Did primary healthcare user fee abolition matter? Reconsidering South Africa's experience

Abstract

South Africa waived user fees for primary healthcare in 1994 and, again, in 1996. The first waiver focused on young children, elderly adults, pregnant women and nursing mothers, while the 1996 reform waived fees for the remainder of the population, subject to means tests. We take advantage of household survey information to examine the impact of the policy on a subset of the reform-eligible population. Although it was expected that public healthcare facility usage would have increased post reform, no statistically significant evidence supported such a claim. Therefore, our results are consistent with some very recent research examining the 1994 reform, but are generally at odds with the general impression in the literature that user fee abolition matters when it comes to alleviating inequities in access to healthcare.

Keywords:

• user fees
• differences in differences
• multinomial logit

JEL codes:

• I18
• H31

1. Introduction

President Mandela, of the newly elected democratic government of South Africa, announced that primary healthcare services would be provided without charge at all state facilities. The official policy, enacted 1 June 1994, was for children under the age of six years, pregnant and nursing mothers, and the elderly, as long as they were not currently members of a medical scheme (South African Government, 1994; Wilkinson et al., 1997; Leatt et al., 2006). Additional abolition measures ensued shortly thereafter. Following an announcement on 1 April 1996, all other South Africans with a few exceptions (members of a medical scheme, and those living in a household earning more than R100 000 per year) were allowed access to primary healthcare at public clinics without user charges (McCoy & Khosa, 1996; Leatt et al., 2006).

The preceding policies have received attention in the literature, although from limited sources of information. According to some, utilisation of public health services increased following the 1994 abolition (McCoy & Khosa, 1996; Wilkinson et al., 1997; Schneider et al., 1997; Schneider & Gilson, 1999). More recent research, however, is less supportive. With respect to the 1996 reform, however, even the early evidence varies. Both increases (Wilkinson et al., 2001; Bayat & Cleaton-Jones, 2003) and decreases (Schneider & Gilson, 1999; Wilkinson et al., 2001) in utilisation have been observed.

A number of other African countries have also abolished public healthcare user fees, and much of the available research finds increases in healthcare utilisation to be associated with these policies, as well. Increased utilisation has been found in Uganda (Burnham et al., 2004; Nabyonga et al., 2005), Zambia (Masiye et al., 2008) and Kenya (Mbugua et al., 1995; Mwabu et al., 1995). However, reviews of the user fee literature suggest that there are serious problems with these earlier studies, as they tend to focus on only a small set of clinics, are not representative, and do not include a proper control group for comparison (Lagarde & Palmer, 2008; Ridde & Morestin, 2011).

The preceding reviews have led to a re-examination of policy impacts in both South Africa (Koch, 2012; Koch & Racine, 2013) and Zambia (Chama-Chiliba & Koch, 2014), amongst others. In each of the previous cases, which make use of more recent developments in programme evaluation, the re-examination has uncovered minimal effects. However, the 1996 reform has not yet been re-evaluated, and thus it remains an open question: has the 1996 reform offered more benefits than the 1994 reform? In an effort to address this question we extend the analysis of Koch (2012) and Koch & Racine (2013), who examine only the 1994 reform. Our data include information collected before and after the 1996 user fee abolition. Since the information is available for both a control group and a treatment group, the analysis hinges upon an application of difference-in-difference (DD) methods. The control group is young children, who had access to free healthcare before the 1996 reform as well as after. This control group is compared with a set of older children, who did not have access to free public healthcare until after the 1996 policy announcement. Given that the 1996 policy focuses on those without access to a medical scheme (health insurance) and on those living in households with less than R100 000 (US$1 = 4.35ZAR on 1 April 1996) in earnings, our treatment and control groups are similarly demarcated. The data are taken from the 1995 and 1996 October Household Surveys (OHSs) (Statistics South |Africa, 1995, 1996) and were combined in an effort to consider healthcare-seeking behaviour for children, focusing on facility choice.

Unfortunately, the results find little, if any, meaningful effect. Neither sick nor injured children, at least those who became eligible for free primary care, were more likely to make use of public healthcare facilities. The results therefore suggest that extending free healthcare to a wider section of the more vulnerable members of society had no statistically significant impact on the use of that healthcare.

2. Background

Preceding 1994, South African health policy was racially stratified; four race groups were classified and segregated, and each had its own health department with varying levels of resourcing. Healthcare expenditure in fiscal year 1992 was R122 per capita in the poorest districts, but R437 per capita in the richest districts (McIntyre et al., 1995). Unsurprisingly, the result was racially stratified health outcomes and healthcare utilisation. In the 10 years between 1988 and 1998, infant mortality rates were 11.4 per 1000 and 53.6 per 1000 for whites and for Africans in non-urban settings, respectively (Medical Research Council et al., 1999).

The new government inherited a fractured health system in need of restructuring. In addition to the racially segregated health departments, there was a system of user charges, although the system was not designed as a full cost recovery system. During the 1992 fiscal year, shortly before fees were abolished, fees covered only 4.5% of recurrent expenditure in South Africa (McIntyre, 1994), a figure more or less in line with the 5% observed in other African countries (Creese, 1990). In 1994, free healthcare covering all services and all children under the age of six, unless they were covered by a medical scheme, was made available at state health facilities, including hospitals, community health centres, clinics, mobile clinics and hospitals, where at least one-half of the expenditure is subsidised by the state (South African Government, 1994). The 1996 extension was announced in a budget speech, and, despite limiting coverage to clinics and those from relatively poorer households, was unexpected (McCoy & Khosa, 1996; Leatt et al., 2006).

In addition to the changes in user charges, the South African government unlocked resources for the health of its citizens. Between fiscal years 1992 and 1998, public resources devoted to the public health sector grew between 1% and 1.5% per year in real terms (Thomas et al., 2000). The fact that increased resources were devoted to the public health sector is important to the analysis for two reasons. The first is that it shows the South African government's commitment to improved health, raising the expectation of some policy success. The second is that it underscores the importance of the DD approach, described below, and the need for observing the treatment and control groups over time.

3. Methodology

The methodology follows the DD estimator (Card & Krueger, 1993; Bertrand et al., 2004). Unlike in standard DD, based on linear regression, this analysis is subsumed in a multinomial logit regression. The employed structure is dictated by the analysis of healthcare provider choice, and there are four healthcare choice outcomes: no treatment, treatment at a public clinic, treatment at a non-clinic public health facility, and treatment at a private facility. Estimation via multinomial regression does assume that choices are independent of irrelevant alternatives; thus, for example, the probability of choosing public clinic care relative to private care is assumed to be independent of non-treatment. Although not reported in the analysis tables, we find that this assumption does not appear to be driving the results.

In terms of the policy, since user fees were abolished at public clinics, an increase in public clinic usage is hypothesised. Indirectly, it is also hypothesised that there will be a significant reduction in children not receiving any healthcare, when sick or injured, while the effects at private facilities and non-clinic public facilities are likely to be the reverse, due to substitution effects. Although we have an assumption regarding the substitution patterns, the true patterns are an empirical matter, and thus we allow the data to speak in this regard.

