Decomposing Wealth-Based Inequalities in Neonatal Mortality in India: Evidence from National Family Health Survey (2019–2021)

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Please see the attachment.

Comments for author File: Comments.pdf

Author Response

Comment 1:  The authors have made a very important discovery, demonstrating that the "perceived quality of antenatal care visits (none/some)" serves as a strong predictor of neonatal mortality (Table 2). This constitutes one of the study's key findings. In the "Discussion" section, it would be beneficial to explore this aspect in greater detail, citing studies that quantitatively analyze precisely what constitutes patient satisfaction and their perception of healthcare quality, as these factors determine their subsequent health-seeking behaviors.

For instance, a recent study by Alieva et al. (2025) employed multivariate analysis to identify key drivers of satisfaction among gynecological and obstetric patients. Although conducted in a different geographical context, the study's findings - which highlight the critical role of specific factors such as physician-patient communication, waiting times, and the quality of information provided - could effectively illustrate precisely which micro-level aspects of the healthcare system warrant attention in order to enhance "perceived quality." Incorporating this perspective would not only bolster the explanatory power of your results but also render your concluding recommendations for improving healthcare quality more concrete and practically actionable.

(Reference: Alieva, S.U., Key predictors of satisfaction among gynecological patients in Almaty, Kazakhstan: a multivariate analysis , (1), 49–56. https://doi.org/10.37800/RM.1.2025.472)

Response 1: We sincerely thank the reviewer for this valuable suggestion. Following revision of the analysis, multivariable logistic regression results indicated that perceived quality of antenatal care was no longer statistically significant in the adjusted model. However, a significant association was observed in the bivariate analysis, suggesting a potential relationship between women’s perceptions of care quality and neonatal outcomes.

In response to the reviewer’s comment, we have incorporated a brief discussion acknowledging the importance of perceived quality of care and women’s experiences within the maternal healthcare continuum. The revised text now states –

 “The findings further indicate that expanding service coverage alone may be insufficient to reduce inequality in neonatal mortality unless the quality and responsiveness of maternal healthcare services are simultaneously strengthened. Persistent socioeconomic disparities in education, autonomy, awareness, and financial capacity continue to influence utilization of timely and quality maternal healthcare services among poorer women” [Line no. 414-418]

Comment 2:  While the cross-sectional analysis of data spanning 2019–2021 is robust, the "Discussion" section could be slightly enriched by including a brief comparison with previous rounds of the NFHS (e.g., NFHS-4). A brief paragraph addressing whether the gap in neonatal mortality rates—stratified by wealth quintile—has widened, narrowed, or remained constant over the past decade would provide valuable historical context for the current findings.

Response 2: We thank the reviewer for this valuable suggestion. In response, we have incorporated a brief discussion comparing the current findings with evidence from previous rounds of NFHS and related literature examining temporal trends in wealth-based inequalities in neonatal mortality in India. The revised text:

“Evidence from successive rounds of NFHS has consistently shown persistent socioeconomic inequalities in neonatal in India. Previous studies reported that although overall mortality levels declined over time, reductions were disproportionately greater among wealthier populations, resulting in only modest narrowing of wealth-based gaps in neonatal mortality. The findings from NFHS-5 indicate that these inequalities continue to persist, with neonatal deaths remaining disproportionately concentrated among poorer households.” [Line no. 361-366]

 

Comment 3: Discussion of Limitations:

The authors adequately acknowledge the limitations inherent in a cross-sectional study, as well as potential biases associated with recall error. It would also be worth briefly noting that, while the quantitative data effectively highlight where disparities exist, future qualitative studies are recommended to explore the cultural and systemic barriers underlying the underutilization of maternal health services among the poorest wealth quintiles.

Response 3: We thank the reviewer for this important suggestion. Accordingly, we have incorporated a statement in the recommendation section highlighting the need for future qualitative and mixed-methods research to better understand the contextual barriers affecting healthcare access and utilization among poorer households.

The statement added is –

“While the quantitative findings effectively identify where disparities exist, future qualitative and mixed-methods research is needed to better understand the cultural and systemic barriers underlying the underutilization of maternal healthcare services among poorer populations.” [Line no. 458-460]

Comment 4: This is a high-quality manuscript with significant policy relevance for maternal and child health in India. The statistical analysis is rigorous, and the narrative is logically coherent. I recommend publication of the manuscript following minor revisions aimed at expanding the discussion on the qualitative aspects of healthcare utilization and patient satisfaction, as suggested above.

Response 4: We sincerely thank the reviewer for the encouraging and constructive feedback. As suggested, we have incorporated the recommended revisions by expanding the discussion and recommendation, thereby further strengthening the overall interpretation and contextual relevance of the manuscript. The changes has been highlighted in yellow colour.

Reviewer 2 Report

Comments and Suggestions for Authors

Comments

Public health implications:

• Need to strengthen the “equity-oriented implementation”….your project is on equality. It is better to use a consistent term.

Abstract

“These findings highlight the need for equity-focused strategies 52
addressing both social determinants and gaps in access to quality maternal and 53
newborn care” from line 52-54.

Dear author, equity and equality are quite different. To which one your manuscript aligns to?

