Does Piped Water Reduce Diarrhea for Children in Rural India?

The effects of public investments aimed at directly improving children's health are theoretically ambiguous, since the outcomes also depend on indirect effects through parental inputs. The authors investigate the role of such inputs in influencing the incidence of child health gains from access to piped water in rural India. Using propensity score matching methods, they find that the prevalence and duration of diarrhea among children under five are significantly less on average for families with piped water than for families without it. But health gains largely bypass children in poor families, particularly when the mother is poorly educated. The author's findings point to the importance of combing infrastructure investments with effective public action to promote health knowledge and income poverty reduction.


Introduction
The World Health Organization estimates that four million children under the age of five die each year from diarrhea, mainly in developing countries. 2 Unsafe drinking water is widely thought to be a major cause, and this has motivated public programs to expand piped water access.
In this paper, we estimate the impacts on child health of piped water in a developing country.
We argue that expanding piped water is not a sufficient condition to improve child health status in this setting. The source of ambiguity lies in the uncertainty about how public and private inputs interact in the production of health conditional on the heterogeneous quality of public inputs.
The private inputs relevant to diarrhea prevalence and duration include hygienic water storage, boiling water, oral re-hydration therapy, medical treatment, sanitation and nutrition. With the right combination of these public and private inputs, diarrhoeal disease is almost entirely preventable.
However, behavior is known to play an important role. Public inputs such as access to a piped water network can either displace parentally chosen private inputs or be complementary to them. Even when there are child-health benefits (factoring in parental spending effects) the gains could well bypass children in poor families, taking account of parental behavioral responses to poverty.
For example, if piped water increases the marginal health benefit for parents of spending more on their children's health, and such spending is a normal good, then the health gains from piped water will tend to rise with income. This is not implausible on a priori grounds. Piped water in rural areas of developing countries is no doubt safer than many alternative sources, but it is often the case that it still needs to be boiled or filtered and stored properly to be safe to drink. This can be a burden for a poor family, a poor, or poorly educated mother may reasonably think that there are better uses of time and money needed to provide this complementary input to piped water. 2 http://www.who.int/aboutwho/en/preventing/diarrhoeal.htm It is plausible that there are private inputs that are cooperant with piped water in determining child health. However, it can also be argued that such private inputs have positive income effects in this setting, and there is supportive evidence. For example, it is estimated that 29% of the poorest quintile (in terms of a composite wealth index) of families in rural India in 1992/93 used oral rehydration therapy when a child had diarrhea, as compared to 50% in the richest quintile (Gwatkin et al., 2000). Similarly, 52% of those in the poorest quintile sought medical treatment, as compared to 78% in the richest.
The upshot of all this is that being connected to a piped water network may well be of limited relevance to the poor from an epidemiological standpoint. Income poverty and lack of education and knowledge may well constrain the potential health gains from water infrastructure improvements.
The incidence of health gains need not favor children from poor families, even when facility placement is pro-poor. This paper looks for evidence of child-health gains from access to piped water. We use a large, representative cross-sectional survey for rural India implemented in 1993-94. India undoubtedly accounts for more child deaths due to unsafe water than any other single country. Parikh et al. (1999) quote an estimate of 1.5 million child deaths per year in India due to diarrhea and other diseases related to poor water quality. Moreover, estimates indicate that one fifth of the population of rural India do not have access to safe drinking water (World Bank, 2000). Expanding access to piped water is considered an important development action in India.
Our aim is not to model the effect of contaminated water on child health in this setting.
Rather we attempt to quantify the child health gains in terms of diarrhoeal disease from policy interventions that expand access to piped water, and to see how the gains vary with household circumstances, notably income and education. The main questions we ask are: Is a child less vulnerable to diarrhoeal disease if he/she lives in a household with access to piped water? Do children in poor, or poorly educated, households realize the same health gains from piped water as others? Does income matter indepefidently of parental education?
The following section establishes the theoretical ambiguity in the effect of access to piped water on child health. Section 3 discusses the methodology we propose to test for child health gains from piped water. Section 4 describes our data for rural India. The results are given in section 5, while section 6 concludes.

A behavioral model of child health
We examine the impact on child health of an exogenous increase in access to piped water, allowing for parental responses in the provision of other inputs to child health. The increase in access could arise from an extension of the piped-water network into a community that had relied previously on a well or stream. We show that once one allows for privately provided health inputs, and assuming that parents care about more than just their children's health, even the direction of the effect on children's health is theoretically ambiguous, and becomes an empirical question.
