R0:

Reviewer #1: I found the study interesting and potentially publishable. The manuscript captures an important aspect of contemporary outbreak communication: new infectious-disease emergencies are being interpreted through pre-existing political, cultural, and institutional frames, particularly those developed during COVID-19. The authors' observation that Ebola discussion repeatedly invokes COVID-19, vaccination, institutional mistrust, international aid, preparedness, and geopolitical concerns is worthy of further development.

My recommendation is major revision rather than rejection. In particular, I encourage the authors to:

(1) temper claims concerning representativeness and public perception. Your sampling strategy does not lend itself to broad generalizability.

(2) describe and validate the transition from LDA topics to qualitative themes. The context in which comments appear is important. I recommend providing, preferably in the main manuscript, descriptive information for each selected video: publication date, channel/uploader type, language, number of views, number of comments retrieved, and other relevant characteristics. This would allow readers to understand the informational environments from which the comments arose.

(3) justify the 20-topic model. The manuscript provides detailed LDA parameters but does not explain the choice of k=20. Was this determined a priori, through topic-coherence measures, inspection of alternative models, or another procedure?

(4) validate or substantially qualify the NRC sentiment analysis, especially the interpretation of “trust”.

(5) provide video-level analyses to determine whether the major findings are broadly distributed or driven by particular videos.

Addressing these issues would considerably strengthen what is already a timely and potentially useful contribution to the literature on outbreak communication, misinformation, and digital public-health discourse.

Reviewer #2: Main comments Thank you for the opportunity to review this interesting paper which analyses public discourse and sentiment expressed in YouTube comments related to the 2026 outbreak of Bundibugyo virus in the DRC and Uganda. Data from social media platforms are now recognized as important sources for monitoring public discourse. As this outbreak continues to unfold, this analysis can offer potentially helpful guidance for health communication and community engagement. Reports of local hostility towards public health officials suggest the need for fuller understanding of public sentiment.

While this is a clearly written paper, in my view, there are several ways that the authors could strengthen this paper to ensure a significant and original contribution to knowledge. First, the introduction could provide a fuller rationale for the study. The authors argue that there has been limited analysis of public reactions to this outbreak to date and that “effective risk communication” can benefit from this study. It would be helpful to provide more context on public reaction to the outbreak locally and internationally, and how this has impacted the response to date. The attacks on public health workers and clinics, and the international travel restrictions imposed, for instance, could be mentioned. A fuller explanation of how analysis of YouTube comments would be relevant to what is happening on the ground is then needed. Why do the comments on YouTube matter?

Second, to reach meaningful results and draw conclusions from this data, the authors need to reflect more fully on the likely sources of the comments on YouTube. Who is the “public” making these comments? Currently, there is no information provided on who is actually making these comments other than they are on YouTube. Social media data is notoriously difficult to disaggregate but, without more knowledge of the sample, the observations reached are weakened. The authors note at the end of the paper that the “comments may not represent the full spectrum of public opinion.” Indeed, they will most definitely not be. Those who comment in social media tend to be from certain population groups. As a result, using social media alone skews towards those perspectives. The demographics of who comments on specific social media platforms is a research topic in itself. For example, X tends to skew right of centre politically. While half of all internet users watch YouTube, only a fraction actively comment. Studies indicate that a staggering 72.6% of YouTube videos have zero comments, meaning active participation is concentrated on a small portion of the platform. There is also evidence that, globally, those who comment tend to be younger and male aged 25 to 34. Thus, the authors need to say more about why YouTube was chosen (over other platforms), what profile might be assumed about those who comment on YouTube, and, importantly, how this then impacts data collection and analysis. Understanding who is commenting ultimately tells us how much we need to pay attention in public health. If the sentiments expressed are largely outside of the affected countries, for instance, what does this mean for the public health response? If they are local voices, what can we take away from these comments?

Third, while the authors clearly describe their methods for collecting this data, more could be said about how the themes were derived to analyse the data. Some of the categories seem to oddly pair different topics such as geopolitics and cultural context. These seem very different things. Cultural context might be better paired with religious and spiritual interpretation perhaps. I also questioned why some comments were put into specific themes. In the geopolitics and cultural context, for example, border and flight restrictions were included, and yet this might arguably be more relevant to disease spread and transmission, or public health measures and preparedness (where they are also mentioned). The theme of public figures, conspiracy theories and misinformation seems an odd mix. Does this suggest discussion of named public figures is necessarily related to misinformation? An explanation in the methods of why these categories and the scope of what is included (and why) is needed. How these themes were validated is also important.

Finally, much of what is currently in the Discussion could be relocated to the Results. This would strengthen the presentation of the results which reads a bit thinly and unsystematic. The Discussion should focus on the “so what” from the results. What meaning can we derive from the Results for understanding public discourse and sentiment, and for public health practice?

Minor comments • I suggest swapping the sequencing of themes presented to start with the themes with the most to least comments (i.e., swap public figures etc. and geopolitical and cultural context).

R0:

Reviewer #1: The title and abstract are clear, concise, and appropriately reflect the scope and objectives of the study. The abstract provides a coherent overview of the background, methodology, key findings, and conclusions, allowing readers to quickly grasp the relevance and significance of the research. The introduction is well structured and supported by sufficient and relevant literature, effectively establishing the public health importance of maternal dietary diversity and clearly justifying the need for the study in the Nepalese semi-urban context. In the methodology section, the authors should clearly describe how the study area was classified as a semi-urban municipality and specify the definition or criteria, along with appropriate references. Although the sources of the original questionnaire are mentioned, the authors should further report the reliability of the adapted instrument. Specifically, the Cronbach’s alpha values obtained from the pretesting should be provided to demonstrate the internal consistency and reliability of the questionnaire. Including this information would strengthen the methodological rigor of the study. The results section is clearly presented, and the tables are well organized and easy to follow. However, the narrative accompanying Table 2 tends to repeat detailed information already provided in the table. The authors are encouraged to summarize and highlight only the key findings, rather than reiterating all tabulated values. The discussion section is satisfactory, with appropriate interpretation of the findings in relation to existing literature, and the conclusions are clear, focused, and adequately supported by the study results.

Reviewer #2: I recommend acceptance with minor revisions. The manuscript is strong and well-written, requiring only modest improvement to enhance clarity, expand the discussion of limitations and strengthen the policy relevance of the conclusions.

R1:

Reviewer #1: The authors have adequately addressed all the comments raised by the reviewers.

Reviewer #3: Manuscript ID: PGPH-D-25-03816R1 Title: Maternal dietary diversity and its correlates in a semi-urban municipality of Nepal: A cross-sectional study General Assessment This manuscript addresses an important and underexplored public health issue: maternal dietary diversity among lactating women in a semi-urban setting in Nepal. The topic is highly relevant to maternal and child nutrition, especially in low- and middle-income countries undergoing rapid urban transition. The study contributes useful contextual evidence regarding socioeconomic, household, and empowerment-related determinants of dietary diversity among lactating mothers. The manuscript is generally well-structured, grounded in relevant literature, and employs recognized tools such as the MDD-W and HFIAS. The statistical analysis is mostly appropriate, and the discussion is adequately contextualized within regional and global evidence. The inclusion of empowerment, food security, and nutrition knowledge variables enhances the study's public health relevance. However, several methodological, analytical, and reporting issues require clarification and revision before the manuscript can be considered for publication. Some inconsistencies in sample size calculations, operational definitions, interpretations of findings, and presentations of results require further attention. In addition, the manuscript would benefit from more critical interpretation of the findings, improved methodological transparency, and language refinement. Major Comments 1. Sample Size Inconsistency and Population Correction The manuscript reports that 700 eligible lactating mothers were identified in the municipality, but the finite population correction formula appears to use a total population size (N) of 2500 rather than 700. This discrepancy should be clarified, as it affects the validity of the final sample size estimate. Recommendation: • Clearly explain the origin of N = 2500. • Recalculate the corrected sample size if necessary. • Ensure consistency throughout the methods section. 2. Operationalization of Women's Empowerment Women's empowerment was categorized as "one or more decisions" versus "none." This binary categorization oversimplifies empowerment, which is multidimensional and context-dependent. Recommendation: • Justify dichotomization. • Discuss the limitations of this operational definition. • Consider reporting the distribution of specific empowerment domains separately. 3. Cross-sectional Design and Causal Language Several sections of the discussion and conclusion imply causal relationships between predictors and dietary diversity. For example: • "Employment provides autonomy enabling women to make independent food choices…" • "Nutrition education interventions improve dietary outcomes…" Because the study is cross-sectional, causal interpretations should be avoided. Recommendation: • Use more cautious language, such as "associated with" rather than "improves" or "leads to." • Reframe interpretations to reflect observational associations. 4. Dietary Assessment Limitations The study used a single 24-hour recall, which may not adequately reflect habitual dietary intake. Although this limitation is acknowledged later, the implications should be discussed more critically. Recommendation: Expand discussion on: • day-to-day dietary variation, • recall bias, • seasonal variation, • social desirability bias, • inability to estimate nutrient adequacy quantitatively. 5. Potential Residual Confounding The multivariable model included several predictors, but important potential confounders were not addressed, including: • maternal BMI, • postpartum duration, • breastfeeding intensity, • household food expenditure, • cultural food taboos, • maternal morbidity. Recommendation: Discuss residual confounding more explicitly in the limitations section. 6. Interpretation of "Hidden Hunger" The manuscript states that low intake of nutrient-rich foods suggests "hidden hunger." This is plausible, but should be interpreted cautiously because no micronutrient biomarkers or quantitative nutrient assessments were conducted. Recommendation: Rephrase to: "may suggest potential micronutrient inadequacies" Rather than implying confirmed hidden hunger. 7. ANC Visits and Statistical Interpretation The adjusted odds ratio for ANC visits is: aOR = 1.9 (95% CI: 1.0–3.4) This borderline confidence interval should be interpreted cautiously. Recommendation: Avoid describing ANC attendance as a definitive predictor and acknowledge the marginal statistical significance. Minor Comments 8. Clarify Time Period of Data Collection The manuscript states: • A study conducted from September to November 2020, • But data collection occurred from 09/10/2020 to 24/03/2021. These periods appear inconsistent. Recommendation: Clarify the exact duration of fieldwork. 9. Food Group Description The list of food groups in the methods section appears merged: "meat, poultry, fish, eggs, legumes, nuts, seeds…" Recommendation: Present the ten MDD-W groups more clearly and consistently according to the FAO classification. 10. Terminology Consistency The manuscript alternates between: • "dietary diversity," • "minimum dietary diversity," • "DDS," • "MDD-W." Recommendation: Use terminology consistently throughout.

1. Repetition in Discussion Some points are repeated multiple times: • semi-urban transition, • education and wealth effects, • LMIC urbanization context. Recommendation: Condense repetitive discussion paragraphs to improve readability.

2. Reference Formatting Several references are incomplete or inconsistently formatted. Examples include: • missing page ranges, • inconsistent capitalization, • URLs without access dates, • formatting inconsistencies in organizational references. Recommendation: Ensure all references comply with PLOS formatting guidelines.

Strengths of the Study The manuscript has several notable strengths: 1. Focus on an under-researched semi-urban population in Nepal. 2. Use of internationally recognized dietary diversity indicators (MDD-W). 3. Consideration of multiple socioeconomic and behavioral determinants. 4. High response rate (95.4%). 5. Use of stratified random sampling across all wards. 6. Inclusion of food security and empowerment dimensions. 7. Appropriate use of multivariable logistic regression with assessment of multicollinearity.