 

Analysis

“…normalized Concentra- 38 tion Index (ECI) and concentration curves, with subgroup analyses by resi- 39 dence, state development status (EAG vs non-EAG), district typology, and re- gion”….Please give emphasis on these and other related GIS….sections in the analysis part than only AOR…

 

RESULT

Please rewrite in a plain language that your readers can be easily understand it. There are some words very difficult to understand them easily.

 

Discusstion

Very good.

 

Conclusion and recommendation

It is better to write conclusion separately.

Rather than “recommendation” implication will be highly recommended for this kind of manuscripts I highly recommend you to show your findings implications.

 

Good luck..

Author Response

Comment 1: Public health implications: Need to strengthen the “equity-oriented implementation”….your project is on equality. It is better to use a consistent term.

Abstract: “These findings highlight the need for equity-focused strategies 52 addressing both social determinants and gaps in access to quality maternal and 53 newborn care” from line 52-54.

Dear author, equity and equality are quite different. To which one your manuscript aligns to?

Response 1: We thank the reviewer for this important observation. As the present study specifically examines socioeconomic inequalities in neonatal mortality, we have revised the relevant sections of the manuscript to ensure consistent use of the term “inequality” where appropriate. The changes has been highlighted in yellow colour.

Comment 2: Analysis: “…normalized Concentra- 38 tion Index (ECI) and concentration curves, with subgroup analyses by resi- 39 dence, state development status (EAG vs non-EAG), district typology, and re- gion”….Please give emphasis on these and other related GIS….sections in the analysis part than only AOR…

Response 2: We thank the reviewer for this valuable suggestion. In response, we have revised the manuscript to place greater emphasis on the concentration indices, subgroup inequalities, and decomposition findings, which constitute the primary focus of the study. Adjusted odds ratios have now been presented more concisely, and the corresponding discussion around regression findings has been streamlined in both the Results and Discussion sections to improve alignment with the study objectives. The changes has been highlighted in yellow colour.

Comment 3: RESULT: Please rewrite in a plain language that your readers can be easily understand it. There are some words very difficult to understand them easily.

Response 3: We thank the reviewer for this suggestion. We have revised the results section, particularly the regression and decomposition findings, to improve clarity and readability. Technical wording and complex descriptions have been simplified where appropriate to ensure that the findings are presented in a clearer and more accessible manner while maintaining scientific accuracy. The changes has been highlighted in yellow colour. [Line no. 335-353]

Comment 4: Discussion: Very good.

Response 4: We thank the reviewer for the positive feedback and encouraging remarks.

 Comment 5: Conclusion and recommendation: It is better to write conclusion separately. Rather than “recommendation” implication will be highly recommended for this kind of manuscripts I highly recommend you to show your findings implications.

Response 5: We thank the reviewer for this valuable suggestion. In response, we have revised the section title to “Conclusion and Implications” to better reflect the translational and policy relevance of the findings. As the concluding section not only summarizes the key findings but also discusses their implications for public health policy, programme implementation, and future research, we considered it appropriate to present the conclusion and implications together in an integrated manner to maintain coherence and avoid repetition.

Reviewer 3 Report

Comments and Suggestions for Authors

The topic is important both from the perspective of the epidemiology of health inequalities and of health policy, especially in the context of programs aimed at reducing inequities in health opportunities. In my view, the paper has potential, but it requires major revision before it can be further considered for publication.

1. The authors state that inequality in the binary outcome variable was assessed using the Erreygers Normalized Concentration Index (ECI), which is justified for a dichotomous variable such as neonatal mortality. However, the description of the decomposition is then based on the classical equation for the standard concentration index. In the current version, it is not clear whether the decomposition refers to the standard CI or to the ECI, whether the contributions presented in Table 5 relate to the standard CI rather than the ECI, and how the consistency between the ECI values reported in the descriptive section and the determinant contributions reported in the decomposition section should be interpreted. Please clarify explicitly what exact procedure was applied, why it is appropriate for a binary outcome, and how it connects to the reported results.

2. In the analytical section, the authors state that associations between explanatory variables and neonatal mortality were assessed using bivariate binary logistic regression, and the results were reported as unadjusted ORs. However, these same variables are later interpreted as the main factors explaining the observed wealth gradient. For such a complex phenomenon, with strongly co-occurring social, environmental, and health-system determinants, interpretation based solely on unadjusted associations may be misleading. Many variables may lose or change the strength of their association once other covariates are taken into account. The authors should clarify whether the coefficients used in the decomposition were derived from a linear model, logistic model, marginal effects, or another procedure, and how the transition from unadjusted ORs in Table 2 to the percentage contributions of determinants in Table 5 was justified.

3. Table 2 is very extensive, but it currently mixes the description of the distribution with the results of unadjusted analyses. It would be better to separate the table describing the sample characteristics from the table presenting the association analyses.

4. Table 5 and the accompanying description raise serious interpretative concerns. The percentage values do not always appear to be consistent with the sign and magnitude of the absolute contribution, for some determinants the percentage contribution is very small yet the interpretation in the text is relatively extensive, and the description of “positive” and “negative contribution” does not always correspond with the narrative of “reducing” versus “increasing” inequality. For example, in the table for unclean cooking fuel, kachha floor, place of residence, exposure to media, and several other variables, the “%” column appears inconsistent with intuitive interpretation and with the text in the discussion. This requires careful checking and probably correction of the table, or at least a much clearer explanation of the principles of interpretation.

