Long-term Direct and Intra-Household Spillover Effects of a Conditional Cash Transfer Program: Experimental Evidence from Colombia

In 2005, the city of Bogotá, Colombia, in collaboration with researchers at Fedesarrollo (Colombia) and JPAL (US), implemented a conditional cash transfer (CCT) program aimed at reducing dropout rates in secondary education among low-income students (In Colombia, secondary education includes grades 6-11). In this proposal, we discuss the estimation strategy of the long-term effects of the program on a rich array of education and labor market outcomes of the beneficiaries and their family members. One important objective of the study is the estimation of spillover effects on non-beneficiary minors living in a household with a treated sibling. We rely on a randomized control trial that allocated the program at random to CHILDREN among a set of families with eligible students.

The intervention took place in 2005, and was implemented in two of the 12 localities of Bogotá, Colombia, under the Conditional Subsidies for School Attendance Program (``Subsidios Condicionados a la Asistencia Escolar'', in Spanish) designed by the city's Secretary of Education. The program evaluated alternative delivery methods of conditional cash transfers by assigning students randomly to three different treatment arms (Barrera-Osorio et al.,2011, 2019):

1) A ``BASIC'' conditional cash transfer in which participant families received 30,000 pesos every two months (around \$15 USD) if the student attended 80 percent of the classes in that month.

2) A ``SAVINGS TREATMENT'' that vary the timing of the transfer. Households in this treatment arm received two-thirds of the amount (20,000 COP or roughly \$10 USD) every two months, and the remaining third was kept in a bank account. The saved funds were available at the beginning of the next academic year. A total of 100,000 (\$50 USD) was given if the students fully met the requirements.

3) A ``TERTIARY TREATMENT'' that modified the conditionality requirement of the transfer. Students received two-thirds of the original bi-monthly sum (20,000 COP), but upon high school graduation they received a total amount of 600,000 COP ($300 USD), which was given immediately if the student enrolled in a tertiary education program or after a year if the student did not enrol.

The saving and basic treatment transfer provided roughly the same amount of money (e.g., they are income-neutral); the transfer in the tertiary experiment was larger than in the first two.

The program was highly advertised in both localities during January and February 2005, and registration took place in a 15-day window at the end of February and the beginning of March 2005. Participating families were not aware of the existence of multiple treatments. The program was advertised as one that provided incentives to participate in school.

2005-07-01

2010-12-31

In the case of treated/control children we plan to analyze:
1) The probability of formal employment;
2) Wages of those who work formally;
3) Type of firm;
4) Access to credit.


In the case of siblings of treated/control children in the experimental sample, we plan to analyze:

1) The probability of graduating from high school;
2) Test scores at the moment of graduation;
3) Probability of college enrolment;
4) Probability of college graduation;
5) Probability of formal employment;
6) Wages in case they work formally;
7) Type of firm;
8) Access to credit.

Finally, in the case of parents of treated/control children we will analyse:

1) Probability of formal employment;
2) Wages in case they work formally;
3) Type of firm;
4) Access to credit, with emphasis on credit for car and house, as a measure of assets. Also, general direct credit and credit cards.

- Probability of formal employment: We merge the list beneficiaries to the universe of formal workers using national identification numbers. We define a dummy variable that takes the value of one if the individual merges and 0 otherwise. This dummy will be considered as our outcome denoting the probability of having a formal employment.

- Wages: We are able to observe the wage for those workers who work formally. We plan to follow Angrist, Bettinger, Kremer (2006) in case we have differences in the likelihood of formal employment (i.e. differences in having the salary observed), and estimate a bounded effect.

- Type of firms: We estimate firm-wage premiums using a linear decomposition model (See Abowd, Kramarz, Margolis (1999)) and the size of firms to investigate the type of firms in which our individuals of analysis work.


- Access to credit: We merge the registry data to the universe of credit loans. We define access to credit as a dummy variable that takes the value of one if the individual merges in the credit data set, and zero if not.

- Test score data: We use the national high-school exit exam as a measure of test scores. Every single student in Colombia who wishes to graduate from secondary education has to take this exam.

- College enrollment and graduation: We merge the beneficiary data to the universe of students in tertiary education in Colombia. We are able to identify those who registered (at least once) and those who actually graduated.

The experiment took place in San Cristóbal and Suba, two localities (out of 12) in Bogotá with high prevalence of low-income households. Treatment assignment was implemented differently in each locality. In San Cristóbal, eligible participants from grade six to 11 were randomized into the control group, the basic treatment, and the savings treatment. In Suba students in grades nine to 11 were randomly assigned to either the control group or the tertiary treatment. Thus, it is not possible to compare the tertiary treatment with the basic or the savings treatment.

Eligibility into the program required that: 1) at least one parent was present at the moment of registration; 2) students had finished fifth grade for the basic and saving treatment, and eighth grade for the tertiary treatment; 3) students were enrolled but had not graduated; and 4) the family was classified in the two lowest categories of Colombia's poverty index created with SISBEN's information. A total of 17,309 students, from 12,674 households, registered: 10,947 in San Cristóbal and 6,362 in Suba. In terms of households, 8,812 registered only 1 individual; 3,190 registered 2 individuals; 580 registered 3 individuals; 83 households registered 4; and 9 household registered 5 individuals.

