It has been well established that education is key to economic development and social welfare. Investments in education yield returns in poverty reduction, improved health outcomes, and economic growth (UNESCO, 2007; Hannum & Buchmann, 2004; Herz & Sperling, 2003). In addition, increased access to education contributes to increased political participation and more equitable sharing of economic and political power (Birdsall, 1999). Education for girls is particularly critical, as improvements in the infant mortality rate, child nutrition, and school enrollment are closely associated with maternal education (Birdsall, Levine, & Ibrahim, 2005; Herz & Sperling, 2003; World Bank, 2008). Yet, more than 100 million primary school aged children are not in school, and of those that are, many—49 percent in Africa, for example—do not complete primary school (Birdsall, Levine, & Ibrahim, 2005). Low educational attainment—or the inability of students to complete their primary and secondary school education--in the developing world is the combined result of children who do not enroll, children who do not progress, and children who drop out (World Bank, 2004). Children may not enroll or complete their schooling for a number of reasons. Research indicates that there are economic reasons and other structural forces that present barriers. For example, in some countries such as India, Mali, and Burkina Faso, school enrollment is very low, due to issues such as the cost of schooling (both direct and opportunity costs), poor school infrastructure, teacher shortages, and safety and sanitation problems (Birdsall, Levine, & Ibrahim, 2005). In others, such as many Latin American countries, enrollment may be nearly universal, but retention and completion may be quite low (ibid) for a myriad of reasons, including those mentioned above, as well as poor health of students or members of their households (Glewwe & Miguel, 2008; UNESCO, 2007), teacher absenteeism or malfeasance (World Bank, 2004), and curricula that do not match students' needs (Glewwe, Kremer, & Moulin, forthcoming). Value systems held within the country may also diminish the importance of enrolling children in school (e.g., Brembeck, 1962). Furthermore, developing nations face significant enrollment and completion disparities between segments of the population such as rich and poor, boys and girls, urban and rural dwellers, and combinations of these factors (Birdsall, Levine, & Ibrahim, 2005). For example, in India, the gender gap (favoring boys) for children from the richest households is only 2.5 percent, while disparity for children from the poorest households is 24 percent (Filmer, 1999 as cited in Birdsall, Levine, & Ibrahim 2005). In many African nations, rural rates of enrollment lag far behind the very modest national rates, particularly for rural girls, whose rate of enrollment is less than 15 percent in several countries (ibid). In addition, ethno-linguistic diversity, disabilities, and conflict situations in fragile states create further barriers for school participation in developing nations (Birdsall, Levine, & Ibrahim 2005). In light of compelling evidence that links expanded education systems and socioeconomic development while highlighting the importance of policies to offset inequality in access (UNESCO, 2007), and spurred by the donor community and such initiatives as the Millennium Development Goals and Education for All, governments in developing nations are, to varying degrees, making efforts to increase school enrollment and equity. Building new schools to increase ease of access in remote areas is one intervention used in developing nations (e.g., Filmer, 2004). Other efforts include improving school infrastructure and safety and abolishing school fees, as well as implementing targeted policies to reach the most marginalized children. Such policies include school feeding programs, flexible schooling models for working children, school-based health interventions, and various types of financial subsidies and conditional cash transfer systems. For example, several Latin American governments and non-governmental partners have experimented with programs that transfer money directly to disadvantaged households—such as in rural, indigenous, migrant, or slum communities—in exchange for children's school enrollment and attendance (UNESCO, 2007). In Asia, stipend programs encourage the transition of girls to secondary school (ibid). Evaluations of some of these recent policies and programs to increase school enrollment and persistence in developing nations include a number of randomized field trials and rigorous quasi-experimental studies. Randomized experiments evaluating conditional cash transfer programs in Latin America include the seminal Progresa school subsidies experiment in Mexico, which gave educational grants to poor mothers of children enrolled in school with good attendance. Communities were randomly assigned to intervention or control conditions and positive impacts for school enrollment and other factors were demonstrated (Schultz, 2004). Similarly, in Ecuador, a lottery provided cash vouchers to randomly selected families in exchange for enrolling their children in school; control families were placed in a “wait-list” condition until the study was completed. The early results were positive, increasing school enrollment by 10 percent and reducing child labor by 17 percent (Lopez-Calva, 2008). In addition, Filmer & Schady (2006) found that a scholarship program for girls in Cambodia making the transition from primary to secondary school had a large, positive effect on enrollment and attendance. Randomized trials of school-based health interventions include a school feeding program in rural Peru, in which schools were randomized to implement a high-quality, ready-to-eat breakfast program or to a control group, with positive results for school enrollment and other outcomes (Cueto & Chinen, 2008). Glewwe & Miguel (2008) review randomized evaluations of school-based health interventions such as that of Miguel and Krema (2004), which found that absenteeism