5. For variables with less than 10% missingness, the authors used multiple imputation by chained equations (MICE), and the results were pooled according to Rubin’s rules. The description is too brief. Basic information is missing, including how many imputed datasets were created, what types of imputation models were used for specific variables, whether convergence diagnostics or comparisons of distributions before and after imputation were performed, and why a 10% threshold was chosen as the criterion for retaining a variable.

6. Several variables were defined in a way that requires better justification:

• high-risk fertility behaviour was reduced to the categories “no / any one,” without clearly showing which exact components and combinations were included in this variable;

• parity includes the category “unavoidable first birth,” which requires terminological and methodological clarification, as it sounds unusual and is difficult to interpret;

• perceived quality of ANC and knowledge of BPCR were operationalized as “all” versus “none/some,” but it was not sufficiently explained how many components were included in these indices and whether the chosen categorization was validated or based on previous literature.
  Since these variables are then included in the decomposition of inequality, their construction has not only descriptive but also interpretative importance.

7. In the discussion, it would be advisable to distinguish more clearly between what follows directly from the analysis and what constitutes political or programmatic interpretation.

8. The manuscript requires clear language and technical editing. For example:

• errors in proper and geographic names, such as “Pondicherry” instead of the current “Puducherry” in the main text, while a different form appears later in the appendix;

• inconsistent spelling of ECI/Erryger’s/Erreyger’s;

• problems with the titles of tables and appendices, as well as with table formatting.
  It would also be worth standardizing terminology and abbreviations, especially ECI, NMR, ENMR, LNMR, and the names of states/UTs.

Author Response

The topic is important both from the perspective of the epidemiology of health inequalities and of health policy, especially in the context of programs aimed at reducing inequities in health opportunities. In my view, the paper has potential, but it requires major revision before it can be further considered for publication.

Comment 1: The authors state that inequality in the binary outcome variable was assessed using the Erreygers Normalized Concentration Index (ECI), which is justified for a dichotomous variable such as neonatal mortality. However, the description of the decomposition is then based on the classical equation for the standard concentration index. In the current version, it is not clear whether the decomposition refers to the standard CI or to the ECI, whether the contributions presented in Table 5 relate to the standard CI rather than the ECI, and how the consistency between the ECI values reported in the descriptive section and the determinant contributions reported in the decomposition section should be interpreted. Please clarify explicitly what exact procedure was applied, why it is appropriate for a binary outcome, and how it connects to the reported results.

Response 1:We thank the reviewer for this important methodological observation. We would like to clarify that the decomposition analysis presented in the manuscript was performed using the Erreyger’s Normalized Concentration Index (ECI), and not the standard concentration index. As neonatal mortality is a binary and relatively rare outcome, the use of the ECI is methodologically more appropriate because it accounts for the bounded nature of dichotomous variables and avoids the limitations associated with the standard concentration index in such cases.

The contributions presented in Table 5 correspond to the decomposition of the ECI values reported in the inequality analysis. The contribution of each determinant was estimated as ECI and % contribution, allowing quantification of the extent to which each factor contributed to the observed wealth-related inequality in neonatal mortality.

To improve clarity and methodological consistency, we have revised the methods section to explicitly state that decomposition was performed for the ECI and have clarified the interpretation of the decomposition estimates and their relationship to the reported inequality measures.

Comment 2: In the analytical section, the authors state that associations between explanatory variables and neonatal mortality were assessed using bivariate binary logistic regression, and the results were reported as unadjusted ORs. However, these same variables are later interpreted as the main factors explaining the observed wealth gradient. For such a complex phenomenon, with strongly co-occurring social, environmental, and health-system determinants, interpretation based solely on unadjusted associations may be misleading. Many variables may lose or change the strength of their association once other covariates are taken into account. The authors should clarify whether the coefficients used in the decomposition were derived from a linear model, logistic model, marginal effects, or another procedure, and how the transition from unadjusted ORs in Table 2 to the percentage contributions of determinants in Table 5 was justified.

Response 2: We thank the reviewer for this important clarification. In response, the multivariable analysis is now presented using adjusted odds ratios to account for the interrelated effects of individual, household and community, healthcare, and newborn related factors. We would further like to clarify that the percentage contribution reported in the decomposition analysis does not represent the strength of association with neonatal mortality alone; rather, it quantifies the extent to which each determinant contributes to the observed socioeconomic inequality in neonatal mortality.

To improve clarity, we have revised the results sections to explicitly distinguish between the adjusted regression estimates and the decomposition-based contribution of determinants to inequality.

Comment 3: Table 2 is very extensive, but it currently mixes the description of the distribution with the results of unadjusted analyses. It would be better to separate the table describing the sample characteristics from the table presenting the association analyses.

Response 3: We thank the reviewer for this helpful suggestion. In response, we have revised the presentation of the results tables to improve clarity and readability. The descriptive characteristics of the study population are now presented separately in the main manuscript, while the multivariate analysis is summarized using a figure presenting the adjusted odds ratios for determinants of neonatal mortality. The detailed table of the unadjusted and hierarchical model of adjusted regression analysis have been moved to the appendix for reference.

