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Keywords:

  • J13;
  • I13

Abstract

  1. Top of page
  2. Abstract
  3. 1. Introduction
  4. 2. Data
  5. 3. Institutional Context and Resulting Empirical Strategy
  6. 4. Descriptive Statistics
  7. 5. Instrumental Variables Estimates
  8. 6. Conclusion
  9. Appendix
  10. References

Understanding the causal impacts of taking at-risk youth into government care is part of the evidence base for policy. Two sources of exogenous variation affecting alternative subsets of the at-risk population provide causal impacts interpreted as local average treatment effects. Placing 16- to18-year-old males into care decreases or delays high school graduation, increases income assistance receipt, and has alternative effects on criminal convictions depending upon the instrument employed. This suggests that asking whether more or fewer children should be taken into care is insufficient; it also matters which, and how, children are taken into care.

L'impact du fait de placer des jeunes hommes adolescents en foyer d”accueil sur l’éducation, l'assistance pour maintenir le revenu, et les condamnations. Comprendre les impacts causés par la prise en charge par le gouvernement d”un jeune à risques est partie intégrale d'une politique fondée sur des données probantes. Deux sources de variation exogène affectant différentes portions de la population à risque engendrent des impacts qui sont interprétés comme ayant des effets sur le traitement local moyen. Placer des jeunes hommes de 16 à 18 ans en foyer d'accueil diminue ou retarde la diplomation au secondaire, accroît la dépendance de l'aide sociale, et a des effets différents sur les condamnations au criminel selon les instruments employés. Voilà qui suggère qu'il n'est pas suffisant de se demander si plus ou moins d'enfants devraient être mis en foyer d'accueil, ce qui est important est plutôt de se demander comment on prend soin des enfants.

1. Introduction

  1. Top of page
  2. Abstract
  3. 1. Introduction
  4. 2. Data
  5. 3. Institutional Context and Resulting Empirical Strategy
  6. 4. Descriptive Statistics
  7. 5. Instrumental Variables Estimates
  8. 6. Conclusion
  9. Appendix
  10. References

Protecting children and youth is a critical function of government and a major component of social programming in Canada. Allegations of abuse and neglect are investigated with the major and most extreme element of service provision being removing children from their homes and placing them in government care. Although there are substantial fluctuations in levels across time, according to HRSDC (2007) over 72,000 children and youth, or about 1% of the population, were in government care in Canada on 31 March 2004.1 (See also Canadian Paediatric Society 2008.) Our estimate for the Canadian province of British Columbia (BC), the focus of our study, suggests that fully 5% of children will be in care at some point in their lives, and about 25% will have some contact with the relevant government ministry. Younger children in care will generally be placed with foster families, but more than 10% of children in care are placed in group homes, and this percentage is higher for older children and for male youth (Ryan et al. 2008; OACAS 2007).

Financial costs are another gauge of the magnitude and importance of a program, and the costs are substantial. In 2010 there were 8,960 children in foster care in BC.2 Gordon Hogg, then Minister of Children and Family Development, reported in 2001 that keeping a child in foster care cost roughly $40,000 per year (McInnes 2001). This implies that BC's total expenditure on foster care in 2010/2011 was more than $350 million, which was more than the budget for 10 of BC's 19 other Ministries (BC 2010).3 This is not just a Canadian issue. In the United States, Scarcella et al. (2006) estimate total expenditure on child welfare services by national, state, and local government at $23 billion in fiscal year 2004, which dwarfs the budgets of Head Start, at $6.8 billion (Head Start Bureau 2006), and the Temporary Assistance for Needy Families (TANF), at $13 billion (McGuire and Merriman 2006).

Despite the societal importance of foster care and the substantial public resources devoted to it, we are aware of no research from an economic perspective using Canadian data. However, BC's Representative for Children and Youth and its Provincial Health Officer (RCYBC and PHO 2006, 2007, 2009) have undertaken an important empirical research program and issued three joint special reports presenting novel and important descriptive analyses. In the context of health services utilization and mortality, educational experience, and youth justice experiences, these reports provide important input for the policy process and paint a statistical picture of a vulnerable population facing many challenges. They are the foundation stones of the current study. Although many quality services are currently provided to children and youth at risk, much more work is needed to better understand the child welfare system and its interconnections with other areas of service delivery and to provide evidence for ongoing evidence-based policy and program development. Outside Canada, in contrast to programs such as Head Start or welfare/income assistance, relatively little economic research has been conducted, especially with respect to long-term outcomes, with the exception of Doyle (2007, 2008).

The policy question on which we focus is the causal impact of being taken into foster care for the marginal male youth who is at risk of coming into care. Key outcomes at age 19 are studied: high school graduation, income assistance use, and criminal convictions. This paper is methodologically and substantively similar to Doyle's (2007, 2008) work, but our data allow us to explore an aspect of heterogeneous treatment effects that was not possible given his data, but is quite revealing. We focus on 16- to 18-year-old males in this empirical analysis (BC's age of majority is 19). Naturally, the broad question is relevant to both sexes and all age groups, and we hope to extend the analysis in subsequent papers. However, there are some advantages to limiting the scope of this first study on the topic in Canada. First, we suspect that the impact of being placed in care varies by age and sex, and so the results are easier to interpret for a more homogeneous group. Second, the policy change driving one of our instruments is particularly dramatic for this group, making that instrument stronger. Third, restricting the analysis to older children allows a large number to have a sufficient follow-up period to permit measurement of outcomes after the children have reached the age of majority and left care. Finally, there is great uncertainty about optimal policy for this age group; Ontario does not normally take children 16 and older into care, and Lindquist and Santavirta (2012) report higher adult criminality for Swedish boys who are placed in foster care or residential care during adolescence (ages 13–18), in contrast to no effect for boys placed before age 13. Further work exploring effects for girls and for other age groups would, of course, be useful and this initial analysis will demonstrate the feasibility of that work.

In making the child removal decision, there is a need to balance the risk of abuse and/or neglect in the home against the trauma of removal and the value of maintaining the family unit. Medium- and long-term considerations regarding the value of alternative environments for each youth's ongoing development are also important factors. Given variation in risk from abuse and neglect across households, and in a context recognizing some degree of risk aversion with respect to each child's safety, the optimal rate of placement in care from the children's perspective would occur at the point where a risk-averse decision-maker would set the expected marginal benefit resulting from removal (placement in care) equal to the expected marginal cost from the harm done as a result of separating the children from their parents. Unfortunately, there is almost no empirical information on the marginal costs and benefits of placement in government care, and it is the causal impacts of this that we seek to estimate.

The challenge in estimating the marginal costs and benefits arises from the selection process that results in the placement in care. Children and youth come to the attention of child protection agencies as a result of concern regarding abuse and/or neglect. Investigations are conducted by social workers and, where the concerns/risks are substantiated, children are placed in care.4 Many investigators have compared the outcomes of children placed in care with those of other children; Eschelbach-Hansen (2006) provides a review drawing on American sources that is in accord with the three BC government reports discussed above. See also Berger and Waldfolgel (2004) and McDonald et al. (1996). It is clear that outcomes are, on average, far worse for former children in care. However, differences in outcomes between former children in care and other children are likely attributable, at least in part, to the preceding context, including abuse/neglect. Worse outcomes for children in care are not necessarily inconsistent with benefits from placement; those children's outcomes might have been worse still if they had not been placed in care.

Lawrence, Carlson, and Egeland (2006) do research that is closer to ours. They compare outcomes experienced by a group of children placed in foster care with those experienced by a group of children who were at risk of entering care, but “who remained with and were reared by caregivers who showed a continuous propensity for maltreating their children” (60). Pre-placement assessments using the Teacher Report Form available for both groups provided a baseline measure of factors affecting adaptation and development. They found that “immediately following placement, children in foster care exhibited an increase in behaviour problems.” Although being taken into foster care is correlated with increased behavioural problems, the impact of being taken into care cannot be separated from that resulting from the traumatic event in the family or the egregious episode of abuse prompting the placement.

To date the only research that makes a credible attempt to separate the effects of placement in care from the preceding conditions are the groundbreaking studies by Doyle (2007, 2008). He uses variation in the tendency of social workers to recommend that children be placed in care as an instrument to estimate the impact of placement in care on four important outcomes: delinquency/criminal activity, teen childbearing, employment, and earnings. He finds that placing children in care between 1990 and 2001 decreases the likelihood that they will be employed in 2002 (not statistically significant in the instrumental variable estimates), reduces their earnings in 2002, increases the likelihood that they will become teen parents (statistically significant at the 10% level in the instrumental variable estimates), and increases the likelihood that they will be classified as delinquent. In his 2008 paper, he reports that children taken into care have two to three times greater arrest, conviction, and imprisonment rates than children who remained in their home.

