Examining the Long-Term Impact of Malaria Chemoprophylaxis in Everyday Life in Rural Gambian Adolescents

Round 1

Reviewer 1 Report (Previous Reviewer 5)

Comments and Suggestions for Authors

This study examined smartphone usage and its impact on mental health in adolescents, focusing on gender disparities in usage patterns and the associated mental health consequences. The authors highlight significant behavioral trends associated with excessive smartphone use in this population to inform prevention and intervention measures. The following section comments are meant to help the authors make the manuscript impactful and the findings useful for practitioners and policymakers.

1. Overall, the paper is well-written. To make their findings directly applicable to public health and clinical interventions, the authors should include the policy and practical implications of their results. They should consider offering policies and practice recommendations, such as promoting digital literacy and mental health screening among teenagers. Recommendations for schools, parents, or mental health professionals can help address the gender-specific consequences of smartphone use.
2. The title is informative but needs clarification and detail. The current title “…long-term impact” suggests a causal and longitudinal research design was used, which is not consistent with the actual cross-sectional design and network analysis. A better title would explain the study approach and focus to improve accuracy and prevent the ambiguous potential of the findings. The title should also include an appropriate term to hint at the age (e.g., youth).
3. Abstract: The abstract effectively summarizes the subject. However, the description of the study design is ambiguous. The authors should first clearly declare the study design before using terms such as “…selected from a longitudinal cohort that previously participated in…” Without this, the reader is likely to assume a longitudinal research design.
4. The authors should also rephrase the abstract in a way that clearly describes the analytical methods before presenting the results, rather than hinting at the methods within the results.
5. Introduction: This section presents background and problem statement well. However, it is wordy and lacks synthesis. For instance, Lines 103-130, comprising three paragraphs, are based on only two studies ( Greenwood et al., 1988, and Jukes et al., 2006). These studies are relatively old, so they may not accurately reflect current realities. The text is unnecessarily wordy. The section should be succinct, with authors considering the synthesis of current literature.
6. In the concluding paragraph of the introduction, the authors mention that they hypothesize xyz; however, network analysis, as described, is exploratory and not suitable for hypothesis testing in the sense of inferential statistical analysis. While network centrality measurements highlight structural patterns and relationships, they cannot test hypotheses or establish statistically significant group differences without the use of inferential statistical tests or comparison models. Framing expectations as exploratory propositions or including formal statistical comparisons, such as permutation tests, or regression on network metrics, will be helpful to the reader.
7. Results: The results are meaningful. However, a principal issue is how the results are presented in the manuscript relative to how they are supported by figures (and lack of tables). There is a lack of alignment between the figures and the narrative description in the text. Specifically, the authors over-rely on visualizations in the absence of suitable interpretation, including the figures (particularly network graphs), which are presented without sufficient explanation in the text, leaving the reader to interpret the findings without adequate direction or context.
8. Furthermore, the authors present statistical coefficients in the text but underutilize the tables, thereby weakening the reader’s ability to connect numerical findings to the results described in the text.
9. The visual results, such as network diagrams, show linkages and themes. However, they are not consistently connected with the hypotheses outlined earlier. The results fall short of linking visual diagrams to the analytical interpretation.
10. To improve the utility of the graphs, specifically the network analysis, the authors should consider making them less cluttered by splitting them into panels based on gender or themes. The improvements may be made by enlarging labels and improving figure captions. The authors should ensure that each figure and table is clearly described in the interpretation of the results and explain how the visual depiction of data supports or rejects the stated hypotheses.
11. Discussion: The discussion section is well-written, but can be improved by enhancing the alignment between the principal findings and the stated hypotheses.
12. While the authors elaborated on limitations well, they should consider addressing potential response biases related to self-reported data. They should also acknowledge the limitations emanating from the use of centrality metrics in social network analysis. Given the study's reliance on thematic coding and network inference, some reflection on the subjectivity inherent in these methodologies would enhance the description of the analytical limitations.

Author Response

This study examined smartphone usage and its impact on mental health in adolescents, focusing on gender disparities in usage patterns and the associated mental health consequences. The authors highlight significant behavioral trends associated with excessive smartphone use in this population to inform prevention and intervention measures. The following section comments are meant to help the authors make the manuscript impactful and the findings useful for practitioners and policymakers.