The random allocation of benefit provides two sources of exogenous variation in treatment assignment: variation across treated and control children which allows to identify the direct treatment effects of the CCT among treated students; and variation of treated and control children within the same household which allows us to identify intra-household spillovers. More specifically, the nature of the randomization allows us to consistently estimate three effects. First, the effect on children who were directly targeted by the program, by comparing outcomes of beneficiaries and non-beneficiaries of the transfer (“direct effects”). Second, the effect on non-treated siblings, by contrasting outcomes of untreated siblings in a household with beneficiaries versus untreated siblings in a household without beneficiaries (“sibling effects”). Third, the indirect effect on parents of eligible children, by comparing outcomes of parents with children who were randomized to receive the transfer with those of parents of eligible children all of whom were randomized to the control group (“parent effects”).

Two studies found positive treatment effects of this CCT program on students' academic outcomes. Barrera-Osorio, Bertrand, Linden, and Perez-Calle (2011) show that, after one year of the program, the savings and tertiary treatments increased enrollment remarkably in secondary and tertiary education. Barrera-Osorio, Linden, and Saavedra (2019) analyse longer-term effects on tertiary education after 8-12 years since the program implementation. They find that the savings treatment does better at inducing students to enroll in better tertiary education programs which was unexpected because the program did not condition on tertiary enrollment.

Not available

The lottery was done publicly under strict surveillance and the lists of beneficiaries were printed immediately. The randomization was stratified on locality, type of school, grade, and gender.

The program's experimental design incorporated a randomization at the INDIVIDUAL(children) level. Families first proposed how many children to enrol in the program. The only requirement was that children had to be in grades 6 to 11. Students (not households) were randomized into one of the three treatment arms or to control. Because of the eligibility requirement, participant households could have received either full treatment (all the children within the household were randomized into treatment), partial treatment (some children within the household were treated), or no treatment at all (pure control households).

No

- Locality 1 (Suba): 6,362 students for models using only eligible students.
- Locality 1 (Suba): 4,571 households for models using siblings/parents of eligible students.

- Locality 2 (San Cristóbal): 10,947 number of students for models using only eligible students.
- Locality 2 (San Cristóbal): 7,923 households for models using siblings/parents of eligible students.

Because we are merging the data with secondary sources, we expect to have some degree of attrition. Details about how we deal with this are presented in the pre-analysis plan that we attach.

- Locality 1 (Suba): 6,362 students for models using only eligible students. - Locality 1 (Suba): 5,012 number of siblings for models using siblings of eligible students. - Locality 1 (Suba): 9,181 number of parents for models using parents of eligible students. - Locality 2 (San Cristóbal): 10,947 number of students for models using only eligible students. - Locality 2 (San Cristóbal): 7,703 number of siblings for models using siblings of eligible students. - Locality 2 (San Cristóbal): 12,969 number of parents for models using parents of eligible students. Because we are merging the data with secondary sources, we expect to have some degree of attrition. Details about how we deal with this are presented in the pre-analysis plan that we attach.

For ELIGIBLE STUDENTS:
- Arm 1 (Suba, Basic): treatment (1,717), control (2,101) students for models using only eligible students.
- Arm 2 (Suba, Tertiary): treatment (1,140), control (1,404) students for models using only eligible students.
- Arm 3 (San Cristóbal, Basic): treatment (3,437), control (7,510) students for models using only eligible students.
- Arm 4 (San Cristóbal, Savings): treatment (3,438), control (7,509) students for models using only eligible students.



For SIBLINGS:
- Arm 1 (Suba, Basic): treatment (1,591), control (3.438) siblings for models using siblings of eligible students.
- Arm 2 (Suba, Tertiary): treatment (866), control (2,420) siblings for models using siblings of eligible students.
- Arm 3 (San Cristóbal, Basic): treatment (2,928), control (9,573) siblings for models using siblings of eligible students.
- Arm 4 (San Cristóbal, Savings): treatment (2,901), control (9,599) siblings for models using siblings of eligible students.


For PARENTS:
- Arm 1 (Suba, Basic): treatment (2,656), control (2,819) parents for models using parents of eligible students.
- Arm 2 (Suba, Tertiary): treatment (1,788), control (1,920) parents for models using parents of eligible students.
- Arm 3 (San Cristóbal, Basic): treatment (5,029), control (7,940) parents for models using parents of eligible students.
- Arm 4 (San Cristóbal, Savings): treatment (5,081), control (7,888) parents for models using parents of eligible students.

NOTES:
1) There are individuals that are are used as a control for two treatment arms. Therefore, the sum of observations by treatment arms does not necessarily match the totals displayed in the previous sections.

2) Even though we report the samples sizes by locality and treatment arm, we plan in many of our specifications to pool the data when locality or intervention variation is not relevant for the estimation.

3) Because we are merging the data with secondary sources, we expect to have some degree of attrition. Details about how we deal with this are presented in the pre-analysis plan that we attach.

0.02 standard deviations