Like Doyle's papers, our analysis uses sources of quasi-randomization in an instrumental variables framework to separate the impact of placement in care from the impact of factors that led to placement in care. However, unlike Doyle, we have access to two such sources: first, we employ a one-time abrupt step up in the child apprehension rate driven by the findings of a judicial inquiry that was followed by a similar step down a few years later; second, like him, we use caseworker administrative discretion as one source of variation. Our two sources of exogenous variation are quite dissimilar, since the second one reflects the “normal” operation of the system, whereas the first is a discontinuous increase and decrease in the scale of operations that reflected anything but normal operations and required, for example, substantial and rapid changes in the number of residential placements that had to be found. Our estimates are for the subset of the population affected by the operation of each source of exogenous variation, and the degree to which these margins (the individuals affected by each instrument) overlap and whether the impacts vary across the two subgroups is an empirical question. We observe little overlap in this case and sometimes find quite different impacts.

Many papers in the program evaluation literature, such as Imbens and Wooldridge (2009) and Heckman, LaLonde, and Smith (1999, 1965), discuss the fact that in a heterogeneous treatment effect environment each instrument identifies a different treatment parameter, but few studies have two – we argue – credible instruments that exploit such different sources of variation (with potentially different impacts) that can be employed simultaneously in a common dataset to explore this issue. We find that for educational outcomes the two instruments provide similar coefficient estimates suggesting that being taken into care delays or reduces the likelihood of high school graduation, but the magnitude of the increase in income assistance use is found to be larger with the judicial inquiry instrument, and the coefficients for convictions actually have opposite signs across the two, as discussed in Section 'Instrumental Variables: Second-Stage Findings'. Overall, the causal effect of being taken into care appears to operate differently on different margins of the population of youth at risk with differing impacts sometimes following. Our results also provide the first estimates of the causal impact on educational attainment and use of the welfare system resulting from being taken into care. They also confirm, although only in part and with caveats, Doyle's results regarding contact with the criminal justice system. Interestingly, we observe very different impacts from our two instruments for income assistance use and the conviction rate; the abrupt across-the-board changes seem much more problematic for long-term outcomes.

In the following section we describe the data. Next, we present the empirical strategy and then our results. Finally, we offer some conclusions and recommendations for future research.

2. Data

  1. Top of page
  2. Abstract
  3. 1. Introduction
  4. 2. Data
  5. 3. Institutional Context and Resulting Empirical Strategy
  6. 4. Descriptive Statistics
  7. 5. Instrumental Variables Estimates
  8. 6. Conclusion
  9. Appendix
  10. References

Central to our analysis are data that derive from investigations of allegations of abuse and/or neglect made between January 1993 and April 2003 to the Ministry of Children and Family Development, which is responsible for child welfare in BC. The opening or reopening of a child protection file indicates that a child had come to the attention of the Ministry, and that for a child services file indicates placement in care.5 However, we do not have access to the contents of these files, therefore, for example, whether the investigation is motivated by allegations of abuse and/or neglect is not known. These administrative records are then linked to records for the same individual from the ministries of Employment and Income Assistance, Education, and Public Safety and the Solicitor General, and then are anonymized.6

The data are divided into two: a primary dataset containing records for boys aged 16 to 18, and an auxiliary one for all other cases that is used to generate the second instrumental variable. Assignment to the primary dataset is based on the earliest contact for each boy after turning age 16 and before age 18 who was not in care at the time of the contact (with or without previous contacts or spells in care) providing one “reference” record per person; all other contacts are in the auxiliary dataset. We cannot measure the duration or frequency of care, nor do we measure repeated occurrences; our datasets contain children and youth with a variety of contact and care histories. Our estimates, therefore, reflect the averages associated with any such factors. Extensions looking at these issues would be worth exploring in subsequent research with access to additional data. From the 26,334 records of contact we drop: 789 observations for those who did not have a record in BC's education system; 1,388 records where the individual had graduated from high school before contact; 1,962 records where we could not construct the worker fixed effect; 6 observations that we could not link to a census subdivision; 395 where care started at age 16, but the break in care was less than a month; 9 observations relating to youth with special needs; 69 that could not be associated with a family; and 989 where contact occurred before May 1993. This leaves 20,727 observations; of these, 2,260 youths were placed in care.

We next match the reference records to data from other Ministries. In BC, income assistance (IA, sometimes called welfare or social assistance) is provided to singles and childless couples as well as to one- and two-parent families. The Ministry of Employment and Income Assistance made available records of all IA recipients (whether on the file as a spouse or child) by month from October 1990 to December 2005. We use these data to construct both explanatory variables reflecting the IA paid to the youth/family before contact with the Ministry of Children and Family Development and outcome variables for IA use after the youth turned 19. Similarly, the Corrections Branch of the BC Ministry of Public Safety and Solicitor General has maintained records of sentences handed down in BC since 1 April 1975. Matching was from an extract of the admissions and discharges from each institution in their dataset. Individuals sentenced to federal institutions pass through provincial institutions so the records are complete. Likewise, education records allowed high school graduation to be measured for the boys in question.

The second, auxiliary, dataset is formed from the records of contacts for girls aged 0 to 18 and boys aged 0 to 15 not in care at time of contact (with or without previous contacts or spells in care). It is used to produce estimates of caseworker fixed effect reflecting administrative discretion – an instrumental variable similar to that used by Doyle (2007, 2008) as discussed below – that is independent of the primary sample of 16- to 18-year-old boys. For this group we received 787,118 records of contact with the child protection system. These records identify the child, the caseworker, and the office as well as whether or not the child was placed into foster care.

3. Institutional Context and Resulting Empirical Strategy

  1. Top of page
  2. Abstract
  3. 1. Introduction
  4. 2. Data
  5. 3. Institutional Context and Resulting Empirical Strategy
  6. 4. Descriptive Statistics
  7. 5. Instrumental Variables Estimates
  8. 6. Conclusion
  9. Appendix
  10. References

In addition to taking advantage of the administrative data to generate a set of control variables, we seek to identify the causal impact(s) of being taken into care by exploiting the institutional context to locate source(s) of exogenous variation that permit the use of an instrumental variables estimator. Quite unusually, two credible instrumental variables are available to us. The first involves sudden and substantial changes in the child apprehension (removal) rate as depicted in Figure 1 for 16- to 18-year-old boys. A book length discussion of various aspects of this transition period is edited by Foster and Wharf (2008). The discrete step up in the child apprehension rate in June 1996 followed a judicial inquiry. A similar discrete jump down followed in April 1999. The second instrument is akin to that employed by Doyle (2007, 2008) and follows from caseworkers exercising their administrative discretion as evidenced by the observation that there are appreciable differences in child apprehension rates across caseworkers, despite children and youth being approximately randomly assigned to them.

image

Figure 1. Count of Boys Aged 16 to 18 at Risk, and Probability of Their Being Taken into Care

NOTES: As plotted, Period 1 = January 1994 to May 1996; Period 2 = June 1996 to March 1999; Period 3 = April 1999 to April 2003

SOURCE: Derived from BC administrative data.

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Our first instrumental variable derives from a very unfortunate incident. In 1992 the murder by his mother of a five-year-old boy who had not been taken into care led to a judicial inquiry into the child welfare system in BC by Judge Thomas Gove. The inquiry held hearings in 1994 and 1995 and its recommendations, released in 1995, emphasized child protection. The province's administrative systems responded with a transition commission in 1996, and in that year nearly 350 new social workers were hired. As a result, between 1995 and 1999, the number of children in care in BC increased from about 6,000 to about 10,000. If this increase had occurred as a result of increasing numbers of children contacted, we might expect the characteristics of the children to be correlated with the increase. However, figure 1 shows that the number of contacts with the Ministry did not spike in 1996, whereas the figure shows that the percentage of investigations that ended up placing the youth in care (i.e., removing the child from his family) did so. This is consistent with the formation of a new Ministry for Children and Families in 1996 to, in the then premier's words, “put our children and their safety first.”7 A few years later an internal review by the Ministry led to an equally abrupt reversal of the new policy in the first month of a new fiscal year, as can also be seen in Figure 1. It occurred less publicly and appears to have been at least partly motivated by budget restraint (Foster and Wharf 2008, 46).

This first instrument is operationalized as a series of indicator variables for the three different periods (Period 1 = May 1993 to May 1996; Period 2 = June 1996 to March 1999; Period 3 = April 1999 to April 2003; denoted P1, P2, and P3 in the tables). Although our analysis focuses on the flow into care, to place this into context: Figure 2 presents the stock of children and youth in care from 1979 to 2007 from official ministry publications. A long decline is evident before the start of our data period in January 1993, which is near the trough. This is followed by an abrupt increase in the stock (though not as abrupt as that in the flow) that reaches a maximum and then reduces to a plateau near the end of our data period in April 2003. When we take a longer perspective of the stock of those in foster care and normalize by the relevant population, the percentage in care peaked in about 1970 at around 1.3% of the relevant population, and the trough was in 1993, when 0.6–0.7% were in care.

image

Figure 2. Total Number of Children in Foster Care in British Columbia from 1979 to 2007

SOURCE: Calculations by the authors, with data from Gerald Merner and Ian McKinnon for years prior to 1998 gratefully acknowledged.

