and Reproducibility The Data Availability Statement is insufficient. PLOS requires full access to underlying data and, where applicable, code. The authors should provide the dataset in an accessible repository and include links. Details on parameter estimation and model fitting procedures should also be expanded.

Model Validation While curve fitting is presented, quantitative goodness-of-fit measures (e.g., RMSE, R², confidence intervals) are not provided. Including these metrics would strengthen the validation of the model.

Overstatement of Novelty The novelty section contains strong claims that are not fully supported by the analysis. The authors should moderate these statements and clearly specify how their approach differs from and extends existing studies.

Figures and Visualization Some figures lack sufficient resolution, clear legends, and readable labels. All figures should be revised to meet publication standards and to improve interpretability.

Ethical and Data Source Clarification The manuscript should clearly state whether ethical approval was required for the use of hospital data and how patient confidentiality was ensured, even if the data are aggregated.

Minor Concerns

Several typographical errors and formatting inconsistencies are present throughout the manuscript.

Some sections are repetitive, particularly in the Introduction and Discussion.

Units and parameter descriptions in the appendix should be clarified and consistently presented.

The structure of some tables can be improved for better readability.

Suggestions for Improvement

Revise the entire manuscript for language quality and clarity.

Replace all missing citations and verify references.

Improve mathematical notation and provide clearer derivations.

Expand the methodology for parameter estimation and numerical implementation.

Provide full data and code access in line with PLOS policies.

Include quantitative validation metrics.

Revise figures and tables for better presentation.

Reframe the novelty claims in a more balanced manner.

Conclusion

The manuscript addresses an important topic and combines mathematical modeling with real data and optimal control analysis. With substantial revision focusing on language quality, citation completeness, data transparency, mathematical clarity, and methodological rigor, the study has the potential to make a meaningful contribution to tuberculosis control research. At present, major revisions are necessary before the manuscript can be considered for publication.

Reviewer #3: PLOS Global Public Health (PGPH-D-26-00093) Reviewer’s Comments The authors studied ‘Dynamical Behavior Analysis of 2-control Strategies on Tuberculosis Model. The authors must be commended for carrying out this research. As the paper is, technically correct formulation of the SEITR system, Standard application of Pontryagin’s Maximum Principle, Inclusion of sensitivity analysis and data fitting and clear policy motivation (treatment and distancing synergy). However, authors need to address the following suggestions to improve the manuscript: Comment 1: Abstract Please consider/incorporate the followings points in the abstract i. aim/ objectives ii. Methods applied iii. Results/ Findings iv. Recommendations to policymakers

Comment 2: Introduction Please consider/incorporate the following points in the introduction. i. Significance of the research ii. Please clearly indicate in a summarized form your observations about the related literature reviewed as compared to your research. Comment 3: Research gap and main contribution At the ending section of the introduction: i. Authors should clearly state the research gap in the manuscript. ii. SEIR/SEITR TB models with: treatment control, distancing or awareness control, PMP-based optimal control, sensitivity analysis have been extensively studied (including several papers already cited). Authors should compare their research with the existing literature and state what exactly is new in their research (main contribution) compared to existing studies. iii. The claimed novelty which comprises “composite analytical methodology integrating control-oriented stability decomposition with normalized forward sensitivity indexing” is not clearly demonstrated mathematically. Authors should check that.

Comment 4: Stability analysis The stability analysis must be improved. Authors analyzed only DFE stability. Authors should consider Endemic equilibrium (EE) existence, Local or global stability of EE and Backward bifurcation analysis. Since TB models, normally exhibit backward bifurcation and highly relevant. Comment 5: Sensitivity analysis Authors conducted so many sensitivity plots, with little insight. Parameter ranges are not clearly justified and some interpretations are inconsistent (e.g., γ showing weak PRCC but strong analytical sensitivity). Authors should correct that. Comment 6: Grammatical Errors There are some grammatical errors in the manuscript. For instance 1. “Pontryagain’s” → Pontryagin’s 2. Repetitive phrases (“It is noted that…”, “It is observed that…”) and 3. Overly long descriptive captions instead of analytical discussion

Comment 7: Inconsistencies in Notations 1. The authors used \lambda for both force of infection and adjoint derivative, 2. Parameters appear in equations but are not always defined immediately 3. Table 1 includes parameter \eta which does not appear in the model Authors should correct that.

Comment 9: In Text-Reference A lot of in-text references are missing in the manuscript. Authors should correct that.

Comment 10: Conclusion State the limitations and future work in this section. Comment 11: Cost-effectiveness analysis Cost-effectiveness analysis can be added to the control model to improve the manuscript. Remarks: Minor Revision Required Thank you

R1: Reviewer #2: The authors have adequately addressed all comments raised in the previous round of review. The revisions have significantly improved the clarity, methodological rigor, and overall presentation of the manuscript. The study presents a well-structured and technically sound analysis of the dynamical behavior of tuberculosis transmission under two control strategies. The modeling framework is appropriate, and the assumptions are clearly stated and justified. The statistical and mathematical analyses appear to be conducted rigorously, and the results are presented in a coherent and interpretable manner. Importantly, the conclusions are well supported by the data and align with the objectives of the study. The authors have also ensured compliance with data availability requirements, which enhances transparency and reproducibility. The manuscript is clearly written in standard English, with improved organization and readability compared to the previous version. Any minor typographical or grammatical issues noted earlier have been appropriately corrected. Overall, the manuscript now meets the publication criteria of PLOS Global Public Health and is suitable for publication.

Reviewer #3: Dear Editor PLOS Global Public Health(PGPH-D-26-00093R1) Reviewer’s Comments The authors studied ‘Dynamical Behavior Analysis of 2-control Strategies on Tuberculosis Model. I have checked the revised version of the manuscript according to the comments given. The authors have revised the manuscript according to the comments. I suggest that the manuscript can be accepted for publication PLOS Global Public Health after this minor suggestion. However, authors need to address the suggestion below to improve the manuscript: Comment on main Contribution The main contributions must not be stated as questions. Authors should correct that. Authors should be: 1. Specific: Focus on what is new (novel theory), the method, or data. 2. Employ Active Verbs: Begin them with phrases such as "We propose," "We discover," "We develop," or "We demonstrate" etc 3. The introduction should state the questions you asked, while the contribution section (or conclusion) should state the answers you found.

Remarks: Accept Thank you

Reviewer #4: Interesting study, here are my recommendations to improve the manuscript:

• Authors need to conform to international guidelines of scientific writing. Sentences like "doctors typically diagnose..." can be better written with "healthcare professionals diagnose..."
• The introduction section has information about the basics of tuberculosis and models design that are not necessarily important to the study. Can revise and shorten. See comment above too.
• In fact, it would be beneficial if you provide details about the current TB control strategy in Bangladesh and some background epidemiologic data about TB in Bangladesh (the country of interest) the introduction.
• tuberculin skin test is use to diagnose TB "infection"- clarify this to readers
• I assume that the first control strategy "treatment" involves treatment of active TB disease, not latent infection.
• Not sure if authors accounted for failure of TB treatment in the model?
• What is the prevalence of MDR-TB in Bangladesh and was this accounted for in the transmission model and cost-effectiveness model?

R0:

Reviewer #1: This study is very interesting, and there are still few publications that link medicines quality with treatment outcomes. However, there are some comments to improve the information and discussion in the paper.

The comments are as follows: * Line 33: of antimicrobials in low- and middle-income countries SF. What does countries SF mean?

• Line 91 Graph: we reanalyzed data from seven clinical trials of ofloxacin as a treatment for typhoid: Is this clinical trial data from the same country as the population/API distribution included in the model? It's described as being from Vietnam, but one API distribution is from Bangladesh.

• Line 129: probability to investigate....... There is no dot after probability.

• How did you measured or calculated for treatment outcomes from Bangladesh in the model? It's known that its API is substandard (less than 60%). LINE 199, while the clinical trial used for modeling is from Vietnam.

• Line 246: When %API followed the ciprofloxacin distribution (mean <100% %; Fig 3B) Why does Fig 3B use SF Cipro survey distribution data as the API estimate when it actually uses clinical trial data from OFLO? -> This is discussed in the limitations section.

• Line277- 278: insufficient doses does not mean that the medicines is substandard or falsified. How to explain the correlation with research titles related to the impact of substandard or counterfeit drugs?

• Line 297: The potential risks of SF fluoroquinolones are also likely to have increased over time as the fluoroquinolone MIC of S. Typhi increases. Why does the potential of fluoroquinolones to act as SF increase as the fluoroquinolone MIC of S. Typhi increases? Can you explain this further?

• Line 337 Our framework for quantifying the impact of SF antimicrobials demonstrates that the population-level impacts of SF antimicrobials on typhoid outcomes may be heightened when the MIC of S. Typhi is high and the SF antimicrobials have low %API.

So, the thought process is this: SF medicine for antibiotics is assessed based on the %API results. Disease severity is assessed by the MIC. The assumption is that when the %API is outside the normal range, it is insufficient to kill the bacteria, thus prolonging the patient's symptoms. For typhoid, there are two drugs: Cipro and Oflo. The SF survey results only show one study for Oflo, while there are seven studies for Cipro. Clinical trials were conducted only for Oflo, with seven studies.

Question: • Why is the SF Cipro survey discussed if it only uses clinical trial data for OFLO? -> This is discussed in the limitations section. • Is there any data on the relationship between %API and outcome, or the relationship between %API and the effect on MIC? If not, how is the impact of %API on MIC and clinical trial outcome calculated? Is it by estimating the %API to be a lower or higher dose? • The distribution of SF Meds Survey results is used to estimate the relative risk of outcome according to Step 3 in Figure 1. Estimate the population-level relative risk of outcome due to medicines with incorrect %API, but is the probability (in addition to the distribution range) of the SF drug %API based on that distribution considered in the estimate/weighting when calculating the relative risk?

