The long-term effects of free care on birth outcomes: Evidence from a national policy reform in Zambia

As women in many countries still fail to give birth in facilities due to financial barriers, many see the abolition of user fees as a key step on the path towards universal coverage. We exploited the staggered removal of user charges in Zambia from 2006 to estimate the effect of user fee removal up to five years after the policy change. We used data from the birth histories of two nationally representative Demographic and Health Surveys to implement a difference-in-differences analysis and identify the causal impact of removing user charges on institutional and assisted deliveries, caesarean sections and neonatal deaths. We also explored heterogeneous effects of the policy. Removing fees had little effect in the short term but large positive effects appeared about two years after the policy change. Institutional deliveries in treated areas increased by 10 and 15 percentage points in peri-urban and rural districts respectively (corresponding to a 25 and 35 percent change), driven entirely by a reduction in home births. However, there was no evidence that the reform changed the behaviours of women with lower education, the proportion of caesarean sections or reduced neonatal mortality. Institutional deliveries increased where care quality was high, but not where it was low. While abolishing user charges may reduce financial hardship from healthcare payments, it does not necessarily improve equitable access to care or health outcomes. Shifting away from user fees is a necessary but insufficient step towards universal health coverage, and concurrent reforms are needed to target vulnerable populations and improve quality of care. We used information contained in the 2007 and the 2013–2014 Zambia Demographic and Health Surveys (DHS) for all the births that women had in the five years before the interview. These 5-year birth histories allowed us to construct a dataset containing detailed information on births over a ten-year period spanning over the two policy changes (see the timeline of policy reforms and data used in Figure B1 in Online appendix). Given the staggered rollout of the policy, we defined three groups in our datasets: (1) individuals living in rural districts where care was free from April 1st, 2006; (2) peri-urban areas in urban districts where fees are removed on June 1st, 2007 and (3) urban areas of urban districts where fees remained in place until January 2012. For the purpose of our analysis we excluded any birth that occurred after January 2012, so that urban areas remain a control group where user charges apply throughout the analysis period. For each birth, we considered the effect of the policy on four outcomes. In this paper we extend the work of Chama-Chiliba and Koch (2016) and look at the effect of user fee removal for another five years post reform. Firstly, we considered the place of delivery, and constructed a binary indicator equal to 1 if the woman gave birth in a public or mission healthcare facility where the policy change occurred, and 0 otherwise. Secondly, we considered if the woman was assisted by a skilled birth attendant (doctor, nurse or midwife) during a delivery. This is relevant because maternal and neonatal health outcomes are likely to be better in the presence of a qualified staff. In addition, if the policy change fuelled staff shortages, the proportion of assisted deliveries could have fallen. Thirdly, we considered whether the delivery was done by caesarean section for two reasons. On the one hand, it is generally recognised that low rates of c-sections, such as the one observed in Zambia before the policy change, are insufficient to cover all the life-threatening events that can occur at birth (Belizán, Minckas et al., 2018). Any increase in the C-section rate resulting from the policy change could therefore be interpreted as an increase in access to life-saving procedures for mothers or babies. On the other hand, one could worry about the capacity of the health system to absorb a sharp increase in the volume of institutional deliveries. Without an adequate response on the supply-side, notably through the provision of adequate medical supplies and staff, one could see a reduction in the proportion of c-sections undertaken. Finally, we considered neonatal mortality, specifically whether the child dies on the day of the delivery or within the first 28 days. Both are strongly linked to the conditions in which women deliver and can be seen as potential indicators of the effectiveness of care received. Table 1 shows the descriptive statistics for the analytical sample of mothers and births, spanning the period 2002–2011. A few salient facts should be noted between the two sets of ‘treated’ areas where fees were removed (rural districts and peri-urban areas) and the control (urban) areas. In treated areas, women were from less wealthy households, had more children and were more likely to have a lower education level. There were also fewer institutional deliveries in these treated areas compared to urban areas, although the overwhelming majority of these deliveries were assisted by a qualified staff. Only a small proportions of births were done by caesarean sections (from 3% in rural and peri-urban areas to 7% in urban areas), and less than 3% of babies born died within the first 28 days. Sample description. Data are n (%) or mean (SD). We use a Difference-in-difference (DiD) approach to identify the intention-to-treat (ITT) effect of the policy. For a given birth event yidt occurring at time t for individual i living in district d, we estimated a specification of the form: where the variable after is coded 1 if the child was delivered after user fees were removed and 0 otherwise and treated is a dummy variable coded 1 if the woman currently lives in a treated area, and 0 if she lives in a control area. We also include district (φd) and year (ψt) fixed effects, allowing us to capture respectively, any time-invariant district characteristics and any changes that would have occurred over the study period (e.g. increase in income). The ITT effect of user fees removal on outcome is given by βˆ3 on the interaction term. Although all outcomes are binary, we estimated linear regressions for ease of interpretation so that βˆ3 can be interpreted as the (percentage point) increase in the outcome in the treated group, compared to its pre-reform level. We also present results from logistic regressions in the online Appendix. We undertook two separate analyses. First, to identify the effect of the policy of the first phase of the policy roll out occurring in April 2006, we restricted the sample to rural districts (treated areas) and urban areas of urban districts (control areas). This analysis estimated the effect of the policy in rural districts. Second, we identified the effect of the policy in peri-urban areas, and restricted the sample to peri-urban (treated) and urban (control) areas of urban districts, with the policy change occurring from June 2007. We used the location of the DHS sampling cluster in which a woman lived at the time of the interview to infer which policy has applied to her during her entire birth history. As DHS data include the name of the district in which the household lives, determining which women lived in one of the 54 districts in which the 2006 policy change occurred was straightforward. To determine whether a woman lived in peri-urban areas of urban districts, we used the GIS coordinates of her sampling cluster and calculated the distance to the administrative centre of the district, the criteria used by health authorities to identify peri-urban areas – see Appendix C in the Online appendix for further details. Note that the assignment to treatment status makes two assumptions. First, we assumed that a woman has always resided in the same area in the last five years. Second, we assumed that the random displacement of the DHS sampling clusters does not interfere with assignment with the treatment status (Perez-Heydrich, Warren, Burgert, & Emch, 2013). We discuss these assumptions later. A key identifying assumption for a valid DiD estimation is that outcomes in the treatment and control group were following a similar path before the policy change. We provide graphical evidence to check this assumption in Figures B2–B4 in the online appendix. The data support the assumption for most outcomes, except neonatal mortality, where trends are only parallel from 2003. Hence, we excluded data from 2002 for this outcome. Beyond the analysis of the main effects of the policy change, we performed three sub-group analyses. To avoid performing an under-powered analysis, we do not perform this analysis on the two outcomes linked to more rare events (caesarean sections and neonatal deaths). First, we considered whether the policy benefitted differently women coming from the poorest and richest households (see supplementary material for the definition of the wealth quintiles). Second, we looked at the effects for women with low education (no or incomplete primary education) and others. Another important policy question, less frequently studied in the literature on fee removal is whether the quality of care provided in a facility contributed to women’s decisions to give birth in a facility, and to changes in health outcomes. We looked at the effects of the policy in areas with low or high quality care at the time of the delivery, based on a proxy indicator for care quality defined based on the average quality of antenatal care received by women in the area (see section D of the online Appendix for more details). We ran separate difference-in-difference models for each group and we report the policy effect for each sub-group in a graph. To test whether differences across groups were statistically significant, we ran triple-difference models on the relevant analytical sample (i.e. including two groups of interest only), where the coefficient on the triple interaction term (δ4) provides the differential effect between the two groups.