Reviewer #4: Comment 1: How do the dietary diversity and health outcomes of older lactating mothers differ from their younger counterparts, and what are the implications for public health interventions? Furthermore, the significant proportion of participants belonging to upper-caste groups and identifying as Hindu warrants an examination of the potential impact of sociocultural factors on dietary diversity and health outcomes. Specifically, what role do caste and religious affiliations play in shaping food choices and access to healthcare services in this semi-urban setting? Comment 2: The study's findings on household characteristics, including the high percentage of male-headed households and land ownership, also merit closer examination. How do these factors influence the decision-making power and autonomy of lactating mothers in terms of their dietary choices and healthcare utilization? Additionally, the relatively even wealth distribution across quintiles may mask underlying inequalities in access to resources and healthcare services. What are the underlying mechanisms driving the observed patterns of healthcare utilization, including the low percentage of mothers who completed four or more antenatal care visits? A more nuanced analysis of the interplay between wealth, education, and empowerment is necessary to understand the complex dynamics at play. For example, how do the 43% of women categorized as empowered differ from their non-empowered counterparts in terms of their dietary diversity, healthcare utilization, and overall health outcomes? Comment 3: What are the key factors contributing to the observed mean dietary diversity score of 5.03, and how do these factors vary across different socioeconomic and demographic subgroups? Moreover, the finding that only 23.1% of mothers completed four or more antenatal care visits highlights a critical gap in healthcare utilization. What are the underlying barriers to accessing antenatal care services, and how can these be addressed through targeted interventions? A more detailed analysis of the relationships between dietary diversity, healthcare utilization, and health outcomes is necessary to inform evidence-based policy and programmatic interventions. For instance, how do the dietary diversity scores of lactating mothers relate to their nutritional status, and what are the implications for the health and well-being of both mothers and their infants? A deeper understanding of the complex interplay between sociocultural, economic, and environmental factors is necessary to develop effective strategies for promoting maternal dietary diversity and improving health outcomes in this semi-urban municipality of Nepal. Comment 4: The study's reliance on a cross-sectional design limits its ability to establish causal relationships between the predictor variables and maternal dietary diversity. How do the authors plan to address potential temporal relationships between these variables? Moreover, the sample size of 251 lactating mothers, although adequate for descriptive analysis, may not be sufficient to detect subtle yet significant correlations between the variables of interest. Did the authors conduct a priori power calculations to determine the required sample size? Comment 5: The demographic characteristics of the study population, as presented in Table 2, reveal a notable skewness in the age distribution, with 69.7% of participants falling within the 18-25 year age range. How do the authors explain this uneven distribution, and what implications might it have on the representativeness of the sample? Furthermore, the dichotomization of certain variables, such as household food security and empowerment, may oversimplify the complexities of these constructs. Would the authors consider using more nuanced, continuous measures of these variables? Comment 6: The study's use of a dietary diversity score, with a mean of 5.03 (SD ± 1.25), raises questions about the construct validity of this measure. How did the authors select the specific food groups included in the score, and what evidence supports the chosen cut-off point for minimum dietary diversity? Additionally, the lack of information about the timing and frequency of dietary assessments may introduce recall bias and limit the accuracy of the dietary data. Can the authors provide more details about their dietary assessment methodology and how they minimized potential sources of error? Comment 7: The findings regarding the predictors of maternal dietary diversity, such as education and employment status, are intriguing but require further exploration. How do the authors propose to tease apart the relative contributions of these variables, given the high correlation between education and employment status? Moreover, the study's results indicate that only 23.1% of participants completed four or more antenatal care visits, which is concerning given the importance of ANC in promoting maternal and child health. What strategies do the authors suggest for improving ANC utilization and, by extension, maternal dietary diversity in this population? Comment 8: “Recent global evidence suggests that targeted nutrition interventions can improve women’s dietary diversity in low- and middle-income countries” Add the following reference: 2025.Digital technology to advance global health by reviewing nutrition interventions and assessing needs in urban Syria. Discover Food 8, 416. Comment 9: The manuscript's discussion of the study's implications for public health policy and practice is somewhat cursory. How do the authors envision their findings informing the development of targeted interventions to enhance maternal dietary diversity and improve health outcomes in this and similar populations? What specific recommendations do they propose for policymakers, healthcare providers, and other stakeholders to address the complex factors influencing maternal dietary diversity in this context? Comment 10: The authors employed the Minimum Dietary Diversity for Women (MDD-W) indicator to assess dietary diversity among lactating mothers. However, it is essential to acknowledge that this indicator has been criticized for its limited ability to capture the nuances of dietary diversity, particularly in resource-poor settings. The MDD-W indicator focuses on the consumption of 10 predefined food groups, which may not accurately reflect the dietary habits of lactating mothers in Nepal. I would like to know whether the authors considered using alternative indicators, such as the Dietary Diversity Score (DDS) or the Food Variety Score (FVS), which may provide a more comprehensive understanding of dietary diversity. Comment 11: The results indicate that 31.9% of participants did not achieve minimum dietary diversity, suggesting potential nutritional inadequacies. However, the authors do not provide a clear explanation for this finding. I would like to inquire about the potential factors contributing to this lack of dietary diversity, such as socioeconomic status, education level, or access to healthcare services. Additionally, it would be beneficial to know whether the authors collected data on the participants' dietary habits during pregnancy, as this may have implications for their dietary diversity during lactation. The results also show that the intake of nutrient-dense food groups, such as eggs, nuts and seeds, and vitamin A-rich fruits and vegetables, was substantially lower. This raises concerns about potential micronutrient gaps among lactating mothers. I would like to ask whether the authors considered assessing the micronutrient status of the participants, using biomarkers such as hemoglobin or serum retinol, to confirm the presence of micronutrient deficiencies. Comment 12: Table 3 presents the proportion of lactating mothers who consumed each of the 10 food groups within the past 24 hours. However, it is unclear whether the authors accounted for the potential seasonal variability in food availability and consumption patterns. Nepal is a country with diverse geography and climate, which may impact the availability and accessibility of certain food groups. I would like to know whether the authors collected data during a specific season or whether they accounted for seasonal variations in their analysis. Comment 13: The authors highlight the potential risk of "hidden hunger" due to the low consumption of micronutrient-rich foods. While this is an important concern, it is essential to consider the broader context of maternal nutrition in Nepal. I would like to inquire about the authors' plans to disseminate their findings to relevant stakeholders, such as policymakers, healthcare providers, and community leaders, to inform the development of targeted nutrition interventions. Note 1: What alternative indicators were considered for assessing dietary diversity, and why was the MDD-W indicator chosen? What factors contributed to the lack of dietary diversity among 31.9% of participants, and how did these factors impact the results? Were data collected on the participants' dietary habits during pregnancy, and if so, how did these data inform the analysis? Were biomarkers used to assess the micronutrient status of participants, and if so, what were the results? How did the authors account for seasonal variability in food availability and consumption patterns? What plans do the authors have to disseminate their findings to relevant stakeholders, and how will these findings inform the development of targeted nutrition interventions? Note 2: The study's finding that 31.9% of participants did not achieve minimum dietary diversity raises questions about the underlying factors contributing to these nutritional inadequacies. Is the low consumption of micronutrient-rich foods, such as eggs, nuts and seeds, and vitamin A-rich fruits and vegetables, a result of economic constraints, limited access to markets, or cultural preferences? Furthermore, the study's reliance on a 24-hour dietary recall may introduce recall bias, particularly among participants with limited literacy or numeracy skills. How did the researchers account for potential biases in the data collection process, and what measures were taken to ensure the accuracy and reliability of the dietary recall data? Comment 14: Does the MDD-W indicator adequately account for the cultural significance of starchy staples, such as rice, maize, and potatoes, which are consumed by all participants, but may contribute to a high glycemic load and potentially exacerbate micronutrient deficiencies? Comment 15: “These settings frequently undergo rapid demographic and socioeconomic changes, including migration, expansion of food markets, and shifts in dietary patterns” Add the following reference: 2025. From plate to planet: reconstructing sustainable food systems in Early Bronze Age Civilization. Human Ecology 53, 821-842. Comment 15: How do the study's results inform our understanding of the effectiveness of existing nutrition interventions, such as the National Nutrition Policy and the Nepal Health Sector Strategy? What policy and programmatic reforms are needed to address the micronutrient gaps identified in this study, and how can these reforms be tailored to the specific cultural, economic, and environmental contexts of semi-urban municipalities in Nepal? Comment 16: The manuscript's conclusion that nearly one-third of the population is at risk of nutritional inadequacies due to low dietary diversity warrants further investigation into the social and economic determinants of dietary diversity. What role do factors such as women's empowerment, household income, and access to education and healthcare play in shaping dietary diversity among lactating mothers? How do these factors intersect with cultural and environmental factors, such as food availability and agricultural practices, to influence dietary diversity and nutrition outcomes? Comment 17: The authors should provide more detailed information on the sampling frame and the representativeness of the study sample. How was the sample of 251 lactating mothers selected, and what efforts were made to ensure that the sample is representative of the broader population of lactating mothers in Tarakeswor Municipality? Comment 18: The authors should provide a clearer justification for the specific cutoff points used to define minimum dietary diversity. How did the authors determine that the chosen cutoff points accurately capture the nuances of dietary diversity among lactating mothers? Comment 19: The multivariable logistic regression model adjusts for several sociodemographic and maternal characteristics. Nevertheless, it is unclear whether the authors controlled for other potential confounding variables, such as access to healthcare services, exposure to nutrition counseling, or the presence of comorbidities. Did the authors consider using propensity score matching or inverse probability weighting to address potential confounding? Comment 20: The significant association between women's empowerment and dietary diversity is noteworthy. However, the authors should consider conducting a mediation analysis to elucidate the mechanisms underlying this relationship. For instance, does access to education or employment opportunities mediate the relationship between women's empowerment and dietary diversity? Comment 21: The authors used a self-reported measure of maternal nutrition knowledge. However, this may be subject to social desirability bias or recall bias. Did the authors consider using a more objective measure of nutrition knowledge, such as a standardized questionnaire or a performance-based assessment? Comment 22: “Understanding dietary diversity among lactating mothers in these contexts is vital for designing equitable nutrition programs” Add the following reference: 2025. Culinary chronicles of ancient Ebla: A multidisciplinary exploration of diet, nutrition, and health in a 3rd millennium BCE Syrian civilization. Journal of Anthropological Archaeology 78, 101689. Comment 23: The association between attending four or more antenatal care visits and better dietary diversity is intriguing. However, the authors should explore the potential mechanisms underlying this relationship, such as the provision of nutrition counseling or the distribution of food supplements during ANC visits. Comment 24: The strong association between food security and dietary diversity is not surprising. Nevertheless, the authors should consider examining the relationship between food security and dietary diversity in more detail, including the potential impact of food insecurity on dietary quality and nutrient intake. Comment 25: The utilization of multivariable logistic regression to identify the correlates of minimum dietary diversity is commendable, but the modelling approach may have been enhanced by incorporating interaction terms to account for potential synergies between sociodemographic and maternal characteristics. For instance, the interplay between employment status and household socioeconomic position may have yield more nuanced insights into the determinants of dietary diversity. Note 3: The study's reliance on self-reported data for variables such as food security and maternal nutrition knowledge may introduce biases, as respondents' perceptions of these constructs may not align with objective measures. Therefore, it is essential to consider the development of more robust instruments for assessing these variables, such as the use of standardized questionnaires or observational methods. Moreover, the finding that women's empowerment is a significant predictor of dietary diversity raises questions about the underlying mechanisms driving this relationship. Is it the case that empowered women are more likely to prioritize their own nutritional needs, or do they possess greater autonomy to make decisions about food choices within their households? Note 4: The generalizability of the findings to other contexts, particularly in urban or rural areas with distinct sociocultural and economic profiles, is uncertain. Consequently, it is crucial to replicate this study in diverse settings to substantiate the results and identify potential variations in the factors associated with dietary diversity. Ultimately, a more comprehensive understanding of the complex interplay between maternal characteristics, household factors, and dietary diversity is essential for devising effective strategies to promote optimal nutrition among lactating mothers in Nepal and beyond. Note 5: How can healthcare providers and policymakers leverage the association between women's empowerment and dietary diversity to inform the development of interventions aimed at promoting maternal nutrition? What role can community-based initiatives, such as nutrition education programs or support groups, play in enhancing dietary diversity among lactating mothers? By exploring these questions, the study could have provided a more concrete foundation for translating its findings into actionable recommendations for improving maternal health outcomes. Comment 26: The mean DDS was reported as 5.03 (±1.25), with 68% of mothers meeting the MDD-W threshold. However, the process of calculating the DDS and the specific food groups considered under the MDD-W framework are not adequately described. Could the authors provide a detailed explanation of their methodology, including how they handled potential variations in food group classifications and portion sizes? Comment 27: The study found that maternal education, employment status, household wealth, and food security were significant predictors of dietary diversity. Yet, the mechanisms through which these factors influence dietary choices are complex and multifaceted. How do the authors suggest policymakers and practitioners address these socioeconomic determinants to improve maternal dietary diversity, especially in semi-urban settings where access to resources can be limited and uneven? Comment 28: What specific nutrition education strategies do the authors recommend integrating into antenatal and postnatal care services to enhance maternal dietary diversity, and how can these strategies be tailored to the semi-urban context of Nepal? Comment 29: How do the authors account for the potential role of cultural beliefs and practices in shaping maternal dietary diversity in semi-urban Nepal, and what implications does this have for the design of culturally sensitive nutrition interventions? Comment 30: The study highlights the need for multi-sectoral strategies that address both structural and behavioral barriers to improving maternal dietary diversity. What specific policy recommendations do the authors have for the government of Nepal and other low- and middle-income countries facing similar challenges, particularly in terms of integrating nutrition-sensitive interventions with social protection programs and livelihood support for women? Comment 31: “Similarly, employment status was positively associated with dietary diversity” Add the following reference: 2024. A cross-sectional study on demographic characteristics, nutritional knowledge, and supplement use patterns. International Journal of Kinesiology & Sports Science 12 (4), 21-30. Comment 32: How do the intersecting dynamics of urbanization, poverty, and gender norms influence maternal dietary practices, and what are the implications for the design of effective nutrition interventions? Comment 33: What are the most effective strategies for delivering nutrition education and counseling to lactating mothers, and how can these interventions be integrated into existing healthcare systems and community-based programs? Additionally, how can policymakers and practitioners balance the need for culturally sensitive and context-specific interventions with the need for scalable and sustainable solutions that can be replicated across diverse settings?