• Finding step 3: we estimated a 4.1h (90% CrI: 0.75–8.7) reduction in fever clearance time for non-susceptible infections with an MIC of 1 mg/L (line 243) -> This is only for the target dose of 52 mg/kg

• Finding step 3: we estimated an 11h (90% CrI: 1.9–25) increase in fever clearance time for an MIC of 1 mg/L (line 246) -> This is only for the target dose of 52 mg/kg ​

Reviewer #2: 1. Analysis assumes that all antimicrobials administered in the clinical trials contained 100% API. Given that this assumption underpins the entire modeling framework, how do you justify its validity, and can you provide quantitative sensitivity analyses to demonstrate how violations of this assumption would affect your conclusions? 2. The clinical data are restricted to Vietnam (1992–2001). How can the findings be considered applicable to current global health contexts, particularly in sub-Saharan Africa, where antimicrobial resistance patterns and treatment practices differ substantially? 3. The medicine quality dataset appears sparse, heterogeneous, and geographically uneven. How do you address potential selection bias and lack of representativeness, and what is the impact of these limitations on the robustness of your estimates? 4. Given that ciprofloxacin data are used as a proxy for ofloxacin due to limited availability, how do you justify this substitution pharmacologically and epidemiologically, and have you assessed the uncertainty introduced by this assumption? 5. The manuscript lacks sufficient detail on model diagnostics (e.g., convergence metrics, posterior predictive checks). Can you provide comprehensive diagnostic results to demonstrate that the Bayesian models are well-calibrated and robust? 6. Approximately 5.9% of observations were excluded due to missing MIC values. How might this exclusion bias your findings, and have you explored imputation methods or sensitivity analyses to assess the impact? 7. The reconstruction of the administered dose based on tablet rounding assumptions introduces potential measurement error. How have you quantified and accounted for this uncertainty in your models? 8. Some results rely on extrapolation beyond observed dose ranges. How do you ensure that these extrapolations are methodologically valid and not driving key conclusions, particularly in low-dose scenarios? 9. The underlying individual-level clinical data are not fully publicly available, which may not comply with PLOS data-sharing requirements. How do you plan to ensure full reproducibility of results, and can the data be deposited in a controlled-access repository? 10. The reported effects on fever clearance time are relatively modest in absolute terms. Could you better justify the clinical and public health significance of these findings and clarify how they meaningfully inform policy or intervention strategies?

R0:

Reviewer #1: The manuscript is well written and presents strong evidence for risk-based RACD. Although the study uses data from 2017–2018, its findings remain highly relevant given the persistent challenges of eliminating malaria among migrant and mobile populations. The results are particularly applicable to malaria elimination settings where transmission continues to occur outside the household. The study offers strong operational evidence in support of risk-based surveillance approach and carries important implications for national malaria programs in Southeast Asia and elsewhere.

Reviewer #2: This is a carefully designed and well-implemented study aiming to test which varieties of reactive case detection are most effective in an area with low incidence of malaria, including the zoonotic parasite, Plasmodium knowlesi. The study was done in a difficult environment; the authors are to be congratulated for managing to execute it. The study was done from March 2017 to September 2018 in two districts of Aceh Province in Indonesia, both of which recently achieved elimination of transmission of the four human parasites, Aceh Besar was certified in 2022 while Aceh Jaya was certified in 2025. However, neither district has (unsurprisingly) eliminated P. knowlesi. Of 32 index cases followed up, 21 were P. knowlesi while the remainder were P. vivax. There were 8 LAMP-positive specimens detected via RACD (of which 7 were detected with risk-based methods); four of the LAMP positive specimens were confirmed at P. vivax by PCR. The four unconfirmed LAMP positive specimens were pan positive but presumably negative for P. falciparum, but results of the P.f. LAMP testing are not reported. Kindly see appended document for suggested statistical test for association. What do the authors make of this result? It would seem that vivax is more likely to be detected than knowlesi via RACD. Why might this be so? Sampling error? (yes sample size is small but still P = 0.023). Or is something biological going on? A fair amount of the discussion is framed around P. knowlesi and how this method might be useful for control of this species, but is this really supported by the data? It would be good if the authors would address this issue head on rather than simply lump the two species together. They might consider the possibility that clusters of P. vivax persist due to relapse, a common phenomenon in Indonesia due to poor PQ compliance. It is a puzzle, but things not well understood are best made explicit. Some minor suggestions: Lines 172-177 suggest moving this paragraph on HH RACD to before the paragraph describing the two types of risk based RACD, noting that HH RACD is MOH policy and that the risk based RACD is supplemental. Flow is better this way, I think. Line 195-6. Was the expert microscopist in the Banda Aceh hospital able to accurately diagnose P. knowlesi as per later PCR results? This would be of interest to readers. Line 181: “Bahasa” is colloquial, even in Indonesian. Better to say “Indonesian and Acehnese language” here. Line 243: in the heading for the Table, kindly define PR, VB, and HH. Some readers will look directly at tables and figures so may miss definitions in the text. For Table 1, it would be useful to specify the species of the LAMP positive and PCR positive plasmodia. The text specifies that all were vivax, but the table should be a useful summary of results.

R0:

Reviewer #1: Manuscript Number: PGPH-D-25-02685 Review Report Male Allyship Overall summary of the review Strength This manuscript addresses the important topic of male allyship in advancing women’s leadership in global health academia, using a well-structured qualitative approach and presenting findings across individual, institutional, and societal levels. Strengths include clear objectives, rigorous methods, and practical insights for policy and leadership. Areas that need improvement include: • Clarify the study type in the title and make it action-oriented. • Expand geographic representation beyond the U.S. and Canada. • Provide context for participant quotes. • Report data saturation and response rates. • Improve readability by breaking up long sentences and structuring results around clear subthemes. • acknowledge limitation for geographic representation beyond the U.S. and Canada Point by point feedback Title: - Male Allyship to Advance Women's Global Health Leadership in the Academy Strength • It addresses a timely and high-Impact Topic: The study area is forgotten by global community especially in academia on the importance of gender equity and leadership. • The title accurately reflects the manuscript’s core theme male allyship in academic global health leadership. • Timely and High-Impact Topic: The study addresses a significant gap in global health leadership literature—moving beyond simply identifying barriers to focusing on actionable solutions (allyship and sponsorship). This shift in focus is highly valuable for policymakers and institutional leaders Weakness • The short and long title of the manuscript is the same; no difference • The title talks about two things one “Global Health Leadership” and second “the academic institution in North America”. the focus of study population is not clear • The kind of the study type is no clearly indicated in the title. • The phrase “in the Academy” could be slightly ambiguous to international audiences—consider specifying “in academic global health institutions.” Suggested Revision • It is better if the title is an action oriented Like “Exploring Male Allyship to Advance Women’s Leadership in Global Health Academia: A Qualitative Study” or Male Allyship to Advance Women’s Leadership in Global Health Academia: A Qualitative Study Abstract Strengths: Introduction • Well-structured abstract with clear objectives, methods, and findings. • Strong justification for the study, citing global gender disproportionate disparities and responsibilities gaps in global health leadership. • Appropriate Methodology: It used a qualitative, semi structured interview approach to explore the perception, experiences and perceptions of high level leaders. Clear thematic analysis • It use clear research question on the experience of global leaders • Findings: Clearly structured around three levels—individual male ally, institutional, and societal level which offers a useful conceptual framework to shift cultural norms on gender roles for practical implications Area of improvement: • Introduction looks like an advocacy; no clearer separation between background and rationale. • • Participants were drawn only from the U.S. and Canada, which limits the geographic coverage of the study. In addition, selecting participants exclusively from the WomenLift Health network may reduce the diversity of perspectives and potentially affect the credibility of the findings. • Conceptual clarity: The term male allyship could be briefly defined in one sentence for clarity. • The conclusion partially repeats ideas from the introduction it looks like the summary of the introduction and better if based on the findings and highlighting the practical or policy relevance to enhance the impact Main Manuscript • The study team approached participants via email and invited them to participate and conduct the interview via zoom; so why the study participants restricted to two high-income countries? Result • Line 178-183: The results section reports the number of participants but does not indicate whether data saturation was achieved. In qualitative research, explaining when and how saturation was reached strengthens the credibility and adequacy of the sample size. • Reporting the response rate as a percentage would help readers interpret the level of participation more easily. • Line 185-191: The paragraph communicates the general findings, better if key themes are mentioned to give readers a concrete examples • Line 202: The quote is powerful, but providing brief context about the respondent role, experience, or institution better if included. • Line Motivation and incentives it is more plausible to read if concrete example of participant quotes are included • Line 252 to 278: the section contains valuable insights, but some sentences are long and dense. Breaking them into shorter sentences will improve readability. Consider structuring the section around clear subthemes: like awareness, role modeling etc., • Line 332-341 quote -P7, F, 40-44 is clear and conventional; however it’s a bit long and better if lightly edit for readability while retaining authenticity Discussion Strength • It is strong in structure, logic, and scholarly tone. It clearly links findings to prior research and offers practical and theoretical insights • Line 633 Toking et al reference number (54). Line 638 Sinha et al (59) need consistency Limitation Strength: Clearly states the population studied & acknowledges selection of diverse perspectives Area of Improvement: Findings may not generalize to early-career leaders, non-academic settings, or global contexts.

Reviewer #2: This paper examines an important topic: male allyship in global health. A key strength of the paper is its focus on solutions as reported by participants. This helps move the focus away from challenges women in global health face, to exploring actual solutions to the problem. The paper presents many examples of what male allyship looks like, many of these being very actionable. I commend the authors for this. That said, there are several areas that need attention.

1. The findings could be synthesized and made more concise. The authors present A LOT of information, which is overwhelming. There are many ways to address this. First, the authors can use much shorter direct excerpts from participants. Second, the authors could move participant excerpts into a table. Third, the authors could synthesize their findings much more which would reduce the number of themes/issues and tell the story a bit differently. The paper would read better if they structured the results based on the subheadings used in Fig 1. It would help tell a more succinct story.

2. It is not clear what Fig 2 is showing.

3. I wonder if to would help to present the findings by gender, that is, by showing similarities and differences between female and male participants.

4. Could the authors present more details on the study participants. Sone of the content in the excerpts suggests that they were from academic institutions. A demographics table would help, in terms of academic vs non-academic institutions etc. The authors should also provide more details on the sampling and recruitment method: how exactly did they find these 21 participants?

5. The Discussion could be strengthened by a more critical analysis of the concept of male allyship. The authors should consider what their findings/study implications are for the potential and pitfalls of the concept.