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We expect this first instrument to be valid because the mechanism for generating contacts (concerns regarding possible abuse and/or neglect expressed by neighbours, teachers, doctors, police, etc.) did not change appreciably over the period in question (see Figure 1 for monthly counts of the number of contacts), but policies and practices regarding placing children in care did. The possibility of confounding fluctuations in other factors is discussed below.

Administrative discretion among caseworkers is the source for the second instrument, which is conceptually identical to that employed by Doyle (2007, 2008), who discusses the justification at length. In short, two elements make it a credible instrumental variable. First, in an effort to ensure that caseworkers have roughly comparable workloads new investigations are effectively randomly assigned to them. For example, new investigations are rotated through caseworkers, and/or the caseworker who is “on duty” during a certain period investigates new cases that arrive. As a result, the characteristics of new cases are not correlated with those of caseworkers.

Secondly, caseworkers – Ministry employees, mostly trained social workers, who make recommendations regarding children's placement in care – have individual-level differences, which we refer to as fixed effects, in their propensities to take children into care. These fixed effects can be substantial, as will be demonstrated below. The variability of attitudes towards placement across workers has long been recognized. Rossi, Schuerman, and Budde (1996) provide an interesting introduction to the literature on variability in worker decisions. While, as noted, the decision to place a child in care is ultimately made by a judge, it is strongly influenced by the recommendation of the social worker. Figure 3 presents a histogram of the percentage of cases investigated that result in a child coming into care in our data period, for all cases handled by caseworkers starting an investigation for at least one 16- to 18-year-old boy in the year. The unit of analysis is a worker-year: the total number of investigations started by each caseworker in each year from 1993 through 2003. Our datasets comprise 10,026 worker-years, of which 4,538 involve workers with at least one contact with a 16- to 18-year-old boy; on average, each caseworker started 81 investigations per year. Clearly, there are massive differences across workers. Some of the variation is from random differences in the cases investigated, and some is affected by factors such as the demographics faced in each local office, but some reflects differences across caseworkers in the proclivity to take children and youth into care; it is this aspect of the variation that we exploit, since cases are quasi-randomly assigned within offices.

image

Figure 3. Caseworker Heterogeneity: Worker-years by Percentage of Investigations Where Children Are Taken into Care

NOTES: Based on all cases handled by workers starting an investigation for at least one 16- to 18-year-old boy in the year

SOURCE: BC administrative data.

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To operationalize the concept of a caseworker-fixed effect as an instrumental variable, we employ the second sample discussed in the data section (comprising investigations for all girls, and boys younger than age 16) and estimate the difference between each worker's propensity to place children in care in each year and that propensity for the other caseworkers in the same office and year. This approach addresses local area effects as well as trends over time. All contacts with the Ministry of Children and Family Development between January 1993 and April 2003, excluding the 16- to 18-year-old males, are employed in these regressions. To ensure sufficient precision, only workers who had more than 10 contacts in the year are included in the sample, and the office that the worker was in had to have more than 10 additional contacts in the year. This provided 787,118 investigations/observations for use across a series of regressions, one per year, as depicted in equation (1).

  • display math(1)

In these ordinary least squares (OLS) regressions for the set of investigations indexed by i, a dummy variable indicating coming into care is regressed on a vector of dummy variables (with one category omitted for each) for each Office, each Month of the year to capture seasonality, each child's Age (in years) and gender (Female). Even though the unit of observation in the regression is the investigation, each residual u is also associated with a particular caseworker, and that worker's annual fixed effect was calculated as the mean of the relevant error terms for that year. A plot of the distribution of worker fixed effects is depicted in Figure 4. Clearly, there is substantial variation across workers; the most extreme workers’ probabilities of apprehension differ by plus or minus 30% from the mean.

image

Figure 4. Administrative Discretion as an Instrumental Variable: Histogram of Caseworker Fixed Effects

SOURCE: BC administrative data; calculations by the authors based on regression analysis.

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One important concern is whether certain caseworkers are preferentially assigned to particular types of cases. Doyle (2007, 2008) is careful to exclude cases with particular characteristics, such as those involving sexual assault, from his sample, since in the jurisdiction he studies they are not randomly assigned to caseworkers but are addressed by specialists. While we know of no such specialization in BC, this identifying assumption is tested empirically. Each caseworker fixed effect (instrumental variable) is regressed on the available characteristics of the cases of boys aged 16 to 18 investigated by that worker. This combines the dependent variable – the worker fixed effect – estimated from the second sample that excludes boys aged 16 to 18 with independent variables from the dataset containing those boys. In an effort to maximize the power of our test we conduct three regressions starting with a small set of independent variables that we think are most likely to be important and then expanding the set of regressors. In the first regression we include only age (measured in months), language, and aboriginal status, while in the second we include the remainder of the variables described in Table A1 (a total of 28 control variables plus age). In a third regression we include an additional 20 variables not employed elsewhere in this analysis – the characteristics of each boy's “key” parent, and that person's spouse if there is one. For each regression we examine the statistic from an F-test of the statistical significance of all of the regressors, excluding the intercept, for any indication of a relationship between the characteristics of the boys and the child apprehension tendency of the caseworker managing their investigations. In all cases there is no evidence of the statistically significant relationship. The F-statistics and the associated P-values are regression 1, F(12, 2900) = 0.75, P-value = 0.70; regression 2, F(29, 2900) = 0.74, P-value = 0.84; regression 3, F(49, 2900) = 0.80, P-value = 0.84. (The 2900 elements of the degrees of freedom derive from there being 2901office-years – statistical clusters – in the relevant data.) Overall, these regressions provide strong support for the contention that there is quasi-randomization of cases to caseworkers.

The combination of quasi-random assignment of cases to caseworkers and caseworker-specific differences in the propensity to take children into care combine to provide a very credible second instrumental variable; however, in the heterogeneous treatment effect context where a Local Average Treatment Effect (LATE; Angrist and Imbens 1994) is being estimated an additional assumption, frequently referred to as monotonicity, is also required. Angrist, Imbens, and Rubin (1996) discuss the situation when monotonicity only holds approximately. This assumption rules out “defiers,” that is, individual youth having a lower probability of being taken into care as a result of being assigned to a caseworker with a higher average propensity to take youth into care. Given the nature of both of our instruments, it appears credible that this condition is substantively met in both cases.

The LATE interpretation in this case is particularly interesting given the substantial differences in the nature of the two instrumental variables (see Heckman, Urzua, and Vytlacil 2006). For the first instrument it is the impact of being taken into care on the marginal child, where marginal can be thought of as those taken into care during period 2 who would have been left with their families in the preceding and subsequent periods (although, formally, there is no need for the first and third period to be identical). This coefficient tells us nothing about those children who would have been apprehended, or not apprehended, in all three policy periods (those whose probability of apprehension did not change as a result of the policy change). In contrast, the marginal child for the second instrumental variable follows from being quasi-randomly assigned to a caseworker with a high, or low, propensity to take children into care. Similarly, those extreme cases where the probability of apprehension is approximately equal across caseworkers do not identify the causal impact being estimated. These two instruments likely represent different margins of being taken into care – alternative, although undoubtedly overlapping, subsets of the at-risk population.

Additionally, as discussed in Foster and Wharf (2008), the abrupt increase and subsequent decrease in the child apprehension rate had important ramifications for the system. New social workers were hired to support the increased in-care caseload, and there was a substantial increase in the number of foster parents, group homes, and the like required.8 This was a period of substantial instability. In contrast, differences in the child apprehension rate across caseworkers – within each year – are in effect differences across randomly assigned children, holding the external context constant (assuming that changes within each year are modest). Having said this, the first instrument is subject to trends over time other than those captured by the abrupt changes on which we focus. In what follows we provide evidence that we believe supports the exogeneity and relevance of the first instrumental variable, but ultimately readers must make their own decisions in this regard. Comparisons with future research, both considering other provinces and at additional age/gender groups for BC, will provide further evidence on these issues.