Reviewer #5: Introduction It looks good and reflects your work properly. Abstract: The abstract represents adjusted odds ratios from Table 4, as it appears internally inconsistent. Check Table 4 and rerun calculations and then write abstract again Introduction: The operational definition of semi-urban should be based on Nepalese administrative classification or a recognized urbanization framework, not a general website. The paragraph on semi-urban food environments is useful but should be linked more directly to the study municipality and available local data. A study area map can be more useful to visualize the study area, and the research gap should be more clarified. Sample size: In line 145, even though they have stated that 700 eligible lactating mothers were identified across 11 wards, the finite population correction formula uses N = 2500. This is not explained. There are also calculation errors related to adjusted n. The authors must clarify the true sampling frame, redo the calculation, and revise the sampling section accordingly. Contradiction between selected sample and completed sample: In line 128, it is stated that 251 mothers were selected using proportionate stratified random sampling, but Table 1 says 263 were selected and then 251 completed interviews (Line 159). This should be corrected too; it may mislead the calculations. Study dates: In the study and design setting, Line (115-117) study period and data collection period are not matched and use a specific date format. MDD-W food groups are incorrectly described in the Methods Although table 3 uses the correct-looking groups, in line 169, you have written "oils and fats." So, check the MDD-W 10 standard food groups of the FAO. Independent variables The research can add more independent variables such as premarital conditions, number of children, age of giving birth, number of family members, etc. Education, age, wealth, food security, and empowerment categories should be described exactly as used in regression.

Table 4 appears mathematically impossible: The final sample size is n = 251, and Table 2 reports dietary diversity as 171 diverse and 80 not diverse. However, many Table 4 rows have totals that exceed n = 251 or contradict Table 2. For example, the age-group rows appear to total 251 for <=24 years and 84 for >24 years, giving 335 observations. Family type, education, employment, food security, nutrition knowledge, and other variables show similar problems. This undermines all reported odds ratios and confidence intervals. Variable coding: There is inconsistent reporting of variable coding. The Methods, Table 2, and Table 4 classify age, wealth, education, and other factors in different ways. Before providing regression findings, the authors should clearly explain all recoding and collapsing choices. The number of predictors compared to the number of result events may cause the regression model to be overfitted. You should describe the precise variables included in the model, provide justification for the model definition, and take into account a more economical model. Regression model: The number of predictors compared to the number of result events may cause the regression model to be overfitted. The authors should describe the precise variables included in the model, provide justification for the model definition, and take into account a more economical model. Inconsistent interpretation of statistical significance The ANC result should be reported with aOR, CI, and additionally an exact P value to make interpretation significant. Conclusion: Even though education and nutrition knowledge have larger reported adjusted odds ratios than food security, you stated food insecurity was the strongest barrier. So, careful justification is needed. References: Careful checking of the reference list is necessary. A number of references, such as the citation for Bennett's Law and URLs with tracking artifacts, are weak, inconsistent, or incomplete.

R2:

Reviewer #4: I highly recommend “Completely Reject” due to the following reasons: 1- Poor response. 2- Chopping response. 3- Erratic report. 4- Incomplete study. 5- Unauthenticated results.

I reiterate my report after blasting All the authors’ responses and add new comments:

