Modelling Welfare Transitions to Prioritise Sustainable Development Interventions in Coastal Kenya
Round 1
Reviewer 1 Report
I think you need to re-orient your thesis and presentation to help the reader understand your focus. I think your amazing findings relate to women as head of households and what can be done to help them. You weave this in and out of your paper -- and yet it is your one true finding. Also, I didn't find a clear description of the three waves. Attached is my comments on your actual paper. The research seems is very impressive!
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Author Response
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Reviewer 2 Report
This article is well researched and well written. My only recommendation would be to include the interview questions. In addition, a brief summary of the responses would also be nice. Finally, how many people were interviewed? Why that number of people? In the interview process what was being observed? In other words did the respondents talk freely?
Author Response
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Reviewer 3 Report
Report
Modelling welfare transitions to prioritise sustainable development interventions in coastal Kenya
Summary
The paper investigates determinants and transition patterns of welfare in the coastal region of Kenya. To this end, the authors use a panel survey of households. They construct a multi-dimensional and a subjective measure of welfare, which they use in a random effects regression to pin down the importance of different (policy and infrastructure) variables. They identify four main areas that are associated with higher welfare: education, (b) energy, (c) drinking water, and (d) sanitation.
I think the paper addresses an important aspect of development policies. While global development goals are often very extensive and overlapping, local government would need a more narrow recommendation to target their policies more efficiently.
General comments
1. While the paper is well written, the analysis is often superficial and leaves the reader with questions. For example, the multi-dimensional index is never clearly derived. The authors follow broadly the KNBS 2018 construction of the welfare measure, line 149. As it is not an exact replication of the index, more information should be provided (at least in an appendix). Similarly, the panel is not well described. Does it follow households. What is the attrition rate, from the data it seems there is non, which is very unlikely.
2. I would have wished more discussion on the multi-dimension welfare measure vs. subjective welfare measure. While the former is often seen as more “objective” the latter matters more for the individual. In this regard, the paper falls dramatically short. It mentioned very briefly cognition bias, but never explains it in detail cites relevant work.
3. In general, the authors show correlation but no causation at all. It is never mentioned in the paper. I think this is very important to point out, especially if any policy recommendations are derived from the analysis. In this regard the authors omit a complete strand of literature in development economics, that explicitly tries to deal with the correlation vs. causation issue and individual policies, i.e., there is a long literature of randomized controlled trials (RCTs) in Africa that assess economic well-being in a very clean empirical way, see for example Bouguen et al. (2019) or the extensive work of the recent Noble prize winners (Abhijit Banerjee, Esther Duflo and Michael Kremer). Thus, their findings need to be embedded much more carefully in the literature and their contribution needs to be pointed out in this regard.
4. The use of the random effects (RE) model is not properly motivated and differentiated from a fixed effects (FE) model. The authors acknowledge in a note that a test is available to differentiate between FE and RE models. They do not use it as it rejects the null too often. Still I would like to see the results of the test, at least in the appendix. If the rejection is only weakly significant in a statistical sense I could agree with the authors, but as they do not show the results, I have to assume that is strongly rejected and using a FE model would only yield insignificant results.
Specific comments
1. After almost 1.5 pages I get the aim of the paper, i.e. line 84 onwards. The authors should state more clearly and earlier what the goal of the paper is and only later explain why it adds to the literature.
2. Is it really a panel, are the same households / individuals interviewed again? What is the panel attrition rate? What was the procedure to deal with non-respondents? HH moving from one region to another?
3. The definition of quintile seems a bit odd. In statistics that usually means that the group is split in five equal (in size) sub-groups. Here it seems that the index was split in 5 equal parts and the size of the group varies for each “quintile” or cutoff of the index.
4. The welfare index is a relative welfare measure, as it is normalized to be between 0 and 1. This should be mentioned.
5. The authors follow broadly the KNBS 2018 construction of the welfare measure, line 149. As it is not an exact replication of the index, more information should be provided (at least in an appendix).
6. Comparing the share of Chronic poor and non-poor with regard to the subjective and multi-dimensional welfare measures in Table 3 and 4 is a bit arbitrary. The authors set the poor definition of the multi-dimensional measure to 0.4, if they would have use 0.3 or 0.5 the shares would change mechanically. I think it makes only sense to compare these measures with regards to the difference between groups, e.g. sex, as done in Table 4. Maybe a sensitivity analysis in this regard would shed more light on this issue.
7. Line 201 -203 argument about enumerators is odd and does not address a FE vs RE decision. If you are interested in (hugely) time-invariant variables such as female HH head or location a FE model will not work, independent of the enumerator. An alternative procedure to deal with this might be interaction of time-invariant variables with time-variant variables, that allow some degree of interference. But again, the authors do not clearly state any reason why they use a RE model.
8. Lines 205-207 from a theoretical point this is correct, but I would like to see a clearer link to the data at hand. How do the authors know that the unobservable is almost time-invariant, it is by definition unobservable? I neither see the Stock and Watson reference as an argument against a FE model, it controls for time-invariant unobservable factors and hence any residual variation of the dependent variable is due to time-variant variation of other independent variables.