4. Descriptive Statistics

  1. Top of page
  2. Abstract
  3. 1. Introduction
  4. 2. Data
  5. 3. Institutional Context and Resulting Empirical Strategy
  6. 4. Descriptive Statistics
  7. 5. Instrumental Variables Estimates
  8. 6. Conclusion
  9. Appendix
  10. References

Descriptive statistics for the dependent variables are presented in Table 1. As can be seen in the top row, roughly 10% of investigations result in a child being removed, with the Gove Inquiry causing an almost 40% increase in the child apprehension rate (or just under 4 percentage points on the base of 10%) in period 2. For the three dependent variables in our analysis – high school graduation by age 20, IA receipt in the 12 months when the person was aged 19, and the probability of being convicted of a crime when aged 19 or 20 – two common patterns are evident. First, outcomes that are commonly judged to be poorer (lower probabilities of high school graduation and higher probabilities of IA receipt and a criminal conviction) are observed for those taken into care. Of course, while some of these gaps may reflect the removal itself, they probably primarily reflect the underlying cause for the removal. Second, across the three periods of our data the trends discussed above are evident.

Table 1. Descriptive Statistics
 TotalPeriod 1Period 2Period 3
NOTES
  1. Standard deviations are in parentheses. Period 1 = May 1993 to May 1996; Period 2 = June 1996 to March 1999; Period 3 = April 1999 to April 2003.

Average removal rate0.1090.0970.1370.099
 (0.312)(0.296)(0.344)(0.299)
Pr (HS grad by age 20)    
If removed0.1230.1100.1150.143
 (0.329)(0.313)(0.319)(0.350)
If not removed0.2920.2490.2940.325
 (0.455)(0.433)(0.456)(0.468)
Months IA When 19    
If removed4.0465.5264.3072.601
 (4.711)(4.807)(4.715)(4.192)
If not removed2.1003.1122.3931.068
 (3.855)(4.355)(3.994)(2.962)
Pr (Convicted when 19 or 20)    
If removed0.0900.1010.1030.069
 (0.287)(0.301)(0.304)(0.254)
If not removed0.0380.0520.0350.028
 (0.190)(0.222)(0.184)(0.165)
Frequency20727666459108153
Percentage10032.1528.5139.34

Background variable descriptive statistics, by period, are presented in Table A1. The most striking demographic characteristic of our sample is the percentage with self-declared aboriginal heritage – about 20% compared with about 8% for the population as a whole (see RCYBC and PHO 2007). Our sample also shows significant contact with the other social services. In particular, it shows an average of more than eight physician visits per person in the two years prior to contact with the child protection system. It is notable, however, that even in our sample, visits that resulted in a diagnosis related to child maltreatment were very rare. The sample also had significant contact with Corrections before contact with the child protection system – about one in six of our sample had such contact. And, on average, the families of the youth in our sample received just under six months of IA benefits in the two years prior to contact.

Rates of high school graduation, welfare use, and criminal conviction all vary systematically over the study period for our sample and in the general population.9 Trends by month for the entire set of those at risk of coming into care are presented in Figures 5, 6, and 7 for related variables. Our indicator of the high school graduation rate, Figure 5, is the percentage of students who graduated by the end of the year in which they turned 19 (i.e., before their 20th birthday), which is over one year longer than the age of the modal student who graduates part-way through his 18th year. In the provincial population this measure increased from 68% to 74% over the period of study. Turning to IA, it also experienced large changes as part of a province-wide trend. The percentage of the entire population receiving IA increased from 9.7% in 1993 to a peak of 10.4% in 1995 and fell to 4.1% in 2002. In Figure 6 we show the percentage of those at risk of coming into care, according to the month that the investigation was initiated, who had any IA use in the year during which they were age 19. Looking next at the number of individuals aged 19 to 25 in the general population starting a sentence in BC, it increased by 21% between 1993 and 1996 and fell again by 7% by 2003. In Figure 7 we depict the age 19 incarceration rate for the at-risk group, which differs numerically from new convictions in Table 1, and it is (mostly) declining. Also, seasonal effects can be informally observed in figures 5, 6, and 7.

image

Figure 5. Probability Graduated from High School before 20th Birthday by Month of Investigation

SOURCE: BC administrative data; calculations by the authors for those at risk of coming into care.

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image

Figure 6. Percentage on Income Assistance in Year While Age 19 by Month of Investigation

SOURCE: BC administrative data; calculations by the authors for those at risk of coming into care.

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image

Figure 7. Proportion Incarcerated in Year When Age 19 by Month of Investigation

SOURCE: BC administrative data; calculations by the authors for those at risk of coming into care.

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Recognizing these background trends/patterns is a potentially important aspect of the analysis and our goal is to control for them in a very flexible way so that the instrumental variable estimates for our first instrument are credible and cannot be posited to result from spurious correlations on these dimensions. Therefore, as will be shown below, we include a third-order polynomial time trend and a set of month indicators for seasonality. We settled on a third-order polynomial by testing down from a fifth-order one, stopping when all of the terms of the polynomial were statistically significant. Section 'Sensitivity Tests' presents relevant sensitivity tests to alleviate concerns about over- or under-fitting the trend. Also, as an alternative to the polynomial trend, we experimented with using a series of year dummy variables for the worker fixed effect instrument and, despite our concern, found that it made little substantive difference.

5. Instrumental Variables Estimates

  1. Top of page
  2. Abstract
  3. 1. Introduction
  4. 2. Data
  5. 3. Institutional Context and Resulting Empirical Strategy
  6. 4. Descriptive Statistics
  7. 5. Instrumental Variables Estimates
  8. 6. Conclusion
  9. Appendix
  10. References

Linear probability models are employed for our main analysis, since we are not interested in fitted values but in average marginal effects, which appear to be reasonably estimated by the linear approximation that is OLS (see, e.g., the discussion by Moffit 1999). Also, we need be less worried about inconsistent estimates from heteroscedasticity and/or omitted variables compared with non-linear models such as logits or probits. Moreover, we do not have testing procedures for over-identification, weak instruments, and the like that are as well developed and understood for non-linear endogenous variable models. All of these factors encourage us to employ simple two-stage least squares models. Nevertheless, in Section 'Sensitivity Tests' we provide sensitivity analysis using a bivariate probit, which is the non-linear specification most commonly employed for endogenous dummy variables. The results are remarkably similar although slightly less precisely estimated.

5.1. Instrumental Variables: First-Stage Findings

A series of alternative first-stage regressions from two-stage least squares estimates are presented in Table 2. They all take the general form:

  • display math(2)

where, building on equation (1), j (as opposed to i) is used as a subscript to indicate that the sample comprises the set of boys aged 16 to 18. Instruments is vector of one or more of the combinations of up to six variables employed, as listed in Table 2. Poly is a third-order polynomial in time measured in months (the models in columns (3) and (5), with only the worker fixed effect [FE in the Tables], employ a set of year indicator variables instead of the polynomial) to control for trends over time. Control is a vector of the 28 background variables listed in Table A1 that is included in some, but not all, specifications.

Table 2. OLS First-Stage Regressions: Dependent Variable is InCare (0/1)
 (1)(2)(3)(4)(5)(6)(7)(8)(9)(10)
NOTES
  1. Heteroscedasticity robust standard errors, clustered on worker-year, are in brackets. P-values are in parentheses:

  2. ***p < 0.01, **p < 0.05, *p < 0.1.

  3. All regressions also include a linear control for age at first contact measured in months. Anderson canonical correlations and Cragg-Donald tests, which have the null hypothesis that the instrumented data matrix is rank deficient, always reject the null with p-values of 0.0000 for these regressions in accordance with statistical identification being satisfied, but these tests are not robust to clustering, so the test statistics are biased toward low p-values. They are therefore not presented. Period 1 = May 1993 to May 1996; Period 2 = June 1996 to March 1999; Period 3 = April 1999 to April 2003. FE is the worker fixed effect instrument, which is sometimes interacted with the period indicators.

Period 10.0377*0.0328    0.0370*0.03200.03670.0317
 [0.022][0.022]    [0.022][0.022][0.022][0.022]
Period 20.0595***0.0572***    0.0609***0.0586***0.0604***0.0582***
 [0.014][0.014]    [0.014][0.013][0.014][0.014]
Worker FE  0.5207***0.5171***0.5185***0.5146***0.5223***0.5201***  
   [0.066][0.066][0.064][0.064][0.066][0.064]  
FE * Period 1        0.4977***0.4864***
         [0.129][0.127]
FE * Period 2        0.4768***0.4822***
         [0.111][0.108]
FE * Period 3        0.5756***0.5724***
         [0.096][0.093]
Partial R20.0020.0020.008 0.008 0.0100.0100.0100.010
F(inst, 2864)16.8317.7861.7464.832.4934.820.0121.49
P-value(0.000)(0.000)(0.000) (0.000) (0.000)(0.000)(0.000)(0.000)
11-Month VarsYesYesYesYesYesYesYesYesYesYes
3rd-order polyYesYes Yes YesYesYesYesYes
Year Vars  Yes Yes     
28 control vars Yes  YesYes Yes Yes
Observations20727207272072720727207272072720727207272072720727
R-squared0.00620.04920.01330.01220.05630.05510.01440.05740.01450.0574

These first-stage regressions are, of course, common to each of the three dependent variables under study and a variety are presented to explore alternative specifications and the stability of our results. The standard errors are heteroscedasticity consistent and clustered at the level of the 2901 local office-years to accord with the estimates of the worker fixed effects. On average, each office started 278 investigations per year. Also presented are partial-R2s for the instruments (as suggested by Bound, Jaeger, and Baker 1995) and the test statistic and p-value for an F-test of the joint significance of the instrumental variables. Staiger and Stock (1997) and Stock and Yogo (2005) provide evidence suggesting that an F-statistic of the instrumental variables in the first stage is a useful measure to ensure the analysis does not suffer from a weak instrument problem. In all cases the test statistics presented are well in excess of the rule of thumb minimum of 10 and are in excess of the critical values presented by Stock and Yogo. Anderson canonical correlations and Cragg-Donald test statistics, which have the null hypothesis of under-identification/weak instruments, are also estimated. These tests always reject the null with p-values smaller than 0.000, but they are not robust to clustering; as a result they are biased towards small p-values and so are not presented.