Comment 34: The manuscript provides a critical foundation for understanding the complex relationships between dietary diversity, nutrition, and health among lactating mothers in Nepal. However, to fully capture the nuances of these relationships and to inform effective policy and programmatic responses, further research is needed to address the methodological, theoretical, and contextual limitations of the study. By doing so, researchers and policymakers can work together to develop more effective and sustainable solutions to address the pressing issue of "hidden hunger" and promote optimal nutrition and health outcomes among lactating mothers and their children. Comment 35: The study's findings may not be generalizable to other contexts, particularly in urban or rural areas with distinct sociocultural and economic profiles. The authors should discuss the potential limitations of their study in terms of external validity and the need for further research to replicate their findings in diverse settings. Comment 36: The study employed a cross-sectional design, which, while useful for establishing associations, does not allow for the determination of causality. How do the authors plan to address the potential limitations of their study design in terms of implying causal relationships between the observed correlates and maternal dietary diversity? Comment 37: Given the cross-sectional nature of the study, longitudinal research designs could provide valuable insights into how maternal dietary diversity changes over time and in response to interventions. What directions do the authors propose for investigating the dynamics of maternal dietary diversity in semi-urban settings, and how can such research contribute to the development of effective, sustainable nutrition programs? Comment 38: The study's findings also highlight the need for more research on the relationships between dietary diversity, micronutrient intake, and maternal and child health outcomes in semi-urban settings. What are the potential consequences of "hidden hunger" and micronutrient deficiencies for maternal and child health, and how can nutrition interventions be designed to address these needs? Moreover, how can the study's findings be used to inform the development of national nutrition policies and programs, such as Nepal's Multi-Sector Nutrition Plan, and what are the implications for the design of targeted interventions in comparable settings undergoing rapid urban transitions? Comment 39: The study relies on a cross-sectional design, which may not be suitable for establishing causal relationships between dietary diversity and its determinants. The authors should justify the choice of study design and discuss the potential limitations of using a cross-sectional approach. Comment 40: The study uses the Minimum Dietary Diversity for Women (MDD-W) indicator, which is defined as the consumption of at least five out of ten specified food groups in the previous 24 hours. However, the authors do not provide sufficient information on how the food groups were defined and measured. For instance, how were the food groups classified, and what specific foods were included in each group? Comment 41: The study also reports that more than half of Nepali women of reproductive age do not meet the MDD-W threshold, highlighting widespread dietary inadequacy and vulnerability to micronutrient deficiencies. However, the authors do not provide sufficient data to support this claim. What are the specific micronutrient deficiencies that are prevalent among lactating mothers in Nepal, and how do these deficiencies impact maternal and child health? Comment 42: The study highlights the importance of combining nutrition education with broader social and economic support to improve maternal dietary practices. However, the authors do not provide sufficient evidence to support this claim. What specific nutrition education programs and social and economic support interventions have been shown to be effective in improving dietary diversity among lactating mothers in semi-urban settings? Comment 43: The study notes that household food insecurity is a primary barrier to dietary diversity, but the authors do not provide sufficient information on how food insecurity was measured. What specific indicators were used to assess food insecurity, and how were these indicators validated? Comment 44: The study also highlights the importance of understanding dietary diversity among lactating mothers in semi-urban settings, but the authors do not provide sufficient context on the specific semi-urban municipality of Nepal that was studied. What are the unique characteristics of this municipality, and how do these characteristics impact dietary diversity among lactating mothers? Comment 45: The study aims to inform locally tailored, equity-driven interventions to promote maternal dietary diversity and improve health outcomes in rapidly urbanizing LMIC settings. However, the authors do not provide sufficient information on how the study's findings can be translated into practice. What specific policy and programmatic recommendations can be made based on the study's findings, and how can these recommendations be implemented in a way that is culturally and contextually relevant? Comment 46: What would be the justification of using the MDD-W indicator in this context, and how the results of this study can be compared with the other studies which have used different indicators? How the authors can rule out the possibility that the observed associations between dietary diversity and its determinants are due to residual confounding or reverse causality? What would be the potential generalizability of the study findings to other semi-urban settings in Nepal and other LMICs, and how the authors can justify the generalizability of the results? How the study's findings can be used to inform policy and programmatic decisions to improve maternal dietary diversity in semi-urban settings, and what specific recommendations can be made based on the study's results? Comment 47: The authors should provide more context on the specific semi-urban municipality of Nepal that was studied, and discuss the potential generalizability of the study findings to other settings. The authors should also provide more information on the potential implications of the study's findings for policy and programmatic decisions, and discuss the potential avenues on maternal dietary diversity in semi-urban settings. So, you must perform (1) Longitudinal studies to examine the causal relationships between dietary diversity and its determinants, (2) Intervention studies to evaluate the effectiveness of specific nutrition education programs and social and economic support interventions in improving dietary diversity among lactating mothers, (3) Qualitative studies to explore the cultural and contextual factors that influence dietary diversity among lactating mothers in semi-urban settings, and (4) Studies to examine the potential generalizability of the study findings to other semi-urban settings in Nepal and other LMICs. Comment 48: The study's reliance on a cross-sectional design limitations its ability to establish causality between the variables under investigation. The authors' conclusions about the relationships between dietary diversity and various sociodemographic, economic, and household-level factors are thus based on correlations rather than causal links. For instance, the authors suggest that household food insecurity is a primary barrier to dietary diversity, but they do not provide longitudinal data to demonstrate how changes in food security status affect dietary diversity over time. Furthermore, the study's use of the MDD-W indicator as the primary outcome measure may not capture the complexity of dietary patterns among lactating mothers. The MDD-W indicator is based on the consumption of at least five out of ten specified food groups in the previous 24 hours, but it does not account for the quality or quantity of food consumed within each group. This oversimplification may lead to misleading conclusions about the adequacy of maternal diets. For example, a mother who consumes a diet rich in starchy staples but limited in animal-source foods, legumes, fruits, and vegetables may meet the MDD-W threshold but still be at risk of micronutrient deficiencies. The authors also propose that targeted nutrition interventions, such as behavior change communication, nutrition education, and women's empowerment programs, can improve dietary diversity among lactating mothers. However, the evidence for these interventions is largely based on studies conducted in rural or urban areas, and it is unclear whether these interventions would be effective in semi-urban settings. The unique socioeconomic and environmental characteristics of semi-urban areas, including mixed livelihoods, evolving food systems, and varying access to services, may require tailored interventions that address the specific needs and constraints of these populations. Comment 49: The study's sample size and selection criteria are not clearly justified. The authors do not provide information on how the sample size was determined or how participants were selected, which raises concerns about the representativeness of the sample and the potential for selection bias. Furthermore, the study's focus on lactating mothers in a single semi-urban municipality limits the generalizability of the findings to other populations and settings. Comment 50: The authors' conclusion that the study's findings can inform locally tailored, equity-driven interventions to promote maternal dietary diversity and improve health outcomes in rapidly urbanizing LMIC settings is overly optimistic. While the study provides some insights into the dietary diversity and correlates among lactating mothers in a semi-urban municipality of Nepal, the methodological limitations and lack of generalizability of the findings undermine the study's potential to inform policy and practice. Further research is needed to address the complex and context-specific challenges of promoting dietary diversity and improving maternal and child health in semi-urban settings. Comment 51: The study's sample size calculation appears to be based on an estimated prevalence of minimum dietary diversity (45%) from a similar study done in a periurban area of Nepal. However, the authors do not provide sufficient justification for using this specific prevalence estimate, which may not accurately represent the study population. This raises questions about the generalizability of the findings. Furthermore, the study uses a 24-hour dietary recall method to assess dietary diversity, which may be subject to recall bias. While the authors attempt to minimize this bias by using probing questions and locally familiar food examples, the reliability of this method is still uncertain. It would be beneficial to explore alternative methods, such as food diaries or weighed food records, to validate the findings. Comment 52: The study also categorizes women's empowerment as a binary variable, which may oversimplify the complex and multifaceted nature of empowerment. The decision to dichotomize this variable may lead to loss of information and potential misclassification of participants. A more nuanced approach, such as using a continuous or ordinal scale, may provide a more accurate representation of women's empowerment. Comment 53: The study controls for various sociodemographic variables, including wealth quintiles, which are collapsed into three categories. However, the authors do not provide a clear justification for this categorization, which may mask important differences between the wealthiest and poorest quintiles. It is essential to explore alternative categorizations or use continuous variables to capture the full range of wealth disparities. Comment 54: The study's regression analysis reveals several significant associations between independent variables and dietary diversity. However, the authors do not provide sufficient discussion on the potential mediating or moderating factors that may influence these relationships. For instance, the role of food security, nutrition knowledge, and women's empowerment in mediating the effect of sociodemographic variables on dietary diversity is not adequately explored. Comment 55: The study's external validity is limited by its focus on a semi-urban municipality in Nepal. The findings may not be generalizable to other contexts, such as rural or urban areas, or to different cultural or socioeconomic settings. The authors should discuss the potential implications of their findings for other populations and settings, and provide recommendations for future studies to address these knowledge gaps. Comment 56: The sample size calculation appears to be based on an estimated prevalence of minimum dietary diversity of 45% from a similar study in a periurban area of Nepal. However, the applicability of this estimate to the current study's population is questionable, given the potential differences in socioeconomic and cultural contexts between the two settings. Comment 57: The use of a finite population correction formula to adjust the sample size may not have fully accounted for the complexities of the study's sampling frame, which comprised 700 eligible lactating mothers identified through field enumeration. The fact that only 251 mothers completed the interviews, resulting in a response rate of 95.4%, may have introduced biases that were not adequately addressed. For instance, the exclusion of 12 mothers who declined to participate or were unavailable despite repeated follow-up visits may have led to an overrepresentation of more cooperative or accessible participants, potentially skewing the results. Another concern lies in the assessment of dietary diversity using the MDD-W indicator, which relies on a 24-hour dietary recall method. While this approach may provide insight into the variety of foods consumed, it may not capture the nuances of dietary habits and preferences that are shaped by cultural, social, and economic factors. Additionally, the classification of foods into ten groups may oversimplify the complexity of dietary patterns, potentially masking important variations in food consumption that are relevant to maternal health outcomes. Comment 58: The study's regression analysis, which aimed to identify the correlates of maternal dietary diversity, also raises questions about the selection of independent variables and the potential for multicollinearity. Although the authors reported that none of the variables exceeded the threshold for multicollinearity (VIF < 2), the inclusion of multiple sociodemographic variables, such as maternal age, educational attainment, and employment status, may have introduced redundancy and compromised the stability of the model estimates. Note 1: The study's generalizability is limited by its focus on a specific semi-urban municipality in Nepal, which may not be representative of other contexts, either within or outside the country. The lack of consideration for potential contextual factors, such as seasonal variations in food availability, agricultural practices, and local food systems, may have further constrained the study's ability to capture the complexities of maternal dietary diversity in this setting. What is the potential impact of the finite population correction formula on the sample size, and how does it affect the generalizability of the results? How does the use of a 24-hour dietary recall method capture the nuances of dietary habits and preferences, and what are the potential biases associated with this approach? What is the justification for the selection of independent variables in the regression analysis, and how does the potential for multicollinearity affect the model estimates? How does the study's focus on a specific semi-urban municipality in Nepal limit its generalizability, and what are the implications for the development of context-specific interventions to promote maternal dietary diversity? Comment 59: The demographic characteristics of the study population, as outlined in Table 2, show a skew towards younger, upper-caste, and Hindu lactating mothers. This raises questions about the representativeness of the sample, particularly given the ethnic and socioeconomic diversity of Nepal. It is essential to consider the potential biases and limitations of these demographics in the interpretation of the findings. Comment 60: The study's primary outcome, dietary diversity, as assessed by the MDD-W indicator, reveals that 68.1% of lactating mothers met the minimum threshold. However, the mean dietary diversity score of 5.03 (SD ± 1.25) warrants further exploration, as it suggests a narrow range of food consumption. The fact that all participants consumed starchy staples, such as rice, maize, and potatoes, is not surprising, given their cultural significance and widespread availability in Nepal. Comment 61: The low intake of nutrient-dense food groups, such as eggs (29.1%), nuts and seeds (17.9%), and vitamin A-rich fruits and vegetables (15.5%), is concerning and may indicate micronutrient deficiencies among lactating mothers. This is particularly worrisome, as it may lead to "hidden hunger," with potential long-term consequences for both maternal and child health. Comment 62: The study's methodology and data analysis also raise several questions. For instance, the MDD-W framework used to assess dietary diversity is based on a 24-hour recall period, which may not accurately capture usual dietary patterns. Moreover, the study does not account for potential seasonal variations in food availability and consumption, which could impact dietary diversity. How do the authors justify the generalizability of their results to the broader Nepalese population, given the demographic characteristics of the study sample? What steps were taken to validate the MDD-W framework in the context of this study, and how did the authors ensure that the 24-hour recall period accurately reflected usual dietary patterns? Can the authors provide further insight into the socioeconomic and cultural factors that contribute to the low intake of nutrient-dense food groups among lactating mothers in this population? How do the authors propose to address the potential micronutrient gaps and "hidden hunger" among lactating mothers, and what implications do these findings have for maternal and child health policies in Nepal? Comment 63: The study's reliance on the MDD-W indicator as the primary outcome of interest is problematic. The MDD-W indicator, which assesses dietary diversity by measuring the consumption of at least five out of ten defined food groups, may not be a comprehensive measure of nutritional adequacy. The fact that 68.1% of lactating mothers met the minimum dietary diversity threshold, yet had low consumption of nutrient-dense food groups such as eggs, nuts and seeds, and vitamin A-rich fruits and vegetables, suggests that the MDD-W indicator may not capture the complexity of nutritional needs during lactation. This discrepancy raises questions about the validity of using the MDD-W indicator as a sole measure of dietary diversity in this context.

Reviewer #6: Reviewer Recommendation I carefully reviewed the revised manuscript and the authors' responses to the previous review comments. I am pleased to note that all of my comments and suggestions have been satisfactorily addressed in this revised version. The authors have made substantial improvements to the manuscript, enhancing its scientific rigor, clarity, methodological transparency, and overall quality. The manuscript now presents a well-structured and valuable contribution to the field of maternal nutrition and public health. The study addresses an important public health issue, employs appropriate methodology, and the findings have clear implications for policy and practice. Based on the satisfactory revisions, I have no further comments and recommend that the manuscript be accepted for publication in its current form.

R0:

Reviewer #1: Many congratulations to the authors of this paper. Without a doubt, a lot of work went into this. I appreciate the details of the report and the use of simple language. Generally, it is good work and I only have a couple of suggestions.

1. To improve on the method (procedures), consider providing some information about the “Study staff”. Where they were sourced, and training, if any. I imagine this also had an effect on results.
2. Line 136; capturing of biometrics. It might be good to further reiterate the voluntariness of the fingerprint biometric capturing
3. Line 113 and 181; to address the inconsistency in reported period. Align the period for consistency, July 2023 to Dec 2024 or July 2023 to Jan 2025?

Reviewer #2: Very promising research in terms of aiding HIV prevention and treatment interventions. Couple of comments for the authors:

1. It is good practice to include the proportion of females in your tables e.g. Table 2 and 4.

2. How were the 8 communities in your study selected? Were any efforts made to ensure that these communities were comparable beyond the population count and communities being in catchment area of a government-associated health center providing HIV care?

3. It is good practice to spell out an acronym such as AUDIT-C in line 240 when it is used for the first time.

4. Your study identified some interesting results which I think you could set up to inform future studies and interventions. One of such is the finding that venues with condoms available on site were associated with higher odds of identifying persons with undiagnosed HIV. One would expect the opposite given the crucial role condoms play in HIV prevention. You should offer more insights and discussions into results such as this which are somewhat unexpected. Insights need not be definitive since you may not have the data or literature to back up claims but it could offer plausible reasons into what may be responsible for this observation and set up the need for further inquiry. In this case for example, the increased odds of undiagnosed HIV in venues offering condoms may be due to factors such as availability does not necessarily mean people use them, or it may suggest improper usage. Since people however associate condoms to HIV prevention, they may therefore not take the risk of transmission serious, thus contributing to undiagnosed HIV. If any or all of this is the case, a need for more condom availability as suggested in line 324 may not enough if people are not using them when they are available or use them improperly. This could be further explored in future research - looking at what may be responsible for increased odds for undiagnosed HIV despite the availability of condoms at these venues. Or you can simply look for literature that may have explored this and discuss them.

R1:

Reviewer #1: (No Response)

Reviewer #2: (No Response)

Reviewer #3: This is an interesting and well-written report. The authors assess the characteristics of alcohol-serving sites and how they affect the linkage to health care and screening for HIV.

Just few issues: 1. The yield of screening, linkage, newly diagnosed etc.. per venue are amng the main results of this manuscript. It is so that the tile has the word yield. So I would suggest to have a figure to show at least overall yield (a bar plot with confidence intervals).

1. About the GEE description in the statistical section:
2. Make it clear what family was used (binomial?) and what link (logit?) was used
3. What working correlation was used here? State this.

4. Whether you used naive or robust standard errors.

5. Tables 3 an 5: please state somewhere in the caption number of participants ​

Reviewer #4: This is a very interesting, relevant, and well-executed manuscript addressing an important public health opportunity for HIV prevention and case-finding in rural East Africa. The study is original, programmatically meaningful, and highly valuable from a public health perspective because it explores how venue-level characteristics can help identify settings where HIV screening, linkage, and prevention interventions may be most impactful.

The revised version has improved substantially. The authors have addressed the main concerns raised in the previous round, particularly by clarifying the role and training of study staff, the voluntary nature of biometric collection, the selection of study communities, the expansion of the acronym AUDIT-C, and the interpretation of the unexpected findings related to condom availability at venues. These revisions strengthen the manuscript.