in Kenyan schools in which students received deworming treatment was 25 percent lower than in comparison schools, and that deworming increased schooling by 0.14 years. Recent randomized evaluations of other types of programs aimed at increasing enrollment and completion include that of Glewwe, Kremer, and Moulin (2007), who found that providing textbooks to students in randomly selected rural primary schools in Kenya had no effect on dropout or repetition rate. The Millennium Challenge Corporation funded a regression discontinuity study to assess the impact of school construction and other associated interventions on female student school enrollment in 132 communities in Burkina Faso versus 161 communities not selected for “treatment”, finding positive results on enrollment (Levy et al. 2009). To our knowledge, a systematic review of randomized controlled trials and quasi-experiments of school enrollment and persistence strategies in developing nations has not yet been reported. By systematically gathering and analyzing rigorous research about the program effects of primary and secondary school enrollment and secondary school completion policies, our review will provide key evidence to inform the next wave of development efforts in this area. For this project, we will be collecting studies that respond to the question: What are the documented impacts of school enrollment policies and programs in developing nations (see definition below) on enrollment and persistence outcomes (e.g., primary and secondary school enrollment, attendance, retention, primary to secondary transition, and secondary school completion), and on learning outcomes (e.g., test scores, grades, etc.)? The Burkina Faso evaluation conducted by Mathematica for the Millennium Challenge Corporation (Levy, et al. 2009) is an example of an evaluation that would be included in our review. Using regression discontinuity design, the study compares the results, at the village level, on girls' school enrollment for those villages that received new school construction and other interventions (via the BRIGHT program) versus those that did not. Results indicate that girls' enrollment 16–19% in the experimental villages. The background section included references to other examples of evaluations that would be eligible for our review. For example, the Ecuador lottery study that randomly assigned families to receive cash vouchers in exchange for enrolling their children in school would be included (Lopez-Calva, 2008). One study that would not be included in our review is that of Bobonis, Miguel, and Sharma (2006), who evaluated a health program that provided iron supplementation and deworming medicine to preschool age children in poor urban areas of Delhi. Although this was a randomized evaluation in a developing nation that reported effects on school absenteeism, we would not include it in our review because it does not evaluate a K-12 strategy, but focuses on the preschool population. Another example of a study that would not be included in our review was conducted by Lockheed and her colleagues (1986) in Thailand. They studied the impact of providing textbooks to Thai students. Although there was a question of whether they used a truly equated comparison group, the study was nonetheless excluded because it did not include any outcome of enrolment, attendance, dropout, or persistence, but exclusively focused on academic achievement. The databases in Appendix A can be somewhat idiosyncratic. Thus, we believe the best strategy is to conduct a broad search of the available databases that errs on the side of sensitivity rather than specificity. In other words, we would rather get many titles and abstracts to sift through rather than potentially miss relevant citations because our search terms were drawn too narrowly. We will use two different search strategies for these databases, depending on their focus. If the database is focused on education (such as ERIC), we will use broad searches that identify evaluation studies conducted in developing nations. To do this, we will use the following keywords to find experimental and quasi-experimental outcome studies: “random,” “experiment,” “control,” “evaluate,” “trial,” “impact,” “effect,” “comparison group,” “match,” “discontinuity,” “propensity” and “outcome.” Our plan is to use truncated versions of these words; for example, we will use “experiment*” to capture titles and abstracts with the word “experiment,” “experimental,” “experimenting,” “experimenter,” and “experiments.” Second, we will combine those keywords with ones that focus the search on developing nations, such as the use of terms like “developing,” “third world,” and “impoverished” with “nation,” “country,” or “region.” In addition, we will use the names of specific developing nations, such as India, Mexico, etc., and the names of regions, such as Africa, Latin America, and Asia. If there is a geographic descriptor for country or region, we will incorporate that into our search process. We will also include keywords that focus on the outcomes of interest including dropout, enrollment, enrolment, and attendance. Such searching is an iterative process and we will modify as we retrieve studies. This strategy may produce a number of false positives, but our experience is that examining the abstracts is not time consuming and researchers can go through them quite quickly. Wherever possible, we will limit our searches by a descriptor that indicates the grades that our review is targeting: K-12 (for example, selecting primary and secondary education, or elementary, middle, and high schools). This would have the advantage of screening out preschool and college age studies. If the database is not focused on education (e.g., Sociological Abstracts), the above strategy must then be supplemented by something that identifies educational research. In some databases, that will be a classification code; for example, in Sociological Abstracts (Sociofile), one can limit the abstracts to those dealing with “sociology of education”. But in many of others, there is no classification