R0:

Reviewer #1: Title: Probabilistic Forecasting of Monthly Dengue Cases Using Epidemiological and Climate Signals: A BiLSTM–Naive Bayes Model Versus Mechanistic and Count-Model Baselines. Manuscript Number: PGPH-D-25-03170

This manuscript presents a rigorous comparative study of probabilistic forecasting models for monthly dengue incidence in Freetown, Sierra Leone, covering the period 2015–2025. It evaluates four major model classes—NB-GLM, INGARCH-NB, Renewal-NB, and BiLSTM-NB—under a leakage-safe rolling-origin evaluation. The article demonstrates strong methodological maturity, careful control of data leakage, and thorough probabilistic evaluation using proper scoring rules, interval coverage, sharpness metrics, PIT diagnostics, and Diebold–Mariano tests. The manuscript is generally well-written, technically sound, and addresses an important operational public health problem. It positions itself as one of the few works offering aligned comparisons of mechanistic, statistical, and deep-learning models under realistic constraints for West African dengue surveillance. This article presents a methodologically rigorous comparison of four probabilistic forecasting approaches—NB-GLM, INGARCH-NB, Renewal-NB, and BiLSTM-NB—applied to monthly dengue case data from Freetown, Sierra Leone (2015–2025). The study addresses an important gap by evaluating mechanistic, statistical, and deep-learning models under aligned, leakage-safe conditions. While the work is comprehensive and technically strong, several critical issues affect its accessibility, interpretability, and broader applicability.

Strengths The study excels in methodological rigor. Its strict leakage safeguards, careful feature-timing rules, and use of expanding-window rolling-origin evaluation significantly strengthen reliability. The inclusion of proper scoring rules, interval coverage, sharpness metrics, PIT histograms, and Diebold–Mariano tests provides a complete probabilistic evaluation rarely seen in dengue forecasting studies. The horizon-specific findings—INGARCH-NB outperforming at 1–2 months and BiLSTM-NB excelling at 3 months—are well supported by aligned comparisons and statistical significance tests. The transparency of data, code, and alignment artefacts enhances reproducibility and credibility. Additionally, the manuscript offers practical guidance for operational forecasting, including a realistic “light climate” input strategy suitable for resource-limited settings.

Limitations Despite its strengths, the manuscript is heavily technical, with extensive mathematical exposition in the main text. This may limit accessibility for public-health practitioners who are likely part of the target audience. The mechanistic renewal model is presented as a baseline but is arguably underspecified; the use of a short, fixed 3-month kernel may not realistically capture dengue’s generation interval dynamics, likely contributing to its poor performance. This limits the interpretive value of the mechanistic comparison. This limitation should be addressed. The study’s climate treatment, while intentionally conservative, may underexploit important environmental drivers. Although justified operationally, this constraint restricts exploration of potentially meaningful lag structures or seasonal climate anomalies. The analysis is limited to a single city and monthly data frequency, raising questions about generalizability across geographies with different climate patterns and dengue transmission dynamics. Moreover, the monthly temporal resolution may obscure rapid outbreak shifts, possibly disadvantaging mechanistic and hybrid models that rely on finer-grained dynamics. This should be addressed. The manuscript makes a valuable and original contribution to dengue forecasting, offering robust methodological innovations and practical insights for real-time surveillance systems. However, improved clarity, stronger justification for mechanistic assumptions, and expanded discussion of generalizability would enhance its usefulness and scholarly impact. With revisions to improve accessibility and contextual depth, the study is well positioned for publication and for informing operational forecasting practice in similar settings.

Reviewer #2: 1. What is PIT in the abstract stand for? The authors should avoid using abbreviations in the abstract. 2. The authors should providing some additional analysis, such as experimenting with alternative or longer serial-interval kernels, or simple sensitivity checks (e.g., different window lengths, or, if possible, finer temporal resolution). 3. Please, justifies the small climate feature set, mentioning any exploratory work with larger sets. 4. The authors should add a clearly labelled missing-data handling subsection that specifies: The imputation method, the number of imputed months, and how they were used in training/evaluation, plus any sensitivity. 5. While the architecture, optimization, and calibration steps are described, the process for choosing hyperparameters is not fully audit-ready. 6. I recommend that the authors conduct an additional experiment to demonstrate the generalizability of the proposed model.

R0:

Reviewer #1: Peer Reviewer’s report for the submission “Reaching the 100 by 2027 target for universal access to rapid diagnostic tests 2 for tuberculosis in Africa: in-sight but out of reach”

Recommendation: Minor Revisions General Comment: This paper addresses a pertinent global health subject, a WHO priority research gap. The methods are sound and innovative. However, the authors need to improve on the clarity of the paper.

Abstract: -The authors did a fantastic work summarizing the study with this abstract -Kindly break the abstract into the standard sections: background, methods, results, conclusion -Please clearly designate and state clearly the name of the study design used in this study. Are we an ecological study with mixed methods or what?

Background -Great job introducing the research gap and pertinence of the research -A brief perspective on funding gaps for diagnostics might strengthen this section -Do not overestimate the knowledge of potential readers on the subject, briefly describe what WRDs are and state list them. Why are they so important?

Methods -This section of the work is a bit to brief and doesn’t present the work in a way that can be easily reproducible by readers. Use standard sub-headers such as study design, study population, study period, data collection and data analysis for clarity. -Again, I ask what is the study design of this study? -WRD were recommended 10 years ago, what is the rationale behind the period 2021-2023? I think the key landmarks for this are 2015 for End-TB, 2018 for the first UNHLM and 2023 for the second UNHLM. -Line 98-101: How were these cutoffs decided? -Study area is completely absent. It is important to shade more light on the 24 countries. Who are they, what is the burden of TB there, any peculiarities? -Benchmarks which needed a secondary calculation following extraction need to be presented clearly, showing the variables used as denominator and numerator.

Results -Kindly provide the exact number of cases tested for the different years, prior to providing proportions. A standalone table could resolve this. -Line 151-161, I find it hard to see trends with just 3 years data points. Probably need to increase the years if you want to discuss trends -Did the Table 2 strategies come from the TB staff or the authors? It appears it came from the authors, in which case I don’t agree with their existence in the results. At best in recommendations

Discussions -The authors did a superb job discussing the available findings of the study -Being a study with policy implications, kindly include a sub-header for Policy implications of the findings and state them clearly -Include sub-headers for strengths and limitations and outline them clearly

Reviewer #2: Review of Title: Reaching the 100 by 2027 target for universal access to rapid diagnostic tests for tuberculosis in Africa: in-sight but out of reach

Summary of research and overall impression This is a well-written and researched article reporting on the availability and use of WHO-recommended rapid diagnostics for TB in African countries where there is significant burden. The authors use routinely reported data to assess access to WRDs, and a small survey of programme staff from a subset of countries to identify barriers and facilitators to the inclusion of WRDs in diagnostic algorithms. The paper makes an important contribution to the TB literature by mapping the gaps in terms of access to and usage of WRDs, which is needed to strengthen TB control efforts. There are minor comments for the authors to address to strengthen the paper.

Methods 1. Include brief details on how/why the 24 countries included in the review were selected. 2. More details are needed to describe the process for the country stakeholder survey. For example:

• Specify what the questionnaire consisted of, i.e., closed and open-ended questions? What topic areas/sections were included/asked about? How/by whom was the questionnaire designed/developed, using/adapting an existing framework/questionnaire?
• How were the questionnaires sent out? Were specific people targeted? How many were sent out? What was the timeframe?

• Provide details of how/why the 6 countries were selected – e.g., 1-2 from each region? Who inputted on these decisions? The authors mention later that these were also selected based on WRD access, which should be mentioned here in methods.

• It is unclear under ‘statistical analysis’ if this refers to analysis of all data, or just the data review. Suggest revising to clarify analysis for data review, and analysis for the stakeholder survey. Two things to consider: 1) Provide details on the data extracted and the analysis conducted. 2) It is unclear what is meant here: “The first author used topic guides that reflected content areas such as barriers and contextual factors influencing WRD use and the themes that emerged during the review of the survey responses to manually organise the data into thematic codes.” Is this referring to the stakeholder surveys? Suggest revising for clarity on the analysis process. Were any frameworks used in analysis to categorise barriers into categories and develop mitigation strategies? This process needs to be detailed in the methods to lead into the results.

• Please clarify/confirm the ethics of surveying country stakeholders without a consent process, even if participants (country stakeholders) are not identifiable.

Results Provide details of how many survey responses were received. Is it only 6 from 6 countries (as in lines 182-186)? How were respondents distributed across the 6 countries? Could they speak to the different country contexts? Later in the text there is mention of 16, suggest clarifying this in the results clearly.

In lines 163 onwards, when referring to the analysed gaps in the TB diagnostic cascade, please clarify in the text throughout what is meant with ‘countries reported’ – is this a comparison of what is found in the data review with what is reported by country stakeholders?

As mentioned earlier, the process for categorising the barriers and developing mitigation strategies must be introduced in the methods. “We then distilled the barriers into five categories and developed mitigation strategies 260 (Table 3) to improve the use of WRDs across all 24 LabCoP countries.” Did you use a framework for this to guide at different health system level? Suggest revising the three theme headings as they read more like recommendations statements now than findings, i.e., optimise…, strengthen…. To read as findings of the barriers and facilitators, they should be descriptive of what was found. - Theme 1: ‘optimise WRD capacity’ – clarify what ‘capacity’ is referring to. Under this heading there are multiple aspects included, i.e., policies, guidelines, as well as examples of how access to WRD has been improved, so examples of optimising WRD capacity? - Theme 2: seems to speak to 2 things: sample transportation and access to testing via active case finding. Clarify if/how these are linked. - Theme 3 – insufficient financing, staffing, and infrastructure to implement WRD.

Discussion Under strengths and limitations, the authors mention that ‘a planned report from our annual meeting will capture responses from all 24 countries’ – lines 362-363. This statement has limited relevance to the article, unless already publicly available and can be referenced. Suggest to delete/remove.

The authors also mention ‘only reached out to the selected countries’ – line 361. Suggest to phrase this more positively, i.e., we purposively selected a subset of 6 countries from the 24 within the LabCoP network, which may limit…’

R1:

Reviewer #2: Well done on an exceptionally well-written and important paper. I do have one pending comment about the number of survey responses, which I do not see reported in the results. It is important to include the number of respondents and how they were distributed across the 6 countries included in the survey.

R0:

Reviewer #1: General Comment

This manuscript examines the relationships between food security, food insecurity, diet quality, and their correlates among mother–child dyads in rural north-eastern Ghana—an area where additional evidence is needed. Overall, the manuscript is reasonably well written; however, it would benefit from a clearer conceptualization of the study aim and from reanalysis of the data to improve clarity and strengthen interpretation of the findings.