Overall, I believe this paper is suitable for publication after minor revision, as only a few residual issues remain.

Minor comments

1. Please check internal numerical consistency in the Results section. In the Results text, the manuscript states: “Of 7,774 participants…” whereas the total number reported throughout the manuscript, including Table 4, is 7,744. This should be corrected for consistency.

2. Please carefully review citation numbering throughout the revised manuscript. After the addition of the SEARCH SAPPHIRE reference, some in-text citations appear to have shifted incorrectly. For example:

the citation used for the national HIV testing/treatment guidelines appears inconsistent with the revised reference order;

the citation attached to the GEE methodology may also be misnumbered;

some discussion citations may no longer correspond to the intended references.

A full check of in-text citations against the revised reference list is recommended before acceptance.

1. Please review the reference list for duplication and ordering errors. There appears to be duplication of at least one citation related to HIV prevention in alcohol venues. The reference list should be checked carefully to ensure that:

duplicate references are removed,

all citations are uniquely numbered,

and numbering matches the in-text citations throughout the manuscript.

1. Clarify the handling of missing data in the regression models. The manuscript notes missingness for some variables, including patron/worker status, marital status, bar area, and condom availability. It would strengthen the Methods if the authors briefly clarified whether the regression models were based on complete-case analysis and, if so, whether the analytic sample varied across models.

2. Consider slightly tempering the wording of the conclusion. The conclusion states that certain venue types “should be prioritized” for interventions. Since the analysis is observational, a slightly more cautious phrasing such as “may be prioritized” or “may represent high-yield settings for targeted outreach” would better align with the design and findings.

Overall assessment

This is a strong and policy-relevant paper. It highlights a creative and pragmatic approach to HIV prevention and screening in high-risk community settings and offers findings that could directly inform differentiated public health outreach strategies. The remaining issues are minor and primarily editorial/methodological clarification points.

Recommendation: Minor Revision

R2:

Reviewer #1: Great work. I appreciate the attention to detail on the issues raised by the reviewers.

Reviewer #3: All comments have been addressed satisfactorily.

Reviewer #4: Dear Authors, Thank you for submitting the revised manuscript (PGPH-D-25-01876R2) titled "Influence of alcohol-serving venue characteristics on yield of HIV status-neutral screening in rural East Africa" to PLOS Global Public Health. I have reviewed the revised manuscript and the responses to reviewers. The authors have adequately addressed the majority of the comments raised in the previous round. The manuscript is well-written and the revisions substantially strengthen the work. Before final acceptance, I recommend the authors verify the following minor outstanding points:

Confirm that confidence intervals are displayed in Figure 2, as specifically requested by Reviewer #3. Provide confirmation that the full citation list has been audited against the in-text references throughout the entire manuscript, including the Discussion and Conclusions sections.

These are minor points that do not require an additional full review. I recommend acceptance pending confirmation of these two items.

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Reviewer #1: No

Reviewer #3: No

Reviewer #4: Yes: Esteban Ortiz Prado

R3:

Reviewer #1: Well done. It is good to see you demonstrate rigor!

Reviewer #4: no more comments

R0:

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: Conteh and colleagues report on a secondary analysis of previously collected data wherein they examine the prevalence and risk factors of respiratory tract infections (RTIs) at 1 and 3 months post a medically attended diarrheal illness among children 6-35 months of age in 7 countries for a 2-year period. The study is observational and the children in the cohort were prospectively enrolled. Study strengths included a large sample size, data over a 2-year period, and geographic diversity in terms of LMIC.

There are some issues that need to be addressed by the authors: 1) A significant limitation is the lack of a control group of infants and children matched for age, sex, season, country, etc., to make sense of what the data mean in terms of the medically attended diarrheal illness. From the data, I cannot tell how other children without a medically attended diarrheal illness would have fared during the same time period in terms of RTI occurrence. How many would have been stunted or underweight? 2) The first sentence of the Abstract is clunky and should be broken into two for clarity. 3) The second sentence of the Abstract mentions "immune stress". This is a vague term that needs to be clarified. Malnutrition is an immune deficiency state as it affects both innate and adaptive immunity, and many of the children in the study had it. 4) Lines 157-161 address the "potential correlates of RTI". I would have included seasonality as well since respiratory illnesses are more common in the winter months. 5) Figure 1 mentions 15 children who died before any follow up. Did they die of the diarrheal illness or some other issue? And what does "eligibility revoked" mean for the 6 children? 6) Table 2: At presentation for the diarrheal illness, 36.5% of the children had signs of a lower RTI, as defined by the authors. Do the authors know if these symptoms had resolved and new RTI symptoms developed by the 4-week visit or were many these symptoms just lingering for a long time? 7) Malawi appears to be an outlier in terms of prevalence of RTIs, including pneumonia diagnoses (22.6%) vs other countries in the study (0.2-3.2%). Any explanation for this? These results skew the data. (Supplementary Table 2) 8) In Supplementary Table 3, cough (as an example) was described in 1131 children at 4-weeks and 1429 at 3 months, but the provided total was 2175. This suggests that 385 children may have gotten ill with cough more than once. For pneumonia, there is a discrepancy of 24 children suggesting that they got this diagnosis more than once. The authors need to provide an explanation for these discrepancies. 9) In Table 4, Malawi has the highest percentage of household members <5 years of age, followed by the Gambia and Pakistan; these 3 countries had the highest prevalence of RTIs during the follow up period suggesting this as a very important variable in terms of RTI risk. 10) Table 2: Who had the moderate or severe diarrhea? Were they the malnourished or wasted children? 11) There is no mention of breastfeeding for the infants in this study. This factor could potentially explain why infants 6-11 months of age may have had a lower RTI prevalence at follow up. 12) Figure 3 shows that the risk of RTI (while not statistically significant) was lower with moderate (0.78, CI 0.54-1.13) and severe (0.57, CI 0.28-1.15) wasting compared to infants without wasting, although this did not reach statistical significance. This merits further examination since the results are counterintuitive. 13) Since most RTIs are viral in etiology, it is hard to understand how improved vaccination rates would help. The WHO Africa Immunization schedule does not include RSV or COVID-19 vaccines. Influenza vaccine is recommended, but the authors give us no idea of its uptake. Pneumococcal vaccine would be the only one that could help with one of the causes of pneumonia.

R0:

Reviewer #1: This manuscript examines associations between ambient temperature and cardiovascular hospitalizations in Brazil (2010–2024) using multi-city time-series and a two-stage DLNM/meta-analysis framework. The authors report higher risk at colder temperatures (≤19 °C), neutral effects ~19–24 °C, and decreasing risk at higher temperatures. They also compare “tropical” vs “temperate” regions and find no significant differences. The topic is important and the two-stage DLNM approach is appropriate in principle. However, issues around outcome labeling (“incidence”), denominator/rate construction, city inclusion criteria, modeling choices (lag length; time-spline df), climate classification, and data availability must be addressed. I recommend major revision focused on (i) correcting the descriptive epidemiology and terminology, (ii) strengthening and documenting the modeling choices with sensitivity analyses, and (iii) clarifying data/selection procedures. Please see below my comments:

1) Throughout, the paper calls the outcome “incidence,” but the data are hospital admissions, not incident disease. Please replace “incidence” with “hospitalization rates/counts” everywhere, including title, abstract, figures, and discussion. (e.g., Abstract; Methods; mapping by state). Using “incidence per 100,000” with hospitalizations is potentially misleading to readers. 2) Excluding any city with fewer events than number of observation days (5,296) is unusual and may exclude many smaller cities/capitals, biasing toward large urban centers (Exclusion criteria). Consider alternative strategies (e.g., weekly aggregation, borrowing strength via hierarchical modeling, or keeping cities and letting the multivariate meta-analysis shrink unstable estimates). At minimum, justify this threshold, quantify how many cities were dropped by region, and assess sensitivity to this rule. 3) The spline for long-term/seasonal control is specified as ns(time, df = 70) “equivalent to 10 per year” (Appendix). Over 2010–2024 (~14 years), 10 df/year would be ~140 df, not 70. Please correct the description and justify the chosen df/year with references or AIC/QAIC diagnostics. Also report checks for residual autocorrelation/overdispersion and the overdispersion parameter. 4) Knot placement: exposure knots are “equally spaced over each city’s temperature range.” Consider standard practice (e.g., percentiles of the pooled temperature distribution) and report the centering temperature (e.g., MMT) used to compute RRs. 5) The model adjusts for DOW and a time spline, but no control for relative humidity, holidays, or air pollution—important confounders/effect modifiers in cardiovascular admissions studies. Even if not available nationwide, please conduct sensitivity analyses (where data exist) or justify omission. The Discussion acknowledges humidity/pollution but the model does not. 6) How were cities assigned to “tropical” vs “temperate” zones? Many states span multiple climate subtypes. Please specify classification source and rule, and show a table of city-level climate assignments. Also, the North region’s pooled analysis excludes Belém (Methods) without justification—please explain and provide sensitivity including Belém. 7) The primary pooled curve suggests decreasing RR at higher temperatures (Figure 3). Before interpreting as “protective,” please: • show city-specific and region-specific exposure–response curves and heterogeneity (I², τ²), • explore different centering/MMT choices, • extend lags, and • assess potential exposure misclassification (station coverage/representativeness, urban heat island, station relocations). These steps will help distinguish a truly protective effect from modeling or exposure biases.

8) The Data Availability statement says “Raw data are available upon reasonable request”, which is incompatible with PLOS policies that require open, unrestricted access to underlying data (with rare exceptions). Please deposit de-identified, aggregate daily counts and the analysis code (R scripts) in a public repository (e.g., Zenodo/OSF) and update the statement accordingly.

9) Describe how hourly station data became a city-level daily mean (station selection radius, multiple stations averaged, handling missing hours/days, QC flags).

10) Provide the exact crossbasis specification (knots/locations) and meta-analysis model formula, including moderators (climate type). Report heterogeneity statistics and (ideally) leave-one-out sensitivity.

11) Improve resolution; add axes labels/units (°C on x-axis, RR on y-axis), show tick marks, and consider 2-panel figures for pooled + regions with the same y-scale for comparability.

12) Add a table listing included 103 cities, population, period coverage, number of events, mean temperature, and assigned climate type.

13) Clarify selection bias from excluding most cities; discuss exposure misclassification (station siting/relocations; representativeness for large urban areas); acknowledge lack of adjustment for humidity/pollution/holidays and for age structure differences when presenting descriptive rates.

Reviewer #2: The manuscript requires substantial revision. The methodology section is insufficiently developed, as it omits critical components such as the study design, study setting, target population, sample size, sampling methods, and details of the statistical analysis. Furthermore, there is a clear discrepancy between the described methodology—particularly the statistical analysis—and the way the results are presented. In addition, the manuscript lacks a conclusion, which is essential for summarizing the findings and their implications. See More detailed comments in the attached reviewed document.

R2:

Reviewer #3: A previous reviewer has already noted quite a few quantitative shortcomings such as the descriptive epidemiology and terminology, strengthening and documenting the modeling choices with sensitivity analyses, and clarifying data/selection procedures. The threshold exclusions were a concern as well as diagnostic checks for df/yr and checks for over dispersion, and various modeling clarifications needed. In addition, standard two-stage analytical approach required clarification which the investigators also addressed. Text additions as well as tables sufficed to meet a number, if not most, of these concerns. Other review concerns dealt less stringently with the modeling corrections and presentation than with more general concerns. Having reviewed the latest version it appears that the latest effort has cleaned up the statistical objections noted. The paper reads much better and the tables and figures are well formatted and interpretable. The conclusion follows from the revised document in that the investigators have had success in associating ambient temperature with hospitalization for cardiovascular diseases across more than 100 cities throughout the national territory.