Turning to the coefficient estimates, we note that the first two columns of Table 2 use only the period indicators following from the judicial inquiry as instruments and show that there is a 5 to 6 percentage point increase in the child apprehension rate, on a base just under 10% as seen in Table 1, in Period 2 relative to Period 3; Period 1 is somewhere in the middle. The coefficient on the Period 1 indicator is on the margin of being statistically significant at the 10% level, the p-value reducing slightly when the background variables are introduced to the regression in column 2 (from a p-value of 0.092 to 0.130, both the coefficient estimate and standard error decrease slightly with the background variables).

Regressions 3 through 6 explore the worker fixed effect instrumental variable. Interestingly, the F-statistic is much larger for the worker fixed effect than it is for the period indicators, as is the partial R2, suggesting that the worker fixed effect is the more powerful instrument. Overall, although there are small changes, none of the instrumental variables’ coefficients are much affected by the introduction of the background variables, or any of the other control variables, which is consistent with the idea that the instruments are not correlated with observable characteristics supporting the maintained hypothesis of quasi-randomization that justifies the instrumental variables approach.

When both instruments are employed together, in columns 7 and 8 (with, and without, the background variables respectively), the coefficient estimates do not move appreciably compared with those in the earlier regressions and the partial R2 is roughly the sum of those from each instrument regressed independently; the instruments do not appear to be correlated with each other or with the control variables. This supports the contention that these two instruments are operating on different margins of the population and we might observe different LATE estimates for each. Columns 9 and 10 introduce interactions between the instrumental variables as additional instruments. As can be seen, the F-statistics in columns 9 and 10 decline relative to 7 and 8. Also, formal tests show that there is no statistically significant difference between the three coefficients of the period indicators interacted with the worker fixed effect (for column 9: F(2,2864) = 0.25, p-value = 0.7750; for column 10: F(2,2864) = 0.25, p-value = 0.7769; this is confirmed by the trivial increase in the relevant R2s for the regressions seen in the bottom row). Overall, the regressions in columns 7 and 8 are the preferred specifications when both instruments are employed, since the addition of instruments (the interactions) that lack additional predictive power can be deleterious.

5.2. Instrumental Variables: Second-Stage Findings

Table 3 presents the instrumental variable results when high school graduation by age 20 is the dependent variable. The regression has the same form as that for Tables 4 and 5:

  • display math(3)

where Y is one of the three dependent variables and inline image is the predicted value of InCare from equation (2). Table 2 has the same format as Tables 3 and 4 for, in turn, IA use and the incidence of conviction. As a sensitivity test, columns 1 through 5 include controls for 28 background variables, whereas columns 6 through 10 do not. Including exogenous background/control variables normally reduces the residual variation improving the estimator's precision. As is common in the literature, we believe these to be the preferred estimates. The first of each set of five regressions (columns 1 and 6) is an OLS regression, and the next four are instrumental variables estimates employing different combinations of instruments for the endogenous right-hand-side indicator variable InCare. Although we have evidence that the instruments are not weak, nevertheless in addition to the standard error and asterisks representing p-values from t-statistics (based on standard errors that are robust to heteroscedasticity and clustering) for each coefficient we also provide the Anderson-Rubin statistic for the statistical significance of the endogenous regressor that is robust to weak instruments as well as to heteroscedasticity and clustering, since it has better statistical properties. Moreover, the Sargan-Hansen J-statistic is employed when there are multiple instruments; it is an over-identification test, or in the context of heterogeneous treatment effects a test with the null of instrument homogeneity. That is, it can be interpreted as a test of whether the LATE estimates from the different (sets of) instruments are equal (see, e.g., Heckman, Lalonde, and Smith 1999, 1965; or Angrist and Pishke 2008, 167).

Table 3. OLS and IV Results with High School Graduation by Age 20 as the Dependent Variable
 (1)(2)(3)(4)(5)(6)(7)(8)(9)(10)
 OLSIVIVIVIVOLSIVIVIVIV
     P1, P2,    P1, P2,
    P1, P2,FE1,   P1, P2,FE1,
Instruments P1, P2Wkr FEWkr FEFE2, FE3 P1, P2Wkr FEWkr FEFE2, FE3
NOTES
  1. Heteroscedasticity robust standard errors, clustered on worker-year, are in brackets. P-values are in parentheses:

  2. ***p < 0.01, **p < 0.05, *p < 0.1.

  3. All regressions also include a linear control for age at first contact measured in months. Instrumental variables: P1 = Period 1, P2 = Period 2, Wkr FE = Worker Fixed Effect; FE1, FE2, and FE3 are the interactions between the period dummies and the worker fixed effect variable. Columns 1–5 (the preferred estimates) include controls for 28 background variables, whereas columns 6 through 10 do not. See Section 'Instrumental Variables: Second-Stage Findings' for more detail.

InCare−0.1301***−0.2744−0.1956*−0.1884**−0.1778**−0.1701***−0.2981−0.1893*−0.2133**−0.2027**
 [0.008][0.204][0.103][0.090][0.091][0.008][0.210][0.105][0.093][0.093]
Anderson-Rubin 3.723.596.368.94 3.93.117.149.68
p-value χ2(inst) (0.1555)(0.0582)(0.0952)(0.1114) (0.1424)(0.0778)(0.0675)(0.0847)
Sargan-Hansen J 1.801 2.0844.339 1.801 2.0634.303
p-value χ2(inst−1) (0.180) (0.353)(0.362) (0.180) (0.356)(0.367)
3rd-order polyYesYes YesYesYesYesYesYesYes
YesYes YesYesYesYesYesYesYes 
28 control varsYesYesYesYesYes     
11-month varsYesYesYesYesYesYesYesYesYesYes
Observations20727207272072720727207272072720727207272072720727
R-squared0.07040.06070.06260.06880.06930.02250.01450.02230.02160.0220
Table 4. OLS and IV Estimates with Income Assistance Use While Age 19 as the Dependent Variable
 (1)(2)(3)(4)(5)(6)(7)(8)(9)(10)
 OLSIVIVIVIVOLSIVIVIVIV
     P1, P2,    P1, P2,
    P1, P2,FE1,   P1, P2,FE1,
Instruments P1, P2Wkr FEWkr FEFE2, FE3 P1, P2Wkr FEWkr FEFE2, FE3
NOTES
  1. Heteroscedasticity robust standard errors, clustered on worker-year, are in brackets. P-values are in parentheses:

  2. ***p < 0.01, **p < 0.05, *p < 0.1.

  3. All regressions also include a linear control for age at first contact measured in months. Instrumental variables: P1 = Period 1, P2 = Period 2, Wkr FE = Worker Fixed Effect; FE1, FE2, and FE3 are the interactions between the period dummies and the worker fixed effect variable. Columns 1–5 (the preferred estimates) include controls for 28 background variables, whereas columns 6 through 10 do not. See Section 'Instrumental Variables: Second-Stage Findings' for more detail.

InCare1.6100***8.8693***1.44242.3442***2.3328***1.9784***9.1839***1.08052.7933***2.7689***
 [0.101][2.311][1.106][0.902][0.887][0.100][2.395][1.058][0.940][0.923]
Anderson-Rubin 20.611.6620.9421.04 19.840.9920.6120.63
p-value χ2(inst) (0.0000)(0.1981)(0.0001)(0.0008) (0.0000)(0.3194)(0.0001)(0.0010)
Sargan-Hansen J 0.001 14.07114.672 0.054 12.53313.376
p-value χ2(inst−1) (0.9715) (0.0009)(0.0054) (0.8162) (0.0019)(0.0096)
3rd-order polyYesYes YesYesYesYesYesYesYes
28 control varsYesYesYesYesYes     
11-month varsYesYesYesYesYesYesYesYesYesYes
Observations20727207272072720727207272072720727207272072720727
R-squared0.16530.13900.11100.16220.16230.08990.22350.08500.08590.0861
Table 5. OLS and IV Estimates with Conviction When Age 19 or 20 as the Dependent Variable
 (1)(2)(3)(4)(5)(6)(7)(8)(9)(10)
 OLSIVIVIVIVOLSIVIVIVIV
     P1, P2,    P1, P2,
    P1, P2,FE1,   P1, P2,FE1,
Instruments P1, P2Wkr FEWkr FEFE2, FE3 P1, P2Wkr FEWkr FEFE2, FE3
NOTES
  1. Heteroscedasticity robust standard errors, clustered on worker-year, are in brackets. P-values are in parentheses:

  2. ***p < 0.01, **p < 0.05, *p < 0.1.