Comment 4: Table 5 and the accompanying description raise serious interpretative concerns. The percentage values do not always appear to be consistent with the sign and magnitude of the absolute contribution, for some determinants the percentage contribution is very small yet the interpretation in the text is relatively extensive, and the description of “positive” and “negative contribution” does not always correspond with the narrative of “reducing” versus “increasing” inequality. For example, in the table for unclean cooking fuel, kachha floor, place of residence, exposure to media, and several other variables, the “%” column appears inconsistent with intuitive interpretation and with the text in the discussion. This requires careful checking and probably correction of the table, or at least a much clearer explanation of the principles of interpretation.

Response 4: We thank the reviewer for carefully examining the decomposition results and identifying these inconsistencies. In response, we have thoroughly rechecked and reassessed the decomposition analysis, including the calculation and interpretation of both absolute and percentage contributions for all determinants. Necessary corrections have been made in the revised model and corresponding tables to ensure mathematical consistency and accurate interpretation of the decomposition estimates. The revised decomposition findings have been updated throughout the manuscript accordingly, and the residual component has also been clarified to improve transparency in interpretation. [Line no. 335-353]

Comment 5: For variables with less than 10% missingness, the authors used multiple imputation by chained equations (MICE), and the results were pooled according to Rubin’s rules. The description is too brief. Basic information is missing, including how many imputed datasets were created, what types of imputation models were used for specific variables, whether convergence diagnostics or comparisons of distributions before and after imputation were performed, and why a 10% threshold was chosen as the criterion for retaining a variable.
Response 6: We thank the reviewer for this comment. In response, we have expanded the description of the multiple imputation procedure in the methods section. The revised manuscript now specifies that MICE was performed under the assumption of missing at random using relevant non-missing background characteristics, including place of residence, wealth status, and maternal education, to inform the imputation models.

We have additionally clarified that variables with less than 10% missingness were retained for analysis, as moderate levels of missing data are generally considered acceptable and unlikely to substantially bias estimates when handled using appropriate imputation methods, supported by existing methodological literature [Bennett DA. How can I deal with missing data in my study? Aust N Z J Public Health. 2001 Oct;25(5):464-9. PMID: 11688629]. [Line no. 207-210]

Comment 6: Several variables were defined in a way that requires better justification:

• high-risk fertility behaviour was reduced to the categories “no / any one,” without clearly showing which exact components and combinations were included in this variable;
• parity includes the category “unavoidable first birth,” which requires terminological and methodological clarification, as it sounds unusual and is difficult to interpret;
• perceived quality of ANC and knowledge of BPCR were operationalized as “all” versus “none/some,” but it was not sufficiently explained how many components were included in these indices and whether the chosen categorization was validated or based on previous literature.
  Since these variables are then included in the decomposition of inequality, their construction has not only descriptive but also interpretative importance.

Response 6: We thank the reviewer for these important observations regarding the operationalization of variables. In response, we have revised the methods section to provide clearer definitions and justification for the construction and categorization of the variables included in the analysis. High-risk fertility behaviour has now been explicitly described as a composite variable constructed using maternal age at birth, exact age of the mother, and parity. The category “any one” indicates the presence of at least one high-risk fertility characteristic. Additionally, the terminology “unavoidable first birth” now clarifies that parity and birth interval-related risks are not applicable for primiparous births. Further clarification has also been added for the composite variables related to birth preparedness and complication readiness (BPCR) and perceived quality of antenatal care (ANC). The manuscript now specifies that these variables were constructed based on the receipt or knowledge of recommended service components, and the categorization of “all” versus “none/some” was used to distinguish complete versus partial receipt of care components.

These revisions were incorporated to improve transparency and interpretation, particularly because these variables were included in the decomposition analysis. [Line no 192-205]

Comment 7: In the discussion, it would be advisable to distinguish more clearly between what follows directly from the analysis and what constitutes political or programmatic interpretation.

Response 7: We thank the reviewer for this valuable suggestion. In response, we have revised the discussion section to more clearly distinguish between findings directly supported by the analysis and the broader policy and programmatic implications derived from these findings. Interpretations related to national programmes and health system responses have now been presented more cautiously and explicitly framed as implications rather than direct analytical findings.

Comment 8: The manuscript requires clear language and technical editing. For example:

• errors in proper and geographic names, such as “Pondicherry” instead of the current “Puducherry” in the main text, while a different form appears later in the appendix;

Response 8a: I have made the necessary changes

• inconsistent spelling of ECI/Erryger’s/Erreyger’s;

Response 8b: I have made the necessary changes

• problems with the titles of tables and appendices, as well as with table formatting.
  It would also be worth standardizing terminology and abbreviations, especially ECI, NMR, ENMR, LNMR, and the names of states/UTs.

Response 8c: I have made the necessary changes

Reviewer 4 Report

Comments and Suggestions for Authors

The manuscript addresses an important public health issue using NFHS-5 data. However, several major concerns weaken the validity of the findings.