9. Line 212, what is this argument about omitted variable bias. That is not only an issue with longitude data or panel data, but in all empirical estimations. A RE model does not fix an omitted variable bias.
10. Why are certain HH characteristics omitted, I am very surprised that HH size nor age of the head of HH or youngest child was recorded. That is very uncommon for this kind of surveys. However, in lines 467 and 468 it seems that this information is available to the authors.
11. The direct interpretation of Table 5 is very clearly described. I think from a policy view one should caution the reader that of course many of the independent variables are highly correlated and adjusting one might impact others. For example providing improved water services of course will improve sanitation. Similarly, better access to energy might imply that it is easier to obtain better education (better infrastructure). In a more general sense all the analysis relies on correlation and does not all imply causation. Basing policy recommendation on correlation is of course very problematic.
Minor comments
Font size change between lines 306 and 307
Table 2 format needs to be improved, very hard to read. Please mark tables with 2a and 2b or maybe use Table 2 and Table 3 instead.
Line 361 table above should be Table 3
Line 383 Table should be Table 4. Also check the numbering of all following tables.
Author Response
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Author Response File: Author Response.docx
Reviewer 4 Report
The data used in this study are considered to be important data related to welfare and sustainable development. However, as a study, you can point out the following:
This study needs to clarify its purpose.
The title is modeling welfare transitions to prioritise sustainable development interventions in coastal Kenya, but the introduction does not mention the relationship between welfare transition and sustainable development.
Nor is the purpose clearly stated.
It is necessary to systematically compare the differences with previous studies in order to acquire and persuade the measurement variables for welfare transition through this study.
However, this study does not systematically conduct literature research.
This study uses data from 2014 to 2016 on the outskirts of Kenya.However, in this area, socio-economic policies began to be implemented in 2013 and 2015. It is questionable whether the changes that occurred during this period could be immediately reflected in the period used in the study.
Table 1 should explain how the groups of variables were selected. This should be explained in the literature study after the introduction. In particular, in the study for modeling as in this study, the problem of variable selection is very important. However, this study does not explain this.
Therefore, it is difficult to secure the validity of the proposed research model.
Author Response
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Author Response File: Author Response.docx
Reviewer 5 Report
The study, based on three household panels from 2014 to 2016, offers an interesting attempt to evaluate welfare transitions in the area of Kwale County (Kenya).
However, there would seem to be a need for some even more detailed informationon the survey structure and contents.
Relating to the paragraph2.2(measuring welfare and transition) it could be interesting to better focus on both how the multidimensional welfare index was constructed and why exactly a welfare index value less than 0.40 was considered an indicator of a situation of poverty (and of non-poverty if equal to 0.40 or greater).
More generally, there is a need to better verify percentage values reported in the text and rounding rules applied: see for example lines 169-173 (51+38+12=101) and Table 1.
Author Response
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Author Response File: Author Response.docx
Round 2
Reviewer 3 Report
The authors made considerable effort to improve the paper. Some of my previous points have been addressed by the authors and I believe the paper has improved after the revision. I still have some concerns regarding the paper and the empirical analysis.
1. The sampling strategy is still not clear. 300 functional hand pumps for each 6 households were selected, thus 1800 survey participants. Where does the number of 3500 survey participants come from?
2. What is the stratum here? Location? Other attributes? Not clear at all what was done. Weights or number of surveyed households were adjusted to the stratum?
3. Please do not select an estimation technique based on the lower standard errors of the coefficients, that is essentially p-hacking. I am fine with the other arguments regarding RE vs. FE models, but the (mechanical) lower standard errors are not an argument in favor of RE.
4. The sentence in line 276 is incorrect: “The key insight being that if the unobserved variable does not significantly change over time, then any changes in the dependent variable may be due to influences other than these fixed effects (Allison, 2005).” If the unobserved variables do not vary significant over time, they will be fully subsumed by the fixed effect and thus any remaining within household variations will be due to changes of other (observable) variables over time. This would be also consistent with the reasoning to select RE model due to the time-invariant gender of the household had, in line 284.
5. I understand the problems of measuring a consistent household size, but excluding household size almost certainly introduces an omitted variable bias. First, the authors should discuss the direction of the bias if they really want to exclude household size. Second, the authors could estimate a mixed model and include survey waves fixed effects that should account for any regular seasonal varying migration patterns of households.
6. Age of the household is clearly an easily measurable variable and I see no reason to justify its exclusion from the regression. Same holds for employment status. Excluding these let me believe that the results are not robust to the inclusion and all the results are actually driven by the omitted variable bias.
Author Response
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Author Response File: Author Response.docx
Reviewer 4 Report
이 연구는 첫 번째 검토에서 지적 된 내용을 충실히 수정했습니다.
특히, 연구의 목적과 이전 연구와의 차이점에 대해 자세히 설명했습니다.
또한 연구 목적에 적합한 변수를 선택하는 과정에 대한 추가 설명이 제공되었습니다.
다른 불가피한 것들이 한계에 언급되어 있습니다.
Author Response
We are grateful to the reviewer for their positive feedback and confidence in the structure and contributions of the paper to literature, policy and practice.
Round 3
Reviewer 3 Report
No further comments