1. Overall, the paper is well-written. To make their findings directly applicable to public health and clinical interventions, the authors should include the policy and practical implications of their results. They should consider offering policies and practice recommendations, such as promoting digital literacy and mental health screening among teenagers. Recommendations for schools, parents, or mental health professionals can help address the gender-specific consequences of smartphone use.

Response: Thank you for your thoughtful review and feedback. We appreciate your emphasis on enhancing the manuscript’s applicability to public health through explicit policy recommendations. However, we respectfully note that your description of our study as examining “smartphone usage and its impact on mental health” appears to refer to a different paper. Our research focuses on the long-term social-emotional impacts of early childhood chemoprophylaxis in rural Gambian adolescents. But, to address your call for actionable recommendations, we have integrated policy implications directly into the conclusion section of the discussion (lines 597-603).

 

2. The title is informative but needs clarification and detail. The current title “…long-term impact” suggests a causal and longitudinal research design was used, which is not consistent with the actual cross-sectional design and network analysis. A better title would explain the study approach and focus to improve accuracy and prevent the ambiguous potential of the findings. The title should also include an appropriate term to hint at the age (e.g., youth).

Response: The title has been revised to explicitly reference the study population’s age group while maintaining terminology consistent with the manuscript’s focus: “Examining the long-term Impact of Malaria Chemoprophylaxis in Everyday Life in Rural Gambian Youth.” While “long-term impact” can imply a longitudinal design, in this context it refers to the timing of the follow-up, data collected many years after the original intervention from a longitudinal cohort. The abstract, methods, and discussion clearly state the cross-sectional design and analytic approach (network analysis), ensuring readers are not misled regarding the study design.

 

3. Abstract: The abstract effectively summarizes the subject. However, the description of the study design is ambiguous. The authors should first clearly declare the study design before using terms such as “…selected from a longitudinal cohort that previously participated in…” Without this, the reader is likely to assume a longitudinal research design.

Response: We agree that stating the study design in the abstract will prevent potential misinterpretation. In our current wording, readers may infer a longitudinal design before reaching the methods section. To address this, we have revised the abstract to clearly specify that the present analysis is a cross-sectional follow-up study using participants from a longitudinal cohort (line 17).

 

4. The authors should also rephrase the abstract in a way that clearly describes the analytical methods before presenting the results, rather than hinting at the methods within the results.

Response: We appreciate the reviewer’s attention to clarity in the abstract. We respectfully note that the current abstract already presents the analytical methods before reporting the results. Specifically, the design, sample characteristics, walking interview methodology, coding framework, and network analysis approach are described sequentially prior to the presentation of statistical findings. While some analytic terms (e.g., emotional response analysis, network analysis) are referenced again in the results sentences for clarity, these are brief restatements rather than new method descriptions. We believe this structure maintains both clarity and readability while adhering to the recommended order.

 

5. Introduction: This section presents background and problem statement well. However, it is wordy and lacks synthesis. For instance, Lines 103-130, comprising three paragraphs, are based on only two studies ( Greenwood et al., 1988, and Jukes et al., 2006). These studies are relatively old, so they may not accurately reflect current realities. The text is unnecessarily wordy. The section should be succinct, with authors considering the synthesis of current literature.

Response: Greenwood et al. (1988) and Jukes et al (2006) are indeed older studies; however, they are the foundational empirical work on this specific Gambian cohort and directly inform our study population. The present analysis is a follow-up with individuals form the original Greenwood et al. (1988) clinical trial, making the contextualization of that work essential for readers to understand the provenance of our sample and the rationale for examining long-term effects. Similarly, the Jukes et al. (2006) follow-up provides only prior assessment of this cohort’s cognitive and educational outcomes, which is critical for situating our work in the broader developmental context.

While these studies are not recent, there is no contemporary equivalent research on this specific population that could replace them without losing the direct longitudinal link. Our intent in devoting space to these studies ensures that readers unfamiliar with the original trial and follow-up have sufficient context to interpret our findings. We also respectfully note that the section already incorporates more recent literature elsewhere in the Introduction to address current realities of malaria prevention and Gambian social dynamics (e.g., Dieye et al., 2021). Nevertheless, we appreciate your feedback and the opportunity to clarify our rationale.