R0:

Reviewer #1: Overall assessment This manuscript examines an important research question about the relationship between abortion legality and severity of abortion complications in sub-Saharan Africa using WHO MCS-A data. This research builds critically on prior evidence on the relationship between legal and abortion incidence, connecting abortion laws to morbidity and the direct consequences of limiting abortion access. While the topic is highly relevant and the data source is robust, there are several methodological concerns that should be addressed before publication.

Main concerns While the paper’s topic and research are critically important, there are a number of important methodological limitations that need to be considered – and there currently undermine the paper. These mainly relate to the sample of countries and categorization of abortion laws. There is only one country included that is broadly legal and one country where it is prohibited all together, and then all 9 other countries are grouped into “for health indications” despite wide variation in their abortion laws on paper and in practice. Without country fixed-effects or other country-level controls in the model, it is not clear to me how the results of this paper are being attributed to abortion laws and not other factors that might vary across countries. It is not clear to me right now that the modeling approach is sufficient to address this concern. I have proposed below a few approaches for how this could be addressed.

This ties to the second concern, which is the lack of any proposed mechanisms – or exploring/testing of those mechanisms. I see two primary pathways through which this relationship would exist between abortion legality and severity of abortion complications. One is a story of access, where people have less access to safer methods/providers the more restricted abortion is, and therefore are more likely to use less safe methods that result in complications. The second is a story of legal risk and fear, where people delay coming for post-abortion care in more restrictive contexts, increasing their risk for more severe complications. Both of these mechanisms could be explore through either additional controls in the models or sensitivity analyses.

For example, if the theory is that delays in care could be driving this, it would be important to include controls for facility access more broadly across countries that is unrelated to abortion, to ensure that access to care differences between countries could explain some of these associations (e.g. control for facility-delivery levels between countries in the model). If it’s about access to safer services, then the authors really need to grapple with and explain their counterintuitive finding around the variable looking at misoprostol availability by country. About 10% of the case were severe complications when miso was available for use, versus 7% when not (I calculated this based on N’s in the table, but this finding is not actually presented in the paper, which I was surprised by). This was very confusing to me and ran counter to what I had been assuming one of the central proposed mechanisms of action was.

MAJOR COMMENTS

Methods

• Model variable selection: The manuscript uses a p<0.20 threshold in bivariate analyses to select variables for inclusion in the adjusted logistic regression model. While this statistical threshold is sometimes used in epidemiological research, it is also critiqued as an approach for modeling building and comes with statistical issues that need to be considered. Variables selected through this data-driven approach may introduce selection bias into the final model. The relationship between the primary predictor (abortion law category) and outcome may be confounded or distorted by the inclusion of variables that were selected based on their empirical association in this particular dataset rather than theoretical justification. Testing multiple variables at p<0.20 without adjustment for multiple comparisons compounds the problem of false positives. Please provide a clear justification for the p<0.20 threshold, including: (1) why this approach was chosen over theory-driven variable selection; (2) how this approach guards against the statistical issues outlined above; and (3) what steps were taken to avoid data-driven selection bias in the final model. • Abortion law categorization: Only one country (Mozambique) represents the 'on request' category, and only one country (DRC) represents the 'prohibited altogether' category. This raises serious concerns about whether the observed associations reflect true legal effects or are driven by country-specific factors unrelated to law. This is not addressed in the paper and raises serious concerns with the interpretation of the paper’s findings. I have proposed below other ways the abortion laws could be categorized and/or other sources of data for sensitivity tests. These are essential given the serious methodological issues with the current model. o The decision to combine 'abortion to preserve health' and 'abortion to save a person's life' into a single category ('abortion for health indications') obscures potentially meaningful legal variation and raises questions about the study's ability to capture the true relationship between law restrictiveness and health outcomes. These two legal grounds represent meaningfully different levels of restriction. Laws that permit abortion only to save a woman's life are substantially more restrictive than those that permit it to preserve health more broadly. The 'health' exception in many countries encompasses physical and mental health and can be interpreted more expansively, while the 'life' exception typically requires immediate life-threatening circumstances. o Even within the combined category, implementation varies dramatically across countries. Some countries with 'health' exceptions have developed clear guidelines and accessible services, while others maintain highly restrictive interpretations. This within-category heterogeneity may be larger than between-category differences, potentially washing out the true relationship between abortion legality and outcomes. Did the authors consider any sensitivity tests using other ways of classifying country abortion laws? For example, did you look at the WHO Abortion Policies Database as an alternative source for a sensitivity analyses? This would help get better at the issue between legality versus application of the law and impacts on abortion access. In addition, it could help address the current limitations of using the CRR categorization of abortion laws, which leave you with only one restrictive and one legally permissible country. o Alternatively, you could create more categorizations, or consider collapsing “to save a life” with “restricted all together” vs. “for health reasons” and “on request” - other ways of collapsing legal categories need to be considered to address the problems of one country pre category and country-level confounding. • Country-level controls: Given the limitations in the sample of countries in each abortion law category, must more work needs to be done exploring necessary country-level controls to address the very serious risk of confounding in the current model. This could include variables that address overall health system access (proxies like facility delivery), or variables that control for post-abortion care provision (which would also impact severity outside of abortion legality) or variables that could get at fear in seeking care (criminalization’s of people seeking PAC). • Standard errors: The manuscript does not adequately address clustering of observations within facilities and within countries. Women seeking care at the same facility are likely to be more similar to each other than to women at other facilities, and facilities within the same country share legal and health system contexts. Standard errors should account for this clustering, likely through multilevel modeling or robust standard errors clustered at the facility or country level. The current approach may underestimate standard errors and overstate statistical significance.

Data

• WHO-MCS-A: Elsewhere I have seen WHO MCS-A described as being at secondary and tertiary facilities, but here it’s described at all facility levels. Please clarify this discrepancy from what is reported in other WHO publications on this dataset. It also wasn’t clear by other regions in the MCS-A survey were excluded, and the decision was made to just focus on SSA. • Facility inclusion/exclusion: What is the potential biases that come from the survey excluding many lower-level facilities? I am thinking this could differ between countries – for example, with more permissive abortion laws, is there more SAC and PAC availability at lower-level facilities? And if so, this could actually lead to underestimating the relationship by excluding lower-level facilities which would have more non-severe cases. The authors note in the discussion that they think the exclusion of lower-level facilities doesn’t bias their findings since they capture more of the severe cases. However, I would argue that there are additional biases imposed by excluding more of the non-severe cases that may be at the lower-level facilities, especially if the proportion of non-severe cases treated at lower-level facilities differs by country abortion laws. • Missing data: The manuscript excludes 45% of observations due to incomplete records, and the supplementary tables indicate that most variables aside from severity differ significantly between complete and incomplete records. This substantial amount of missing data raises important concerns. That data are not missing at random introduces potential bias in a complete case analysis. At minimum, please provide more detailed information about patterns of missingness (which variables had most missing data, whether missingness was clustered by facility or country) and discuss how missing data might bias your findings. • By relying on data from medical record extraction, was there any concern that abortion severity and information input into medical records could be impacted by country abortion laws? I’m thinking here of Siri Suh’s ethnographic work in Senegal on post-abortion care and findings around how abortion laws and provider’s fears and stigma may shape what is put into medical records to being with, which would be another source of bias to consider in this study. The manuscript notes that poor record-keeping in low- and middle-income countries contributed to missing data, and suggests this particularly affects sensitive topics like abortion. This raises the question of whether systematically poorer data quality in countries with more restrictive laws could itself bias the results. If restrictive legal environments lead to both worse health outcomes AND worse data quality, complete case analysis may underestimate the true effect of restrictive laws. • Where there any issues in the WHO-MCS-A sample with non-response from facilities selected? No information is provided on facility non-response to the survey, only incomplete records.

Discussion

Most of the discussion focuses on ways to improve access to safe abortion care and the need for policy change. I think more time in the discussion needs to be placed diving into the findings of this paper – what they do and don’t show us, and thinking through the mechanisms through which this happens. The discussion right now doesn’t seem appropriate and is better placed in the conclusions or a new section added on policy implications.

MINOR COMMENTS • Please check the references. Some of are incomplete in the reference list (eg. #16) • 251-252 - I think you meant to say least rather than less safe here, otherwise it sounds as if the less safe abortions, or unsafe versus safe. Currently it makes is sound like less (versus safe or least safe) are leading to more complications

R1:

Reviewer #1: Thank you for the opportunity to review this revised submission. The authors have thoughtfully addressed many of my initial comments, including adding facility-clustered standard errors, elaborating on the treatment of missing data, clarifying the facility inclusion criteria, and engaging more fully with the proposed mechanisms. These changes have strengthened the paper and I appreciate them.

My central concern from the first review remains unresolved, and it is a fundamental one - whether the analysis is designed to measure what it claims to measure.

The authors defend their categorization of laws on the basis of discussion within a multidisciplinary team and reflecting real differences in abortion law application and access. I do not disagree with the conceptual categorization and process of generating these categories. The problem is that the sample of countries does not provide sufficient variation within these categories. The exposure of interest, abortion law category, does not vary within countries, and two of the three categories contain only one country each. The "on request" category is Mozambique alone, and the "prohibited altogether" category is the Democratic Republic of Congo alone. Every odds ratio in Table 2 is therefore, in substance, a comparison of Mozambique against the nine health-indication countries, and of DRC against those same nine countries. Any country-level characteristic that differs across these groupings, including health-system capacity, referral patterns, urbanization, income, and the quality of medical recordkeeping, is fully confounded with the law variable. There is no way, within this design, to separate the effect of the law from the effect of being Mozambique or being DRC.

This is why country fixed effects, the standard remedy, cannot be added, as the law variable is collinear with country. Moreover, the individual-level covariates in the adjusted model (marital status, education, gestational age, parity, and prior abortions) do not help, as they do not vary with the exposure. Adjusting for individual characteristics cannot remove confounding at the country level.

The authors respond that "this is a constraint of the available data" and note it in their limitations. This is not a limitation in the ordinary sense. It undermines the analysis, because the variation being modeled across the three categories cannot be separated from comparisons specific to these individual countries. I do not believe the paper is publishable with the current categorization, because the authors cannot demonstrate that the results reflect abortion law rather than other country-level factors, and therefore cannot rule out spurious conclusions arising from the identification strategy.

The authors' own discussion of the misoprostol result makes this point for me. They now write that the higher severity observed where misoprostol is approved "likely reflects country-level confounding rather than a causal effect," noting that the three non-approval countries "may differ from other countries in ways that affect complication severity independently." I agree with that reasoning. But it is precisely the reasoning that applies to the headline finding. The authors invoke country-level confounding to set aside a result they find counterintuitive, while declining to apply the same logic to the result they wish to report. If country-level confounding can generate the misoprostol association across a three-country contrast, it can generate the law association across an even smaller one, with a single country in each of the extreme legal categories. The manuscript needs to reconcile these two positions. The authors in their response have refused all suggestions I provided to try to address this, and most concerning, offered no alternative proposal themselves. This is not a serious engagement with a methodological issue that threatens the central findings of this paper.

These methodological problems make the paper's language particularly problematic. The abstract describes the model as estimating "the effect of restrictive abortion laws" and states that "easing restrictions on abortion could significantly reduce abortion complications," and the conclusions extend this to specific policy prescriptions. These are causal claims. Given the identification limits above, the evidence supports only a descriptive statement - that the severity of abortion complications differs across these eleven countries, which also differ in their abortion laws. It does not support a causal one.

I do not see how this paper can be published with such a fundamental problem in the identification strategy in their model. I therefore ask the authors either to reconsider the analysis to address this fundamental problem, or to substantially rewrite the paper so that it does not merely list the issue as a limitation but makes clear how weak the analytic basis for this association is.