I have comments under 3 broad headings:

1. Statistical/methods

• The restriction to 176,843 most recent live births from 257,995 total births over five years is justified on grounds of minimizing recall bias, but this decision has critical implications that are not adequately addressed. Restricting to the most recent birth introduces selection bias.
• The Wagstaff decomposition is performed over concentration index (C), yet the study's primary inequality measure is the ECI.
• Please clarify was the decomposition applied to C or to ECI?
• Table 5 reports the "Decomposition of Concentration Index," which implies C, not ECI. If the decomposition is on C but inference and interpretation are on ECI, this represents an analytical inconsistency that undermines the findings.
• The Erreygers decomposition method exists for ECI specifically and should be used, or the

The rationale for using Wagstaff's method on C should be explicitly justified.

• The authors report only bivariate/unadjusted odds ratios for determinants of neonatal mortality. Neonatal mortality is influenced by highly correlated socioeconomic, demographic, and healthcare factors. Unadjusted ORs are likely confounded and may produce misleading interpretations. Many conclusions in the Discussion rely on these unadjusted associations. My suggestion is to conduct multivariable regression analysis, adjusting for all relevant covariates, and report adjusted odds ratios with 95% CIs.
• The MICE procedure is insufficiently described.
• Several categorizations appear arbitrary, like maternal age: “16–34 vs <=15 & >=35” . In India, the categorization should be <18 vs >18 years. Justify other cutoffs, such as family size, income, etc., using prior literature or WHO recommendations.
• Define “community wealth status” operationally.
• Since a lot of variables are related to each other, one should not treat them independently. These are highly correlated social determinants. My suggestion is to assess VIF/ multicollinearity, report diagnostics, and consider dimension reduction or hierarchical modeling.
• Why ECI was preferred over the Wagstaff correction.
• Add a para explaining positive and negative contributions.

2. Results:

• The North India shows the lowest inequality despite having states like UP with the highest NMR. This paradox is not discussed.
• Skin-to-skin contact is associated with an OR of 0.31 for neonatal mortality. While skin-to-skin contact is protective, this magnitude is extraordinarily large and likely reflects reverse causality, i.e., sick neonates who subsequently die may not have received skin-to-skin contact due to their clinical condition. This critical confounding must be explicitly acknowledged and discussed as a major limitation
• The decomposition results are internally inconsistent and mathematically unclear.
• Several values in Table 5 appear inconsistent. “Type of cooking fuel”:

• Absolute contribution = -0.0034, % contribution = 0.002. These are incompatible.
• Type of toilet: check % contribution .
• Mode of delivery: CS and home delivery % same?.
• Please recheck all data again and provide a supplementary calculation appendix or Stata code.

• Appendix A2 reports state ECIs, but many states have very small sample sizes, and hence, estimates may be unstable. Please report CIs. Discuss instability for UTs/small states.

 

Minor interpretation/ language issues:

• Please avoid causation language despite a cross-sectional design.
• The paper states that ASHA contact increased inequality. they often target disadvantaged women. This may reflect program targeting rather than adverse effect.
• The finding that non-aspirational districts have greater wealth inequality than aspirational is counterintuitive requiring deeper exploration. Are aspirational districts more homogeneously poor (thus less inequality despite higher mortality)?
• Table 2 is excessively dense. Please split it. Use consistent decimal formatting.
• The Introduction is somewhat long and repetitive regarding national initiatives.

Comments on the Quality of English Language

It needs editing. 

Author Response

The manuscript addresses an important public health issue using NFHS-5 data. However, several major concerns weaken the validity of the findings.

I have comments under 3 broad headings:

1. Statistical/methods

Comment 1:The restriction to 176,843 most recent live births from 257,995 total births over five years is justified on grounds of minimizing recall bias, but this decision has critical implications that are not adequately addressed. Restricting to the most recent birth introduces selection bias.

Response 1:We thank the reviewer for this important observation. We acknowledge that restricting the analysis to the most recent live birth may introduce selection bias and may limit the representativeness of all births occurring during the reference period. However, this approach was adopted to minimize recall bias and improve the reliability of information related to maternal healthcare utilization and newborn care practices, which are more accurately reported for recent births. We have now explicitly acknowledged this potential limitation in the Strengths and Limitations section of the manuscript. [Line no 438-440]

Comment 2:The Wagstaff decomposition is performed over concentration index (C), yet the study's primary inequality measure is the ECI.

Response 2: We would like to clarify that the primary measure of socioeconomic inequality used in the study was the ECI, both for the assessment of overall inequality and for the decomposition analysis. Concentration curves were presented only for graphical representation of the distribution of neonatal mortality across wealth groups.

The decomposition analysis was performed for the ECI using an elasticity-based decomposition framework adapted for bounded outcome variables, rather than for the standard concentration index. We acknowledge that the earlier methodological description may have created ambiguity by referring generally to the concentration index decomposition framework. To address this, we have revised the methods section to explicitly state that the decomposition pertains to the ECI and clarified the relationship between the reported ECI estimates and the determinant contributions presented in the decomposition analysis.

# Comment 3: Please clarify was the decomposition applied to C or to ECI?

Response 3: We would like to clarify that the primary measure of socioeconomic inequality used in the study was the ECI, both for the assessment of overall inequality and for the decomposition analysis. Concentration curves were presented only for graphical representation of the distribution of neonatal mortality across wealth groups.