Specific Comments Introduction • The introduction is overly burdened with background information on global and national food security and diet quality issues. There is no systematic synthesis of literature directly related to the study objectives, representing a critical gap. This may have contributed to a weak problem statement and unclear research objectives. • The authors state that “despite the region’s high nutrition vulnerability, few studies have comprehensively examined the complex relationships between food insecurity, diet quality, and maternal–child nutrition outcomes in the North-East Region.” However, this alone is not a sufficiently strong rationale, as evidence does not need to be generated separately for every geographic setting. The authors should clarify why existing literature cannot be directly applied to rural north-eastern Ghana, highlighting specific contextual factors (e.g., agro-ecological conditions, food systems, cultural dietary practices, livelihood patterns, or health and nutrition service delivery contexts) that limit the transferability of existing evidence. • The stated objective—“This study addresses these critical gaps by providing the first integrated analysis of food insecurity, diet quality, and their correlates among mother–child dyads in rural North-East Ghana”—lacks clarity and specificity. It is unclear whether the study aims to examine the effect of food insecurity on diet quality, the bidirectional relationship, or their independent associations with maternal and child nutrition outcomes. The term “integrated analysis” is also not well defined. Objectives should be explicitly stated, with clear exposures, outcomes, and analytical focus. Methods and Materials • This section requires substantial revision. • Sample Size and Recruitment: The sample size calculation is inadequate, as it appears to have been designed only to estimate the correlation between food insecurity and diet quality. This is insufficient for additional analyses, such as estimating prevalence, assessing diet quality indicators, or conducting subgroup/multivariable analyses. Extending recruitment post hoc to 248 households “to accommodate potential incomplete responses, missing data, and to enhance statistical power for subgroup analyses” is not scientifically robust. The authors should clearly specify the primary outcomes used for power calculation, justify effect sizes, and provide appropriate sample size calculations aligned with all planned analyses. • Exclusion of Ill Participants: Households with participants experiencing fever or diarrhoea were excluded to avoid bias due to temporary changes in appetite or feeding practices. However, this exclusion may introduce selection bias, especially in contexts where infectious morbidity is common and linked to food insecurity. This could underestimate the prevalence and severity of food insecurity and poor diet quality. The authors should justify why analytical adjustment for recent illness was not considered and discuss the implications as a study limitation. Exclusions due to refusal of consent are acceptable. Results and Discussion • I strongly recommend that the results—particularly analyses related to the main study aim—be reanalyzed using appropriate multivariable methods rather than simple correlation analysis. Correlation analyses are limited to bivariate associations and do not account for confounders that may influence both food insecurity and diet quality. Multivariable regression would allow a more robust and interpretable assessment of these relationships. • The results include a subsection on “Food Insecurity and Nutritional Outcomes,” which does not align clearly with the main study aim. Any findings here are unlikely to differ meaningfully from existing literature unless analyzed with appropriate multivariable methods. Mann–Whitney U is insufficient for studying correlates; multivariable regression is the correct approach. Final Remarks • In general, the manuscript requires reanalyzing the data and refining analyses to ensure alignment with study objectives and to produce robust, interpretable findings. • I suggest using standard conceptual frameworks to guide the risk factor analysis, carefully selecting exposure and outcome variables, and applying the correct analytical methods. • I will review the discussion section after the authors have conducted a focused, revised analysis to determine whether this leads to changes in results or interpretation.

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Editor Comments: My editorial assessment identifies substantial weaknesses in the manuscript that extend beyond minor revision. The manuscript contains multiple grammatical and language errors, and several sections are poorly articulated, which significantly limits clarity, coherence, and scientific rigor. In addition, it is unclear whether ethical considerations were addressed regarding the photographs taken in public places, and the duration of data collection has not been indicated, making it difficult to assess the adequacy of the observation period. In its current form, the manuscript would require major revision before it can be reconsidered for publication. The specific concerns are outlined below. 1. Language and Presentation There are numerous grammatical and typographical errors throughout the manuscript. For example, on Line 32, “ashtrays” is misspelled as “astryas.” In the Introduction (Line 57), phrases such as “Among of the 8 million global death from tobacco use…” reflect major grammatical inaccuracies. Comprehensive language editing is required. Additionally, the Introduction is underdevelopveloped and too brief to adequately situate the study within the existing literature or clearly articulate the study rationale. 2. Lack of Strategic Analytical Focus The manuscript does not clearly articulate a strategic analytical gap or sufficiently justify how the study advances existing knowledge. The rationale for the analysis is underdeveloped, and the findings are not convincingly linked to broader conceptual or policy-relevant implications. 3. Insufficient Characterization of Public Places The categorization of public places lacks clarity and specificity. The authors are requested to: • Clearly define and characterize each type of public place, including size, function, and typical foot traffic; and • Provide concrete examples (e.g., specify the six government offices included). Such details are necessary for meaningful interpretation, reproducibility, and external validity. 4. Missing Analytical Plan and Sample Size Justification The Methods section does not describe a clear analytical plan for identifying associated factors, nor does it justify the sample size used. Furthermore, the inclusion of the general population without a defined sampling strategy raises concerns regarding representativeness and analytical coherence. In summary, the manuscript currently contains significant conceptual, methodological, and presentation weaknesses. A major revision is therefore required for further consideration.

Reviewer #1: Dear Author The reviewers appreciate the relevance of the topic and the effort invested in conducting field observations in a rural Nepali setting. However, several substantive issues need to be addressed to strengthen the manuscript’s methodological rigour, analytical clarity, and contextual interpretation. I strongly encourage the author to improve the manuscript and submit in local journals. The findings could help the local enforcement and intervention efforts.

1. Lack of Strategic Analytical Focus The manuscript does not clearly articulate a strategic analytical gap or justify how the study advances existing knowledge. The rationale for the analysis remains underdeveloped, and the findings do not convincingly demonstrate a broader conceptual or policy‑relevant contribution.
2. Insufficient Characterization of Public Places The categorization of public places lacks clarity and specificity. Reviewers request that the authors:
3. Clearly define and characterize each type of public place, including size, function, and typical foot traffic.
4. Provide concrete examples (e.g., specify the six government offices included). This level of detail is essential for interpreting the observed patterns and ensuring reproducibility.
5. Issues With Variable Categorization and Small Cell Sizes Several public‑place categories contain extremely small numbers of observations (e.g., groups with only two subjects). Such small cell sizes make percentage calculations statistically meaningless and may distort interpretation. Recategorization or aggregation of variables is recommended to ensure analytical validity.
6. Limitations of Short Observation Period The study draws strong conclusions from a very short observation window. Reviewers note that such limited temporal coverage may not adequately capture typical behaviors or pattern.
7. Missing Analytical Plan and Sample Size Justification The analysis section does not describe any plan to identify associated factors, nor does it justify the sample size for such analyses. Additionally, the inclusion of the general population without a clear sampling strategy raises concerns about representativeness and analytical coherence.
8. Contextual Misalignment in Interpretation The study was conducted in a small rural community of fewer than 20,000 people. Reviewers caution that:
9. Findings from this setting may not be generalizable to urban areas in Nepal.
10. Comparisons with nationwide studies or studies conducted in different contexts should be made carefully. Overstating comparability may mislead readers about the scope and applicability of the findings.

Reviewer #2: This is a commendable piece of work. Auditing compliance with existing laws in LMICs is highly important for informing policymakers and strengthening efforts to reduce tobacco consumption. The authors need minor revision in submitted manuscript for further validate the findings.

R0:

Reviewer #1: This manuscript addresses antimicrobial resistance in Ecuador through a One Health lens, focusing on governance, infrastructure, and equity. The topic is highly relevant to PLOS Global Public Health, particularly given the emphasis on health systems, intersectoral governance, and equity in low and middle income country contexts. The study makes a valuable contribution to regional and global discussions on AMR governance. Some points need to be addressed: 1. While the conclusions are generally consistent with the qualitative findings, some claims, particularly those related to macro level political shifts, austerity policies, and governance deterioration, would benefit from clearer and more explicit linkage to the empirical data presented. In several instances, the discussion moves toward a normative or interpretive tone that appears to draw as much from secondary literature as from the study’s primary data. Strengthening signposting between interview findings, document analysis, and specific conclusions would improve analytical clarity. 2. The manuscript would benefit from more explicit clarification that the study is a qualitative governance and policy analysis rather than an epidemiological assessment of antimicrobial resistance trends. Readers may otherwise expect microbiological or quantitative AMR indicators, which are outside the scope of this work but not always clearly distinguished in the framing. 3. The Data Availability Statement indicates that all relevant data are included within the manuscript and that additional information is available upon reasonable request. However, this does not fully meet PLOS data policy requirements. The primary qualitative data underlying the findings, such as anonymized interview transcripts, coded data excerpts, or NVivo codebooks, are not publicly available as supplementary files or deposited in a repository. If there are ethical or confidentiality constraints that prevent public sharing of these materials, these restrictions should be clearly specified in the Data Availability Statement. Alternatively, the authors are encouraged to share de-identified qualitative data, coding frameworks, or analytic matrices as Supporting Information to enhance transparency and reproducibility. Here minnor suggestions: a) Consider minor language and stylistic revisions throughout the manuscript to improve clarity and flow, particularly in the Introduction and Discussion sections. b) Ensure consistent terminology when referring to governance structures, committees, and surveillance systems. c) Some tables (e.g., interview results) could benefit from brief interpretive summaries to guide readers unfamiliar with the Ecuadorian institutional context. The equity analysis is a strong component of the manuscript; however, explicitly distinguishing between findings derived from interview data versus document analysis would further strengthen this section.

