Abstract
This paper demonstrates how the availability of family planning and maternal and child health services alters the structure of intra-household bargaining. The overall welfare gains from such programs are likely to be large, but when women obtain access to services only through marriage, some of these gains may be partially offset by changes in their bargaining power and in the dowries that they pay their husbands. I examine these marriage market effects using a family planning and health services program in rural Bangladesh, finding that compared to women without program access, women in the treatment area are 35% less likely to be able to make purchases without permission from their husbands or another household member. Moreover, a difference-in-difference specification confirms that women pay 14% higher dowries in order to obtain husbands with access to the program. The fact that adjustments are made both before and within marriage suggests that marital contracts in rural Bangladesh are negotiated along multiple margins.
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Notes
These households cover 2,687 baris (approximately 33% of the total number of baris). A bari is a group of households living and working closely together.
Even if a woman grows up in the treatment area, she loses access to the program if she marries a man outside the treatment area.
Another potential explanation for the empirical results of this paper is that treatment area boys who receive child health services grow up to be healthier and more desirable on the marriage market. Their higher quality enables them to extract larger dowry payments and more bargaining power within their marriages. However, only two women in my dataset have husbands born after the program begins (who would have received services from birth), and my empirical results on bargaining power are robust to the exclusion of the youngest cohorts of women (whose husbands, although born before program inception, may still have been children at the time and received some health benefits). Thus, my results preclude this alternate explanation.
Spillovers occur if women from comparison areas travel to nearby treatment village clinics for services. Although any spillovers should only understate the true effects of the MCHFP project, the main results of this paper are robust to limiting the sample to border villages, where the potential for spillovers is greatest (i.e. treatment villages that share a border with a comparison village, and vice versa, see Table 7).
I define labor force participation for women as claiming some job other than housework as their primary activity over the past month. Nearly half the women who currently work cite rearing hens and ducks as their job, with a further third husking paddy. There do not appear to be any differences in 1974 between labor force participation rates of married women in the treatment and comparison areas (see Table 1). I am unsure why the 1974 census results vary from the labor force results shown by the smaller MHSS sample in 1976 and 1996; consequently, I am careful to control for it.
Initial health services included tetanus toxoid immunizations for pregnant women, neonatal vitamins, maternal and child nutritional advice, and oral rehydration for diarrheal diseases.
This sample, which is used in the empirical specifications, excludes the 22 women reporting employment in ICDDR,B hospitals (the MHCFP sponsor), whose average 1996 earned income is 47 times the average earned income of other women and therefore represent clear outliers.
Treatment area women in both pre and post-program marriages receive larger transfers than control area women, though the difference is much larger and significant for post-program marriages. However, it is uncertain whether these differences existed before the MCHFP began or in fact resulted from the program (as an effort to partially offset the negative program effects on treatment area women). The empirical specifications control for unearned income, finding that it is significantly positively associated with increased bargaining power over household resources (results not shown, from probit models in Table 7). This result is shared by Anderson and Eswaran (2009). Thus, even if it was not controlled for, the fact that treatment area women have higher levels of unearned income should only bias the empirical results upwards toward zero.
An alternative framework that would predict a similar result is the collective model of marriage (Chiappori 1992). In that model, bargaining weights determined by distribution factors govern intra-household resource allocations, with the outcome being dependent on the marital threat point (the allocation that occurs if couples cannot agree).
If this figure illustrates aggregate supply and demand on the Matlab marriage market for treatment area men, then e 0 represents the allocation for the average husband and wife on that market.
Coefficient and standard error estimates for all probit models reported in this paper are available upon request.
Marriages in Matlab are usually arranged by the couple’s families, with over 75% of marriages in my sample being arranged directly by the couples’ parents. For simplicity, I assume fully benevolent parents who, despite arranging the marriage, do not consider any utility other than their child’s when making decisions.
Due to limited education and the widespread practice of purdah, Matlab women have few opportunities outside of marriage (Bhuiya et al. 2005). When divorce does occur, it is often initiated by the husband rather than the wife. The exogenous shock of the family planning and health services program will not be enough to trigger divorce among Matlab women, because the gains to marriage for them remain so large (Weiss 2001).
A few women are missing spousal information, so I lose observations depending on the control variables used.
I focus on these specific purchases because they are considered large purchases in the Matlab setting, following Williams (2005). The data also includes information on small purchases (kerosene or cooking oil for the family, bangles or soap for their own use, and sweets or ice cream for children). However, the significant differences that I find in probit models do not extend to the ability to make small purchases, likely because the amount of resources required are simply too small to matter in daily life. In addition, Williams (2005) observes that several papers have argued that the ability to make small purchases is not adequately reflective of female power in rural Bangladesh.
The exception to being exogenous to female choices occurs if there are program spillovers with untreated women seeking services, but as discussed earlier, these exceptions should only bias the results towards zero.