Let the health status (h) of a child depend on its access to piped water (w), parental spending (s) on private inputs to child health, and a vector of personal and environmental characteristics (x).
The latter could include parental education, which could well enter non-separably with w; for example, a well-educated mother knows how to make piped water safe to drink and how to treat illnesses such as diarrhea. The health production function for the i'th child is: The function h is assumed to be strictly increasing and twice differentiable in both s and w and to be at least weakly concave in s (ruling out increasing returns to s). While w is likely to be a discrete variable, for analytic convenience we treat it as a continuous variable in this section.
In choosing the level of private spending on child health, the family takes account of its lost opportunity for consumption of other private goods, treated as a composite. We assume that spending on child health has no intrinsic value to parents beyond its contribution to child health. However, access to piped water also raises parental welfare. For example, having piped water reduces the time spent collecting water from a well or stream. Exogenous income is y andy -s is left for parents' consumption after deducting purchased inputs to child health. This gives parents utility u (y -s, w, x) in which the function u is strictly increasing and concave in y -s and strictly increasing in w. Child health matters directly to parental welfare, but separably to their utility from consumption. Thus the level of s is chosen by parents to maximize: The solution equates the marginal impact of spending on child health with the marginal utility of own consumption, uy (y -s, w, x) = h5 (s, w, x) (using subscripts to denote partial derivatives), which can also be written as: This yields a maximum utility to parents of: v(w, y, x) _ H(w, y, x) + u [y -s(w, y, x) where child health when parental inputs are optimal is given by: By the envelope theorem, v(w, y, x) must be increasing in w. However, this need not hold for both the components of parental utility. The effect of w on child health in a neighborhood of the equilibrium in which private inputs are optimal is given by: where: UW -hs SW=hss + u - It can be seen that sw has the same sign as hsw -u which could be positive, negative or zero.
Since the direct health effect is positive (hW > 0), it can be seen from (6) that hs, -u0w > O is sufficient for piped water to improve child health.
Now consider the income effect on the health gain from piped water. This is given by: In the special case in which there are no interaction effects in parental utility between piped water and income or spending on child health (h 3 w = u,m = 0), we find that Hwy = 0; the child health gain from piped water is independent of household income. More generally however the direction of the income effect-could go either way. Consider the case in which parental direct utility is additively separable between consumption and piped water (u,* = 0 ) and piped water does not alter the marginal propensity to spend on private inputs to child health (syw = 0). Then Hwy = s2h, (using (7) and (9)). So in this special case, the child health benefit from piped water will increase (decrease) with income if the piped water is a complement (substitute) for the private inputs.
So far we have taken piped-water placement to be exogenous. In the empirical work we will allow placement to be a function of a wide range of observable characteristics at household and village level. Here we can think (quite generally) of the placement as maximizing some weighted sum of v(w,, xi, y 1 ) over all i, with weights determined by a vector of characteristics of the individual and his or her socio-political environment. (This might also include any variables affecting the costs of service provision.) The solutions take the form wi = w(x;, A) where A denotes one or more multipliers on the constraints, including on resources available for providing the public inputs. The task of the empirical work is then to measure the welfare gains from higher w, recognizing that the observed levels of w in the cross-sectional data reflect purposive placement, assuming that the relevant x's are observable.

Identifying health impacts in cross-sectional data
We use propensity-score matching (PSM) methods to estimate the causal effects of piped water on child health in a cross-sectional sample without random placement. PSM balances the distributions of observed covariates between a treatment group and a control group based on similarity of their predicted probabilities of having a given facility (their "propensity scores"). The method does not require a parametric model linking facility placement to outcomes, and thus allows estimation of mean impacts (including impacts conditional on income, for examnple) without arbitrary assumptions about functional forms and error distributions. We exploit this flexibility to test for the presence of potentially complex interaction effects as discussed in theoretical terms in the last section. In this section we first outline the method, and then summarize its differences with other methods found in the literature.