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: Thanks for the opportunity to review the manuscript. While it has sufficient merit and it addresses an important issue it requires major revision to be scientifically suitable for publication. My specific comments for consideration is below:

Abstract 1. First need to mention that NCD is a growing problem in Nepal and that there is increasing risk associated with several risk factors. 2. Briefly state who FCHVs are and what they are currently doing. 3. Line 30- What do you mean by organizational representatives? 4. Tighten the recommendations, now it looks very broad

Introduction 1. You should use a reference for the first sentence 2. Detail out a bit more around community health workers globally and how they can contribute to management of chronic disease using a community-based approach. 3. More perspective is required, such as around government health system trust issues associated with FHCV intervention in NCD management in Nepal. 4. Lines 68-74: Why you bring forward mHealth issues here? Is the FCHV delivers interventions using mHealth? Need clarity around this issues. 5. I do not see in objective statement for the research rather findings are presented in the last paragraph of Introduction. Please state your objective and rationality for the research in the last paragraph.

Methods 1. How are the participants recruited? What are the eligibility criteria for selection? Need more details on participant recruitment. 2. Methods section is inadequate. More detailed description of data collection, management and analysis is required.

Results Results seems to be quite elaborative but scattered. It would be good to structure the result using any framework such as Socio-ecological model.

Discussion The discussion section looks mostly focusing on the implementation and sustainability of FCHVs in NCD management which is good. But discussion needs to be aligned with the result section. I would ask the authors to put more thoughts around structuring discussion and results which are aligned together.

Reviewer #2: Dear authors, Hello Thank you for the opportunity to review this valuable and timely manuscript. The topic of community-based approaches to non-communicable disease care in peri-urban Nepal is highly relevant, and the study provides rich qualitative insights from multiple stakeholders. The manuscript has several notable strengths, including the relevance of the research question, inclusion of diverse participant groups, and use of authentic, contextualized qualitative data. However, there are a number of areas where clarification and revision would strengthen the manuscript. My major and minor comments are outlined below. Major Comments 1. The manuscript highlights several systemic and structural challenges, particularly around sustainability of the FCHV volunteer model, supply chain gaps, and mistrust in public services. However, the final conclusions frame community-based task-sharing as highly promising without sufficiently addressing these constraints. Reframe conclusions to more explicitly acknowledge these limitations and avoid overgeneralization of feasibility. 2. While thematic analysis is well-described, the interpretation remains largely descriptive. A guiding framework (e.g., WHO Task-Sharing Implementation Framework, Health System Trust Framework, or CHW Motivation Theory) could deepen the explanatory power of the findings. Introduce a framework in the methodology and use it to structure the discussion. 3. The manuscript does not clearly describe recruitment procedures, sampling rationale, or how thematic saturation was determined. These are essential for qualitative rigor. Add details on inclusion criteria, participant selection methods, and saturation assessment. 4. Given the sensitive nature of discussing motivation, performance, or institutional trust, social desirability bias is likely. Acknowledge and discuss this limitation explicitly in the Methods or Discussion. 5. The study was conducted in a single metropolitan area, but some statements are generalized to the national level. Clarify contextual boundaries and avoid sweeping claims beyond the study setting. 6. The section on mHealth perceptions is informative, but the implications remain unclear. Discuss feasibility in terms of digital literacy, system infrastructure, and cost sustainability. 7. Consider adding a table summarizing key themes and representative quotations to improve readability. This is a meaningful and well-conceived study that makes an important contribution to understanding the opportunities and challenges for community-based NCD care in Nepal. Addressing the points above, particularly around alignment of conclusions with data, methodological transparency, and incorporation of a theoretical framework, will considerably strengthen the manuscript. I appreciate your efforts and look forward to seeing the revised version. Sincerely, Reviewer

R1:

EDITOR:

In the previous review, both reviewers requested substantial refinement of the findings / results section. While your response to their comments and the sentiment of staying true to what participants reported is noted, the section still reads as overly descriptive and lacking in analysis. It reads like an overall report of the first-level descriptive analysis / thematic organisation of the data, and not like a critical analysis of what was learnt relative to the objectives that you state. My strong suggestion is that you engage the reviewers' comments on this section more thoroughly. Specifically, move more of the illustrative quotations into Table 1 to support your analytic argument, and then dramatically shorten the in-text representation of the findings to be answering the stated objectives. I believe that this revision is minor, editorial re-organisation of the findings rather than substantive / major. I hope that you are encouraged to complete it.

R2:

We are pleased to inform you that your manuscript 'Non-communicable disease care in peri-urban Nepal: Potential for community-based interventions' has been provisionally accepted for publication in PLOS Global Public Health.

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: Thank you for the opportunity to review this manuscript. It addresses a highly relevant and timely topic, the impact of transitioning advanced HIV disease (AHD) services to Ministry of Health leadership in Malawi, particularly in the context of declining official development assistance (ODA) in the Global south. The study contributes important evidence on sustainability and national ownership of HIV programs.

Please see my detailed comments below:

Study design and data collection • Clarify data collection process: Please specify who collected the data during both pre- and post-transition phases, and whether they received standardized training or mentorship. Were the same cadres of data collectors involved across phases? This is critical for assessing consistency and potential bias. • Timing of data abstraction: Pre-transition data collection began one month before the end of the period, while post-transition data collection started 10 months before the end. Please explain the rationale for this difference and discuss whether it may have influenced data completeness or quality.

Eligibility criteria and diagnostics • Shift in AHD eligibility: The manuscript notes that WHO staging was more frequently used post-transition, while CD4 testing coverage declined. Please elaborate on the reasons for reduced CD4 access, was this due to procurement challenges, supply chain disruptions, or reduced prioritization? Was this anticipated during transition planning? • Implications for programming: What are the consequences of relying more heavily on WHO staging? Could reduced CD4 coverage lead to under-diagnosis of AHD clients? Please discuss the potential programmatic losses and whether strengthening CD4 testing remains essential for accurate case identification. • WHO stage conditions: The manuscript should clarify which WHO stage 3 and 4 conditions were most frequently identified post-transition. For example, TB and oral candidiasis diagnoses declined, while bacterial infections increased. This discrepancy warrants further explanation.

Opportunistic infections and preventive therapy • OI detection: The discussion states that patients presented with fewer opportunistic conditions post-transition. However, this could also reflect reduced screening sensitivity rather than true declines. Effective programs should detect OIs if present. Please consider this alternative interpretation. • TPT uptake: The decline in TB preventive therapy uptake post-transition is concerning. Was this due to procurement or supply chain challenges? Please provide more detail on systemic factors that may have contributed.

Interpretation and discussion • Program sustainability: While mortality declined, the reduction in CD4 testing and TPT uptake highlights vulnerabilities in sustaining comprehensive AHD care. Please expand on how these gaps could be addressed in future nationally-led models. • Equity considerations: Were there differences in outcomes by age, sex, or facility type? Disaggregated analysis could strengthen the discussion on equity and inform targeted interventions. • Policy implications: The findings have clear relevance for other high-burden countries considering similar transitions. Please highlight how lessons from Malawi can inform broader WHO or UNAIDS guidance on AHD programming.

Additional suggestions • Strengthen the limitations section by explicitly acknowledging potential biases from data collection timing, reduced diagnostic coverage, and reliance on retrospective records. • Consider adding a sensitivity analysis to test whether mortality declines remain robust when adjusting for diagnostic coverage differences. • Expand the conclusion to emphasize both the successes (mortality reduction, sustained retention) and the risks (diagnostic gaps, preventive therapy decline), providing a balanced perspective for policymakers.

Reviewer #2: This manuscript addresses an important and highly relevant topic in global HIV implementation science: the transition of Advanced HIV Disease (AHD) services from donor-supported implementation to Ministry of Health (MoH) ownership in Malawi. The study contributes valuable real-world evidence regarding sustainability, health systems strengthening, and nationally led HIV service delivery in high-burden settings. The use of routine programmatic data from 22 facilities, combined with survival and competing-risk analyses, represents a meaningful contribution to the literature on AHD outcomes and transition science.

The manuscript is generally well structured and demonstrates substantial public health relevance. The findings suggesting reduced mortality following transition to MoH stewardship are important and potentially impactful for HIV policy and implementation programs across sub-Saharan Africa. The transition framework presented across multiple operational domains is also a notable strength and may serve as a useful model for similar programs.

However, the manuscript requires major revision before it can be considered for publication.

The principal concern relates to interpretation of the findings in light of the observational pre-post study design. The pre- and post-transition cohorts differ substantially at baseline with respect to age distribution, inpatient enrollment, ART exposure, WHO staging, and CD4 eligibility criteria. These differences introduce potential confounding and limit causal interpretation of the mortality reduction observed. While the analyses demonstrate an association between the transition period and improved outcomes, the manuscript occasionally overstates causality. Conclusions should therefore be moderated and framed more cautiously.

The statistical analysis methods are broadly appropriate, including the use of Kaplan–Meier survival curves, Cox proportional hazards models, and Fine and Gray competing-risk regression. However, the statistical methods section lacks sufficient methodological detail for reproducibility and rigorous interpretation. The authors should clearly specify:

variables included in multivariable models, model-building strategy, handling of missing data, assessment of proportional hazards assumptions, whether clustering at facility level was accounted for, and whether sensitivity analyses were conducted.

The substantial decline in CD4 testing coverage post-transition is one of the manuscript’s most important findings and deserves deeper operational explanation. The discussion currently provides only limited speculation regarding this decline. The authors should clarify whether this reflects national policy changes, diagnostic stockouts, equipment limitations, reduced donor support, laboratory system challenges, or other structural factors. Similarly, the decline in TPT uptake requires stronger contextual and operational interpretation linked to implementation realities in Malawi.

The exclusion of the 2022 transition year from the analysis also requires additional justification and explanation. Since the transition phase likely represents the most operationally informative period, readers would benefit from clearer rationale regarding its exclusion and a brief description of transition dynamics during that period.

The manuscript would also benefit from substantial English language editing. Although generally intelligible, there are several grammatical errors, awkward sentence constructions, inconsistent terminology, formatting inconsistencies, and typographical issues throughout the text that should be corrected prior to publication.

Regarding data availability, the current statement does not fully satisfy PLOS data-sharing expectations. While the ethical and legal restrictions are understandable, the authors should provide a clearer explanation regarding access procedures and whether a de-identified dataset can be made available through a controlled-access mechanism.

Despite these concerns, the manuscript has strong scientific merit and considerable policy relevance. With substantial revision to strengthen methodological transparency, improve interpretation, clarify operational findings, and refine language, the study has good potential for publication.

R0:

Additional Editor Comments (if provided):

Comments This manuscript addresses an important and sensitive topic by exploring the experiences of family caregivers of children with congenital craniofacial anomalies (CCAs) in Colombia. The study covers a range of craniofacial conditions and provides valuable insights into the emotional, social, and healthcare-related challenges faced by caregivers.

The findings have the potential to inform healthcare policies, family-centered care models, and service delivery for children with CCAs and their families. The manuscript demonstrates several strengths, including the inclusion of caregivers from two geographical regions and the use of qualitative methods to explore a relatively under-researched topic. However, substantial revisions are required before the manuscript can be considered for publication. Major concerns relate to the conceptualization of the study, methodological coherence, analytical depth, organization of findings, and interpretation of results.

Abstract Line 36: Replace “primary caregivers” with “family caregivers” to better reflect the study population and maintain consistency throughout the manuscript. Line 42: Consider replacing “semi-structured interviews and focus groups” with “individual interviews and focus group discussions,” as semi-structured interviewing is a data collection approach that may be used in both methods. Lines 45–50: The statement that findings highlighted the “emotional complexity” of caregiving is too narrow. The findings extend beyond emotional challenges and include issues related to diagnosis, communication, healthcare access, service fragmentation, caregiving burden, and coping mechanisms.