code. Whether classification codes exist or not, we will use truncated versions of keywords related to the educational outcomes of interest, such as dropout, attendance, and enrollment/enrolment to try to reduce the number of false positives. Again, if there are geographic descriptors for country or region, we will incorporate that into our search process. We recognize that specific search strategies may have to be developed for each database. What works in identifying potential studies in ERIC will not work in searching World Bank Documents. The appendices to our final review report will carefully document all keywords used for each database to permit replication. Search methods will identify a large number of citations and abstracts. Many of these will be easily excluded as not being relevant to the proposed review. In some cases, however, they will identify potentially eligible studies. The first and second authors will review all citations and determine if the cited study should proceed to a second screening, i.e., is a potentially relevant study. If so, the full text documents of those potentially eligible studies will be retrieved and screened by the first two authors before the study can be formally included in the review. Fortunately, with the advent of the Internet and full-text electronic journal access, we will be able to rapidly retrieve the reports to do a more thorough reading. When a full text report is received, we will scan it to ensure that it includes randomization or quasi-experimental equating of study subjects and includes at least one outcome of school enrollment or persistence. If the first two Investigators do not agree on the inclusion of a particular study, it will be excluded and documented in the final report. We have established a bibliographic reference database to maintain a log of all included and excluded studies. The log includes a field that allows the research team to document the reason for exclusion. We have designed a preliminary instrument to guide us in recording information from each study (see Appendix B). Although the instrument contains several open-ended items, these will be collapsed when appropriate into a smaller number of categories to permit further analysis. For example, items such as “how equating was performed” can be collapsed into three or four larger categories representing the most frequent responses (e.g., discontinuity, covariate matching, propensity score, post-hoc statistical matching) and an “other” category that captures all those responses that do not fit into the most common methods of equating in this set of studies. The instrument has items in the following areas: Study reports can be used to provide information about the publication and characteristics about the experiment and the context. For example, we will extract data about the type of publication the study was reported in and the setting in which the trial was conducted. If the documents provide information on the context in which the study takes place, we will also include it. These items will solicit detailed descriptions of the intervention and control condition, including the “dosage” of the treatment being implemented, and the number of participants assigned to each group. We anticipate that the evaluations in this review sample will be comprised of a single intervention and a single control group. When this is not the case, we will select the most policy relevant groups to compute our experimental versus control condition contrast. In most cases, it will be the groups that experience the greatest contrast between conditions, i.e., the most intensive intervention condition versus the least intensive control condition. We recognize the importance of documenting these decisions for full transparency. These items solicit detail about the type of participants in the trials, including information on the country where the study took place, the nationality of the participants, the age and school level targeted, gender, whether an urban or rural setting was involved, and the socioeconomic status of the students. For each eligible study (each eligible study will have, at minimum, one outcome measure of enrollment or persistence), we will extract information on reported outcomes including impacts on learning, health, child labor, costs, and equity. We will also code any other outputs or data on key “mechanisms” that would provide clues as to why the intervention did or did not have its intended impact. Note that investigators may publish several articles on the same study. Our unit of analysis is the individual evaluation and not the individual research article, and so it is reasonable to extract information from all documents to complete the coding instrument for one experiment. When reports on the same study contain conflicting information, we will employ a number of strategies, including contacting the original investigator(s) for resolution. Each study will be represented by a single effect size to prevent the analysis from being compromised by non-independence (multiple effect sizes from one study). Although some evaluations may report just a single outcome at one time interval, it is more likely that evaluation reports will include analyses at various time intervals and may use various constructs that reflect school enrollment and persistence. Therefore, decisions have to be made about what outcome will represent the effect size for that study. For this review, we will keep outcomes distinct. That is, we will analyze enrollment, school attendance, dropout, and other learning or non-educational (health, behavioral, etc.) outcomes separately. The Table provides an example of how four such outcomes would be reported. We do not know as of yet how such outcomes will be reported, i.e., will they be prevalence measures (percentage of groups that enroll or attend) or incidence measures (the mean rate for some outcome of interest, such as the mean number of days attended per student). If results are varied and include prevalence and incidence rates, we will discuss the best way to report these (combine or separate out) and make such decisions explicit in our review. We also propose to report three different analyses to handle the studies that report outcome data at various time intervals. As the Table indicates, we will report effect sizes at first follow-up (the first time interval reported), the middle effect (the middle time interval closest to the exact point between the first and longest), and the longest effect (the effect size for the longest follow-up period). If one time interval (e.g., 1 year) is reported in the study, it will be used in all three analyses. If two time intervals (e.g., 6 months, 1 year) are reported, the results will be averaged and the mean will be reported for the “middle effect.” If more than three time intervals are reported (e.g., 6, 12, 18 and 24 months), we will select the result that is closest to the exact middle. In this instance, the exact middle between 0–24 months is 12 months and would be reported as the middle. If regression-adjusted estimates are reported for the experimental versus control groups, we will rely on them for any quantitative synthesis since they theoretically reduce statistical “noise” that may have come from chance fluctuations or randomization violations (in the case of well implemented experiments) or uncontrolled variables (in the case of quasi-experiments). Some studies report analyses at multiple levels (e.g., Schultz, 2004), i.e., for schools or localities and for studies. Our rule is to capture this information separately, but to compute effect sizes for the analysis done at the level of assignment. So, for example, in Progresa, the randomization was done at the locality/community level, and so the main effect size will be that computed for treatment and control localities. We will code information, however, about the analyses done at the student, family or school level. Some studies also report effects at all grade levels (e.g., Schultz, 2004). This is very important to policy and practice decision-makers. The main effect will again be computed at the larger analysis level, so that if schools are assigned to groups, the effect size will be computed for all schools in treatment versus all schools in control. However, we will record subgroup effects such as breakdowns by grade and gender. To ensure that we achieve good coding reliability, we will have two of the co-authors read and record information from a random sample of reports (25%). We will assess coding reliability (i.e., inter-rater agreement) by using the percentage of agreement for each item, rather than reporting a global inter-rater reliability statistic. This will avoid inflating reliability measures with study characteristics that generally achieve perfect agreement (e.g. year of publication) with those that do not. Items with lower rates of agreement (less than 80%) will be investigated to determine the source for conflict. The authors will meet to resolve disagreements and discussing coded items. We will drop those items from our database in which resolution could not be reached, as well as items that lack clear interpretation. The data will be entered into the Comprehensive Meta-Analysis (CMA), version 2. We will use CMA to statistically combine results from the evaluations. We will report standardized mean differences (Cohen's d), as it is a very flexible effect size metric and many formulae are available to estimate Cohen's d from information often reported in evaluation articles (e.g., statistical test data, probability levels). Forest plots will be used to display the results from the effect sizes. The plot will display, for each study, the effect size, confidence intervals and significance level. The plot will also display the same for the average effect across studies. Note that this will be reported assuming a random effects model, and the estimate will be weighted by sample size. When describing results in the text, we will report the effect size, the confidence intervals and whether the analysis indicates that the result is statistically significant. Because of the likely heterogeneity in interventions, samples, countries, and outcomes, we will assume random effects models in our analyses, which tends to be more conservative than the fixed effects approach. For our analyses, we will conduct tests for heterogeneity to determine if the average effect size is a good representation of the sample of studies being used in the analysis. We anticipate the heterogeneity will be present, given the variations in intervention type, nation, sample populations and the like in these development studies. Using CMA, we will confirm heterogeneity in each summary analysis (of each outcome at each of the three time intervals: first, middle and longest) through the Q-Value, which is reported as a summary indicator of the extent of variance across studies in the sample. We do not anticipate, at this time, conducting a study of publication bias. The reason is that economists conduct and report many of the studies relevant to this area. The tradition in the field of economics is to make unpublished papers available online. However, a large percentage of these are eventually published in economics journals. Therefore, papers may only be temporarily “unpublished.” We are tracking all relevant documents for an evaluation, but do not believe a comparison of “published” versus “unpublished” studies would be particularly useful at this time. It is very unlikely, because of our focus on experiments and quasi-experiments, and our focus on quantifiable outcomes that can be converted into an effect size metric, that we will uncover much qualitative research. However, we will code the presence or absence of ancillary qualitative studies, what the studies focused on, and what the main findings are. Certainly, qualitative data from the experiments and quasi-experiments will be used to illuminate three particular areas: (1) the context for the intervention; (2) the theory or mechanisms by which the program is supposed to impact the ultimate outcomes; and (3) the quality and nature of the intervention and