DD analysis is prefaced on fixed-effects panel data estimation, although it can be undertaken with either panel data or repeated cross-section data; the latter are used here. Within DD it is assumed that there are at least two groups, and that those two groups can be observed over at least two different points in time; for this analysis, there are exactly two groups and two points in time. The two groups will be referred to as younger (control) children and older (treated) children, because the policy affected these groups differently. The younger children, those under the age of six, are the control group, due to fact that these children had access to free primary healthcare at public clinics in both 1994 and 1996. On the other hand, children aged six years and older are placed in a treatment group, because these children were not included in the 1994 policy announcement but were included in the 1996 announcement.

To set the stage for understanding DD, we relate it to randomised controlled trials. In an ideal randomised controlled trial, the treatment and control groups would be identical before treatment, while everything outside the randomised controlled trial is assumed to remain constant, such that any difference following treatment can be ascribed directly to the treatment. However, outside the laboratory it is difficult to keep everything constant. Intuitively, in an ideal setting, DD removes differences between groups over time (Angrist & Pischke, 2009), such that any remaining difference can be ascribed to the treatment.

The operationalisation is accomplished through the use of dummy indicator variables. As noted above, the analysis is prefaced on fixed-effect panel analysis. One indicator is required to separate the younger (control) and older (treatment) children, another is used to separate the before and after samples, while a third indicator is used to separate the treated older children in the post-policy sample from all other subgroups; this last indicator variable underpins the DD estimate, and is referred to as the DD indicator. In addition to the indicator variables, a series of control variables are also included in the analysis, to account for the possibility that the initial treatment and control groups are not identical and to control for other aspects of healthcare utilisation decisions.

Although one would be tempted to consider only the before and after treatment group difference, this would ignore other changes; for example, the amount of public healthcare financing available to the public system. Changes in user fee policies as well as changes in government funding foci could have affected financing, and thus healthcare utilisation. However, comparing before and after across the two groups – that is, taking the difference between the differences – removes the bias that would arise from ignoring an important explanatory variable (Bertrand et al., 2004). In DD, the first set of differences is taken at the group level, and these describe the changes within the groups over time. The second difference is taken between groups, after the group differences have been calculated; thus, the second difference measures the relative change between the treatment group and the control group following policy reform. That relative change measures the effect of the policy.

In this analysis, unfortunately, the pre-1996 sample does not have the same characteristics as the post-1996 sample. We therefore undertake two further analyses, to see whether our results are affected by this sample difference. In the first additional step, as implied above, we considered the DDs of the control variables, because identification in DD requires common covariate trends. In other words, it might not matter if the samples are different. For example, as is the case here, the 1996 sample is poorer – see Table 1 – than the 1995 sample. Importantly, however, old children are not systematically poorer than young children (or vice versa) in 1996 than in 1995. Given that the control variables in the data are found to have common trends, we are not particularly worried about the underlying mean differences identified in the sample. However, for further surety, we took a second step. In the second additional step, we account for the asymmetry through the inclusion of separate time trends amongst the covariates that are found to have significant mean differences across the sample period. As there are only two time periods, variable-specific time trends are merely interaction terms based on a time period indicator crossed with each of the (significant) control variables. In other words, we control for differences in the samples by identifying observations as occurring in one or the other time period.

Table 1: Descriptive statistics of control variables

Variable	1995	1996	DD	Variable	1995	1996	DD
Survey year	0.000	1.000		Mother alive	0.973	0.977	–0.007
	(0.00)	(0.00)		(=1 if mother is known to still be alive)	(0.00)	(0.00)	(0.01)
Treated group	0.419	0.393		Father alive	0.879	0.865	0.014
(=1 if child is at least six years old)	(0.15)	(0.15)		(=1 if father is known to still be alive)	(0.01)	(0.01)	(0.03)
DD indicator	0.419	0.000		Urban	0.498	0.547**	0.037
(=1 if age ≥6 & year=1996)	(0.15)	(0.00)		(=1 if lives in urban locale)	(0.01)	(0.02)	(0.04)
African	0.780	0.856***	0.026	Distance to medical facility: <15 minutes	0.307	0.301	–0.038
(=1 if black African)	(0.01)	(0.02)	(0.03)	(=1 if household lives within 15 minutes)	(0.01)	(0.01)	(0.02)
White	0.030	0.023	–0.008	Distance to medical facility: 15 to 30 minutes	0.336	0.316	0.020
(=1 if white)	(0.00)	(0.00)	(0.01)	(=1 if household 15 to 30 minutes away)	(0.01)	(0.01)	(0.04)
Asian	0.046***	0.026	0.006	Distance to medical facility: 30 to 60 minutes	0.196	0.199	0.038
(=1 if Asian)	(0.00)	(0.01)	(0.01)	(=1 if household 30 to 60 minutes away)	(0.01)	(0.01)	(0.02)
Coloured	0.144***	0.095	–0.024	Distance to medical facility: >60 minutes	0.161	0.175	–0.025
(=1 if mixed race)	(0.01)	(0.01)	(0.03)	(=1 if household lives at least 60 minutes)	(0.01)	(0.01)	(0.02)
No children <6	0.195*	0.163	0.050	Own home	0.461	0.816***	0.049
(=1 if no children under six in household)	(0.07)	(0.06)	(0.03)	(=1 if household lives in a home they own)	(0.01)	(0.01)	(0.03)
One child <6	0.425	0.465***	–0.013	Access to tap water	0.583	0.549	–0.008
(=1 if one child under six in household)	(0.02)	(0.02)	(0.02)	(=1 if have tap water in or near house)	(0.01)	(0.02)	(0.04)
Two or more <6	0.380	0.371	–0.037	Access to flush toilet	0.399***	0.325	–0.030
(=1 if two children under six in household)	(0.05)	(0.05)	(0.02)	(=1 if have a flush toilet in or near house)	(0.01)	(0.01)	(0.03)
One adult	0.109	0.100	0.016	Access to phone	0.176	0.254***	0.040
(=1 if only one adult in household)	(0.01)	(0.01)	(0.02)	(=1 if own or rent phone)	(0.01)	(0.01)	(0.03)
Two adults	0.408	0.411	–0.061	Refuse regularly collected	0.457	0.480	0.015
(=1 if two adults are in the household)	(0.01)	(0.01)	(0.05)	(=1 if refuse is regularly collected)	(0.01)	(0.01)	(0.03)
Two + adults	0.483	0.489	0.045	Log expenditure	7.023***	6.061	–0.115
(=1 if more than two adults in household)	(0.01)	(0.01)	(0.04)	(= natural log of reported expenditure + 1)	(0.02)	(0.05)	(0.09)
Western Cape	0.088	0.085	–0.017	Rooms per capita	1.145	1.180	0.074
(=1 if lives in Western Cape)	(0.01)	(0.01)	(0.02)	(= rooms per person in dwelling)	(0.02)	(0.02)	(0.05)
Eastern Cape	0.214*	0.178	–0.013	Prop adults in union	0.078	0.077	0.011
(=1 if lives in Eastern Cape)	(0.01)	(0.01)	(0.02)	(= proportion adults in labour union)	(0.01)	(0.00)	(0.01)
Northern Cape	0.044	0.040	–0.013	Prop adults NLFP	0.385	0.573***	0.021
(=1 if lives in Northern Cape)	(0.00)	(0.01)	(0.01)	(= proportion adults not participating work)	(0.01)	(0.01)	(0.03)
Free State	0.080	0.071	–0.005	Prop adults employed	0.508***	0.316	–0.029
(=1 if lives in Free State)	(0.00)	(0.01)	(0.02)	(= proportion of adults that are employed)	(0.01)	(0.01)	(0.03)
KwaZulu-Natal	0.287***	0.151	–0.017	Prop adults matric	0.144	0.154**	–0.006
(=1 if lives in KwaZulu-Natal)	(0.01)	(0.01)	(0.02)	(= proportion of adults with matric)	(0.00)	(0.00)	(0.01)
Northwest	0.105	0.110	0.054**	Prop adults no school	0.154	0.159	–0.014
(=1 if lives in Northwest Province)	(0.01)	(0.01)	(0.03)	(= proportion of adults no schooling)	(0.01)	(0.01)	(0.03)
Gauteng	0.077	0.163***	0.011	Prop adult smokers	0.269	0.247	–0.050
(=1 if lives in Gauteng Province)	(0.00)	(0.01)	(0.03)	(= proportion of adults that are smokers)	(0.01)	(0.01)	(0.03)
Mpumalanga	0.080	0.079	–0.017	Children hungry	0.570***	0.285	0.037
(=1 if lives in Mpumalanga Province)	(0.01)	(0.01)	(0.02)	(=1 if children ever went hungry past year)	(0.01)	(0.02)	(0.04)
Limpopo	0.026	0.122***	0.016
(=1 if lives in Limpopo Province)	(0.00)	(0.01)	(0.02)	Observations	1 803	1 163