Propensity score matching
Two groups are identified: those households that have piped water (denoted Di =1 for household i) and those that do not (D 1 =O). Units with piped water (the "treated" group) are matched to households without (control group) on the basis of the propensity score: where x, is a vector of pre-exposure control variables. It is known from Rosenbaum and Rubin (1983) that if (i) the Di's are independent over all i, and (ii) outcomes are independent of participation given xi, then outcomes are also independent of participation given P(xi), just as they would be if participation were assigned randomly. 3 PSM uses P(x) (or a monotone function of P(x)) to select controls for each of those treated. Exact matching on P(x) implies that the resulting matched control and treated subjects have the same distribution of the covariates. PSM thus eliminates bias in estimated treatment effects due to observable heterogeneity.
In practice the propensity score must be estimated. Here we follow the common practice in was less than 0.001 (an absolute difference in odds less than 0.032).5 Letting AHj denote the gain in health status for thej'th child attributable to access to piped water, the estimator of mean impact is: where h; 1 is the post-intervention health indicator, hi,o is the outcome indicator of the ith non-treated matched to the/h treated, Tis the total number of treatments, C is the total number of non-treated 3 Assumption (ii) is sometimes referred to in the literature as the "conditional independence" assumption, and sometimes as "strong ignorability." 4 Dehejia and Wahba (1999) report that their PSM results are robust to alternative estimators and alternative specifications for the logit regression. 5 We experimented with more stringent tolerance limits and the results were robust. However, with more stringent limits we also had to discard many more participants while calculating our impacts. Given that we already run into small sample problems for certain cells even with this tolerance limit when we categorize the sample on the basis of income and the level of female education (discussed later), we chose to report the results pertaining to a tolerance limit of 0.001. households, q 's are the sampling weights used to construct the mean impact estimator, and the W, 1 's are the weights applied in calculating the average income of the matched non-participants.
Conditional mean impact estimators can be similarly defined by calculating equation (11) conditional on observed characteristics. For example, comparing the conditional mean AHIy across different incomes y gives us a discrete estimator of the cross-partial derivative in equation (8).
There are several weights that one can use, ranging from "nearest neighbor" weights to nonparametric weights based on kernel functions of the differences in scores (Heckman et al., 1997).6 We use the nearest five neighbors estimator, which takes the average outcome measure of the closest five matched non-participants as the counter-factual for each participant. 7 Following Rubin (1973) we also use a regression-adjusted estimator. This assumes a conventional linear model for outcomes in the matched comparison group, ho = xfi 0 + Po in obvious notation. (The regression is only run for the matched comparison group, so it is not contaminated by access to piped water.) The impact estimator in this case is then defined as: j=l i=I where 80 is the OLS estimate for the comparison group sample.

Other non-experimental methods
When feasible, pure randomization clearly dominates non-experimental methods such as PSM. Unlike randomization, PSM still requires the conditional independence assumption (such that participation and outcomes are independent given x). How does PSM compare to commonly used non-experimental methods in this context? 6 Jalan and Ravallion (2000b) discuss the choice fiurther, and find that their results for estimating income gains from an anti-poverty program are reasonably robust to the choice. ' Rubin and Thomas (2000) use simulations to compare the bias in using the nearest five neighbors to just the nearest neighbor; no clear pattern emerges.
There are two main methods of assessing infrastructure impacts found in the literature. The first is to compare average outcome indicators between villages (or other geographic units) that have the facility and those that do not. Past methods of assessing health gains from water and sanitation have often compared villages with piped water and those without (Esrey et al., 1991, review numerous studies). The outcome indicators have sometimes been at village level and sometimes at household or individual level. Diverse methods have been used to control for heterogeneity; in some cases no controls are used, but often some form of matched comparison is made. Clearly failure to control for differences in village characteristics could severely bias such comparisons. Unlike some commonly used matching estimates, PSM at village level would optimally balance the observed covariates. To the extent that there is heterogeneity within villages, the aggregation could make it hard to identify impact. Against this effect, aggregation to village level may well reduce measurement error or household-specific selection bias. Moreover, since typically available villagelevel data are less comprehensive than individual survey-based data, village-level matching will be prone to greater bias due to unobserved covariates. We will compare our results using individual PSM versus village PSM.