Reviewer #2: Overview: This study examines national approaches to addressing antimicrobial resistance (AMR) in Ecuador from a One Health (OH) perspective, with emphasis on governance, public policy, health infrastructure, and equity. The authors use a qualitative design combining document review, scientific literature analysis, and semi-structured interviews with key informants representing multiple OH sectors. The manuscript offers a useful overview of the challenges Ecuador faces in implementing an OH approach to AMR prevention. However, many of the broader claims are not sufficiently supported by the evidence currently presented. In particular, findings from the document analysis, the central component of the study, are not reported in a clear or substantive way, making it difficult to assess how the conclusions were derived. Strengthening the presentation of document-analysis results, clarifying how these findings were integrated with interview data, and improving the organization and flow of the manuscript would substantially increase its rigor and impact. With these revisions, the paper has the potential to become a valuable contribution to the literature on AMR and One Health in Ecuador. Major revisions • The Introduction would benefit from a brief description of Ecuador's National Plan for the Prevention and Control of AMR (2019-2023)-including its overarching goals, structure, key components/strategic axes, and intended governance/implementation approach. This context is necessary for readers to understand what was constrained in implementation and to interpret the claims made in the Discussion and Conclusions. • The Methods section needs substantial revision to clearly describe how the qualitative research was conducted and analyzed. I recommend aligning the reporting with SRQR (Standards for Reporting Qualitative Research) and citing: O'Brien BC, Harris IB, Beckman TJ, Reed DA, Cook DA. Standards for reporting qualitative research: a synthesis of recommendations. Academic Medicine. 2014;89(9):1245-1251. Please consider including an SRQR checklist as Supplementary Information to improve transparency and reproducibility of the qualitative analysis. • The manuscript currently provides limited explicit reporting of findings from the document analysis, despite this being a central component of the study. Please present clearer, more detailed results from the document analysis (e.g., what patterns/themes emerged, concrete examples), and explain how these findings were integrated with (or triangulated against) the semi-structured interview data. • As written, the Results and Discussion sections are difficult to follow. Consider restructuring the manuscript around the four analytical themes/framework domains used in the study: 1. Intersectoral governance analysis; 2. Situational analysis; 3. Transitions toward One Health; 4. Equity analysis using a GBA+ lens. Using these as consistent subheadings throughout would strengthen coherence and readability. • The Discussion does not yet fully unpack what the findings mean, nor does it adequately situate them in relation to experiences from other countries (Latin America, LMIC settings, and high-income settings where implementation has been more effective or similarly constrained). Additionally, the manuscript states that it proposes a "context-specific action framework," but this framework is not clearly presented or easy to locate. If this is a key contribution ("So what? What now?"), please make it explicit. • Several conclusions currently extend beyond what is clearly supported by the Results section. Please ensure the Conclusions are tightly grounded in the reported evidence (from both document analysis and interviews), or revise/soften claims where direct supporting data are not presented. Minor revisions Introduction • Line 46: Please briefly define selective pressure and explain how it contributes to the emergence and spread of antimicrobial-resistant microorganisms. • Line 59: Before discussing constraints, it would help to briefly describe the Ecuadorian National Plan for the Prevention and Control of AMR (2019–2023), for example, its overarching goals, structure, key components/strategic axes, and intended governance/implementation approach. This context will help readers understand what specific aspects were constrained. • Line 72: Grammar: “reduced” instead of “reduces.” • Lines 75–78: These statements read as interpretive claims; please clarify whether they are based on cited literature or derived from your data. If they are claims about broader context, references are needed. • Line 75: Consider starting a new paragraph around here to introduce the National Plan/Committee context more clearly before transitioning into limitations. Methods • Line 106: Please briefly define semi-structured interviews and include a reference for the approach. • Lines 106–108: The study objective is already stated earlier; consider removing repeated objective language here to streamline the Methods. • Recommend adding a clearly labeled Ethics subsection (IRB approval/waiver, consent procedures, confidentiality protections). • Lines 150–151, 157–158, 160–161: These appear related and could be consolidated into one coherent paragraph to improve flow. • Table 1: Please provide more detail on the “affiliated agencies”/ “agencies” included. For example, within the Ministry of Health, does this include INSPI or other specific bodies? Consider organizing the table using headings aligned with your interview sampling frame (e.g., human health, animal health, environment, academia, civil society) to match the manuscript text. • Line 173: Please define the acronym GBA+ at first use. The Methods section would benefit from clearer subsections. Suggested structure:1. Study design and setting; 2. Sampling and participants (sampling strategy, eligibility criteria, recruitment, number approached/interviewed; how you determined sampling adequacy/saturation); 3.Data sources and data collection document analysis: document types, inclusion criteria, extraction approach interviews: interview guide development, interviewer training/positionality if relevant, interview mode, audio recording, transcription/translation, any iterative changes to guides; 4. Data management (storage/security, de-identification/anonymization, coding workflow); 5. Data analysis (analytic approach for documents and interviews; how themes were developed; triangulation across methods; reflexivity/rigor strategies such as audit trail, double coding, member checking if used). • Consider including (as Supplementary Information) an SRQR checklist to improve transparency Results • The Results section would be clearer if organized explicitly around your four analytical themes/framework domains: 1. Intersectoral governance analysis; 2. Situational analysis; 3. Transitions toward One Health; 4. Equity analysis using a GBA+ lens. Consider using these as subheadings and presenting findings under each. • There is currently little explicit reporting of what was found from the document analysis. Please include concrete results from that component (e.g., what patterns/gaps were identified, and specific examples). • Lines 207–212: This reads like interpretation more appropriate for the Discussion (and would likely need supporting references if it’s a broader claim). Consider moving it. • Lines 223–226: These statements also appear interpretive and would fit better in the Discussion. • Line 228: “Barriers and facilitators” are introduced here but not clearly set up earlier. If identifying barriers/facilitators is a central objective, please introduce it in the Introduction/Aims and ensure consistent framing throughout. • Lines 234–241; 243–249: These sections read like discussion/interpretation rather than results. Consider revising to focus on what participants/documents explicitly reported (with evidence) and move broader implications to the Discussion. • Consider adding a small number of representative verbatim quotes from the semi-structured interviews to support each major theme. Including 1–2 quotes per theme (with anonymized participant identifiers/roles) would strengthen credibility and transparency and is standard for reporting semi-structured interview findings. If space is limited, quotes can be placed in a table or supplement.

Discussion • Consider organizing the Discussion using the same four analytical themes as the Results to improve coherence and readability. • The Discussion would benefit from deeper comparison with related work from Latin America and other LMIC settings, as well as contrasting with experiences in high-income settings where national AMR plans may have been implemented more effectively. This would strengthen interpretation and generalizability. • The Introduction indicates that a “context-specific action framework” is proposed; however, this is not easy to locate in the current manuscript. Please clearly identify where the framework is presented (potentially Lines 320–327?) and consider adding a figure/table or a clearly labeled subsection so readers can easily find and understand it. Conclusion • Overall, the conclusions are plausible, but some claims appear stronger than what is currently supported by the Results section, especially without clearly presented document-analysis findings. • For example, the statement about deterioration in governance capacities, information system interoperability, laboratory infrastructure, and budget allocations would be strengthened by explicit evidence from the document analysis and/or interviews. If budget shifts were assessed, please report what sources were used and what changes were observed; if not directly assessed, consider softening the language or clarifying that it reflects stakeholder perceptions rather than documented budgetary evidence.

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EDITOR:

The reviewers agree that your manuscript addresses an important topic. They have also raised a number of well-justified concerns and points requiring clarification. I hope that you see these as opportunities to further improve your manuscript such that it may be accepted for publication.

Review Comments to the Author

Please use the space provided to explain your answers to the questions above. You may also include additional comments for the author, including concerns about dual publication, research ethics, or publication ethics. (Please upload your review as an attachment if it exceeds 20,000 characters)

Reviewer #1: The author wrote this manuscript quite well. However, there are some suggestions for improving it better including,

Abstract: The abstract is written well. However, the results showed about self-stigma representing at 49% so this result should be suggested in conclusion as well.

Introduction: The introduction is organised and written well. However, there are some suggestions about referencing that should be revised along with Vancouver style and the journal format, such as (6)(7)(8), should be (6-8) or (Mbuthia et al., 2020) should be a number of reference. Another point, the abbreviation of drug-resistant TB (DR-TB) should be the same with DRTB in table 2 (page 10). Moreover, in terms of objective of the study, it should be written clearly. The author stated in line 98-100 (page 3), but it seems like expected outcomes rather than its objectives.

Methodology: Ethics statement: It is a clear statement, however, the date of approval should be presented as well to ensure the data were collected after approval.

Study population: The author stated that the target population comprised people with TB who were on treatment and were 15 years and above. However, the results showed that there were some participants aged under 15 years (0-14) as well. Thus, the author should revise and make it correct.

Sampling procedures: The author stated that the data were collected in 12 regions, however there were only 11 regions stated in line 139-140.

Sample size: The author showed some details of sample size calculation that met 421 persons (line 147). However, there were only 367 participants recruited to this study which is less than the appropriate sample size calculated. So, the author needs to explain more details about the sample size. It should be 421 as the result of calculation with the appropriate formula. Moreover, if there are sources of the number used to calculate, the reference needed to be stated as well.

Eligibility criteria: In terms of inclusion and exclusion criteria, the author stated that all people with TB aged 15 years and older would be recruited to the research and all people who were below the age of 15 years were excluded. This is the main point that needs to be clarified because in the results, there are some participants aged 0-14 years as stated before. Moreover, in terms of ethics, participants aged less than 18 years cannot sign the consent form by themselves, their parents should sign the consent form. So, the author needs to revise and clarify further.

Data collection tools and procedures: There is no information about the questionnaire well. The questionnaire should be clarified the details, especially the items used to categorise into "no stigma and stigma (binary). If you use only one item, it should not be appropriate to categorise. This is an important point of this study that needs to be explained. As well as, if the questionnaire was conducted by previous researchers, it should be cited correctly. Moreover, the author stated in this part that stigma was assessed using a set of standardised questions rated on a five-point Likert scale (0 = Strongly disagree to 4 = Strongly agree), while, in page 6, the author used (1 = Strongly agree to 5 = Strongly disagree) as well as the data were categorised in to 5 groups staring from 1.00 - 5.00. Please check the details again.

Data analysis: The Cronbach's alpha value needs to be presented with the exact value instead of >=0.70 that it will present the reliability of tools better. Moreover, the author stated in line 181 and table 2 "TB type" but in the conclusion, the author used "treatment type". So, this point needs to be the same. For the binary classification, the author needs to explain more details about how to categorise into 2 groups: no stigma and stigma. In terms of inferential statistics, the binary logistic regression and multiple logistic regression were not used and shown in the results. So, the author needs to revise about this point again.

Results: The sum of percentage, the details in Table 1 & 2 showed the percentage of each variable, which is good. However, the author needs to check the sum of each variable should be 100%. The author may use two decimal points for presenting the percentage. Moreover, some sub-variables which there is no data (0) does not need to present in the table. Please find the details in the attached file.