 

6. In the concluding paragraph of the introduction, the authors mention that they hypothesize xyz; however, network analysis, as described, is exploratory and not suitable for hypothesis testing in the sense of inferential statistical analysis. While network centrality measurements highlight structural patterns and relationships, they cannot test hypotheses or establish statistically significant group differences without the use of inferential statistical tests or comparison models. Framing expectations as exploratory propositions or including formal statistical comparisons, such as permutation tests, or regression on network metrics, will be helpful to the reader.

Response: We thank the reviewer for this observation and agree that many network analyses are exploratory in nature. In the present study, however, we complemented descriptive network centrality metrics with formal inferential statistical comparisons using edge randomization permutation tests to evaluate whether observed differences in centrality measures exceeded what would be expected by chance. To make this explicit to the readers, we have added a sentence to the introduction (Lines 168-169) noting that the network-related hypothesis was evaluated using permutation-based inferential tests. We believe this addition clarifies that the stated hypotheses were intended to be formally tested rather than framed as exploratory.

 

7. Results: The results are meaningful. However, a principal issue is how the results are presented in the manuscript relative to how they are supported by figures (and lack of tables). There is a lack of alignment between the figures and the narrative description in the text. Specifically, the authors over-rely on visualizations in the absence of suitable interpretation, including the figures (particularly network graphs), which are presented without sufficient explanation in the text, leaving the reader to interpret the findings without adequate direction or context.

Response: We have addressed this comment by adding Table 2, which summarizes the basic structural characteristics of each network. In the results section, we also added wording introducing the table to provide context for the centrality measures (line 436 – 437)

 

8. Furthermore, the authors present statistical coefficients in the text but underutilize the tables, thereby weakening the reader’s ability to connect numerical findings to the results described in the text.

 Response: We have added in-text references to supplementary heatmaps and centrality bar graphs (Lines 437 – 440) so readers can easily cross-reference statistical values with the corresponding visual representation.

 

9. The visual results, such as network diagrams, show linkages and themes. However, they are not consistently connected with the hypotheses outlined earlier. The results fall short of linking visual diagrams to the analytical interpretation.

Response: The network diagrams are intended as visual representations of the complex interaction (gender x treatment) among themes. To aid interpretation, supplementary figures providing additional details are included and have been referenced in the text to more clearly connect the visual results to the analytical interpretation.

 

10. To improve the utility of the graphs, specifically the network analysis, the authors should consider making them less cluttered by splitting them into panels based on gender or themes. The improvements may be made by enlarging labels and improving figure captions. The authors should ensure that each figure and table is clearly described in the interpretation of the results and explain how the visual depiction of data supports or rejects the stated hypotheses.

Response: While we have still retained the single integrated network figures to preserve comparability across all groups, we have enhanced figure readability by increasing resolution and ensuring that each figure is clearly addressed in the text.

 

11. Discussion: The discussion section is well-written, but can be improved by enhancing the alignment between the principal findings and the stated hypotheses. 

Response: In the revised manuscript, we have clarified the alignment between our stated hypothesis (Line 520 – 527) in the beginning of the discussion to reorient our reader before expanding on our findings.

 

12. While the authors elaborated on limitations well, they should consider addressing potential response biases related to self-reported data. They should also acknowledge the limitations emanating from the use of centrality metrics in social network analysis. Given the study's reliance on thematic coding and network inference, some reflection on the subjectivity inherent in these methodologies would enhance the description of the analytical limitations.

Response: We have expanded the Limitations section (lines 629 – 634) to address potential response biases in self-reported data, as well as the methodological constraints of using centrality metrics and thematic coding in social network analysis. These additions highlight the potential for subjective interpretation inherent in qualitative coding and network inference, and the possibility that self-reported accounts may not fully reflect participants’ behaviors or experiences.

Reviewer 2 Report (Previous Reviewer 3)

Comments and Suggestions for Authors

Abstract:

Please include the study design, i.e., a cross-sectional study, for clarity.