I do not find evidence for this second type of selection; the quality of the match achievable by treatment area males does not appear to change along observable dimensions outside of dowry after the program begins. Difference-in-difference regressions show no differential changes in the age, education, or relative wealth of spouses chosen by treatment and control area males.
For these tests, the t-statistic for the actual program coefficient is always greater than the t-statistic for any false program. When the actual and false program groups are both included in the same regression, the actual program coefficient is always significant at the 10% level, and the false program coefficient is never significant.
I focus on measures of decision-making power over purchases because they are reflective of the allocation of resources within the household. There are several other measures of female empowerment (Williams 2005), including freedom of movement outside the bari and preferences over modesty in the public sphere (i.e. the use of head coverings or burqas). However, because these measures may be governed largely by individual preferences or perceptions of status rather than control over the allocation of household resources, the MCHFP should not necessarily induce any relative changes in these measures. Accordingly, probit models using these measures as dependent variables do not show strong differences between treated and untreated women. Moreover, the MCHFP has a statistically significant effect on the measures of bargaining power used in this paper (i.e. the specifications with controls in Table 7) even under a Bonferroni correction for false discovery rates (the Bonferroni correction in this case requires a p-value below .0053 to retain significance at the 10% level; this number is based on the identification of 19 different empowerment outcomes within the MHSS data).
This result distinguishes my model from that of Arunachalam and Naidu (2008), who explain the increase in dowry payments paid to treatment area men after the Matlab program begins by assuming that women are pre-paying for a decrease in the price of contraception. However, this explanation would also predict that such compensation should be similar throughout the program area, rather than varying based on village location. Thus, the variance in bargaining power according to treatment village location is inconsistent with their model. This result also precludes another potential explanation for the empirical results of this paper- that dowry and bargaining power adjust in order to account for possible increases in female life expectancy due to improved maternal health services from the program. If these adjustments can be entirely attributed to changes in life expectancy, then the differences in bargaining power should be uniform throughout the program area, regardless of village location (due to the fact that increases in life expectancy should likewise be uniform throughout the program area).
Results available in Appendix 1. Village controls include travel time in minutes to the nearest large market, travel time in minutes to the nearest small market, the proportion of households with electricity, whether the village is protected by the Meghna-Dhonogoda flood embankment, and dummy variables for whether the village has a credit institution, irrigation for crops, some type of cottage industry, or some type of other industry (including a mill, factory, or workshop).
Since only two women in the full sample have husbands born after the program begins, there is no concern about endogenous sorting before the husband’s birth (i.e. that his parents moved into the treatment area before he was born, in order to ensure his access to program services).
Finally, although control variables account for selection of women into post-program marriages with treatment area men along observable measures, there may exist some remaining concern regarding potential selection on unobservables. A potential instrument for a selection model must be correlated with a female’s choice to marry a treatment area male while remaining independent of her subsequent bargaining power within that marriage, which is itself a function of her outside options for any future marriage. Since a plausible instrument does not exist, I create propensity scores (Rosenbaum and Rubin 1983) for all women in post-program marriages that estimate their probability of marrying a man living in the treatment area, based on a probit model with the following regressors: age at marriage, age at marriage squared, education, marriage year, religion, and age at menarche. I keep only those observations with propensity scores in the area of common support [.28, .80], which eliminates comparison women who are most unlike treatment area women in their observed covariates. Following Robins and Rotnitzky (1995)) and Hirano and Imbens (2002), the inverse of each observation’s probability of marrying into the treatment area becomes weights in the post-program marriage regressions (the probability of marrying into treatment for those in the treatment area is the estimated propensity score, and the probability of marrying into treatment for those in the comparison area is one minus the estimated propensity score). I balance the mean propensity scores between the treatment and comparison area within 8 blocks, and bootstrap the standard errors from the weighted regression results. Even after including these propensity score weights, women who marry men in the treatment area are still on average nearly 5 percentage points less likely than women in the comparison area to make purchases (significant at the 1% or 5% level in each regression). Thus, it does not appear that any bias resulting from unobserved selection into post-program marriages with treated men is likely to be large enough to fully account for the difference in bargaining power observed between treated and untreated women.
Lack of statistical significance may be a result of the small sample size (40–50 observations), so caution must be used when interpreting this result.
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Acknowledgments
I thank Terra McKinnish, Randall Kuhn, Jennifer Lamping, Tania Barham, and especially A. Mushfiq Mobarak and Murat Iyigun for valuable discussion and suggestions. All errors remain my own.
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Peters, C. Effects of family planning and health services on women’s welfare: evidence on dowries and intra-household bargaining in Bangladesh. Rev Econ Household 9, 327–348 (2011). https://doi.org/10.1007/s11150-010-9100-7
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DOI: https://doi.org/10.1007/s11150-010-9100-7