Source: 1995 and 1996 OHS data used in the analysis, limited to children under the age of 12 and reported as ill in the past 30 days. Reported standard errors clustered at the level of the household and reported in parentheses, along with tests of mean differences between 1995 and 1996. ***p <0.01, **p <0.05, *p <0.1 denote statistical significance of differences between 1995 and 1996, or, in the case of DD, represents significant difference from zero. The DD column provides a simple (without additional covariates) difference-in-difference estimate of the variable to determine whether the variable is potentially confounding the identification strategy used in the analysis. NLFP = non-labour force particpant.

Finally, as there are multiple healthcare options from which to choose, policy effects are likely to be substitutable. Benefits are expected to accrue with respect to ‘public clinic treatment’, and therefore some other option is not used. However, the pattern might be complicated, depending upon whether the policy made treatment more likely. Specifically, once an individual is ill, they can choose not to receive any healthcare, or they can choose to take advantage of a public clinic, another part of the public sector or the private sector. Thus, reducing the cost of public clinic access could reduce the probability that individuals seek no treatment, or it could reduce the probability of treatment from private providers or non-clinic public providers. Given the multiple options and the required substitutability of options, the DD representation we estimate is set within a multinomial logit framework. However, the parameter estimates from a multinomial regression are not informative about the size of the effect, only the direction. Therefore, effect sizes are calculated from the marginal effect of the DD indicator on each facility choice. The marginal effect of the DD indicator is the estimate of the change in the probability of choosing one of the four facilities.

4. The data

4.1 Data source

Data for the analysis were sourced from two South African OHSs, one from 1995 and another from 1996. The first of these surveys is the most recent available preceding the 1996 reform, while the second occurs only a few months after user fees were abolished for all. Data also exist for 1993, 1994, 1997 and 1998. Unfortunately, in 1993 and 1994 the surveys did not properly capture the public–private divide in healthcare facility use; the 1997 data did not include most of the health questionnaire responses; while the 1998 data could be deemed too many years after the reform. However, it should be noted that earlier analysis did consider 1998; the results from that survey were not all that different from what is reported below, when it comes to the impact of policy on public clinic use.

Each year, the OHS obtains responses from a stratified random sample of individuals in the population, and these can be weighted to match the demographic profile of the country. However, weights are not used in the analysis, since they are meant to reflect the population make-up, and not illness make-up. Stratification is based on province, magisterial district, urban or rural locale and population group, and is set to match the census frames. However, as noted in the methodology, these surveys are different in a variety of respects, which are dealt with in the analysis.

The main purpose of the OHS was to collect information from households and individuals across the nine provinces of South Africa, focusing specifically on socioeconomic development and labour market issues. Although the surveys collect detailed information related to socio-demographics and employment, only limited information related to health and healthcare behaviour is available. Health data include injuries or illnesses in the 30 days prior to the interview, whether or not the individual had access to a medical aid scheme, whether or not care was sought for the illness or injury, and the ownership of the facility (public or private) at which care was sought.

As the policy reform was meant to cover only those without access to health insurance, and living in households with less than R100 000 in earnings, information on these two variables were needed to limit the sample to an appropriate sample. Furthermore, given that the initial 1994 policy reform only affected children up to the age of six, this analysis focuses only on children near that age, which was chosen to be up to the age of 11. After limiting the sample, the 1995 sample included 1803 children while the 1996 sample contained 1163 children. Although not reported here, a previous analysis with children up to the age of 18 was also undertaken, and it led to similar results (Brink, 2012). The analysis focuses on the treatment received by an ill or injured child and the location thereof: an ill or injured child receiving no treatment, an ill or injured child receiving treatment at a public clinic, an ill or injured child receiving treatment at a non-clinic public facility, or an ill or injured child receiving treatment at a private facility.

4.2 Control variables

The empirical literature on health facility choice suggests the inclusion of a number of different types of variables, such as price, travel time, illness characteristics, sex, age, education, income, household size, ethnicity and migrant status (Pronyk et al., 2001; Mariko, 2003; Moïsi et al., 2010). The South African empirical literature suggests a number of similar, as well as different, measures: income either in quintiles or in logs, asset measures, race, location, time to facility, insurance access, measures of facility quality, household size, number of dependents, head's education, head's gender, head's age and age squared, the proportion of working to non-working individuals, measures of illness and facility level information, where available (Havemann & van der Berg, 2003; Grobler & Stuart, 2007; Alaba & Koch, 2009). One weakness of our data, unfortunately, is that they do not contain information on either illness condition or quality of care, expected or actual.

Although the OHS data are limited in two important dimensions, quality of care and depth of illness, the data are rich in a number of other dimensions. In terms of demographics, and in line with the previously discussed literature, we include controls for location, ethnicity and whether or not either of the child's parents is alive. Although it is not possible to be certain whether the child lives with either of their parents, given the structure of the surveys, whether or not either of the child's parents is alive is used as a proxy.