Introduction:

 The authors try to highlight the gap between existing longitudinal cognitive work (Jukes et al., 2006) and the present study. However, the gap is not clear. Please elaborate, and how different is the present study compared to Jukes et al. (2006)?

 

Methods:

About the adapted Specific Affect Coding System (SPAFF5), Has a forward–back translation of SPAFF5 items been performed? Please explain. Additionally, please provide information about the individuals who performed the coding (i.e., the coders) and specify the language used.

Results:

Please provide a descriptive comparison of node and edge counts across networks to contextualise the centrality differences. It’s critical to report basic network size (nodes) and connectivity (edges) alongside centrality measures. This allows readers to see whether, for instance, higher average degree scores simply reflect a denser network rather than a truly more “central” role for a theme. Please report effect sizes (e.g., Cramér’s V) for χ² tests to convey practical magnitude. Adding Cramér’s V (V) quantifies the strength of association accordingly (small, medium, large).

Discussion:

Please understand that network centrality patterns may reflect gender roles rather than treatment effects. The manuscript should highlight the impact of gender roles on network topologies in the Gambian setting, rather than focusing just on malaria preventive status (Kea, 2013; Carney, 2017). To avoid over-attribution of social-structural variation to the intervention, please consider making a clear remark in the discussion section.

It is advised that the author link their findings to various SEM levels (individual, interpersonal, and communal) to improve theoretical integration. Such an approach is critical to the reader's comprehension of where (at what ecological level) each observable impact acts, which could improve both theoretical coherence and practical insight.

Comments on the Quality of English Language

Minor English checks are required.

Author Response

Please include the study design, i.e., a cross-sectional study, for clarity.

Response: To make the study design explicit from the outset, we now specify in the abstract (line 17) that this was a cross-sectional follow-up study to ensure readers understand the design immediately.

Introduction:

The authors try to highlight the gap between existing longitudinal cognitive work (Jukes et al., 2006) and the present study. However, the gap is not clear. Please elaborate, and how different is the present study compared to Jukes et al. (2006)?

Response: To strengthen the distinction between the present study and the 2006 follow-up by Jukes et al., 2006, we have added sentences (Lines 137 – 139) to the Introduction to clarify the difference. The Jukes et al study focuses soley on cognitive and educational outcomes assessed through standardized tests, whereas the present study examines social integration and emotional well-being in daily life using a walking-interview approach.

Methods:

About the adapted Specific Affect Coding System (SPAFF5), Has a forward–back translation of SPAFF5 items been performed? Please explain. Additionally, please provide information about the individuals who performed the coding (i.e., the coders) and specify the language used.

Response: Walking interviews were conducted in participants’ preferred language. Field notes were subsequently translated to English, and all affect, valence, and thematic coding was performed on the English translations using the adapted SPAFF5 rubric. Because the SPAFF5 coding scheme itself was not translated into local languages, a forward-back translation of SPAFF5 items was not applicable. We have clarified this workflow in the Methods section (lines 316 – 317). In addition, the limitation section now acknowledges (lines 602 – 603) that translation may not capture all nuances of idiomatic speech.

Results:

Please provide a descriptive comparison of node and edge counts across networks to contextualize the centrality differences. It’s critical to report basic network size (nodes) and connectivity (edges) alongside centrality measures. This allows readers to see whether, for instance, higher average degree scores simply reflect a denser network rather than a truly more “central” role for a theme. Please report effect sizes (e.g., Cramér’s V) for χ² tests to convey practical magnitude. Adding Cramér’s V (V) quantifies the strength of association accordingly (small, medium, large).

Response: We thank the reviewer for this helpful suggestion. In the revised manuscript, we have addressed both requests as follows: (1) We have added a new table (Table 2) to the results section reporting the number of nodes, number of edges, average total degree, average weighted degree, reciprocity, and global transitivity for each of the four gender x treatment networks. This provides the necessary context for interpreting centrality differences. And (2) we have now calculated and included Cramér’s V for all X² tests in the Results section of the emotional valence and affect analyses.