In table 2, inferential statistics, the author stated in data analysis that binary logistic regression and multiple logistic regression would be used to analyse to identify the predictors. However, in the results, there is no any results based on these statistics. So, the author needs to revise about the statistics stated in data analysis. Moreover, about chi-square, the author needs to check the assumption of chi-square because No cell should have an expected frequency < 1, and at least 80% of cells should have expected frequencies of 5 or more. So, if it does not meet the assumption, its results might be wrong.

Aged 0-14, the author stated in the methodology that the participants need to be 15 years or over. So, please check the data again.

Some words should be changed for example in line 213 from prevented to obstructed. Moreover, about abbreviation "DSTB and DRTB", for DSTB, the author did not state before so it needs to be mentioned in previous part first before using in this part. As well as, DRTB, the author used DR-TB in line 79 so it needs to be the same, with or without -.

Discussion: The author wrote this part quite well, however, the author needs to check about the number of percentage presented in this part again. Moreover, citation should be revise and rewrite following the format.

References: In terms of references, the author should check the format of Vancouver style referencing in both in-cited and references part again. As well as, the author needs to check the format along with the journal format. For example, (xx) to [xx]. Please revise and rewrite following the formats.

Reviewer #2: Please see my report. I think the manuscript transition from a dissertation to a paper is incomplete. Please review my report for details. I raise concerns regarding the sampling, statistical analysis and the conclusions made regarding the results.

Reviewer #3: This cross-sectional study tackles an important global health problem, TB-related stigma among people with TB. This study has significant merits including 367 people living with tuberculosis sampled over one year; and captures various contexts, specifically 180 health facilities across 11counties aiming for a nationally representative survey of TB-related stigma in Kenya. Two hundred and twenty-eight patients provided information regarding TB-related stigma, of whom 24 reported experiencing TB-related stigma.

Several areas remain unclear to me and require further clarification, elaboration or consideration for reformatting.

1. The referencing style used is inconsistent. e.g. introduction section lines 60-61(Mbuthia et al. 2020), whereas other areas have a different style that is numbered. Consider reformatting for consistency.

2. Previous research on TB-related stigma measurement and its implications to TB related outcomes in the Kenyan context has not been highlighted.

3. Ethics statement section could be aligned for consistent formatting with other text sections of the manuscript.

4. The sample size calculation could be further clarified for the readers to judge its robustness. a. Is there a proportion of TB-related stigma assumed from a previous study? b. What is the rationale of a 90% response rate? – Lines 147 to 150. c. What was the actual response rate?

5. From the manuscript, the sample size calculated was 421 TB patients, but only 367 are reported and 228 TB patients provide information related to TB stigma. These patients were sampled over one year from 180 health facilities across 11 counties in Kenya. a. Further clarification on the sampling frame is needed. b. How many patients were sampled per health facility? Was there any gender consideration per health facility? c. How were the 12 regions chosen and how do they relate to the current national or programmatic divisions? d. It is indicated that one county was chosen from the 12 regions but only 11 counties included.

6. Elaborating on the tool and procedures used is needed for the readers to judge the robustness of the methodology used. This information is crucial in the methods section. Lines 164-165: “Stigma was assessed using a set of standardized questions rated on a five-point Likert scale (0 = Strongly Disagree to 4 = Strongly Agree).”

(i) What is the set of standardized questions? (ii) What tool was used? (iii) Has this tool been previously used in the literature? (iv) Has the tool been previously used in the Kenyan context? (v) Is this a validated tool? (vi) In what language/s were the questions asked? (vii) Who administered the survey? Provide relevant references.

These details are missing in the methods section; and need to be considered for inclusion in the main text and/or supplementary material based on journal guidelines.

1. What do the authors think could be the implications of handling neutral scores as missing? Lines 189-190: ‘Responses with a "Neutral" score were treated as missing in the binary variable.’ Please elaborate and describe the possible limitation.

2. Lines 192 to 194: “Variables with p-values <0.05 in bivariate analysis were entered into a multivariate logistic regression model to identify independent predictors of TB-related stigma” – Do the authors mean a multivariable logistic regression model?

3. In the results section, 10 participants are aged 0-14 years however, one of the study inclusion criteria is that participants should be aged 15 years and above. Further clarification is needed.

4. Are the age group categories shown in Table 1 meaningful? Would other summary descriptive statistics for age central tendency and dispersion be considered to provide more information about patient characteristics.

5. The term “Pagan” in Table 1 may be considered derogatory – consider an alternative word.

6. Several other participant characteristics would be important to understand TB-related stigma, including: a) the type of tuberculosis; b) the timing of treatment for the TB patient at which this survey was being performed; c) disclosure of a TB diagnosis; among others. There is existing global, regional and particularly Kenyan literature that supports the importance of these particular characteristics. Consider including these in Table 1.

7. Lines 228-230: “Out of 367 participants, 228 individuals with TB shared their experiences regarding stigma. Among them, 24 (11%) reported experiencing TB-related stigma, while 204 (89%) did not. The remaining 139 participants did not provide an opinion and were excluded from the bivariate analysis.” a. Based on this statement, it is not clear what the procedures for study participation were. The study was to assess TB-related stigma, but 139 participants did not provide an opinion. Please elaborate the study procedures for the readers to gain clarity. b. What are the characteristics of the individuals of TB patients who did not share their experiences regarding stigma? c. Were they different from those who did?

8. Clarification is needed regarding the proportions of stigma provided in different sections of the manuscript. TB-related stigma dimensions in Figure 2 report relatively high TB-related stigma levels (49% for self-stigma, 68% of community-level stigma); compared to the overall TB-related stigma reported as 11% and also shown in Table 2.

9. Consider including whether the type of TB was pulmonary or not, in Table 2. This is not clear.

10. Data analysis:

Lines 171-175: “Exploratory factor analysis (EFA) was conducted to test the internal consistency and construct validity of the stigma scale in the Kenyan context. Cronbach’s alpha was calculated to assess internal reliability, with values ≥0.7 indicating acceptable consistency. The principal components extraction method was used to identify underlying factors, with factor loadings ≥0.4 considered acceptable.”

• Although this section is included in the data analysis methods section, there is no data in the manuscript to support this. Please provide this information if it is available.

Lines 182-186: “Stigma-related responses covering domains such as guilt, fear, social avoidance, and disclosure concerns were numerically encoded (1 = Strongly Agree to 5 = Strongly Disagree). Scores were aggregated row-wise per participant to generate a mean stigma score, which was then categorized as follows: 1.00–1.49: Strongly Disagree, 1.50–2.49: Disagree, 2.50–3.49: Neutral, 3.50–4.49: Agree and 4.50–5.00: Strongly Agree.”

• Similarly, although this section is included in the data analysis methods section, there is no data in the manuscript to support this. Stigma is reported as a binary variable and not continuous. Please provide this information if it is available.

Lines 192-194: Variables with p-values <0.05 in bivariate analysis were entered into a multivariate logistic regression model to identify independent predictors of TB-related stigma. Outputs are presented in Table 1 and Table 2 of the Results section.

• Again, this section is included in the data analysis methods section, but there is no data in the manuscript to support this. No results are provided for multivariable logistic regression in Table 1 or Table 2. Please provide this information if it is available.

Was there a justification of including age group instead of age as a continuous variable instead in the data analyses models used?

Was the sample size calculated powered to determine the factors associated with TB-related stigma?

1. Results, Discussion and Conclusion. The main confusion for me is around denominators and the respective proportions related to TB stigma that have been presented. Clarification on this is needed.

2. Study limitations need to be acknowledged.

R0:

Review Comments to the Author

Please use the space provided to explain your answers to the questions above. You may also include additional comments for the author, including concerns about dual publication, research ethics, or publication ethics. (Please upload your review as an attachment if it exceeds 20,000 characters)

Reviewer #1: 1. The manuscript primarily shows that adding a visual inspection step increased the proportion of prosthetic feet deemed usable (83% to 94%). This outcome is predictable and does not constitute meaningful scientific innovation. The work reads as an operational description rather than rigorous research; novelty and contribution are therefore limited. 2. The proposed checklist is not validated. There is no mechanical or structural testing, no clinical functional outcomes, no prospective field evaluation, no inter-rater reliability assessment, and no sensitivity or specificity analysis. Accordingly, the checklist cannot be considered a standard, and the conclusions overstate the evidence. A formal validation phase is required. 3. Safety, mechanical integrity, and lifespan have not been evaluated. Visual inspection alone is inadequate for medical devices. No ISO-aligned static or cyclic loading tests are presented, nor are durability or time-in-service data available. This is a critical omission given the manuscript’s intent to inform international practice. 4. No patient-level outcomes are included (for example, fit success, comfort, skin issues, mobility, abandonment, repair frequency, or time-to-failure). Without these data, the practical value of the intervention remains uncertain. 5. Brand-level comparisons are underpowered, and model-level or material-level analyses are not presented. Despite acknowledging this limitation, the manuscript still interprets brand-related effects. 6. The Introduction and narrative sections are disproportionately long and repetitive; substantial condensation is recommended. In contrast, the Methods and Results require greater depth and clarity. 7. The statistical analysis is limited. Logistic models do not account for key confounders such as service age, storage duration, materials, or model type. Model diagnostics, effect sizes with confidence intervals, and multiple-comparison considerations are not reported. 8. Economic evaluation is absent. Donation and reuse programs in low and middle income settings are cost sensitive, and without cost modeling, the recommendations have limited actionable value. 9. Several claims are overstated, including suggestions related to circular economy effects, international standard development, and safety assurance. These assertions are not supported by the presented data and should be moderated.

Reviewer #2: It is suggested to review the Nippon Foundation/Exceed Cambodia in proposing the standards of P&O. The case study that has been done in Cambodia, Myanmar, Laos, Vietnam and Sri Lanka in will guide the current P&O Standard in low and middle income countries.

It is best to review the minimum standards of P&O in these countries as a underlying theory to govern the foundation of foot reuse and donation used.

A robust systematic reviews are vital in proposing standards for foot reuse and donations used in low and middle income countries. An updated literature are needed.

It is suggested to explore the preliminary findings in these low and middle income countries.

Reviewer #3: GENERAL This reviewer welcomes the ambition of the authors to start developing standards for donated prosthetic componentry to LMICs. Such standards are indeed much needed as one important factor to improve the quality of the prosthetic devices provided within LMICs.