The second method found in the literature is to run a regression of the outcome indicators on dummy variables for facility placement, allowing for the observable covariates entering as linear controls. 8 The widely used OLS regression method requires the same conditional independence assumption as PSM, but they also impose (typically arbitrary) functional form assumptions concerning the treatment effects and the control variables. Interaction effects have sometimes been allowed; for example, Merrick (1985) included interactions between piped water and income and education in regressions for child mortality in Brazil.
s Early examples include Rosenzweig and Wolpin (1982), Wolfe and Bebrman (1982) and Merrick (1985); recent examples include Lavy et al. (1996), Hughes and Dunleavy (2000) and Wagstaff (2000). Strauss and Thomas (1995) survey the large literature following this approach in studying health outcomes in micro data.
A variation on this second method is to use an instrumental variables estimator (IVE) treating placement as endogenous. This method does not avoid an untestable conditional independence assumption; in the case of IVE this is the exclusion restriction that the instrumental variable is independent of outcomes given participation. And again the validity of causal inferences rests on the ad hoc functional form assumptions required by standard (parametric) IVE. Under these assumptions, IVE identifies the causal effect robustly to unobserved heterogeneity.
The validity of the exclusion restriction required by IVE is questionable with only a single cross-sectional data set; while one can imagine many variables that are correlated with placement, such as geographic characteristics of an area, it is questionable on a priori grounds that those variables are uncorrelated with outcomes given placement. There is more potential for identification with longitudinal (panel) data, using methods that allow for latent (household and geographic) heterogeneity (Rosenzweig and Wolpin, 1986;Pitt et al., 1995;Jalan and Ravallion, 2000a).
PSM also differs from commonly-used regression methods with respect to the sample used.
In PSM one confines attention to the matched sub-samples; unmatched comparison units are dropped. By contrast, the regression methods commonly found in the literature use the full sample.
The simulations in Rubin and Thomas (2000) indicate that impact estimates based on full (unmatched) samples are generally more biased, and less robust to miss-specification of the. regression function, than those based on matched samples.
A further difference relates to the choice of control variables. In the standard regressionbased method one naturally looks for predictors of the outcome measure, and preference is usually given to variables that one can argue are exogenous to outcomes. In PSM one is looking instead for covariates of participation, possibly including variables that are poor predictors of outcomes. Indeed, analytic results and simulations indicate that variables with weak predictive ability for outcomes can still help reduce bias in estimating causal effects using PSM (Rubin and Thomas, 2000).

Data
We use a household survey conducted by India's National Council of Applied Economic Research in 1993-94. This is a nationally representative survey collecting detailed infornation on education and health status of 33,000 rural households from 1765 villages covering 16 states of India.
Multi-stage sampling design was used where income from agriculture and rural female literacy rates were the variables used to form homogeneous strata. From these strata a certain number of districts were selected with probability of selection proportional to the rural population in the district. The survey collected detailed information on health status of household members. The income survey used 12 questions to arrive at a total income, comprising income from allied agricultural activities, artisan/independent work, petty trade/small business, organized trade/business, salaried employment, qualified profession, cattle tending, rent, interest, dividends, other sources, imputed income from agriculture, annual income of the household from agricultural work and annual income of the household from non-agricultural work.
We aim to measure the child-health effects of access to piped water. The latter is indicated by whether the household reports access to piped water from a tap either inside or outside the house.
Applying the household weights in the data, 24.8% of households had piped water (7.6% inside the house and 17.3% outside).' The proportion of households with piped water varies little with income (Table 1). In the main analysis we do not distinguish whether the tap is inside or outside the house, on the grounds that this difference only matters to health outcomes via parental behavior, so the difference is subsumed in studying the relationship between access to a piped water and child health.
However, it is still of interest to test for differences in impact according to whether the piped water is a tap inside the house or a public tap, given the obvious possibilities for stored water contamination.
We provide such a test.
We examine impact on the prevalence of diarrhea among children under five years of age and the reported illness duration. And we assess incidence against household income per person and by the highest education level of any female in the household.
The sample includes 9,000 households with piped water and 24,000 without. Table I gives sample sizes for those with piped water stratified by income and female education. Unlike standard matching techniques we match "treatment" group with "non-treatment" group from the same household survey. This means that standard requirements of getting better matches are easily met, such as that treatment and counterfactual groups have the same questionnaire administered to them and that they belong to the same economic environment. While we saw little sign of correlation between households with piped water and income in Table 1, there are a number of significant explanatory variables of piped water placement in Table 2.