Discussion:

Please understand that network centrality patterns may reflect gender roles rather than treatment effects. The manuscript should highlight the impact of gender roles on network topologies in the Gambian setting, rather than focusing just on malaria preventive status (Kea, 2013; Carney, 2017). To avoid over-attribution of social-structural variation to the intervention, please consider making a clear remark in the discussion section.

Response: We have clarified the discussion of our social network analysis findings to emphasize that gendered socio-cultural norms are more likely explanation for variation in network centrality than early-life malaria prophylaxis timing (line 569 – 570).

It is advised that the author link their findings to various SEM levels (individual, interpersonal, and communal) to improve theoretical integration. Such an approach is critical to the reader's comprehension of where (at what ecological level) each observable impact acts, which could improve both theoretical coherence and practical insight.

Response: We have incorporated a new paragraph in the Discussion (lines 536 - 545) explicitly mapping our findings to the individual, interpersonal and community levels of the SEM. This addition anchors each level to specific results from our study, this framing strengthens theoretical integration.

Reviewer 3 Report (Previous Reviewer 2)

Comments and Suggestions for Authors

The authors have made changes and additions in response to the reviewers' comments, which basically answer the questions posed by the reviewers, but it is better for the authors to indicate where the changes have been made to make it easier for the reviewers to conduct a second review.

Author Response

The authors have made changes and additions in response to the reviewers' comments, which basically answer the questions posed by the reviewers, but it is better for the authors to indicate where the changes have been made to make it easier for the reviewers to conduct a second review.

Response: We appreciate this suggestion and have indicated all revisions in the manuscript using tracked changes. In addition, in the response letter, each reply specifies the section and approximate line numbers where the corresponding change appears, to facilitate the second review.

Reviewer 4 Report (New Reviewer)

Comments and Suggestions for Authors

• Treatment group: Since all participants eventually received chemoprophylaxis, the study should be framed explicitly as comparing early vs. delayed prophylaxis, rather than treatment vs. no treatment.
• Bias: High attrition rate (25% follow-up) raises concerns about selection bias. Please discuss how those lost to follow-up might differ from those included.
• Confounders: Factors such as education, socioeconomic status, and village-level differences were not controlled for and may influence emotional and social outcomes.
• Gender differences are interesting but may be over-attributed to biology; more socio-cultural explanation is needed.
• The manuscript is quite long. Some methodological definition or details (e.g., coding training steps) could be moved to supplementary materials.

Author Response

Treatment group: Since all participants eventually received chemoprophylaxis, the study should be framed explicitly as comparing early vs. delayed prophylaxis, rather than treatment vs. no treatment.

Response: We appreciate the reviewer’s suggestion. We agree that the “placebo” group in this follow-up did receive chemoprophylaxis one to two years after the original trial concluded. As described in the methods, our comparison reflects the early versus delayed prophylaxis rather than treatment versus no treatment. We have retained the historical terms “chemoprophylaxis” and “placebo” to ensure continuity with prior publications on this cohort (e.g., Greenwood et al., 1988; Jukes et al., 2006), but have clarified this timing difference at the first mention of the groups in both the Methods (lines 268 – 272) and Abstract (lines 18 – 21)  so readers are immediately aware of the intervention history without needed to refer to the Methods.

 

Bias: High attrition rate (25% follow-up) raises concerns about selection bias. Please discuss how those lost to follow-up might differ from those included. 

Response: We understand the reviewers point and note that the potential for selection bias due to attrition is already addressed in the participant section of the methods (Lines 265 – 267) and in the Limitations section of the discussion (Lines 570 – 578). Specifically, we acknowledge that participants who remained available for follow-up may differ from those lost to attrition in socioeconomic stability, health outcomes, or social support systems. To address the reviewer’s concern more directly, we have slightly expanded the discussion (lines 579 - 581) to explicitly note that these differences could influence social- emotional outcomes in either direction, although the absence of comparable data on non-participants prevents definitive conclusions.

 

Confounders: Factors such as education, socioeconomic status, and village-level differences were not controlled for and may influence emotional and social outcomes. 