Household resources that can be mobilised for the care of the sick or injured child are also included. As with the previously outlined literature, these measures include: a proxy for income, home ownership, and whether or not children in the household went hungry during the past year, due to lack of food. Other resources, household services, also form part of the control variable set, including tap water, flush toilets, landline or cellular telephones, and refuse that is regularly collected by a local authority.

A number of other variables are included to control for potential opportunity costs of time. We include the distance of the household, in minutes, from the health facility they would most likely use in the event of a need for healthcare; distance is self-reported. Although the distance does not capture resources, it does provide a proxy for the resource use that would be required to treat a sick or injured child. We also include household structure via categorical variables related to the number of children under the age of six (either zero, one or more), as well as the number of adults in the household (either one, two or more). We include two additional measures of adult availability, the proportion of employed adults in the household and the proportion of non-labour force participant adults in the household. We also include the proportion of adults in the household that are union members to control for the ability of employed household members to get time away from work, if a child needs additional attention related to healthcare-seeking activities.

In addition to the above controls, education has been shown to be positively associated with the demand for health, theoretically (Grossman, 1999) and empirically (Grobler & Stuart, 2007). For that reason, the proportion of adults having completed matric (high school) is expected to be associated with an increase in health-seeking behaviour, while the proportion of adults without any schooling is expected to reduce it. Along similar lines, the willingness to invest in health is also affected by preferences for health (Grossman, 1999), and therefore we include the proportion of adults in the household who are smokers to control for health preferences. Although measures of self-reported health or exercise would likely be a better measure, they are not available in the survey.

The most complex data development process was related to the calculation of earnings. In many surveys, including those undertaken in South Africa, it is not uncommon for earnings, either in business or in work, to not be recorded (Simkins, 2004). Although a number of options are available, and we considered a number of them, we finally settled on household expenditure. For the 1995 OHS, it is possible to merge the 1995 Income and Expenditure Survey (Leibbrandt et al., 2005); thus, it is possible to recover household expenditure. For 1996, on the other hand, it is necessary to trust the self-reported household expenditure information. Importantly, the expenditure information was more complete than the income information, and, since our focus in this analysis is not on the income effect, the measurement effect on the estimated parameters is not as worrisome.

5. Results

5.1 Data summary

The data are summarised in Tables 1 and Table 2, separated by survey year. Table 2 outlines the simple differences in the outcome variables over the survey years. Although no other controls are included, the estimates reported in Table 2 are not particularly encouraging, since they suggest increases in non-treatment, and, at best, limited effects of policy on public clinic use. The robustness of these results will be discussed below.

Table 2: Descriptive analysis of outcome variables

Outcome	1995	1996
No treatment	0.220	0.350***
	(0.02)	(0.02)
Public clinic	0.282	0.255
	(0.01)	(0.02)
Public other	0.298***	0.221
	(0.01)	(0.01)
Private	0.200**	0.174
	(0.01)	(0.01)
Observations	1 803	1 163

Source: Author's calculations of means. Robust standard errors in parentheses are clustered by household; ***p <0.01, **p <0.05 refers to statistical significance of the mean difference with respect to the opposite column.

Table 1, on the other hand, describes the data in the two samples. As has been noted, there are a number of differences between the children over the two sample periods, and thus a more careful analysis was also undertaken. To summarise, the data in 1996 are decidedly less urban, and contain fewer Asians and coloured children but more black children. In 1996, compared with 1995, fewer children are living in the Eastern Cape and KwaZulu Natal, while more children are living in Gauteng and Limpopo provinces. More households in 1996 have one child under the age of six, while fewer have no children under the age of six. Households in 1996 spent less but are more likely to own their home than in 1995. However, children in those households were less likely to go hungry at some point during 1995 than 1996. In terms of the adult proportional variables, there is a switch between non-labour force participant (NLFP) and employment, with the NLFP proportion higher in 1996 than 1995, while the opposite is true for the employment proportion; there is also some evidence of an increase in the proportion of adults having completed matric in 1996. Despite these statistically significant differences across sample years, there is little in the way of differential trends. In other words, the reductions or increases observed across the samples are not dependent on the age groups used in the analysis. Thus, we are confident that the results reported below are an appropriate representation of the average policy effect.

5.2 Difference-indifference estimates

Two sets of multinomial regressions were estimated. In the first, the variables described in the data section were used to control for potential confounding factors that could influence the choice of healthcare facility. The multinomial logit estimates for this regression can be found in Table 3. In the second analysis, trends in the control variables were also included. The multinomial logit regression estimates for the second analysis can be found in Table 4.