comparison condition. We will report on any economic data included in the primary studies that are included in the review. This includes information on the costs of the program, any analysis of the cost-effectiveness of the intervention (e.g., the cost per child enrolled) and cost-benefit studies (e.g., the sum costs and benefits of the program). It is important that this information be linked in some way to the primary outcome studies so that it can be retrieved. Anthony Petrosino, Ph.D., is Senior Research Associate at Learning Innovations at WestEd, and Associate Director of Research for the Regional Education Laboratory, Northeast and Islands. Anthony has worked on a number of projects during the past 20 years to identify, retrieve, appraise, analyze and report on separate but similar studies. For example, he was one of the founding members of the Campbell Collaboration, assisting in the development of its first trials register (C2-Spectr), co-authoring its pilot review (on “Scared Straight” and other juvenile awareness programs), and serving as Founding Coordinator for its Crime and Justice Group. A version of the “Scared Straight” review received the prestigious Pro Humanitate Literary Award from the Center for Child Welfare Policy of the North American Resource Center for Child Welfare. Although most of his training and experience has been in the justice area, he has more recently been working in education, and has co-authored government reports on the school dropout issue and the use of interim assessment in low-performing schools in Massachusetts. Claire Morgan, M.A., is a Research Associate at Learning Innovations at WestEd. She brings rich experience and sensitivity to issues facing developing nations. Morgan has lived and worked in Mexico, Central America, and the South Pacific, and has considerable experience conducting research in international issues and among marginalized populations, including a study of the education and work experiences of Tongan immigrants, action research around non-formal education of Latino immigrants, and current work on English language learners, education policy issues in Puerto Rico, and the achievement of Hispanic immigrant students in the U.S. Virgin Islands. Morgan serves as the lead researcher for Puerto Rico and the U.S. Virgin Islands for the U.S. Department of Education-funded Regional Educational Laboratory (REL) Northeast & Islands. In this capacity, she consults with the Departments of Education of Puerto Rico and the U.S. Virgin Islands and provides research and technical assistance to address their education policy priorities. Morgan's other research and evaluation work includes evaluation of National Science Foundation (NSF) university-school partnerships, evaluations of the federally-mandated Supplemental Educational Services (SES) program for the Massachusetts Department of Education and of the English to Speakers of Other Languages (ESOL) program for Prince Georges County, Maryland, and an evaluation of a language-minority community schools initiative in Quebec, Canada. Prior to joining WestEd, Morgan, who is fluent in Spanish, developed and directed a community-based adult education program for Nuestra Casa, a nonprofit organization serving Latino immigrants in Northern California. This initiative, a partnership with an underserved school district serving a large Hispanic student population, increased parent participation in schools and contributed to community development. In addition, she completed an internship at International Development Exchange (IDEX) in San Francisco, providing support to micro-ventures in Latin America. Morgan is currently directing the expansion of a nonprofit Latina women's work cooperative that she co-founded in 2006. She received an MA in International Education Administration and Policy Analysis from Stanford University. She is particularly skilled in designing and conducting quantitative and qualitative research and evaluation, including instrument development and coding, literature reviews, interviews and observations, and analyzing demographic and achievement data. Robert Boruch, Ph.D., is University Trustee Chair Professor of Education and Professor of Statistics (Wharton School) at the University of Pennsylvania. He has also served as faculty in the Fels Center for Government and at the Annenberg School Statistical Institutes. He is principal investigator for the What Works Clearinghouse (US Department of Education) and co-chairs the Steering Group of the international Campbell Collaboration. Dr. Boruch is a leading expert in experimental design research methods and related science policy on estimating effects of interventions. He has advised governments, private foundations, and research firms on randomized field trials in education, criminal justice, employment and training, and social welfare in the US and in other countries. His earliest contributions, during the 1970s, included service as advisor on the Cali Colombia randomized trials on cultural enrichment programs and the Nicaraguan trials on radio based mathematics education. Boruch chaired the National Academy of Sciences Committee on Evaluation of AIDS prevention programs in the 1980s and contributed to the WHO committee on the topic during the same period. He has authored numerous books and peer reviewed articles on related subjects. The most recent products include Evidence Matters: Randomized Trials in Education Research (2001), edited by Mosteller and Boruch (Brookings Institution Press), and a special edition of the Annals of the American Academy of Political and Social Sciences on place randomized trials in developed and developing countries (May 2005, volume 599) which covers health, crime and justice, welfare, housing, and education.. Boruch has been leader in institutes on generating better evidence for the US National Academy of Sciences and the Israel Academy of Sciences and Humanities, the Campbell Collaboration, workshops/seminars for the World Bank’ IPDET, and in other venues. Boruch is an elected Fellow of the American Statistical Association, the