Estimated child-health impacts using PSM at household level
The results are generally unsurprising. Households living in larger villages (in terms of population), villages with a high school, a "pucca" ("sealed") road, a bus stop, a telephone, a bank, and a market were more likely to have piped water. The probability of scheduled tribe (but not scheduled caste) households having access to piped water was lower compared to the non-minority population.
Christian households were more likely to have access to piped water. Owning a home made it less probable; this is unlikely to be a (perverse) wealth effect, but to be related to the fact that demand for rental housing tends to come from relatively well-off people in rural India, and so this type of housing tends to be better equipped. Other housing characteristics have the expected effects, such as living in a pucca house and having electricity. Female-headed households are more likely to have piped water. A positive wealth effect controlling for these other characteristics is indicated by the fact that the more land one owns the greater the probability that one has access to piped water.
Prior to matching, the estimated propensity scores for those with and without piped water were respectively 0.5495 (standard error of 0.285) and 0.1933 (0.184). Figure 1 reports the histograms of the estimated propensity scores for the two groups. From the original sample, we lose approximately 650 treatment households due to our inability to find a sufficiently good match. After matching there was negligible difference in the mean propensity scores of the two groups (0.3743, with a standard error of 0.189, for those with piped water versus 0.3742, with a standard error of 0.189, for the matched control group). Table 3 reports descriptive statistics for the full sample of households with piped water as well as when the sample is stratified by both income and the highest level of education among female members. (Here and elsewhere we use the sampling weights provided in the data). The overall prevalence of diarrhea is L1 1% in the sample, with an average of 0.33 days of illness and a mean expenditure of 0.74 rupees per episode of diarrhea. Disease prevalence and length of illness fall with higher income and education. For example, diarrhea prevalence amongst infants in families with piped water is twice as high for those in the poorest quintile than the richest.
The estimated mean impacts on the child-health indicators are also given in Table 3. The results for mean impact indicate that access to piped water significantly reduces diarrhea prevalence and duration. Disease prevalence amongst those with piped water would be 21% higher without it.
Illness duration would be 29% higher. The regression-adjusted impact estimator (equation 12) gave very similar results (using the full set of regressors in Table 2 as the x vector). The impact estimator for diarrhea prevalence was -0.0023 (with a standard error of 0.053) and for diarrhea duration it was -0.1005 (standard error of 0.021).
Once we stratify the sample by quintiles based on income per capita, we find no significant child-health gains amongst the poorest two quintiles (roughly corresponding to the poor in India, by widely used poverty lines). However, from the 40t quintile onwards there are very significant impacts on child health in households with piped water. We see that the income gradient amongst those with piped water is almost entirely attributable to piped water. For example, we can infer that without piped water there would be no difference in infant diarrhea prevalence between the poorest quintile and the richest. Health impacts from piped water tend to be larger and more significant in families with better educated women. We found a similar pattern when we stratified instead by the highest education of the household head.
In Table 4 we report the joint effects of income and female education to test the hypothesis that income and female education interact jointly with piped water in determining child health. When we stratify by both income and education, we find that even in the bottom two quintiles, if a woman in the household has more than primary school then the household extracts significant gains from piped water in terms of lower prevalence and duration of diarrhea among children. However, these gains are not visible if the highest level of education among female members in the household is at most primary school. The effect of education is absent in the upper quintiles. Irrespective of the education levels of the female members in the household, there are significant gains to child health in households with access to piped water. These results suggest that among poorer households, the education of women matters greatly to achieving the child-health benefits from piped water.
We have defined a household with piped water to be one with access either via a tap in the premises of the household or from a public tap nearby. A concern with this broad definition is that perhaps it disguises the differences in impacts of having the facility inside the house versus outside.
To test for such differences we analyze the sub-sample of households with access to either source of piped water and compare the health outcomes (prevalence and duration of diarrhea) of children among households with a tap in the household to those who rely on public tap to get drinking water.
Our results are reported in Tables 5 and 6.
There is little overall difference in the impact on the prevalence of diarrhea between households with piped water inside the home versus those using a public tap (Table 5). However, illness duration is nearly 40% higher in households where the source of drinking water is a public tap rather than a tap within the household premises, suggesting less contamination due to storage and hence less severe illness in the latter case.
We find a very strong differential impact of a private tap on both the duration and the prevalence of diarrhea among households where the female member is uneducated. With some education, however, there is no difference in the health outcomes of children across households categorized on the basis of source of piped water. Finally, when we stratify the sample with respect to income and education, we find that it is only among households where the female member is illiterate that there are strong impacts of having the piped water source inside the household.