Table 3: Multinomial regression results

	Location and household controls			Wealth controls			Other household controls
Variable	Public clinic	Public other	Private	Public clinic	Public other	Private	Public clinic	Public other	Private
Survey year	0.584***	0.842***	0.634***	0.462***	0.812***	0.498**	0.463***	0.742***	0.363*
	(0.15)	(0.16)	(0.18)	(0.17)	(0.18)	(0.19)	(0.17)	(0.18)	(0.20)
Affected by policy	–0.731***	–0.562***	–0.616***	–0.746***	–0.575***	–0.625***	–0.745***	–0.569***	–0.593***
	(0.18)	(0.19)	(0.20)	(0.18)	(0.19)	(0.20)	(0.18)	(0.19)	(0.21)
DD – indicator	0.045	–0.136	–0.069	0.053	–0.129	–0.055	0.043	–0.126	–0.034
	(0.22)	(0.22)	(0.24)	(0.22)	(0.22)	(0.24)	(0.22)	(0.22)	(0.24)
Eastern Cape	0.156	0.165	0.180	0.210	0.202	0.273	0.237	0.271	0.340
	(0.30)	(0.27)	(0.31)	(0.29)	(0.28)	(0.31)	(0.30)	(0.28)	(0.32)
Northern Cape	–0.156	–0.492	–1.206***	–0.132	–0.447	–1.126***	–0.095	–0.338	–0.945**
	(0.33)	(0.32)	(0.41)	(0.33)	(0.33)	(0.42)	(0.34)	(0.33)	(0.42)
Free State	–1.556***	–0.571*	0.043	–1.532***	–0.513*	0.085	–1.524***	–0.499	0.073
	(0.37)	(0.31)	(0.32)	(0.38)	(0.31)	(0.33)	(0.38)	(0.31)	(0.34)
KwaZulu-Natal	–0.094	0.258	0.301	–0.073	0.288	0.345	–0.030	0.350	0.366
	(0.30)	(0.27)	(0.31)	(0.30)	(0.28)	(0.32)	(0.30)	(0.28)	(0.32)
Northwest	0.585*	–0.003	0.761**	0.649**	0.065	0.829**	0.691**	0.142	0.889***
	(0.32)	(0.31)	(0.33)	(0.33)	(0.32)	(0.34)	(0.33)	(0.32)	(0.34)
Gauteng	–0.432	0.212	0.423	–0.397	0.247	0.453	–0.391	0.208	0.365
	(0.32)	(0.28)	(0.32)	(0.32)	(0.28)	(0.32)	(0.31)	(0.28)	(0.33)
Mpumalanga	–0.301	–0.556*	0.287	–0.222	–0.464	0.328	–0.179	–0.391	0.370
	(0.35)	(0.33)	(0.35)	(0.35)	(0.34)	(0.36)	(0.35)	(0.34)	(0.36)
Limpopo	–0.229	0.087	–0.024	–0.163	0.164	0.023	–0.075	0.269	0.125
	(0.35)	(0.34)	(0.40)	(0.35)	(0.34)	(0.41)	(0.36)	(0.34)	(0.42)
Urban residence	0.012	0.196	0.304*	0.113	0.302	0.314	0.112	0.272	0.292
	(0.15)	(0.15)	(0.17)	(0.21)	(0.21)	(0.25)	(0.22)	(0.21)	(0.25)
White	–0.153	0.255	0.508**	–0.133	0.278	0.473*	–0.179	0.262	0.477*
	(0.25)	(0.23)	(0.25)	(0.25)	(0.23)	(0.26)	(0.26)	(0.23)	(0.26)
Asian	–1.320***	–0.286	0.383	–1.280***	–0.245	0.297	–1.211**	–0.232	0.168
	(0.49)	(0.33)	(0.32)	(0.50)	(0.34)	(0.32)	(0.50)	(0.34)	(0.33)
Coloured	–2.530***	0.141	0.852**	–2.447***	0.219	0.765**	–2.347***	0.203	0.465
	(0.76)	(0.35)	(0.37)	(0.76)	(0.36)	(0.38)	(0.78)	(0.39)	(0.41)
One child <6	–0.233	–0.369**	–0.335*	–0.232	–0.378**	–0.337*	–0.233	–0.399**	–0.385*
	(0.19)	(0.19)	(0.20)	(0.19)	(0.19)	(0.20)	(0.19)	(0.19)	(0.21)
Two + children <6	–0.306	–0.345*	–0.408*	–0.326	–0.368*	–0.407*	–0.335	–0.379*	–0.406*
	(0.21)	(0.20)	(0.23)	(0.21)	(0.20)	(0.23)	(0.21)	(0.20)	(0.23)
Two adults	–0.345	–0.109	–0.115	–0.375*	–0.126	–0.156	–0.388*	–0.118	–0.085
	(0.21)	(0.22)	(0.25)	(0.21)	(0.22)	(0.25)	(0.21)	(0.23)	(0.26)
Three adults (or more)	–0.421**	–0.335	–0.328	–0.427**	–0.347	–0.343	–0.414**	–0.279	–0.136
	(0.21)	(0.22)	(0.25)	(0.21)	(0.22)	(0.25)	(0.21)	(0.22)	(0.25)
Distance 15 to 30 minutes	–0.251	–0.001	–0.236	–0.275*	–0.016	–0.231	–0.273*	–0.015	–0.240
	(0.16)	(0.16)	(0.17)	(0.16)	(0.16)	(0.17)	(0.16)	(0.16)	(0.17)
Distance 30 to 60 minutes	–0.227	0.117	–0.404**	–0.269	0.081	–0.383*	–0.271	0.079	–0.368*
	(0.18)	(0.19)	(0.21)	(0.19)	(0.19)	(0.21)	(0.19)	(0.19)	(0.21)
Distance >60 minutes	–0.633***	–0.128	–0.625***	–0.666***	–0.154	–0.584**	–0.663***	–0.138	–0.523**
	(0.21)	(0.20)	(0.24)	(0.21)	(0.21)	(0.24)	(0.21)	(0.21)	(0.24)
Log expenditure				0.014	–0.025	0.051	0.023	–0.034	0.019
				(0.05)	(0.05)	(0.06)	(0.05)	(0.05)	(0.06)
Rooms per capita				0.014	–0.066	0.052	0.026	–0.063	0.050
				(0.08)	(0.08)	(0.08)	(0.08)	(0.08)	(0.08)
Owns home				–0.308**	–0.156	–0.247*	–0.305**	–0.134	–0.261*
				(0.14)	(0.14)	(0.15)	(0.14)	(0.14)	(0.15)
Tap water access				–0.101	–0.157	0.148	–0.086	–0.171	0.108
				(0.18)	(0.18)	(0.22)	(0.18)	(0.19)	(0.22)
Flush toilet				–0.065	0.118	0.010	–0.071	0.078	–0.023
				(0.19)	(0.19)	(0.21)	(0.19)	(0.19)	(0.22)
Phone access				–0.121	–0.011	0.010	–0.116	–0.021	–0.019
				(0.19)	(0.18)	(0.20)	(0.19)	(0.18)	(0.20)
Regular refuse				0.017	–0.075	–0.118	0.025	–0.065	–0.117
				(0.22)	(0.21)	(0.26)	(0.23)	(0.21)	(0.26)
Union proportion							0.254	0.486	–0.006
							(0.39)	(0.34)	(0.37)
NLFP proportion							0.042	–0.366	–0.555*
							(0.28)	(0.29)	(0.33)
No school proportion							–0.145	–0.199	–0.417
							(0.22)	(0.25)	(0.30)
Matric proportion							–0.511	–0.095	0.475*
							(0.31)	(0.25)	(0.25)
Employed proportion							0.058	0.073	0.391
							(0.30)	(0.31)	(0.33)
Smokers proportion							0.032	0.083	–0.199
							(0.23)	(0.22)	(0.23)
Father alive							0.088	–0.221	0.025
							(0.18)	(0.18)	(0.23)
Mother alive							–0.439	–0.106	–0.360
							(0.34)	(0.37)	(0.41)
Constant	0.962**	0.140	–0.174	1.159**	0.519	–0.416	1.419**	0.980	0.219
	(0.42)	(0.41)	(0.44)	(0.49)	(0.51)	(0.57)	(0.62)	(0.65)	(0.72)
Observations	2 966	2 966	2 966	2 966	2 966	2 966	2 966	2 966	2 966

Source: Results from multinomial regression (STATA 12) application of DD. Standard errors clustered at the level of the household. ***p <0.01, **p <0.05, *p <0.1 denote statistical significance of parameter estimates. Log-likelihood values reported in Table 5.