  3. All regressions also include a linear control for age at first contact measured in months. Instrumental variables: P1 = Period 1, P2 = Period 2, Wkr FE = Worker Fixed Effect; FE1, FE2, and FE3 are the interactions between the period dummies and the worker fixed effect variable. Columns 1–5 (the preferred estimates) include controls for 28 background variables, whereas columns 6 through 10 do not. See Section 'Instrumental Variables: Second-Stage Findings' for more detail.

InCare0.0228***0.0975−0.0833−0.0506−0.05630.0527***0.0768−0.0770−0.0437−0.0491
 [0.006][0.093][0.055][0.046][0.045][0.006][0.096][0.059][0.050][0.049]
Anderson-Rubin 6.252.398.6114.41 5.291.826.7911.5
p-value χ2(inst) (0.0440)(0.1217)(0.0349)(0.0132) (0.0711)(0.1773)(0.0789)(0.0423)
Sargan-Hansen J 5.604 7.44911.325 5.084 5.9359.239
p-value χ2(inst−1) (0.0179) (0.0241)(0.0231) (0.0241) (0.0514)(0.0554)
3rd-order polyYesYes YesYesYesYesYesYesYes
28 control varsYesYesYesYesYes     
11-month varsYesYesYesYesYesYesYesYesYesYes
Observations20727207272072720727207272072720727207272072720727
R-squared0.11600.10360.08910.10400.10210.01030.00900.02880.01130.0138

In column 1, with controls for the various background variables, the OLS coefficient estimate for InCare indicates that those who come into care are 13 percentage points less likely to graduate from high school by age 20 than those who are investigated but not taken into care; the gap is 17 percentage points, as seen in column 6, when the control variables are not included, indicating that some of the cross-sectional gap can be explained by the observable characteristics in the data. Using only the period indicators as instruments, the point estimates in both columns 2 and 7 grow more negative, but the standard errors of the instrumental variables estimates are substantial and the coefficients are not statistically different from either the OLS coefficient or zero at conventional levels, though there is a roughly 85% chance that the instrumental variables coefficient differs from zero. In these, as in the other pairs of instrumental variable regressions in Table 3, including the control variables makes only a small difference to the coefficient estimates.

Using the worker fixed effect as an instrument on its own, in columns 3 and 8, the point estimate is more negative than that for OLS and the standard error is substantially smaller than for the period indicators. Both t-statistics are significant at the 10% level, which accords with the p-values on the Anderson-Rubin statistics. While the instrumental variables coefficient in, for example, equation (3) is not statistically different from that estimated by OLS, the interpretation is dramatically different. OLS provides the difference in the average outcome, conditional on the covariates, between those male youth taken into care and those who remain with their families. However, the instrumental variable coefficient should be interpreted as the causal impact of being taken into care on the marginal children affected by the instrument, in this case the discretion of the social workers.

When the period indicators and the worker fixed effects are simultaneously employed as instrumental variables, the point estimate is very similar to that for the worker fixed effect alone. However, the J-statistic cannot differentiate between the instrumental variables. The estimate of the standard error decreases slightly causing the p-value of the t-statistic to increase slightly. In contrast, with controls for the background variables the Anderson-Rubin test statistic has a larger p-value because the degrees of freedom adjustment from the increased number of instruments outweighs the numerical increase in the statistic, whereas without controls the p-value decreases slightly, since the point estimate of the coefficient is slightly larger. We show the results for the interacted set of instruments in columns 5 and 10, but we do not focus on them, since they are not our preferred specification as discussed with respect to the first-stage regressions.

Overall, we believe that the evidence suggests that on the margin taking children into care has a causal impact to reduce the probability that they graduate from high school by age 20. Given the available data, we are not able to discern if this is a permanent reduction in the high school graduation rate, a delay in high school graduation, or a combination of the two. In terms of economic and social policy, this decline (or delay) is appreciable. Focusing on the more precisely estimated worker fixed affect point estimate of about −0.19, then a difference in the probability of apprehension of 0.5 (an extremely large difference, as seen in Figure 4) would be associated with roughly two-thirds of the average difference between those removed and those not removed, as seen in Table 1.

The OLS estimates in Table 4 suggest that being taken into care is associated with an increase in IA use in the year before turning 20. Like the results seen in Table 3, the regressions with control variables have slightly smaller point estimates, but the basic pattern is similar with and without controlling for these background characteristics. Column 1 indicates that those taken into care receive approximately 1.6 additional months of IA. Column 2, employing only the period indicators, has a point estimate that is substantially larger than that estimated by OLS, and it is statistically significant at the 1% level by both the t-statistic and the Anderson-Ruben test. When the worker fixed effect is employed on its own, the point estimate is slightly smaller than, but quite similar to, the OLS estimate. However, the standard errors are sufficiently large that the coefficient is not statistically significantly different from zero.

In columns 4 and 8, when both instruments are employed simultaneously, the point estimate is part way between those in the previous two instrumental variables regressions and the coefficient estimate is clearly statistically different from zero, but the J-statistic suggests that the sets of instruments are not providing estimates that are consistent with each other; informally, this can be interpreted as indicating that the point estimates in columns 2 and 3 (and 7 and 8) are statistically different from each other. It appears likely that the effect of the across-the-board increase in the child apprehension rate following the judicial inquiry had a larger effect in causally increasing IA use following the age of majority for those taken into care as a result of that policy change. Although we can only speculate, the increase following the judicial inquiry “flooding” the number of foster care spots available and thereby reducing the quality of service provision, and/or the associated reduction of an aspect of caseworkers’ discretion (i.e., the bluntness of across-the-board increases) may be behind this substantial increase of approximately eight or nine months of IA use in the year as a result of being brought into care.10 In practice, much of this likely stems from a substantial decrease in the proportion receiving any IA as discussed below and seen in Figure 6. Assuming the instrumental variables identification is valid, it appears that the LATE estimates for these two sources of exogenous variation are different, and that alternative margins to generating variations in the probability of coming into care have different impacts. However, if the time trend is not adequate, then the period (judicial inquiry) instrument might be picking up some of the “tightening” of IA that occurred (mostly following 2001) and would likely be biased up as a result. This would not affect the worker fixed effect instrument.

Table 6. Probit and Bivariate (Instrumental Variables) Probit Coefficients
 (1)(2)(3)(4)(5)(6)(7)(8)(9)(10)
 ProbitIVProbitIVProbitIVProbitIVProbitProbitIVProbitIVProbitIVProbitIVProbit
     P1, P2,    P1, P2,
    P1, P2,FE1,   P1, P2,FE1,
Instruments P1, P2Wkr FEWkr FEFE2, FE3 P1, P2Wkr FEWkr FEFE2, FE3
NOTES
  1. Heteroscedasticity robust standard errors, clustered on worker-year, are in brackets. P-values are in parentheses:

  2. ***p < 0.01, **p < 0.05, *p < 0.1.

  3. All regressions also include a linear control for age at first contact measured in months. Instruments: P1 = Period 1, P2 = Period 2, Wkr FE = Worker Fixed Effects; FE1, FE2, and FE3 are the interactions between the period dummies and the worker fixed effects.