Response: We agree with the reviewer that these factors may influence social and emotional outcomes. As described in the Limitation section (lines 587 –592) we acknowledge that village-level cultural differences could have affected the findings. We have expanded this section (lines 592 – 595) to also note that other potential confounders, such as education level and socioeconomic status, were not statistically accounted for. These variables were not consistently available for the full sample due to loss of contact with our data coordinator; however, we agree they should be considered in future studies to better isolate the effects of early versus delayed prophylaxis.

 

Gender differences are interesting but may be over-attributed to biology; more socio-cultural explanation is needed.

Response: We agree that social-cultural dynamics are critical to interpreting the observed gender differences. While our discussion includes both biological and cultural factors, we have expanded the socio-cultural interpretation (lines 531-540) to better parallel the level of detail provided for biological explanation.

 

The manuscript is quite long. Some methodological definition or details (e.g., coding training steps) could be moved to supplementary materials. 

Response: We understand the reviewer’s concern about the length of the manuscript. In the previous review round, detailed methodological information was requested (e.g., the coding scheme and definitions); it was specifically requested to ensure transparency and facilitate interpretation of the findings. These elements are critical to understanding our analytic framework and directly inform the results presented. For this reason, we believe it is important to retain them in the main text, where they provide essential context for readers without requiring reference to supplementary materials.

Reviewer 5 Report (New Reviewer)

Comments and Suggestions for Authors

The manuscript titled “Examining the long-term impact of malaria chemoprophylaxis in everyday life in rural Gambia” makes for interesting reading. The manuscript is generally well-written and provides a lot of insights.

The methodology was appropriate and the results were clearly presented and discussed.

There are a few errors and inconsistencies in the presentation of the text and these have been indicated in the reviewed manuscript.

The temporal gap between the first study and the current one is a major limitation, with other attendant limitations that have been appropriately noted by the authors.

It is interesting that even though the study was conducted in The Gambia, none of the authors was affiliated with any institution in The Gambia. It is equally surprising that in the era of helicopter research, the team could not collaborate with any Scientist/Researcher from The Gambia who could have contributed significantly to merit authorship.

Comments for author File: Comments.pdf

Author Response

The manuscript titled “Examining the long-term impact of malaria chemoprophylaxis in everyday life in rural Gambia” makes for interesting reading. The manuscript is generally well-written and provides a lot of insights. The methodology was appropriate and the results were clearly presented and discussed.

Response: We thank the reviewer for their positive feedback on the clarity and insights of the manuscript

There are a few errors and inconsistencies in the presentation of the text and these have been indicated in the reviewed manuscript.

Response: We have carefully reviewed the annotated manuscript, corrected the noted errors, and ensured consistency in terminology, formatting, and style throughout the text

 

The temporal gap between the first study and the current one is a major limitation, with other attendant limitations that have been appropriately noted by the authors.

Response: We thank the reviewer for recognizing our discussion of the temporal gap between the original trial and the current follow-up, as well as our acknowledgement of other attendant limitations.

 

It is interesting that even though the study was conducted in The Gambia, none of the authors was affiliated with any institution in The Gambia. It is equally surprising that in the era of helicopter research, the team could not collaborate with any Scientist/Researcher from The Gambia who could have contributed significantly to merit authorship.

Response: We appreciate the reviewer’s comment and agree on the importance of equitable authorship and collaboration in global health research. The present manuscript reports a follow-up analysis of a historical cohort originally established through a clinical trial conducted by Greenwood and colleagues, with full approval from the Gambian Government. Two of the senior authors (Dr. Grigorenko and Dr. Jukes) have conducted significant work within this community over many years, including their roles in the 2006 follow-up study. For this study, local research assistants and community partners in The Gambia were essential to participant recruitment and data collection and are recognized in the Acknowledgements. While these contributions did not meet the criteria for authorship, we value and acknowledge the critical role of these collaborators.

 

This manuscript is a resubmission of an earlier submission. The following is a list of the peer review reports and author responses from that submission.