Table 4: Multinomial regression results with year interactions

	Location and household controls			Wealth controls			Other household controls
Variable	Public Other	Private	Public Clinic	Public Clinic	Public Other	Private	Public clinic	Public other	Private
Survey year	1.238***	1.083**	0.144	0.186	–0.701	–2.373**	–0.890	–0.333	–2.024
	(0.47)	(0.44)	(0.48)	(0.98)	(1.01)	(1.15)	(1.13)	(1.15)	(1.32)
Affected by policy	–0.774***	–0.567***	–0.478**	–0.789***	–0.568***	–0.479**	–0.777***	–0.575***	–0.415*
	(0.20)	(0.22)	(0.21)	(0.20)	(0.22)	(0.21)	(0.20)	(0.22)	(0.22)
DD – indicator	0.102	–0.123	–0.287	0.105	–0.150	–0.301	0.079	–0.135	–0.332
	(0.26)	(0.27)	(0.28)	(0.26)	(0.27)	(0.28)	(0.26)	(0.27)	(0.29)
Eastern Cape	0.910***	0.754**	0.729*	0.931***	0.801**	0.797**	1.013***	0.965***	0.962**
	(0.35)	(0.35)	(0.39)	(0.35)	(0.35)	(0.39)	(0.35)	(0.36)	(0.40)
Northern Cape	–0.160	–0.481	–1.177***	–0.135	–0.424	–1.110***	–0.048	–0.289	–0.828**
	(0.34)	(0.32)	(0.41)	(0.34)	(0.33)	(0.42)	(0.34)	(0.33)	(0.42)
Free State	–1.067**	0.458	0.166	–1.098**	0.530	0.246	–1.084**	0.553	0.189
	(0.52)	(0.43)	(0.51)	(0.54)	(0.43)	(0.52)	(0.54)	(0.43)	(0.52)
KwaZulu-Natal	–0.121	0.239	0.332	–0.139	0.251	0.343	–0.067	0.357	0.372
	(0.30)	(0.27)	(0.31)	(0.30)	(0.28)	(0.32)	(0.30)	(0.28)	(0.32)
Northwest	0.632*	0.052	0.831**	0.637*	0.092	0.872***	0.694**	0.202	0.904***
	(0.33)	(0.32)	(0.33)	(0.33)	(0.32)	(0.34)	(0.33)	(0.32)	(0.34)
Gauteng	–0.326	0.212	0.381	–0.372	0.197	0.421	–0.412	0.173	0.129
	(0.37)	(0.35)	(0.38)	(0.38)	(0.35)	(0.39)	(0.38)	(0.36)	(0.40)
Mpumalanga	–0.289	–0.536	0.331	–0.243	–0.488	0.324	–0.144	–0.366	0.349
	(0.35)	(0.34)	(0.36)	(0.35)	(0.34)	(0.36)	(0.35)	(0.35)	(0.37)
Limpopo	0.098	0.397	0.120	0.144	0.489	0.145	0.273	0.687*	0.239
	(0.39)	(0.39)	(0.48)	(0.39)	(0.38)	(0.48)	(0.40)	(0.39)	(0.48)
Urban residence	0.113	0.317	0.295	0.079	0.420	0.252	0.068	0.389	0.123
	(0.24)	(0.24)	(0.27)	(0.30)	(0.28)	(0.35)	(0.30)	(0.29)	(0.35)
White	–0.207	0.462	0.987***	–0.311	0.525	1.063***	–0.379	0.426	0.639
	(0.36)	(0.34)	(0.37)	(0.38)	(0.35)	(0.38)	(0.39)	(0.36)	(0.40)
Asian	–1.353	–0.598	–0.353	–1.464	–0.574	–0.333	–1.398	–0.480	–0.721
	(0.90)	(0.63)	(0.58)	(0.92)	(0.63)	(0.59)	(0.90)	(0.63)	(0.63)
Coloured	–2.666***	0.267	1.286***	–2.567***	0.322	1.181**	–2.619***	0.247	0.486
	(0.81)	(0.45)	(0.49)	(0.81)	(0.46)	(0.50)	(0.84)	(0.51)	(0.54)
One child<6	–0.230	–0.364	0.044	–0.256	–0.365	0.053	–0.282	–0.425	–0.001
	(0.30)	(0.30)	(0.34)	(0.31)	(0.30)	(0.33)	(0.31)	(0.31)	(0.35)
Two + children <6	–0.446	–0.377	–0.008	–0.450	–0.321	0.028	–0.493	–0.356	0.082
	(0.33)	(0.34)	(0.35)	(0.33)	(0.34)	(0.35)	(0.34)	(0.35)	(0.37)
Two adults	–0.389*	–0.141	–0.139	–0.412*	–0.193	–0.234	–0.446**	–0.182	–0.162
	(0.21)	(0.22)	(0.25)	(0.22)	(0.22)	(0.25)	(0.22)	(0.23)	(0.26)
Three adults (or more)	–0.462**	–0.376*	–0.348	–0.478**	–0.463**	–0.471*	–0.460**	–0.361	–0.235
	(0.21)	(0.22)	(0.25)	(0.21)	(0.23)	(0.25)	(0.22)	(0.23)	(0.26)
Distance 15 to 30 minutes	–0.245	0.012	–0.244	–0.275*	–0.006	–0.247	–0.282*	–0.002	–0.248
	(0.16)	(0.16)	(0.17)	(0.16)	(0.16)	(0.17)	(0.16)	(0.16)	(0.18)
Distance 30 to 60 minutes	–0.230	0.131	–0.410**	–0.278	0.086	–0.402*	–0.294	0.092	–0.399*
	(0.18)	(0.18)	(0.21)	(0.19)	(0.19)	(0.21)	(0.19)	(0.19)	(0.21)
Distance >60 minutes	–0.633***	–0.094	–0.640***	–0.655***	–0.109	–0.591**	–0.647***	–0.071	–0.544**
	(0.21)	(0.21)	(0.24)	(0.21)	(0.21)	(0.24)	(0.21)	(0.21)	(0.24)
Log expenditure	–0.075	0.272	0.682*	–0.248	0.283	0.762*	–0.253	0.182	0.278
	(0.41)	(0.38)	(0.40)	(0.43)	(0.39)	(0.42)	(0.43)	(0.40)	(0.44)
Rooms per capita	0.057	0.796	1.684**	0.221	0.799	1.580**	0.105	0.563	1.409*
	(1.10)	(0.79)	(0.75)	(1.11)	(0.78)	(0.75)	(1.10)	(0.77)	(0.79)
Owns home	–0.234	–0.093	0.549	–0.188	0.019	0.619	–0.269	–0.012	0.654
	(0.42)	(0.43)	(0.46)	(0.43)	(0.43)	(0.46)	(0.43)	(0.43)	(0.48)
Tap water access	–0.265	–0.084	–0.008	–0.175	0.013	0.037	–0.208	0.020	0.104
	(0.28)	(0.28)	(0.32)	(0.28)	(0.29)	(0.33)	(0.29)	(0.29)	(0.33)
Flush toilet	–1.242***	–0.952***	–0.847**	–1.219***	–0.948***	–0.766*	–1.264***	–1.055***	–0.927**
	(0.33)	(0.35)	(0.41)	(0.33)	(0.35)	(0.40)	(0.33)	(0.35)	(0.41)
Phone access	–0.810	–1.674***	–0.191	–0.739	–1.611***	–0.122	–0.791	–1.658***	–0.142
	(0.59)	(0.49)	(0.53)	(0.59)	(0.49)	(0.55)	(0.60)	(0.49)	(0.55)
Regular refuse	0.030	0.313	0.441	0.116	0.355	0.369	0.197	0.412	0.684
	(0.47)	(0.44)	(0.47)	(0.49)	(0.45)	(0.48)	(0.50)	(0.46)	(0.50)
Union proportion	–0.710	–0.548	–0.234	–0.724	–0.583	–0.292	–0.807	–0.707	–0.369
	(0.56)	(0.58)	(0.67)	(0.56)	(0.59)	(0.67)	(0.57)	(0.60)	(0.68)
NLFP proportion	–0.157	–0.197	–0.001	0.050	–0.201	0.047	0.134	–0.145	0.213
	(0.28)	(0.29)	(0.32)	(0.33)	(0.32)	(0.36)	(0.33)	(0.33)	(0.37)
No school proportion				–0.022	–0.079	–0.020	–0.023	–0.084	–0.041
				(0.05)	(0.05)	(0.06)	(0.05)	(0.05)	(0.06)
Matric proportion				0.010	–0.084	0.017	0.025	–0.086	0.043
				(0.09)	(0.08)	(0.08)	(0.09)	(0.08)	(0.08)
Employed proportion				–0.460*	–0.406*	–0.196	–0.477**	–0.431*	–0.243
				(0.24)	(0.24)	(0.28)	(0.24)	(0.25)	(0.28)
Smokers proportion				–0.128	–0.155	0.184	–0.149	–0.186	0.147
				(0.18)	(0.18)	(0.22)	(0.18)	(0.19)	(0.22)
Father alive				–0.093	0.413	0.401	–0.118	0.393	0.370
				(0.31)	(0.31)	(0.32)	(0.31)	(0.31)	(0.34)
Mother alive				0.292	–0.287	–0.378	0.264	–0.330	–0.416
				(0.30)	(0.30)	(0.33)	(0.30)	(0.30)	(0.34)
Year*African				0.050	–0.086	–0.152	0.082	–0.062	–0.133
				(0.23)	(0.21)	(0.27)	(0.23)	(0.22)	(0.27)
Year*Asian				0.217	0.321	–0.111	0.242	0.385	–0.074
				(0.30)	(0.30)	(0.33)	(0.30)	(0.30)	(0.33)
Year*no child <6				–0.132	–0.474	–0.645	–0.125	–0.512	–0.666
				(0.38)	(0.37)	(0.40)	(0.38)	(0.38)	(0.41)
Year*one child <6				–0.787*	0.289	0.436	–0.772*	0.309	0.447
				(0.41)	(0.38)	(0.42)	(0.41)	(0.39)	(0.43)
Year*Eastern Cape				0.141	0.228*	0.354**	0.167	0.161	0.275*
				(0.13)	(0.13)	(0.15)	(0.14)	(0.14)	(0.16)
Year*KwaZulu-Natal							0.144	0.333	–0.214
							(0.39)	(0.35)	(0.37)
Year*Gauteng							–0.626	–0.378	–1.103**
							(0.40)	(0.45)	(0.49)
Year*Limpopo							–0.167	–0.230	–0.405
							(0.23)	(0.24)	(0.30)
Year*urban							–0.393	–0.601	0.523
							(0.45)	(0.40)	(0.38)
Year*own home							–0.377	0.312	0.671
							(0.48)	(0.52)	(0.52)
Year*flush toilet							0.092	0.164	–0.111
							(0.23)	(0.22)	(0.23)
Year*phone							0.071	–0.231	–0.010
							(0.18)	(0.18)	(0.23)
Year*log expenditure							–0.572	–0.183	–0.416
							(0.35)	(0.38)	(0.41)
Year*NLFP							1.349**	0.195	1.040
							(0.56)	(0.59)	(0.64)
Year*employment							0.998	–0.104	–0.182
							(0.62)	(0.64)	(0.67)
Year*matric							–0.179	0.711	–0.128
							(0.61)	(0.52)	(0.52)
Year*hungry							–0.314*	–0.177	–0.094
							(0.17)	(0.17)	(0.19)
Constant	0.791	–0.129	–0.674	1.377**	0.803	–0.423	2.410***	1.346	0.485
	(0.49)	(0.49)	(0.53)	(0.60)	(0.63)	(0.68)	(0.76)	(0.82)	(0.89)
Observations	2 966	2 966	2 966	2 966	2 966	2 966	2 966	2 966	2 966