The decomposition analysis was performed for the ECI using an elasticity-based decomposition framework adapted for bounded outcome variables, rather than for the standard concentration index. We acknowledge that the earlier methodological description may have created ambiguity by referring generally to the concentration index decomposition framework. To address this, we have revised the methods section to explicitly state that the decomposition pertains to the ECI and clarified the relationship between the reported ECI estimates and the determinant contributions presented in the decomposition analysis.

Comment 4: Table 5 reports the "Decomposition of Concentration Index," which implies C, not ECI. If the decomposition is on C but inference and interpretation are on ECI, this represents an analytical inconsistency that undermines the findings.

Response 4: We would like to clarify that the primary measure of socioeconomic inequality used in the study was the ECI, both for the assessment of overall inequality and for the decomposition analysis. Concentration curves were presented only for graphical representation of the distribution of neonatal mortality across wealth groups.

The decomposition analysis was performed for the ECI using an elasticity-based decomposition framework adapted for bounded outcome variables, rather than for the standard concentration index. We acknowledge that the earlier methodological description may have created ambiguity by referring generally to the concentration index decomposition framework. To address this, we have revised the methods and results section to explicitly state that the decomposition pertains to the ECI and clarified the relationship between the reported ECI estimates and the determinant contributions presented in the decomposition analysis.

Comment 5: The Erreyger’s decomposition method exists for ECI specifically and should be used, or the rationale for using Wagstaff's method on C should be explicitly justified.

Response 5: We would like to clarify that the primary measure of socioeconomic inequality used in the study was the ECI, both for the assessment of overall inequality and for the decomposition analysis. Concentration curves were presented only for graphical representation of the distribution of neonatal mortality across wealth groups.

The decomposition analysis was performed for the ECI using an elasticity-based decomposition framework adapted for bounded outcome variables, rather than for the standard concentration index. We acknowledge that the earlier methodological description may have created ambiguity by referring generally to the concentration index decomposition framework. To address this, we have revised the methods section to explicitly state that the decomposition pertains to the ECI and clarified the relationship between the reported ECI estimates and the determinant contributions presented in the decomposition analysis.

Comment 6: The authors report only bivariate/unadjusted odds ratios for determinants of neonatal mortality. Neonatal mortality is influenced by highly correlated socioeconomic, demographic, and healthcare factors. Unadjusted ORs are likely confounded and may produce misleading interpretations. Many conclusions in the Discussion rely on these unadjusted associations. My suggestion is to conduct multivariable regression analysis, adjusting for all relevant covariates, and report adjusted odds ratios with 95% CIs.

Response 6: We thank the reviewer for this important suggestion. In response, we have now conducted and presented multivariable logistic regression analysis using adjusted odds ratios with 95% confidence intervals to account for the interrelated effects of individual, household, community, healthcare, and newborn-related factors on neonatal mortality. In addition, a forest plot presenting the adjusted odds ratios has been included in the main manuscript, while the detailed results of both unadjusted and adjusted regression analyses have been provided in the appendix.

Comment 7: The MICE procedure is insufficiently described.

Response 7: We thank the reviewer for this important observation. In response, we have expanded the description of the multiple imputation procedure in the methods section. The revised manuscript now explicitly specifies the variables included in the imputation process and clarifies that MICE was performed using relevant non-missing background characteristics, including place of residence, wealth status, and maternal education, to inform the imputation models under the assumption of missing at random. We have also included the appropriate methodological reference supporting the use of this approach. [Line no. 207-210]

Comment 8: Several categorizations appear arbitrary, like maternal age: “16–34 vs <=15 & >=35” . In India, the categorization should be <18 vs >18 years. Justify other cutoffs, such as family size, income, etc., using prior literature or WHO recommendations.

Response 8: We thank the reviewer for this important observation. In response, we have provided additional justification and clarification for the construction and categorization of composite variables in the methods section .

With regard to maternal age at first birth, the categorization was based on established demographic and reproductive health literature identifying adolescent pregnancies and advanced maternal age as biologically high-risk groups associated with adverse maternal and neonatal outcomes. Therefore, mothers aged below 16 years and above 34 years were categorized separately from those aged 16–34 years, representing the relatively lower-risk reproductive age group. [Line no 192-205]

Comment 9: Define “community wealth status” operationally.

Response 9: We thank the reviewer for this observation. The operational definition of “community wealth status” has now been clarified in the Methods section. Community wealth status was derived by aggregating the household wealth index at the cluster/community level and categorizing communities based on the proportion of households belonging to poorer wealth quintiles. Communities with a higher concentration of poorer households were classified as “poor communities,” while the remaining were categorized as “not poor.”

Comment 10: Since a lot of variables are related to each other, one should not treat them independently. These are highly correlated social determinants. My suggestion is to assess VIF/ multicollinearity, report diagnostics, and consider dimension reduction or hierarchical modeling.

Response 10: We thank the reviewer for this important methodological suggestion. We have checked the correlation by assessing multicollinearity, but no variable was found strongly correlated. We have checked spearman’s correlation as well between similar variables, but that also didn’t come very strongly correlated, but moderately correlated. Based on the analysis, and correlation, we then dropped certain household level variables and education related variable that were moderately significant and influencing largely on inequality contribution.

Comment 11: Why ECI was preferred over the Wagstaff correction.