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

I commend the authors for a very well written paper on an innovative topic that is of interest for this journal. I only have a few minor comments below

1. Why were only 144/579 participants recruited for the follow up study? What were the main reasons for not being able to contact the rest of the sample?
2. Since many of the participants were minors, could you describe the role of the parent/caregiver during the walking interviews?
3. Who did the walking interviews and how were these staff trained/supervised?
4. Since participants were from 5 different villages, could there be other social/economic/ community/geographical factors that could explain differences observed in outcomes? I would think this would at least require a discussion

Reviewer 2 Report

Comments and Suggestions for Authors

This study examines the role of chemoprophylaxis on social well-10 being in minors in rural Gambia. And a walking interview methodology was used. This study provides an example of how the social-ecological framework and ecologically valid assessment methods like the walking interview can be applied to investigate the interplay between early childhood health interventions, social dynamics, and individual development in rural Africa contexts. It's an interesting study, but major revision is needed before considering publication.  

1. X2, X² ? Please write uniformly.
2. Please harmonize the representation of decimals (with and without integer parts) with the number of decimal places.
3. Please standardize image annotations and replace high resolution images. And the font is too small to read in figures 3-6.
4. Please optimize the “conclusion” section.
5. Please standardize references, some references do not have page numbers.
6. Please streamline and optimize the “introduction” and “methods” sections.
7. The research methodology should be spelled out in the “abstract” section.

Comments on the Quality of English Language

The language needs polishing.

Reviewer 3 Report

Comments and Suggestions for Authors

I have thoroughly reviewed the manuscript, and the methodologies and analyses presented are very insightful. However, I have a few observations to share.

Abstract:

Some findings suggest some societal differences between chemoprophylaxis and placebo groups (higher centrality in social and familial themes versus higher centrality in well-being themes), but it was not deliberately interpreted in the conclusion. Likewise, the impact of degree and betweenness centralities within those groups was also examined.

Introduction:

I find the information on the touring method in the introduction section to be verbose. The methodology section should include a summary of this information instead.

The aims of the study are unclear. The authors should state the aims of the study at the end of the introduction part.

Methodology:

The process is lacking in how respondents are approached in two groups during the walking tour method. How many tours did you initiate? How many participants are involved in a tour per group?

N=144; please demonstrate the sample size calculation including the attrition rate.

About ‘the other group was given a placebo and then treated with a delay (n = 69)”. Please clearly define the placebo group. Please improve for clarity. Were they given chemoprophylaxis too? What is the duration of the delay?

About “Initial coding categories were developed through a preliminary analysis of response patterns and consideration of cultural norms in rural Gambian communities” Please elaborate more on this. How many respondents were involved? Were they included in the actual survey? Who validates the response patterns and cultural norms?

About “Valence captured the emotional tone used to describe events or places themselves,” Are there any biases anticipated for this assessment, such as the influence of recent unfortunate events or varying interpretations by different coders?

 

Results and discussion

The reliability of the affect coding value is very low (α = 0.22 ); this would suggest there is poor agreement among coders in identifying affect-related parameters. Hence, the results are invalid. The authors still use the results for the network analysis, which are not adequately  addressed and raise concerns about the validity of affect-related results. This is a major concern in the manuscript.

The authors have overextended the results to draw some conclusions. For example, Page 13, Lines 454–466: “These differences suggest that early childhood malaria interventions… supports the idea that early childhood malaria intervention may have influenced how social connections were formed and maintained within the networks.” However, the authors acknowledged in Page 8, Lines 313–319 (Reliability section) that the lower reliability for affect coding implies specific difficulties in identifying internal emotional states from translated responses. It is clearly observed that the treatment effect on social behaviour is not fully supported statistically.

Similar comment on females showing more “emotional expressivity”. It is stated that on Page 10, Lines 366–367: a two-sample proportion test revealed no significant difference between genders in the proportion of positive responses (X² = 2.16, p = 0.14).” But the authors still highlight the links without valid statistical backups. It would be good if the authors could address that some findings are explanatory rather than subject them to the “causal inferences”.

The network construction is unclear. For example, how a theme like “romance” having high betweenness could imply some meaningful behavioral insight.

 

Reviewer 4 Report

Comments and Suggestions for Authors

The authors have conducted an interesting study. My comments are:
The introduction section lacks a coherent flow. It is too long.

The gender differences section is introduced too abruptly, making it unclear to the reader what it is about.