Source: Results from multinomial regression (STATA 12) application of DD. Standard errors clustered at the level of the household. ***p <0.01, **p <0.05, *p <0.1 denote statistical significance of parameter estimates. Log-likelihood values reported in Table 5.

However, the primary focus of the analysis is the impact of the 1996 policy reform, which was estimated as the marginal effect of the DD indicator for each healthcare utilisation outcome in the multinomial logit regression. The marginal effects are reported in Table 5. The marginal effect was calculated as the difference in the probability for all of the alternatives in the model. The effect is the probability of using that alternative post reform, if in the post-reform eligible subgroup, net of the probability of using that alternative pre reform. As the probabilities are predicted from non-linear functions, it is important to set the control variables to a particular level. We do so by considering the median household; in South Africa, the median household is relatively poor, its young children were eligible for the 1994 reform, and therefore any of that household's older children would be covered by the 1996 reform. With respect to the results reported, regardless of whether or not control variable trends were incorporated, they are disappointing. User fee abolition had no statistically significant effect on the healthcare facility choice decisions made for ill and injured children.

Table 5: DD estimates for multinomial logit regression models

	Without year interactions			With year interactions
Outcome	Model 2	Model 3	Model 4	Model 2	Model 3	Model 4
No treatment	0.017	0.016	0.014	0.033	0.033	0.031
	(0.04)	(0.04)	(0.04)	(0.05)	(0.04)	(0.05)
Public clinic	0.011	0.011	0.011	0.023	0.027	0.027
	(0.02)	(0.02)	(0.02)	(0.02)	(0.03)	(0.03)
Public other	–0.025	–0.026	–0.027	–0.007	–0.010	–0.011
	(0.04)	(0.04)	(0.04)	(0.05)	(0.05)	(0.05)
Private	–0.004	–0.001	0.002	–0.049	–0.051	–0.047
	(0.04)	(0.04)	(0.04)	(0.04)	(0.05)	(0.04)
Log-likelihood	–3 874.7	–3 864.6	–3 829.6	–3 843.9	–3 819.6	–3 772.3
Observations	2 966	2 966	2 966	2 966	2 966	2 966

Source: Author's calculations of DD marginal effects with balanced factors, average household distance (in time) from health facility and all continuous variables at their median values. Robust standard errors in parentheses are clustered at the level of the household.