Response 11: We would like to clarify that the primary measure of socioeconomic inequality used in the study was the ECI, both for the assessment of overall inequality and for the decomposition analysis. Concentration curves were presented only for graphical representation of the distribution of neonatal mortality across wealth groups.

The decomposition analysis was performed for the ECI using an elasticity-based decomposition framework adapted for bounded outcome variables, rather than for the standard concentration index. We acknowledge that the earlier methodological description may have created ambiguity by referring generally to the concentration index decomposition framework. To address this, we have revised the methods section to explicitly state that the decomposition pertains to the ECI and clarified the relationship between the reported ECI estimates and the determinant contributions presented in the decomposition analysis.

Comment 12: Add a para explaining positive and negative contributions.

Response 12: We thank the reviewer for this helpful suggestion. In response, we have further clarified the interpretation of positive and negative contributions in the decomposition analysis within the results section, while the methodological explanation has already been provided in the methods section. The revised text now more clearly explains how the direction of contribution reflects whether a determinant increases or offsets the observed socioeconomic inequality in neonatal mortality. [Line no 263-264]

Results:

Comment 13: The North India shows the lowest inequality despite having states like UP with the highest NMR. This paradox is not discussed.

Response 13: We thank the reviewer for this insightful suggestion. In response, we have incorporated an additional discussion in the revised manuscript noting that lower relative inequality may coexist with persistently high mortality when adverse outcomes remain widespread across multiple socioeconomic groups rather than being concentrated only among poorer households.

The revised text now states: “Lower relative inequality observed in North India despite the high neonatal mortality burden may partly reflect the persistence of elevated mortality across multiple socioeconomic groups in these states. Previous evidence from India suggests that although wealth-based inequalities in child mortality have narrowed over time in several states, high-burden states continue to experience substantial overall mortality levels. This indicates that reductions in relative inequality do not necessarily correspond to improvements in the overall burden of neonatal mortality.” [Line no 393-397]

Comment 14: Skin-to-skin contact is associated with an OR of 0.31 for neonatal mortality. While skin-to-skin contact is protective, this magnitude is extraordinarily large and likely reflects reverse causality, i.e., sick neonates who subsequently die may not have received skin-to-skin contact due to their clinical condition. This critical confounding must be explicitly acknowledged and discussed as a major limitation.

Response 14: We thank the reviewer for this important observation. We agree that the strong protective association observed for skin-to-skin contact may partly reflect reverse causality, whereby severely ill neonates or neonates who died shortly after birth may have been less likely to receive skin-to-skin contact because of their clinical condition. In response, we re-analysed the model using multivariable regression adjusting for relevant covariates, and the association remained statistically significant in the adjusted analysis.

However, we acknowledge that the NFHS dataset does not capture detailed information on neonatal clinical condition or severity of illness at birth, limiting our ability to fully account for this potential confounding. We have therefore explicitly acknowledged the possibility of reverse causality and residual confounding related to neonatal illness as an important limitation in the revised manuscript.

“The strong protective association observed for skin-to-skin contact should therefore be interpreted cautiously, as the NFHS dataset does not capture information on neonatal illness severity, raising the possibility of residual confounding and reverse causality” [442-444]

Comment 15: The decomposition results are internally inconsistent and mathematically unclear.

Response 15: We thank the reviewer for carefully examining the decomposition results and identifying these inconsistencies. In response, we have thoroughly rechecked and reassessed the decomposition analysis, including the calculation and interpretation of both absolute and percentage contributions for all determinants. Necessary corrections have been made in the revised model and corresponding tables to ensure mathematical consistency and accurate interpretation of the decomposition estimates. The revised decomposition findings have been updated throughout the manuscript accordingly, and the residual component has also been clarified to improve transparency in interpretation.

Comment 16: Several values in Table 5 appear inconsistent. “Type of cooking fuel”:

• Absolute contribution = -0.0034, % contribution = 0.002. These are incompatible.
• Type of toilet: check % contribution .
• Mode of delivery: CS and home delivery % same?
• Please recheck all data again and provide a supplementary calculation appendix or Stata code.

 

Response 16: We thank the reviewer for carefully examining the decomposition results and identifying these inconsistencies. In response, we have thoroughly rechecked and reassessed the decomposition analysis, including the calculation of absolute and percentage contributions for all determinants. Necessary corrections have now been made in the revised model and corresponding tables to ensure internal consistency and accurate interpretation of the results. The revised decomposition estimates have been updated throughout the manuscript accordingly.

 

Comment 17: Appendix A2 reports state ECIs, but many states have very small sample sizes, and hence, estimates may be unstable. Please report CIs. Discuss instability for UTs/small states.

 

Response 17: We thank the reviewer for this comment. We acknowledge that ECI estimates for smaller states and UTs may be less stable because of relatively smaller sample sizes and lower numbers of neonatal deaths. In response, we have now reported standard errors alongside the state-level ECI estimates in Appendix A2 to provide an indication of the statistical variability and precision of the estimates. We have additionally included a brief note in the Discussion section acknowledging the potential instability of estimates for smaller states and UTs and recommending cautious interpretation of these findings.