Village-level estimator
We compared the above results to village-level matching, as might be done with only villagelevel data. For the purpose of comparison, we confine the matching to village-level data from a village survey (not using village aggregates formed from the household data). Out of 1624 villages in the sample, 324 had piped water. Far fewer control variables were available at village level; we included 20 variables, instead of the 90 variables used for household-level matching. The control variables for estimating the propensity score at village level were (log)village size, share of land irrigated in gross cropped area, schools in the village, female to male student ratio, proportion of people belonging to a scheduled caste/tribe, and (agricultural and non-agricultural) wages and prices in the village. Only the wage rate variables were individually significant, though the LR test indicated the explanatory variables were jointly significant and the pseudo-R 2 was 0.2294. After checking for common support, we could estimate impact for 262 villages against a matched control group of nearest neighbors in terms of the propensity score. We used the nearest neighbor as opposed to nearest five neighbors to match villages because it was difficult to find matches which satisfied our tolerance limit criterion in terms of the metric distance between the propensity score ratios of the treated and the controls for a large number of observations.
Wer found that diarrhea prevalence and duration were not significantly different in the villages with piped water compared to the matched control villages. The impact estimates were 0.0012 for diarrhea prevalence and 0.1001 for duration and neither was significantly different from zero at even the 10% level (standard errors of 0.024 and 0.1001 respectively).

Conclusions
It can be expected that parental choices about private inputs to child health will respond to changes in the household environment. This has implications for understanding the incidence of child-health benefits from local infrastructure development. Potential health benefits may not be realized in practice. For example, there may be little benefit to children in poor families if private inputs (with positive income effects) and public inputs have cooperant effects on health. Or the incidence of child-health gains could be decidedly pro-poor if the private and public inputs are in fact substitutes.
To investigate this issue we have used the propensity score matching method to quantify the expected health gains to children from piped water, and to examine how those gains vary according to income and education. This method is well suited to the present application since it allows a flexible (nonparametric) description of the interaction effects with income and education. While the method does not require ad hoc assumptions about the functional form of impacts and exclusion restrictions, it only eliminates selection bias due to observable differences between those with piped water and those without it. While we have used a rich data, allowing us to match on a wide range of characteristics, the possibility remains of latent factors correlated with both access to piped water and child health.
We have estimated impacts on diarrhea prevalence and duration in children under five. We find significantly lower prevalence and duration of the disease for children living in households with piped water as compared to a comparison group of households matched on the basis of their propensity scores. However, matching at village level instead does not indicate lower diarrhea prevalence or duration.
There are striking differences in the child-health gains from piped water according to family income and adult female education. While there are significant health gains overall from access to piped water, we find no evidence of significant gains for the poorest 40% in terms of incomes.
Indeed, the income gradient in disease prevalence and duration is attributable to piped water; no income effect is found for the matched control group. Health gains from piped water tend to be lower for children with less well-educated women in the household. Here education is no doubt proxying for knowledge about how to assure that water is safe to drink and how best to treat illness. The income effect on the child-health benefits from piped water is also found at given levels of education, though it is not as pronounced.
When we look at only the sub-sample of households with access to either source of piped water and compare the prevalence and duration of diarrhea among children under five across households with access from a tap inside the house versus access via a public tap we find two striking effects: first the duration of illness is reduced significantly if households have drinking water source within the premises. Second, the impact is greater in households where the female member is illiterate.
A number of messages for policy emerge from this study. We confirm that there are statistically significant, and quantitatively non-negligible, mean impacts of piped water on an important aspect of child health. However, we also find that the average impact is a deceptive indicator for inferring gains to children in poor families. Policy makers trying to reach children in poor families-who are typically the most prone to disease-will need to do more that relying on making facility placement pro-poor, such as by locating interventions in poor areas. The incidence of health gains need not favor children from poor families even when placement favors the poor. The evident weakness of the impacts we find amongst the income poor, and poorly educated, points to the importance of combining public investments in this type of infrastructure with other interventions in education and income-poverty reduction.  Notes: In addition to the above variables 15 dummies were included to control for state specific effects.   Notes: *indicates significance at the 5% level or lower, ** indicates significance between 5%-10%