Panel A: High School Graduate before 20th Birthday
InCare−0.498***−1.050*−0.710**−0.712**−0.676**−0.619***−1.069*−0.672**−0.762**−0,729**
 [0.039][0.651][0.354][0.310][0.320][0.037][0.645][0.343][0.302][0,310]
Wald Exog Test 0.670.370.480.31 0.460.020.230.13
p-value χ2(1) (0.4127)(0.5419)(0.4895)(0.5778) (0.4982)(0.8747)(0.6329)(0.7218)
Panel B: Any Income Assistance While Age 19
InCare0. 576***2.338***0.706*0.925***0.941***0.660***2.332***0.5141.017***1.024***
 [0.032][0.411][0.387][0.350][0.355][0.029][0.405][0.365][0.338][0.341]
Wald Exog Test 9.510.230.971.04 8.930.161.091.12
p-value χ2(1) (0.0020)(0.6317)(0.3236)(0.3089) (0.0028)(0.6877)(0.2963)(0.2897)
Panel C: Convicted While Age 19 or 20
InCare0.218***0.780−0.879*−0.734−0.8110.444***0.597−0.751−0.529−0.624
 [0.048][1.362][0.530][0.510][0.510][0.042][1.297][0.509][0.486][0.497]
Wald Exog Test 0.163.643.163.62 0.014.803.694.17
p-value χ2(1) (0.6871)(0.0563)(0.0754)(0.0570) (0.9060)(0.0295)(0.0547)(0.0412)
3rd-order polyYesYes YesYesYesYesYesYesYes
28 control varsYesYesYesYesYes     
11-month varsYesYesYesYesYesYesYesYesYesYes
Observations20727207272072720727207272072720727207272072720727

Table 5 has a similar layout to the previous two tables, but the incidence of a criminal conviction while 19 or 20 years of age is the dependent variable. Columns 1 and 6, displaying the OLS output, indicate that those taken into care are a few percentage points more likely to be incarcerated than those not taken into care. Given that a conviction is a relatively rare event, as seen in Table 1, these differences are appreciable. In columns 2 and 7, using the indicators resulting from the jump in the apprehension rate as a result of the judicial inquiry, the point estimate is seen to be substantially larger than that for OLS. Interestingly, the point estimate is not statistically significant when judged relative to the estimate's standard error and the resultant t-statistic, but the Anderson-Rubin statistic, which may be argued to have better statistical properties in this context, suggests that the instrumental variables point estimate is different from zero with p-values of about 4% and 7%. Perhaps more surprisingly, the J-statistic suggests that the two period indicators provide different point estimates; the impacts of a step up and a step down in child apprehension rates are not mirror images of each other. This makes some sense if, for example, one believes that the stock and quality of foster care placements is an important factor in the outcomes of youth taken into care. Following the step up the quality would deteriorate, since the supply of potential foster care placement spots would take time to adjust, but the step down is associated with an increase in quality (i.e., less demand on the existing number of spots).

In dramatic contrast to the results just observed, when the worker fixed effect is employed on its own, the point estimate is negative as opposed to positive! Although it is not statistically significant at conventional levels, it is seen to be statistically significant at a level only slightly larger than 10% in the Anderson-Rubin test (especially in column 3), and the p-value on the coefficient's t-statistic is 0.12 in column 3, and 0.18 in column 8. This suggests that there is a substantial probability that the true coefficient estimate is below zero. Moreover, the column 3 point estimate does appear to be statistically significantly less than the OLS point estimate, which might be a more important comparison than zero is.

When the two sources of exogenous variation are employed simultaneously, in columns 4 and 9, the point estimate is negative and not statistically different from zero according to the t-statistic, but statistically significant according to the Anderson-Rubin test. Further, and as expected given the results to this point, the J-statistic suggests that the instruments have statistically significantly different estimates. That is, the across-the-board changes in the child apprehension rate, as well as caseworker discretion, appear to have different impacts on conviction rates later in life. While further work will be required to confirm these results, a plausible interpretation is that the across-the-board changes in the child apprehension rate subsequent to the judicial inquiry had a causal impact increasing the rate of conviction for those taken into care as a result of the policy change. In stark contrast, the administrative discretion exercised by social workers appears to beneficially reduce the subsequent rate of conviction for those taken into care by caseworkers with higher propensities to take children into care. This is a remarkable finding and a very strong illustration of the point that different sources of exogenous variations are estimating different LATE parameters. However, these findings must be viewed as preliminary. Further analysis of these or similar data by others (since independent replication is the hallmark of good science and public policy, especially for such important policy issues) and analyses of other age and sex groups are required to confirm (or refute) the results and their interpretation.

5.3. Sensitivity Tests

Table 6 presents a compact version of the regressions presented in Tables 3 through 5, but employing probit and instrumental variables probit specifications, since we have mostly indicator dependent variables. The one exception is months of IA while aged 19, which for this sensitivity test we specify as one if the person receives any IA in the year before their 20th birthday, and zero otherwise. Note that the results presented throughout the table are coefficients, not marginal effects, since the latter are unavailable for the instrumental variables probit specifications.11 Although not presented, the probit marginal effects (which are available) appear to be quite similar to the OLS results in the earlier tables. For example, the coefficient from the OLS regression in column 1 of Table 3 is −0.13, and the marginal effect at the mean of the probit coefficient in column 1, panel A, of Table 6 is −0.14.

For panel B in Table 6 the dependent variable is defined differently from that in Table 4, but the basic pattern of statistical significance is similar. In panel C the patterns are again quite similar – even the sign reversal between, for example, columns 2 and 3. Exogeneity tests have the null hypothesis that the correlation coefficient of the bivariate normal distribution (or, equivalently, a non-linear transformation of that coefficient) is equal to zero. Comparing the p-values from these tests to those from the Anderson-Rubin exogeneity test presented in Tables 3 through 5, we can see that the Anderson-Rubin is more likely to reject exogeneity, particularly for high school graduation. While the source of the differences in the conclusions from these tests is not entirely clear, we suspect it may result from lower power (less precise estimates) and more restrictive functional form assumptions for the probit.

Although we ran a number of versions of the model and determined that none of the polynomial specifications interact with the worker fixed effect instrument, this specification issue is clearly crucial for identification related to the instruments associated with the time periods. Our preferred model employs a third-order polynomial, since when we tested down from a fifth-order specification, all the coefficients from the third-order polynomial were statistically significant, whereas few were so for the fifth. Of course, there is always the danger of having too flexible a specification – one that overfits the data. Therefore, a second sensitivity test, presented in Table A2, explores the impact of different specifications for the time trend (the Poly vector). This model focuses on the issue at hand and does not include the worker fixed effect instrument or any control variables. Since the control variables are omitted, it is estimated on the sample that includes those not matched to data from other ministries. When we look across rows, it is clear that the time trend, as expected, has some effect on the parameter estimates but they are qualitatively similar. The most important difference is in panel A, where the magnitude of the coefficient reduces and loses statistical significance in moving from a cubic to a linear specification. Of course, even with the cubic specification the coefficient is on the margin of statistical significance, since it is not statistically significant at the 10% level in equation (2) or equation (7) in Table 3, where the point estimate is similar but the standard errors are larger than those in Table 6. Overall, given the size of the standard errors of the coefficients on the InCare variable, we consider the estimates to be relatively insensitive to the specification of the time trend.

6. Conclusion

  1. Top of page
  2. Abstract
  3. 1. Introduction
  4. 2. Data
  5. 3. Institutional Context and Resulting Empirical Strategy
  6. 4. Descriptive Statistics
  7. 5. Instrumental Variables Estimates
  8. 6. Conclusion
  9. Appendix
  10. References

We view this paper as only scratching the surface with respect to the potential for empirical research that could be of benefit to policy-making for foster care. Clearly, the results found here apply only to 16-, 17-, and 18-year-old male youth, and it would be very interesting to undertake similar analyses for different demographic groups were the data to be made available. It would also be valuable to extend the analysis to other dependent variables, particularly those associated with health outcomes, and to look at related aspects of being taken into care, such as the duration away from the family. Given the importance of the policy issue, in addition to extensions independent replication would also be of great value to validate these findings.

Overall, the background research cited shows clearly that those taken into care have quite poor outcomes, but we are interested in more subtle effects – the causal impacts of being taken into care for those on the margin of being apprehended. We observe that the impact on some outcomes under study, assuming that both types of instruments are taken to be credible, varies according to the source of exogenous variation used to identify the causal impact. Aside from the substantive findings, this is a useful example of heterogeneous treatment effects where alternative instrumental variables sweep out effects that are statistically different from each other – that is, they estimate different LATE parameters (Heckman, Urzua, and Vytlacil 2006). In effect, there are different margins of being taken into care as demonstrated by the lack of correlation between the instruments in predicting being taken into care in the first stage of two-stage least squares.

These data suggest that high school graduation becomes less likely and/or delayed as a result of both sources of exogenous variation, that IA use increases dramatically more as a result of the across-the-board increase in the child apprehension rate, and that the causal impacts on the probability of a criminal conviction likely go in different directions as a result of the treatments. The across-the-board increase appears to causally increase conviction rates for those marginal youth taken into care as a result of the abrupt increase in apprehension rates. In contrast, in the context of within-year comparisons resulting from being taken into care by caseworkers with different apprehension probabilities, conviction rates (statistically insignificantly) decreased for those affected children. Of course, the interpretation of these results needs more information. It might not be the act of being taken into care that is driving much of the observed difference; rather, it may follow from the ability of the foster care system to deal with a dramatic and sharp change in the number of children flowing into care.