The authors’ work has carefully been imbedded into a wealth of information and reasons for why the need is urgent for developing standards of donated prosthetic components. This information has been mindfully drafted including viewpoints and situation of many LMICs as well as HICs. Well done!

What left this reviewer wondering is why the development of the checklist has not been carried out with locals at the two centers, where MB and PM were able to collect the data of the stored feet. The rationale for not doing so should be included into the Limitations section.

Further, why has no testing of the developed checklist been carried out with the two centers? For example, dividing the available feet into two equal sized groups would have raised the opportunity to develop the checklist with one group of feet including the regression model and then test it on the remaining feet in the second group. Why was this not considered? One could classify all available feet as indicated in Table 1, but then consider only these feet who were mostly used in the field or were mostly available. Lowering the numbers of independent variables to the those variables that would represent the essence of the checklist best would have given the option for a regression model, or is this reviewer mistaken? These points should be discussed in the paper. In case the paper gets too long (word count), it is recommended to concise the actual discussion section as it provides similar points stated in the introduction.

And lastly, this reviewer does not think that retesting used feet similar to the stated ISO standards would be feasible. Instead, it might be worthwhile checking in other industries (aviation, deep-sea shipping) what type of non-mechanical controls for checking of wear and tear on materials/motors are available without dismantling motors or testing of used structures. Perhaps some light and/or sonar evaluation would be a way to check the mechanical structure of used prosthetic feet and other componentry without putting any more strain on the used materials. That might be some thoughts for the Future Work section. Also probable collaboration with universities in LMICs should be considered as a close source of additional brain power for the development of standards within a given country.

DETAILED The reviewer finds the word ‘prosthetics’ difficult and prefers the (correct) term ‘prosthetic componentry or prosthetic components’ instead. In her experience using the nomenclature of the P/O profession adds clarity in an interdisciplinary context. It is often unclear to people outside of or adjacent to the P/O profession that a ‘prosthetics’ is composed of different products, i.e. some industrial produced prosthetic components and – in most cases – a bespoken locally fabricated prosthetic socket. By using prosthetic components or prosthesis/prostheses when referring to the final product – the authors will signal directly that there are ‘pieces’ needed to compose an entire prosthesis. Further, using the correct term assists in distinguishing prostheses fabricated with componentry from those being fabricated by 3D printing, also a field needing standards for C2C design. Therefore, please change the wording accordingly within the entire paper – thank you!

Lines 165-168. This sentence seems to be incomplete – please check.

Line 229. This statement is incorrect. In Switzerland (and the reviewer is sure this is the case in France, Netherlands and the UK), prosthetic componentry has different life/warranty cycles depending on the type of prosthetic component and its model. Please rephrase this sentence pointing out that different prosthetic components and their models have different life/warranty cycles set by the industrial manufacturers.

Lines 284-286.This sentence is unclear: Are the authors checking prosthetic feet shipped to Africa prior to the study or as part of the study when these feet arrive in Africa? If they are analyzed prior to the study how do the authors make sure that the damage seen is indeed due to shipping and not due to storage, for example? If the authors controlled feet within the study time period, would the sentence not needed to be stated “… we review prosthetic feet ALSO in Africa.”? Or did the authors not review the feet at the study place, but only in Africa? Please clarify and rephrase – thank you. These clarifications/details seem to be better placed within the Materials and Methods Chapter.

Lines 287-311, in particular lines 311-317. Because the authors use an experimental setup, variables are usually considered as ‘independent’ or ‘dependent’. Please clarify what variables (independent, dependent) were considered. All variables the authors used to classify the different feet need be listed together with the rationale for the decision to include them into the regression model, including their order.

Ok – are the variables listed on line 314 the once considered as independent variables to classify a prosthetic foot as ‘reusable’ or ‘not reusable’? If so, why? In other words, why do the authors consider the ‘brand’ to be more important than the condition of the foot itself? Or is it the case because only those feet that passed the visual test of being 'usable' were included into the regression model? Up to this point, this reviewer understood the aim of the study as being to develop a set of criteria to classify a prosthetic foot as reusable or not. If a visual pre-selection needs to be carried out first, how good/robust is the regression model that follows? Please clarify and add this clarification to the text – thank you.

Lines 296-298. What variables (the authors call them ‘flaws’, if understood correctly) did the authors consider during the usability tests? How were these tests carried out? What happened with the feet the authors did consider as ‘not usable’: where they removed from the total sample of 366 feet (see below remarks to line 319)? For illustration: assuming the authors used for their visual check a variable called ‘cracks within the cosmetic’: did the authors classify a foot as still usable when only surface cracks were available, or did they exclude any foot with a crack in its shell? What were the criteria to classify a SACH foot as ‘usable’? More detailed information about the entire method for the visual checks and the resulting classification needs to be stated.

When did the authors add any of this variable into the regression model and they give some of the variables a weighting, i.e. were some of the variables considered more important than others, and if so, why? Please add this information and make a reference to Table 2 or better, create a new Table or flowchart showing the authors thoughts and decision process including the variables used upon which they based their decision to classify a foot as ‘usable’ or ‘not usable’. Clarification on this matter will strengthen the work as it helps the reader to better understand the authors’ rationale – thank you!

Line 319. Please start the results section with “A total of 366 feet where analyzed, 196 left and 170 right feet…”

Line 320. Please add “… and A brand could be identified for… ” – thank you.

Lines 320-322. Based on the information given in Table 1, there were 12 brands identified as categories plus one category with feet unknown to the authors. Because ‘unknown’ is not a brand, the sentence needs to be rephrased – thank you.

Lines 353-357. These sentences seem to be missing some text, at least, they do not make sense to this reviewer. In lines 353-355 the authors state that the feet of Trulife and Ossur performed worst. Then in the following lines the authors state that they are (nevertheless??) considered as appropriate for donation. Please clarify – thank you.

Table 4. Please explain/add, either in the corresponding text (lines 350 and subsequently) how the negative signs have to be read. Why has the measurement made against ‘BioQuest’ and not ‘Janton’ and how do the authors explain the difference in the coefficient between these two feet? Both feet were represented with n=1, why is there a difference? Please explain and add the clarification into the text within the Discussion section – thank you.

Figure 2. Please add to Fig. 2, a, b, and c, as done in Fig. 1. This assists in clarifying matters. Please add this clarification into the text: line 364 = Figure 2a; line 378: delete (Figure 2) and add after ‘NCRPPD’ (Figure 2b); line 379: add (Figure 2c) after ‘K4C’.

Line 388. Add at the end of the sentence ‘(Figure 3)’.

Line 395. Please expand this sentence like or similar as proposed “…can be a burden to the recipient LMIC [31, 39,40], as indicated by Marks et al (2019 – Please check PLOS rules!!):” and then have the quotation followed. This will connect the quotation with the text and makes it easier to read.

Line 469. Please check this sentence – the word ‘design’ seems to be twice stated. If this is correct, consider rephrasing as the sentence reads strange, thank you.

Checklist questions: • Question (1): Please add example of ‘completeness’ of a prosthetic foot, as you did for Question 2. • Question (3): Add examples of what the authors consider ‘compliant’: forefoot, heel, middle section? All of these, only one? Usable for light persons, like children if only one part of the foot is too compliant? If so, which one do the authors consider as the most important variable for a foot to be still considered ‘usable’?

Line 529. Word missing: “..cost of what” was the biggest barrier? Please complete.

Line 533. Please consider replacing ‘in this way’ with ‘Therefore’ or similar that would connect clearer the content of the previous paragraph with this new one.

Line 544. Typos: ‘reduce’ instead of ‘reduces’, ‘limit’ instead of ‘limits’.

Line 567. Stop the sentence after ‘repair of equipment’ and continue with a new sentence starting, for example with “Hamner et al (please check PLOS rules!!) point out that … and than add the quotation.

Line 570. Please delete ‘etc.’ This should not be used in a text as it lefts the reader wonder what else – in this case – could have had an influence. Instead write ‘for example’ and list the three most missing points that were not considered.

Line 620. Keep the number correct: the authors tested 306 feet. The number speaks for itself, no need to bolster it. To this reviewer bolstering looks bad, stay with the figures.

Line 622. Replace ‘are’ with ‘were’, as this was the case for the authors' sample. Samples of other authors might vary.

R0:

Review Comments to the Author

Please use the space provided to explain your answers to the questions above. You may also include additional comments for the author, including concerns about dual publication, research ethics, or publication ethics. (Please upload your review as an attachment if it exceeds 20,000 characters)

Reviewer #1: Full Title:

Manuscript full title does not match with the short title. Full title reads "Climate change, livelihoods, gender and violence in Rukiga, Uganda: intersections and pathways". While short tile reads "Climate Change and Gender Based Violence". 'gender based violence' may not necessarily mean the same as 'gender and violence'. Authors should consider revising the wording in the full time if they meant gender based violence.

Abstract:

Inconsistency in FGD size, harmonize to consistent range across the manuscript. Author said "Between April and July 2021, we conducted 28 focus group discussions (FGDs), comprising 6-8 participants each (line 29-30" and in methods author said "From 20 April 2021- 02 July 2021 five focus group discussions (FGDs) were conducted in each community (28 in total) each consisting of four to six participants (lines 135-136)".

clarify the CBV emergent theme. You said "This study, though not originally intended to focus on GBV, examines how it interconnects with poverty, shifting gender roles, alcoholism, environmental stress, and family planning dynamics." (lines 26-28). Consider adding a statement signalling GBV emerged inductively during data colletion and/or analysis.

Methods: Revise the methods section to ensure the study can be reprodcible, and signal reliability of findings.

What study design did you use? not clear

Author said participants were " purposively selected... with the help of community leaders" (lines 140-141). Clearly elaborate the eligibility criteria and how the gatekeepers' influence was mitigated, and proper justification why 28 FGDs and 40 KIIs were sufficient. Talk about saturation, was maximum variation considered? and how?

Results:

Tag all quotes with data source (FGD or KII), sex, age to evidence diversity across the groups.

Make sure all quotes are in clear quotations marks (lines 220-222). fix that for the entire results section and be consistent.

Authors said "When describing their experiences and perceptions of poverty and its associated consequences including poor diets, sickness, and lack of ability to pay for healthcare and transport to medical facilities, most respondents explicitly identified poverty as a direct cause of GBV:" (lines 311-314). Revise the wording on participants' perceptions to avoid implying causality from qualitative data. Check the entire document for this including the abstract lines 36 to 41.