In summary, the policy has had no positive effect on overall treatment. Overall, treatment has not increased; in fact, the sign suggests more children are not receiving treatment. Public clinic use has not risen significantly, although the sign is as expected. Similarly, private facility use is lower, even if not statistically significantly so.

One worry that arises in the multinomial regression setting is that the independence of irrelevant alternatives assumption could be violated. A violation of the assumption suggests that the results could be dependent upon the set of alternatives within the model structure. Therefore, we considered a few other specifications with a different set of alternatives: public clinics versus all others, public facilities versus all others, public clinics versus non-treatment, and public facilities versus non-treatment. There are no substantive differences in the conclusions, and thus we are comfortable assuming that independent alternatives are irrelevant, at least in this setting (results available from authors upon request).

5.3 Discussion

The DD analysis points to a statistically insignificant policy effect, when comparing no treatment, public clinic usage, other public facility usage and private facility usage. Since user fees were cut for primary care in the public sector, which is primarily delivered through the clinic structure, we expected a positive effect on public clinic usage, and a reduction somewhere else, to offset the increase. Our results generally disagree with the findings previously reported in the user fee literature, especially the early literature outside South Africa; however, the literature on the effects of curative care utilisation following user fee changes inside and outside South Africa is not extensive. In South Africa, for example, only a few studies are available. Curative care is found to increase amongst children under the age of six, following the 1994 policy change, and there was an observed increase in adult curative care services over the 1992–98 period (Wilkinson et al., 2001; Lagarde & Palmer, 2008). Recent analysis making use of more representative data related to the 1994 policy reform finds increases unlikely to exceed 5% (Koch, 2012; Koch & Racine, 2013), a figure much lower than the 44.7%, 77.3% and 300% implied by others (McCoy & Khosa, 1996; Wilkinson et al., 1997; Bayat & Cleaton-Jones, 2003).

A few studies are available in other African countries, as well. In Madagascar, curative care visits increased by 17% (Fafchamps & Minten, 2007). In Uganda, studies have found 28% increases in under-five visits and 53% increases in new visits (Burnham et al., 2004). In the same country, others have observed 25% increases at public facilities and 44% increases at referral centres (Nabyonga et al., 2005), as well as an 18% increase in care for under-fives and a 26% increase in care for all (Deininger & Mpuga, 2005). In a related study, informal care increased by 10%, public service care increased by nearly 11%, while non-use increased by 16%, which suggests that user fee abolition effects in Uganda were not as pronounced as was found in previous studies (Deininger & Mpuga, 2005; Xu et al., 2006; McPake et al., 2011). Finally, in Zambia, increases in rural district utilisation have been found nearer to 50% (Masiye et al., 2008), although this effect does not carry through to child delivery services (Chama-Chiliba & Koch, 2014).

There are a number of reasons our results could differ from the rest of the literature. All but a few of the previous studies (Deininger & Mpuga, 2005; Xu et al., 2006; Koch, 2012; Koch & Racine, 2013) collected data from healthcare facilities, some from as few as one facility. Furthermore, as pointed out in a detailed review of the literature, the data used in the previous analyses are likely to be unreliable, due to the limited number of facilities, while control groups were lacking. Therefore, the analyses were unlikely to be able to account for a number of changes that occurred around the same time as user fees changed (Lagarde & Palmer, 2008). A similar concern can be raised with respect to the earlier household-level studies (Deininger & Mpuga, 2005; Xu et al., 2006). Control groups, for comparison purposes, are not available, and therefore the increases observed in those studies could reflect broad increases in the country, rather than increases that can be attributed directly to the policy.

Although the sample employed in this analysis is more representative than the samples employed in a number of other studies, data both before and after the policy change contain a large number of observations and the analysis is based on an empirical model designed to deal with a variety of confounding factors, there are limitations to the analysis. The 1996 policy followed closely on the heels of an earlier policy abolishing user fees in the public healthcare sector for young children, nursing and pregnant women and the elderly, which was implemented in 1994. It is possible that the time horizon was too short to uncover an effect. It is also the case that the two samples used for the analysis were not as similar as would have been preferred. However, we uncovered no significant differences in sample trends across the treatment and control groups, while adjusting for sample differences through the inclusion of additional control variables did not alter the substantive conclusions. Also, it should not be forgotten that policy implementation on the ground does not always match the policy goal. Unfortunately, it is not possible to go back and see how effectively these policies were implemented, or whether the implementation of these policies increased public clinic queues and waiting times. Although there is some evidence of imperfect user fee abolition implementation, there is rather strong evidence that fees were less likely to be paid by those eligible for the 1994 reform (Koch, 2012).

Another limitation of the study arises from the lack of clinic-level information for corroboration. It would have been preferable to compare the results reported here with a broader set of clinic-level information. Efforts have been ongoing to uncover clinic-level information, but have been largely unfruitful. Even though it would have been nice to compare individual level results with clinic-level effects, any analysis at the clinic level would not be able to consider substitution across health facilities, and therefore this analysis, despite uncovering no substitution, has something to offer that clinic-level studies do not.

Finally, the policy impact was estimated for a rather narrow band of the population, albeit a band of the population that was targeted for the policy intervention. Given the narrow range of the target population, it cannot be concluded that the policy had no impact, only that there was no statistically identifiable impact on public clinic utilisation in the analysis population. Although extending the analysis to other children did not affect the results (Brink, 2012), it is possible that the policy had a greater effect on adults. Adults were not included in the analysis, because the treatment and control groups needed to be similar. We felt that the inclusion of adults was not appropriate, because of the decision-making process. Primary caregivers are assumed to make healthcare decisions for very young children, who are in the control group. Therefore, it was preferred that primary caregivers also made the decisions for the treatment group. Since adults typically make their own healthcare choices, adults are not an empirically relevant treatment group.

6. Conclusion

South Africa has availed public health facilities to more individuals by waiving user fees for primary healthcare, first in 1994 and again in 1996. Since the 1994 plan focused on young children and elderly adults, as well as pregnant and nursing mothers, the 1996 change, which waived fees for the remainder of the population, subject to means tests, was examined via DD applied to a subsample of young children. Although the policy provided free primary care to all at public clinics, the results of the analysis do not support the hypothesis that free primary care increased public clinic visits amongst ill and injured children.

Given the lack of empirical support for the hypothesis, coupled with the broad support in the empirical literature for utilisation increases associated with the 1994 user fee abolition, further abolishing user fees for more of the population was not an effective option for improving the utilisation of public health facilities in South Africa. The result further suggests that the barrier to accessing healthcare for this segment of the population is not user fees; rather, there are other barriers that matter. Therefore, in order to improve the utilisation of public health facilities, future research should focus on developing a deeper understanding of healthcare access barriers, and develop policies to address those barriers.

Acknowledgements

The author would like to thank seminar participants at the University of Pretoria and the Eastern Mediterranean University, as well as Olufunke Alaba for their comments on earlier drafts of this research. All remaining errors are the sole responsibility of the author.