Data on the socio-ecological method and touring method should be included in the methods section, and the information should be restructured as these sections are too long.

The introduction section should clearly state the aim of the study.

Lines 40-41 - the authors should provide more recent references.
The results, discussion, and conclusion sections are well-structured and do not require major changes.

Reviewer 5 Report

Comments and Suggestions for Authors

Peer review

QUALIFYING THE LONG-TERM IMPACT OF MALARIA CHEMOPROPHYLAXIS IN EVERYDAY LIFE

This research analyzed the social and emotional impacts of malaria chemoprophylaxis in adolescents. The study used a mixed-methods approach to assess the impact of interventions. However, the following points must be addressed to improve the quality of this study. Overall, the research makes a meaningful contribution to the existing research evidence.

1. Title: The title must specify the place (at least the country’s name). The findings are culture-specific and should therefore be reflected in the title.

ABSTRACT:

2. The authors have not described the research design in the abstract.
3. Lines 15-16: The sentence “examining the relationship .. across treatment group and gender.” Is vague. Are there sub-groups within “treatment group?”
4. The authors report that "Emotional response analysis revealed predominantly positive affect and valence across all participants, with no statistically
5. significant differences between treatment groups (Chi-square = 0.57, p = 0.45) or genders (X2 = 2.16, p = 0.14). Given this, for most readers, will consider them a chace association but the authors say these "suggestive associations" which is misleading--there is absence of association. Further, the statement about the chemoprophylaxis group ...showing higher centrality in well-being themes and the p-value for treatment group differences in betweenness centrality (p = 0.077) "approaching significance," actually shows non-significance at p<= 0.05, the most liberal threshold used in research. The authors should re-write their central findings. The current narrative is misleading because it leads the reader to believe that chemoprophylaxis significantly impacts social well-being based on network analysis. The emotional response analysis, which is a direct measure, did not show significance. Also, the key findings and message are overshadowed by the technical details.
6. The authors must specify the age range of adolescents for their study because it can vary.
7. The implications are not specifically well described, tying them to findings.

 

INTRODUCTION:

8.  Lines 42-51: The study rationale is weak.
9. Lines 65-74: Some of the articles are older (e.g., Greenwood et al., 1988); the authors should try to find more recent literature because the science of Malaria may have changed. The research by Greenwood et al. (1988) and Jukes and Grigorenko (2010) is foundational, but the article does not fully explain how the new study builds upon or differs from these works.
10. This section emphasizes malaria chemoprophylaxis but falls short on discussing its broader developmental implications (Angrist et al., 2023).
11. The authors may want to expand on the gap this work addresses to convince the reader of its contribution to the research literature on the topic.
12.  

 

Methods

13. Lines 248-257: It is unclear the impact of reducing the sample of 579 to 144 actual participants. Also the authors should provide clarification on whether the final sample is a random subset, convenience sample of reachable participants, or participants who agreed. Discuss how selection bias may effect results.
14. Lines 283-296: The description of coding lack details on resolving differences between coders and addressing new issues beyond designated categories. The authors should add details about the adjudication procedure for inter-coder differences, using a grounded-theory method to identify evolving patterns and handling partial or ambiguous responses.
15. Lines 317-319: The Krippendorff's alpha = 0.22 for “emotional states” measurement is indicative of low reliability. The authors should address this by providing a brief explanation of how the coding reliability was challenging.
16. Lines 320-350: The description lacks clarity on incomplete or partial responses in walking interviews. The authors must add a statement on how they handled missing or incomplete data. This transparency lets readers better contextualize the findings.
17. The details about the translation and recording of interviews in local languages are also inadequate, which may have introduced some errors.
18. The authors should consider elaborating on the sampling and whether the approach used may have introduced selection bias.

 

Results:

19. Figures 4, 5, and 6 are not legible; therefore, the reader cannot read the labels for various domains.
20. Lines 388-417: To strengthen the interpretation of the network analysis, the paper should explain how the described network clusters connect with Gambian societal structures. The authors must consider better connecting network discoveries to the social-ecological framework. For instance, the authors may discuss what it means for “Familial” to be bridging (high betweenness).