Ethics: Include ethical committee name that gave ethical clearance for the study, also include the reference number and date.

describe safeguardings and referral procedures followed in the study if any.

Conclusion: The concept for this paper is timely and relevant. However several important elements require revision before the manuscript can meet PLOS Global Public Health Standards. Work on the clarity and consistency of the methods (study design was not clearly mentioned, there are several qualitative designs one can use, e.g. phenomenology, case study, etc. what design did you use?). PLOS Global Public Health guidelines on data sharing require that you provide some de-identified data, nevertheless authors stated that they would share data and the justification for that leaves much to be desired.

Reviewer #2: 1. Kindly mention the methodological orientation adopted for the study? 2. Discrepancy between number of participants in FGD mentioned in abstract and methods – (6 – 8 in abstract and 4 – 6 participants in methods)…Kindly make it uniform 3. Additional context on domestic violence and related statistics can be added in study setting 4. Details on steps taken to ensure internal validity/rigor to be mentioned – member checking, reflexivity 5. Give details of the parent project briefly 6. Any conceptual model/framework adopted to guide data generation/analysis? 7. What efforts were taken to address/refer victims of GBV once disclosed? 8. Socio - demographic details of the respondents could be added for better interpretation 9. Key themes are restated multiple times; Many dimensions of GBV (more details on each typology, coping strategies, prevention, etc) not elicited

Reviewer #3: Overall Comments The paper takes a qualitative approach to “examine locally held perceptions of the relationships between climate and livelihood-related stressors and changing dynamcis, including the risk of Rukiga district. Climate change remains a global threat, with many countries and communities within Africa, ill prepared to adapt and mitigate the consequences. The paper is an attempt to paint a picture of climate-related impacts, particularly how gender-based violence, a persistent public health, socioeconomic and development issue is shaped by and influencing social, economic and environmental stressors.

In its current form, the paper need to be strengthened to get it to be sufficiently robust for publication in PLOS Global Public Health. The paper needs to be strengthened in at least three ways:

1) Overall, the paper needs to better contextualise their goal. Authors state in line 115 to 117, that their purpose is to understand locally held perceptions of the relationship between climate and livelihood-related stressors, and in several other sections, indicate make clear that, their original intention was not GBV, but undertook a thematic analysis on the latter. This can be confusing making it difficult for readers to follow. Authors need to clarify their focus – if it is on GBV, they may consider better contextualising their paper, especially in the introduction.

As part of contextualising, authors may consider highlighting the initial primary research focus – this helps to provide context for readers to begin to appreciate how and why GBV took center-stage during the analysis. In doing so, it also provides an opportunity for authors to properly situate their contributions to the literature.

Other minor issues include: • Authors make claims about projected exponential increase (line 51-52) and yet, do not support with any data. Similarly, authors may want to consider revising the sentence, as it appears redundant.

• In line 55-57, it argued “Uganda’s vulnerability to climate change and climate-sensitive disasters is extremely high – it is not immediately clear to readers what this means. By which benchmark or metric are authors assessing Uganda’s vulnerability. Authors may consider revising to ensure clarity (also see lines 108-110 for punctuation issues).

• Lastly, the study takes place in Rukiga District – it would be helpful if authors provided some additional background context. Will the results be different, if the study was conducted in a different district rather than Rukiga? Basically, some discussions of the rationale and/or choice of the selected district is be useful.

2) Overall, authors need to improve their methods by revising and clarifying, some of the sections. For example, under study setting (line 128-130), it is not clear if the concluding sentence is provided additional context for the prior statement. Authors may want to revise for clarity purpose.

I. Reconcile the number of participants for FGDs – in the abstract, authors indicate 6-8 people form a FDG and in line 136, it says “…each consisting of four to six participants,…”. II. For both FGD and KII, it is useful to indicate and/or describe the demographic/characteristics of the people participating in the study (Perhaps, authors could outline their demographics by sex and age, and any other stratifier in the results section in a tabular format. How were participants selected, especially among the FGD participants? III. On ethics statement, although the data emanates from key informants and community members, authors do not indicate whether they sought ethnical approval for their study. If ethics was obtained, it is useful to indicate so. IV. Regarding data collection, lines 172 to 173, authors indicate that “discrepancies in the coding were re-examined…”. It useful to explain how the independent assessor resolved discrepancies and reached consensus. V. In the data collection section (line 155 to 157), authors indicate that they “undertook a specific analysis of what participants said about GBV”. However, in the results, it is often not clear, the specific thematic issues or results arising from this analysis. Related to this and linked to the analysis, it is not clear to readers how the two main clusters (line 188 to 191) link to GBV. While lines 193 to 212, describe nature of GBV, for the most parts (for example, line 213 to 308), it is difficult to follow how GBV is an interconnector in the results being discussed. At times, it difficult to see, where the analysis departs from its original intended goal. Were the issues around climate change and environment among others emergent from the data?

3) Overall, the results section outlines some very interesting insights. However, I do feel this section can be deepened. In many instances, the narratives are often not immediately supported by the relevant quotes, linking to GBV. • In line 230 – 323, authors reflect that the disruption to livelihoods leading to family instabilities and conflict, demonstrate how GBV is triggered. This assumption is challenging to sustain, considering that “unrest in families” and not having “peace in a home” do not necessarily connote GBV. Similar reflections are presented at line 306 (“...they both resort to quarrels…”), lines 316 to 320 (…start quarrelling and fighting…”) and (“…you fight with the woman”). • Although authors indicate these are “euphemisms for GBV” (line 208) that participants use – without critical analysis, we risk painting a picture that may not be correct. For example, will readers be correct to assume, that in Ugandan context, such referencs always mean GBV?. To avoid readers assuming without appropriate understanding of context, authors may consider, making explicit any additional nunaces related to the quotations or contexts for this pharses, to clarify and make the links to GBV much clearer.

Minor • Line 199 – please clarify how and why unintended pregnancies is considered a form of GBV • Line 208 to 209 – revise sentence – it is not clear what authors mean by throughout their experiences and perceptions • Line 211 – “GBV was raised during the discussions of a wide range of factors” – perhaps, useful to outline the contexts which GBV was raised

R0:

Reviewers' comments:

The study addresses the ongoing H5N1 panzootic, a topic of major global health concern. By focusing on zoonotic spillover and potential human-to-human transmission, it connects well to pressing pandemic preparedness questions. Here are my suggestions

The study acknowledges asymptomatic cases but doesn’t deeply explore realistic ranges of asymptomatic infection in H5N1. Since asymptomatic carriage in humans is poorly understood, exploring a wider range of assumptions (from very low to moderate prevalence) would add robustness. Maybe authors can discuss this point

While the UK setting is clear, the contact structures and public health response capacity differ in low- and middle-income countries where zoonotic spillover risk is high. Discussion of transferability would broaden the relevance.

The agricultural contact data are valuable, but heterogeneity within and across communities (e.g., multi-generational households, seasonal work, market interactions) could have been discussed more fully. This heterogeneity may affect outbreak potential.

Only contact tracing and self-isolation are modeled. In reality, outbreak management could include infection control, health care facility and capacity, movement restrictions, or culling of infected animals. Considering at least one additional intervention would make the study more comprehensive.

The study convincingly demonstrates that early interventions like contact tracing and self-isolation can substantially reduce outbreak size when R₀ is low and symptomatic detection is reliable. However, if R₀ increases or asymptomatic transmission is significant, these interventions may not suffice. Authors can discuss this point

For policymakers, this suggests that contact tracing and self-isolation are valuable but fragile tools—effective only under certain epidemiological conditions. Maybe authors can discuss they should be embedded in a layered response strategy including rapid diagnostics, surveillance, and (eventually) vaccines or antivirals.

Editor comments: - Given that there is little to no evidence of human-to-human transmission for avian influenza (H5N1), is self-isolation recommended as a control measure for human cases? Additionally, is self-isolation applicable in the context of seasonal influenza as well? - Introduction section: Line number 66: However, cases without zoonotic exposure and limited human-to-human transmission have been documented. Specify the virus name. Seasonal or avian influenza. - In method: you mentioned "contact with birds". It is better to mention the name bird or poultry or chicken or turkey. The meaning of bird is different than poultry. - Does the model possess adequate capability to address avian influenza, considering the virus exhibits limited human-to-human transmissibility?

R1:

All comments have been addressed.

R0:

Reviewer #1: The review is important to improve outcomes on cholera surveillance and response. However, there are a number of critical issues that must be addressed to ensure the manuscript conforms to the standard of scientific writing and scoping review. 1. Certain sections were ommitted e.g Quality assessment and Data analysis 2. The roles of the authors in the scooping exercise also omitted 3. The results and discussion sections are mixed up. The authors began discussing the findings in the result.

Reviewer #2: Given the ongoing cholera pandemic and its recurrent outbreaks in sub-Saharan Africa, it is commendable that the authors undertook a comprehensive mapping of cholera research in Kenya. 1.For the search strategy, the query “cholera AND Kenya” across all databases is overly restrictive and likely excluded studies using alternative terminology such as “Vibrio cholerae”, “waterborne disease”, or “WASH-related cholera”. I would recommend providing the full keywords, filters and timelines used for each database, to help in reproducibility, as stated in the PRISMA-ScR Checklist (Item 8). 2.Please provide the last search date or timeframe. 3.The authors mentioned the systematic search of five databases, including Google Scholar, Web of Science, PubMed, Embase, and Scopus. However, in the PRISMA flow diagram (Figure 1), there is no data for Google Scholar. 4.The use of Rayyan is recognized. However, reviewer roles, conflict resolution, and data extraction validation are not stated. 5.The authors mentioned the inclusion of non-primary studies, such as reviews, but stated “ineligible study design” as a reason for exclusion in Figure 1. A clarification on this is could be beneficial. 6.For each included study, the authors should present the characteristics of the data charted with respective citations in a table. 7.In section 3.2, the authors provide an informative table which shows the geographic focus of the studies across multiple countries, including Kenya. For a scoping review centered on Kenya, a similar table or map that shows the distribution of studies/ data on the county-level could be added. 8.Themes such as mortality and risk factors of cholera could be explored and discussed further to strengthen the manuscript. 9.The Results-Discussion boundary seems blurred. Discussion begins to appear within “Future directions” paragraphs under each theme. I would recommend that the authors consolidate all “Future directions” into a single Discussion summarising what is known and unknown.