Children at risk is clearly an important area of study affecting many of the most vulnerable individuals in our population, and the magnitudes of the observed coefficients are non-trivial, suggesting that the decisions of the child welfare system matter on the margin. Many very interesting technical/econometric challenges are also raised in the analysis. This looks like an area in which much fruitful future work could be undertaken not only in BC but across Canada.

Appendix

  1. Top of page
  2. Abstract
  3. 1. Introduction
  4. 2. Data
  5. 3. Institutional Context and Resulting Empirical Strategy
  6. 4. Descriptive Statistics
  7. 5. Instrumental Variables Estimates
  8. 6. Conclusion
  9. Appendix
  10. References
Table A1. Descriptive Statistics by Period
 Period 1Period 2Period 3
NOTES
  1. Means, with standard errors in parentheses. Each health variable is derived from the ICD9 codes on physician billing records and counts the number of days in which the subject had one of the named diagnoses. Where these classifications overlap, the larger group reports is reported. The three variables from Corrections indicate any contact, incarceration, and incarceration for a violent offence, in the year prior to contact with child protection. Of the four variables reflecting income assistance, two variables measure receipt of benefits through the child in the home of a relative program (CIHR), and two indicate receipt of income assistance benefits through their family. In each case the first counts the number of months in the three months prior to contact, and the second counts the number of months in the 22 months prior to that. Aboriginal is an indicator for self-declared aboriginal status in the education system, and there are 10 dummy variables indicating the mean of self-declared language spoken at home.

Health (number of days with visit related to named diagnosis)
Substance Abuse0.0630.0730.085
 (0.598)(0.548)(0.803)
Psychoses0.0830.0790.130
 (1.190)(1.139)(1.550)
Disturb. conduct0.0790.0930.103
 (0.701)(0.805)(0.687)
Adolescent problem0.0690.0860.086
 (0.710)(1.069)(0.972)
Hyperactivity0.0900.1440.165
 (0.910)(0.986)(1.122)
Devel. Delay0.0210.0140.015
 (0.448)(0.332)(0.210)
Neuroses0.4140.4300.494
 (2.315)(1.975)(2.295)
STD0.0050.0050.004
 (0.097)(0.087)(0.076)
Maltreatment0.0220.0140.018
 (0.199)(0.127)(0.223)
Health Other8.3417.7577.274
 (9.247)(8.841)(7.858)
Contact with Corrections in Previous Year 
Incarceration0.0420.0380.026
 (0.200)(0.190)(0.158)
Violent Offence0.0170.0230.016
 (0.130)(0.148)(0.124)
Any Contact0.1880.1640.129
 (0.391)(0.370)(0.336)
Income Assistance (IA)   
CIHR in past 3 months0.0720.0780.072
 (0.425)(0.449)(0.435)
CIHR in past 24 months0.3790.4370.434
 (2.219)(2.544)(2.584)
Months of IA in past0.7760.7280.656
3 months(1.250)(1.220)(1.191)
Months of IA in past5.0525.5604.863
24 months(8.030)(8.273)(8.020)
Demographic (aboriginal status and minority language spoken at home)
Aboriginal0.1640.2010.233
 (0.370)(0.401)(0.423)
Chinese0.0100.0150.013
 (0.101)(0.123)(0.114)
Punjabi0.0130.0120.012
 (0.112)(0.110)(0.110)
Vietnamese0.0060.0120.014
 (0.080)(0.108)(0.118)
Spanish0.0120.0140.013
 (0.110)(0.117)(0.111)
Tagalog0.0030.0070.008
 (0.055)(0.083)(0.092)
Hindi0.0050.0060.007
 (0.068)(0.076)(0.086)
Persian0.0030.0040.005
 (0.057)(0.061)(0.073)
French0.0050.0090.008
 (0.072)(0.093)(0.091)
Portuguese0.0030.0060.010
 (0.050)(0.077)(0.097)
Other, Non-English0.0260.0430.046
 (0.158)(0.203)(0.210)
Table A2. Sensitivity Test for Specification of Time Trend
 (1)(2)(3)(4)
NOTES
  1. Heteroscedasticity robust standard errors, clustered on worker-year, are in brackets.

  2. a p < 0.01, ** p < 0.05, * p < 0.1

Order of   0 (No time
time trend5th3rd1stcontrol
polynomial(Quintic)(Cubic)(Linear)variable)
Panel A: Graduate by 20th Birthday
InCare−0.292**−0.278**−0.088−0.126
 [0.167][0.142][0.087][0.089]
Panel B: Any Income Assistance While Age 19
InCare5.162a7.648a5.043a6.183a
 [1.546][1.424][0.805][0.872]
Panel C: Probability of Conviction with Age 19 or 20
InCare0.1790.0620.0450.060
 [0.108][0.091][0.056][0.057]
Observations24694246942469424694
  1. 1

    Foster care levels within a jurisdiction can vary appreciably across relatively short time intervals as various policy changes come into effect. For example, in the US between 1999 and 2003 there was at least a 30% increase in the number of children in care in Hawaii, West Virginia, Idaho, Wyoming, and South Dakota, while there was simultaneously at least a 30% decrease in Illinois, Delaware, and New York (AFCARS 2006; US Bureau of the Census 2007). Evidence of fluctuations in BC will be presented below. There appears to be no consistent and widespread view of the appropriate thresholds and/or proportions of children to take into foster care. For a broad overview of child welfare issues see Kamerman, Phipps, and Ben-Arieh (2010). Relatedly, inequality among youth's households is seen to have a very large “permanent” component by Burton and Phipps (2009), who observe considerable “stickiness” in children's position in the income distribution.

  2. 2
  3. 3

    Foster care expenditure is larger than the budgets of each of Labour; Small Business, Technology and Economic Development; Energy, Mines and Petroleum Resources; Aboriginal Relations and Reconciliation; Finance; Agriculture and Lands; Healthy Living and Sport; Tourism, Culture and the Arts; and Environment; and Community and Rural Development.

  4. 4

    In BC, children may be removed under the authority of the Child, Family and Community Service Act. If the removal is done without a court order, the social worker must present in court within seven days. While the decision to place a child in foster care is made by a judge, it is strongly influenced by the recommendation of the social worker (see, e.g., Saunders and Goddard 1998, 30; they report, “Ultimately, decisions rest with workers”).

  5. 5

    This definition of placement in foster care is close, but not identical, to the official Ministry definition. For the period for which we had access to official “end of month” lists of children in foster care, we found that 85% of child services files that opened were on the list. An additional 4% had entered care during the month but were not on the official list because they had left care before the month end. The remaining 11% had a legal status that did not meet the official definition of being in care, but we view it as substantively similar.

  6. 6

    Access to these data was obtained under the authority of the Representative for Children and Youth Act. All work was done on a secure machine in the controlled premises of the Representative for Children and Youth for BC; only aggregate data were released by the representative's office and only aggregate data were observed by the academic co-authors. Significant effort was put into preparing the data for analysis to ensure that the matching across the various data sources was appropriate and that the administrative data were appropriately “cleaned” for the analysis. We believe that the final data for analysis are reliable.

  7. 7

    Quoted in a press release entitled “B.C. Child Protection System Overhauled,” issued by the BC Government Communications Office, 23 September 1996, accessed 18 March 2008, http://www2.news.gov.bc.ca/archive/pre2001/1996/0341.asp. Discussions with people who had been Ministry employees at the time confirm explicit direction to take more children into care, backed up by high-profile suspensions of social workers who did not do so (see Foster and Wharf 2008).

  8. 8

    It is also worth considering the types of foster care placement provided to these youth. Although we have no data on this and there is little that is publicly available for BC, Rutman et al. (2005, 15) report: “Of the youth who were under 19 at the time of the interview (n = 20), 25% were living with foster parents, 10% were living in a group home and 10% were living with a family member of some type. The remaining 11 participants reported a variety of living arrangements such as living at a friend's house, in low-income housing, at youth housing, or with a roommate.” They also report that changing living arrangements is common.

  9. 9

    BC Progress Board. Third Annual BC Progress Board Benchmarking Report Volume II – Internal Performance Review: Appendix D RPI17-SI: Percent of Population 0–64 years Receiving Basic BC Benefits, accessed 18 March 2008, www.bcprogressboard.com/2003Report/V2Appdf

  10. 10

    The administrative operation of social services in BC may explain a large part of this causal impact, since it facilitated those who were in foster care near the age of majority in transitioning to income assistance.

  11. 11

    Unfortunately, we no longer have access to the data and did not initially calculate marginal effects for the instrumental variables probits. We therefore show coefficients throughout the table for consistency. The presentation varies compared with the earlier tables, but the conclusions do not.

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  1. Top of page
  2. Abstract
  3. 1. Introduction
  4. 2. Data
  5. 3. Institutional Context and Resulting Empirical Strategy
  6. 4. Descriptive Statistics
  7. 5. Instrumental Variables Estimates
  8. 6. Conclusion
  9. Appendix
  10. References
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