“Substantial interstate variation in wealth-related inequality in neonatal mortality was also observed. States such as Uttarakhand, Chhattisgarh, Meghalaya, Jharkhand, and Odisha demonstrated particularly high levels of pro-poor inequality. However, the estimates for certain smaller states and UTs should be interpreted cautiously because relatively smaller sample sizes may reduce the precision and stability of ECI estimates. Although statistically significant inequalities were observed in several states, wider confidence intervals in smaller populations may limit comparability across regions.” [Line no 388-393]

• Results:

Comment 18: Please avoid causation language despite a cross-sectional design.

Response 18: We thank the reviewer for this important observation. We have carefully revised the manuscript to replace causal language with more appropriate terms indicating association, contribution, or relationship throughout the results and discussion sections.

Comment 19: The paper states that ASHA contact increased inequality. they often target disadvantaged women. This may reflect program targeting rather than adverse effects.

Response 19: We thank the reviewer for this important interpretation. We agree that the observed positive contribution of ASHA contact to inequality should not be interpreted as an adverse effect of the programme itself. Rather, it likely reflects the targeted engagement of ASHA workers among socioeconomically disadvantaged and higher-risk populations, where the burden of neonatal mortality is already greater. We have explained this in the discussion sections to clarify that this finding may represent appropriate programme targeting toward vulnerable groups rather than an increase in inequality attributable to ASHA contact. [Line no 412-418]

Comment 20: The finding that non-aspirational districts have greater wealth inequality than aspirational is counterintuitive requiring deeper exploration. Are aspirational districts more homogeneously poor (thus less inequality despite higher mortality)?

Response 20: Thank you for the suggestion. This issue has now been acknowledged and discussed in the revised manuscript.

The discussion section now states that “the relatively lower wealth-related inequality observed in aspirational districts, despite their poorer health indicators, may reflect a more homogeneous distribution of deprivation, resulting in elevated neonatal mortality across socioeconomic groups and consequently lower relative inequality. The revised discussion also highlights the possible influence of intensified monitoring, targeted resource allocation, and focused implementation under the Aspirational Districts Programme. However, we also note that further investigation is required to determine whether these patterns reflect actual improvements in equity or differences in the socioeconomic distribution of neonatal mortality within districts.” [Line no 379-387]

Comment 21: Table 2 is excessively dense. Please split it. Use consistent decimal formatting.

Response 21: We thank the reviewer for this helpful suggestion. In response, we have revised the presentation of the results tables to improve clarity and readability. The descriptive characteristics of the study population are now presented separately in the main manuscript, while the multivariate analysis is summarized using a figure presenting the adjusted odds ratios for determinants of neonatal mortality. The detailed table of the unadjusted and hierarchical model of adjusted regression analysis have been moved to the appendix for reference.

Comment 22: The Introduction is somewhat long and repetitive regarding national initiatives.

Response 22: Thank you for the valuable suggestion. The Introduction has been substantially streamlined to reduce repetition, particularly regarding national initiatives and policy programmes. Relevant sections have been condensed to improve clarity, readability, and focus on the study objectives and research gap.

Round 2

Reviewer 4 Report

Comments and Suggestions for Authors

Thank you for addressing queries. I still have a few reservations:
1. Maternal age at first birth classification should be 18- 35 years, not <16- 35. The legal marriage age in the country is 18 years. Why do we want a 16-year cut-off?

2. What threshold of anemia was used (please mention in Table 2)
3. Figure 1- Mention for which parameters the adjustment was done. 

Comments on the Quality of English Language

It still needs editing. 

Author Response

Comments and Suggestions for Authors:

Thank you for addressing queries. I still have a few reservations:
Comment 1. Maternal age at first birth classification should be 18- 35 years, not <16- 35. The legal marriage age in the country is 18 years. Why do we want a 16-year cut-off?

Response 1: We thank the reviewer for the valuable input. The categorization of maternal age at first birth was based on the distribution of the study population and the operational definition used in the original analytical framework. However, we agree that the threshold of 18 years has greater public health and policy relevance in the Indian context, particularly given the legal minimum age at marriage. Accordingly, we have revised the categorization to <18 and ≥35 years and 18–34 years, and updated the methods, analysis, results and corresponding tables throughout the manuscript

Comment 2: What threshold of anemia was used (please mention in Table 2)

Response 2: Thank you for the suggestion. Anemia was defined using the World Health Organization threshold of Hb <11.0 g/dL during pregnancy. To improve clarity, we have now specified this threshold in Table 2 and the corresponding variable description in the Methods section.

Comment 3: Figure 1- Mention for which parameters the adjustment was done. 

Response 3: We thank the reviewer for this suggestion. Figure 1 presents the adjusted odds ratios obtained from the final hierarchical multivariable logistic regression model (Model V). As the estimates are derived from the fully adjusted model, each variable is adjusted for all other variables retained in the final model. To improve clarity, we have revised the figure caption to explicitly state that the reported odds ratios represent mutually adjusted estimates from the final multivariable model.

Comment 4: Comments on the Quality of English Language. It still needs editing. 

Response 4: We thank the reviewer for this comment. The manuscript has been carefully edited throughout to improve clarity, readability, grammatical accuracy, and overall language quality, with particular attention to sentence structure, consistency of terminology, and adherence to academic writing standards.