Academy of Experimental Criminology, and the American Academy of Arts and Sciences, and is a Lifetime Associate member of the National Academy of Sciences (US). He has received awards for the work from the American Evaluation Association (Myrdal Award), American Educational Research Association, the Campbell Collaboration, and the Policy Studies Organization. We plan to update this review in 36 months, in concert with C2 guidelines. We would like to thank International Initiative for Impact Evaluation (3ie) of the Global Development Network (GDN) for their support of this project. We thank the following persons for their helpful comments on this protocol (in alphabetical order): Campbell Education and Methods Group peer reviewers, WestEd colleagues Mary Cazabon, Sarah Guckenburg, Sue Henderson, Daniel Mello, and Eliza Spang, and 3ie officials Hugh Waddington and Howard White. We do not have any conflicts of interest regarding school enrollment policies. None of the authors has any financial or other personal interest in the results of this review. CODING INSTRUMENT Citation for Primary Document: ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ What year was the primary document published? ____________________________ How many documents were considered in coding this study? ___________________ What was the type of document? In what country did the evaluation take place? ________________________ World Bank country classification at time of study What was the setting for the evaluation? __________________________________ Who conducted the evaluation? (e.g., medical researchers, economists, etc.) _________ _____________________________________________________________________ What other information was provided on the context for the evaluation? ____________________________________________________________________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ Was random assignment used to assign groups? (Yes/No) At what level was randomization conducted? ________________________________ How was the randomization specifically done?_______________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ Were there any randomization problems noted? (Yes/No) ____________________________________________________________________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ If random assignment was not used, what quasi-experimental method was used to equate groups? (e.g., matched comparison schools; post-hoc statistical matching of individuals; regression discontinuity; propensity scores; etc.) ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ Where did comparison group come from? __________________________________ ______________________________________________________________________ ______________________________________________________________________ At what level was non-random assignment made? ____________________________ Were any substantive differences in pretests of group equivalence noted? (Yes/No) ____________________________________________________________________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ Were there any overall attrition problems noted? (Yes/No) Was differential attrition noted? (Yes/No) ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ _____________________________________________________________________ How were attrition problems dealt with by investigators? ______________________________________________________________________ Number of groups in the study: ___________________________________________ Rationale for selecting intervention and control contrast if multiple groups: ______________________________________________________________________ ______________________________________________________________________ List excluded study groups with brief description: ____________________________________________________________________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ Describe the intervention below, with particular attention to the “dosage” of the treatment: ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ ____________________________________________________________________ Were program implementation problems described by investigators? (Yes/No) ____________________________________________________________________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ __________________________________________________________________________________ Please detail program theory (or mechanisms for why it should work): ____________________________________________________________________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ ____________________________________________________________________________________ What is the control or comparison condition? Describe the control or comparison condition (including “dosage” if applicable): ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ ____________________________________________________________________ Type of school ______________________________________________ Age/school level/grade ______________________________________________ Percentage of participants that were female _______________________________ Poverty/SES ______________________________________________ Other data on participants (e.g. health, child labor, past enrollment status, achievement level) _______________________________________________ ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ Include all data on treatment and control, including results, sample sizes used in analysis, the statistical technique, whether regression-adjusted or not, (and if so, what controls were used), statistical significance and probability level. Please detail all subgroup effects below, particularly gender and grade level: ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ ___________________________________ Please detail all cost/economic information below: ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ ______________________________________________________________________ _______________________________________________ ANY OTHER COMMENTS ON THE PROGRAM OR EVALUATION
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