Introduction The introduction requires substantial strengthening to better justify the study and establish its contribution to the literature. • The introduction focuses primarily on the clinical classification and epidemiology of CCAs. Greater emphasis should be placed on caregivers’ experiences, caregiving burden, healthcare navigation, psychosocial consequences, and quality-of-life implications. • The literature review should include both quantitative and qualitative studies examining caregiver experiences, emotional burden, healthcare access, coping mechanisms, and support needs. • Additional epidemiological data are needed regarding the prevalence of CCAs, healthcare utilization, caregiver burden, and service needs. • The research gap is not sufficiently articulated. The authors should clearly explain what remains unknown regarding caregivers’ experiences, particularly within the Colombian context, and how this study addresses these gaps. • The study objective is overly broad. Consider presenting a general aim supported by more specific objectives that clearly identify the aspects of caregivers’ experiences being explored.

Methods Several methodological issues require clarification.

Study Design and Philosophical Alignment The rationale for selecting Giorgi’s descriptive phenomenology should be strengthened. The authors should explain why this approach was chosen over other qualitative methodologies and how it aligns with the study objectives. • A major concern is the apparent inconsistency between Giorgi’s descriptive phenomenology and thematic analysis. The manuscript states that the study is grounded in Giorgi’s phenomenology but analyzes data using thematic analysis. These approaches are based on different analytical traditions and require clarification. • If thematic analysis was adapted within a phenomenological framework, the authors should explicitly explain how this was accomplished and how the analytical procedures remained consistent with phenomenological principles. • The analytical steps described do not correspond to Giorgi’s method. The authors should either revise the methodological description or justify their chosen analytical strategy more clearly.

Sampling and Participants Although purposive sampling is mentioned, the rationale for participant selection is insufficiently described. • Characteristics of caregivers are largely absent. Information such as age, education, marital status, occupation, socioeconomic status, relationship to the child, and caregiving duration is important to contextualize findings and explore variation in experiences. • The sample description currently focuses mainly on children’s characteristics. Greater attention should be given to describing the caregivers themselves.

Data Collection The interview guide should be described in greater detail. Consider including the interview guide as an appendix. • The types of questions used, probes employed, and the progression of interviews and focus groups should be outlined more clearly. • Saturation requires further explanation. Describe how saturation was assessed, who determined that saturation had been reached, and what criteria were used.

Data Analysis and Trustworthiness The analysis process should be presented in a more systematic and transparent manner, including coding procedures, development of categories, and generation of themes. • Consider providing a table illustrating the analytical process from codes to categories and themes. • The section on trustworthiness should be separated from the data analysis section. • Trustworthiness procedures should be described more comprehensively, including reflexivity, audit trail, researcher positioning, triangulation, and strategies used to enhance credibility, dependability, confirmability, and transferability. • Line 181: Reliability is reported as being ensured through sample characterization; however, caregiver characteristics are not adequately presented.

Results The results section contains rich data and meaningful participant quotations. However, several structural and analytical issues should be addressed.

Organization of Themes The organization of themes closely mirrors the interview guide domains, raising concerns regarding whether themes truly emerged from participants’ experiences or were largely predetermined by the interview structure. • This issue should be clarified, particularly given the phenomenological orientation of the study. • Consider reorganizing the themes to reduce overlap and improve conceptual coherence. For example: Theme 1: Diagnosis and Impact on Family o Diagnostic challenges (late diagnosis, communication failures, pessimistic prognoses) o Emotional consequences (guilt, depression, uncertainty) o Coping and resilience (information seeking, spirituality, family support) • Such restructuring would provide a more coherent narrative and better reflect the progression of caregivers’ experiences.

Depth of Analysis Findings remain largely descriptive. Greater explanation is needed regarding the meaning of each theme and how participants experienced these situations. • For example, the subtheme “Failures in communication and information delivery” discusses deficiencies in information quality, timeliness, and clarity but does not adequately explain the communication problems themselves or their consequences. • Similar concerns apply to several other themes and subthemes.

Presentation of Findings • Indicate the relative frequency of findings where appropriate (e.g., many participants, several participants, only a few participants). This helps readers appreciate the prominence of different experiences. • Differences between Bogotá and Cali are insufficiently explored. • Variations according to caregivers’ and children’s characteristics are not examined. • Line 270: Information-seeking behavior should not automatically be interpreted as a coping strategy. It may also represent dissatisfaction with information provided by healthcare professionals or a response to unmet informational needs.

Experiences with Healthcare • The first four subthemes (care pathways, specialized care, therapeutic services, and COVID-19-related barriers) could be reorganized under broader concepts such as healthcare system fragmentation, referral inefficiencies, and organizational barriers. • This would strengthen the analytical contribution of the findings. • The reasons underlying restricted access to therapeutic services should be explored in greater detail. • The subtheme “Angels in White Coats” is not an appropriate scientific title unless it directly reflects participants’ language. Consider replacing it with a more neutral title such as “Positive Experiences with Healthcare Professionals.” • The role of non-governmental organizations should be described more thoroughly, including the specific forms of support provided.

Caregiver Role and Daily Care • Consider consolidating findings related to emotional burden and psychological impact to reduce redundancy across themes. • The role of fathers is almost entirely absent from the analysis. Whether this reflects participant experiences, cultural norms, or caregiving patterns should be identified. Gendered caregiving burden emerges as a prominent finding and deserves stronger analytical treatment. • The social consequences of caregiving and living with CCAs are not sufficiently explored. • Differences between regions remain underdeveloped.

Discussion The discussion requires substantial revision and restructuring. At present, it reads largely as a repetition of the results accompanied by supporting citations. The discussion should move beyond description and provide deeper interpretation of the findings. • Findings are frequently restated and linked to previous studies without adequate explanation of why these experiences occur or what underlying mechanisms may explain them. • The discussion lacks a clear organizing framework and proceeds theme by theme without developing an overarching interpretation of caregivers’ experiences. • Consider developing a conceptual narrative that follows caregivers’ journeys from diagnosis, emotional responses, coping strategies, interactions with healthcare systems, and long-term caregiving responsibilities. • A conceptual model linking these experiences would significantly strengthen the manuscript.

• Several important findings require deeper interpretation: • The emotional impact of diagnosis and delayed diagnosis. • Communication failures and their consequences. • Caregiver resilience and active problem-solving. • Fragmentation of healthcare services and its effect on families. • Gender inequality and the disproportionate burden placed on mothers. • Positive experiences with healthcare providers and their role in supporting adaptation.

• Given that the study claims to be grounded in Giorgi’s descriptive phenomenology, the discussion should engage more directly with the meaning of the lived experience. Questions that remain largely unanswered include: • How did caregiving reshape caregivers’ identities, roles, priorities, and relationships? • How did participants make sense of their experiences? • What meanings did they attribute to caregiving? • How did these experiences transform their daily lives?

• The discussion should also provide a more critical examination of healthcare system deficiencies in responding to the needs of children with CCAs and their families. • Finally, the last paragraph primarily contains recommendations for healthcare professionals and educational institutions. These recommendations are better suited to the conclusion or a dedicated implications section rather than the discussion itself.

Conclusions The conclusion generally reflects the findings but includes recommendations that are broader than the data presented. • Recommendations should be more explicitly grounded in the study findings. • Consider emphasizing the key contribution of the study and the implications for healthcare delivery, caregiver support, and future research.

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: Review Comments to the Author The topic of this manuscript does not get nearly enough attention in the literature - how families, and particularly mothers, navigate the healthcare system when caring for a child born with a craniofacial anomaly. The Colombian context makes this especially valuable, as most published work in this area comes from high-income, English-speaking settings. The two-city design is a sensible choice, and the use of both interviews and focus groups is well justified. I do think this paper has real potential, but there are a number of issues I'd ask the authors to address before it's ready.

Major Issues The first thing I want to flag is the tension between the stated methodology and what was actually done. The authors describe the study as being grounded in Giorgi's descriptive phenomenology, but the data analysis follows the three-step thematic approach outlined by Sundler et al. (2019). These are not the same thing. Giorgi's method has specific procedural requirements, including naive reading, the identification of meaning units, and their psychological transformation, none of which are described here. I'm not saying one approach is better than the other, but the authors need to pick one and stick with it. As written, the mismatch casts doubt on the methodological foundation of the entire study. Second, the saturation claim needs more support. The authors say they collected data until saturation was reached, but there's no explanation of how that was assessed, particularly given that interviews and focus groups were running simultaneously across two cities. More importantly, with 25 participants spread across 10 different diagnoses, it's hard to see how saturation could realistically have been achieved for the rarer conditions. This should either be better justified or acknowledged honestly as a limitation. Third, there is no reflexivity statement anywhere in the paper. For this kind of qualitative work, that's a significant omission. The research team comes from dentistry and nursing backgrounds, and their clinical and institutional positioning will inevitably have shaped how questions were asked and how data were interpreted. Readers need that transparency. A short but honest reflexivity section would go a long way. Fourth, the data availability statement needs work. "Data available on request" doesn't meet PLOS policy. The authors should state specifically what can be shared, who to contact, and if participant confidentiality is a barrier to full sharing, that should be spelled out explicitly rather than left implied. Fifth, the Results section feels more like a themed collection of quotes than an analysis. The themes are clearly identified, and the participant voices are vivid, but the analytical layer is thin. For example, it's not clear how "Holding on to God's hand" and "The family as a fundamental support network" differ from each other conceptually; are these the same coping resource described differently, or genuinely distinct? The Discussion does a better job of situating the findings, but some of that interpretive work needs to happen in the Results, too.

Smaller Points There's a typo in the abstract "provideed" on line 40, and the language needs a careful pass throughout. "Search for information as coping strategie" (line 270) and "for manage CCAs" (line 468) are two other examples. Since PLOS doesn't copyedit, this has to be clean before acceptance. The section header "d) DISCUSSION" is capitalized differently from the others, minor but worth fixing for consistency. Table 1 is clear and useful. One addition that would help: a note clarifying how children with more than one diagnosis were categorized. The observation that girls outnumber boys in this sample, which runs counter to the epidemiological literature, is mentioned briefly but left unexplained. Was this a feature of the referral patterns at the participating institutions? Even a sentence of speculation would be better than leaving it hanging. Finally, Reference 29:Chen and Kanekar (2022) appears to be an imaging paper, yet it's cited in the Discussion in the context of caregiver support and early detection. Please check that references are correctly matched to the specific claims they're supporting throughout the manuscript.

Overall There is a solid study underneath these issues, and the findings matter for clinicians, for health system planners, and for the families themselves. The participant accounts are powerful, and the structural critique of the Colombian healthcare system that emerges from the data is well-grounded. I'd encourage the authors to revise and resubmit. My recommendation is a revision.

Reviewer #2: The paper reports the experiences of caregivers while navigating through health systems and while caring for their children with congenital craniofacial anomalies in Colombia explored through qualitative study. The reporting of findings reflect the comprehensiveness in exploration, analysis and thematic presentation of findings The narratives are powerful and support the findings. There are some minor recommendations for the authors to consider that may add value to the paper- 1) Authors have mentioned some contextual factors but if they could add a few details like whether there were any variations in ethnicity and socioeconomic conditions of caregivers and if it has shaped the healthcare seeking pathways? 2) Authors have mentioned that majority of Colombian population has been covered by General Social Security Health System (SGSSS) in the background. So if there are any findings related to how it has protected or failed to protect the caregivers from Out of Pocket Expenses(OOPE) can be added to the results section. 3) Some details in the analysis section- like the language in which interviews were conducted and in how many steps the translation and transcription to English happened?

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.

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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.

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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.

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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.

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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.