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Randomization and Impact evaluation

Randomization and Impact evaluation

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Randomization and Impact evaluation

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  1. Randomization and Impact evaluation

  2. The Types of Program Evaluation • Process evaluation • Audit and monitoring • Did the intended policy actually happen (2) Impact evaluation • What effect (if any) did the policy have?

  3. Why Impact Evaluation ? • Knowledge is a global public good • Long term credibility • Help choosing best projects: build long term support for development

  4. The evaluation problem and alternative solutions • Impact is the difference between the relevant outcome indicator with the program and that without it. • However, we can never simultaneously observe someone in two different states of nature. • So, while a post-intervention indicator is observed, its value in the absence of the program is not, i.e., it is a counter-factual.

  5. Problems when Evaluation is not Built in Ex-Ante • Need a reliable comparison group • Before/After: Other things may happen • Units with/without the policy:May be different for other reasons than the policy (e.g. because policy is placed in specific areas)

  6. We observe an outcome indicator, Intervention

  7. and its value rises after the program: Intervention

  8. However, we need to identify the counterfactual… Intervention

  9. … since only then can we determine the impact of the intervention

  10. How can we fill in the missing dataon the counterfactual? • Randomization • Matching • Propensity-score matching • Difference-in-difference • Matched double difference • Regression Discontinuity Design • Instrumental variables

  11. 1. Randomization“Randomized out” group reveals counterfactual. • Only a random sample participates. • As long as the assignment is genuinely random, impact is revealed in expectation. • Randomization is the theoretical ideal, and the benchmark for non-experimental methods. Identification issues are more transparent compare with other evaluation technique. • But there are problems in practice: • internal validity: selective non-compliance • external validity: difficult to extrapolate results from a pilot experiment to the whole population

  12. 2. MatchingMatched comparators identify counterfactual. • Propensity-score matching: Match on the basis of the probability of participation. • Match participants to non-participants from a larger survey. • The matches are chosen on the basis of similarities in observed characteristics. • This assumes no selection bias based on unobservable heterogeneity. • Validity of matching methods depends heavily on data quality.

  13. 3. Propensity-score matching (PSM)Match on the probability of participation. • Ideally we would match on the entire vector X of observed characteristics. However, this is practically impossible. X could be huge. • Rosenbaum and Rubin: match on the basis of the propensity score = • This assumes that participation is independent of outcomes given X. If no bias give X then no bias given P(X).

  14. Steps in score matching: 1: Representative, highly comparable, surveys of the non-participants and participants. 2: Pool the two samples and estimate a logit (or probit) model of program participation. Predicted values are the “propensity scores”. 3: Restrict samples to assure common support Failure of common support is an important source of bias in observational studies (Heckman et al.)

  15. Density of scores for participants

  16. Density of scores for non-participants

  17. Density of scores for non-participants

  18. Steps in score matching: 4: For each participant find a sample of non-participants that have similar propensity scores. 5: Compare the outcome indicators. The difference is the estimate of the gain due to the program for that observation. 6: Calculate the mean of these individual gains to obtain the average overall gain.

  19. 4. Difference-in-difference (double difference) Observed changes over time for nonparticipants provide the counterfactual for participants. • Collect baseline data on non-participants and (probable) participants before the program. • Compare with data after the program. • Subtract the two differences, or use a regression with a dummy variable for participant. • This allows for selection bias but it must be time-invariant and additive.

  20. Selection bias Selection bias

  21. Diff-in-diff requires that the bias is additive and time-invariant

  22. The method fails if the comparison group is on a different trajectory

  23. Diff-in-diff: if (i) change over time for comparison group reveals counterfactual and (ii) baseline is uncontaminated by the program,

  24. 5. Matched double differenceMatching helps control for bias in diff-in-diff • Score match participants and non-participants based on observed characteristics in baseline • Then do a double difference • This deals with observable heterogeneity in initial conditions that can influence subsequent changes over time

  25. 6. Regression Discontinuity Design • Selection function is a discontinuous function • UPP in Indonesia: two similar kecamatan in the same kabupaten that have scores within the neighborhood of the cut off score can be treated differently Selection 1 0 Kecamatan score control treatment

  26. 7. Instrumental variablesIdentifying exogenous variation using a 3rd variable Outcome regression: D = 0,1 is our program – not random • “Instrument” (Z) influences participation, but does not affect outcomes given participation (the “exclusion restriction”). • This identifies the exogenous variation in outcomes due to the program. Treatment regression:

  27. Randomization: An example from Mexico • Progresa: Grants to poor families, conditional on preventive health care and school attendance for children. Given to women • Mexican government wanted an evaluation; order of community phase-in was random • Results: child illness down 23%; height increased 1-4cm; 3.4% increase in enrollment • After evaluation: PROGRESA expanded within Mexico, similar programs adopted throughout other Latin American countries

  28. Randomization: An example from Kenya • School-based deworming: treat with a single pill every 6 months at a cost of 49 cents per student per year • 27% of treated students had moderate-to-heavy infection, 52% of comparison • Treatment reduced school absenteeism by 25%, or 7 percentage points • Costs only $3 per additional year of school participation

  29. Lessons randomized experiments • Randomized evaluations are often feasible • Have been conducted successfully • Are labor intensive and costly, but no more so than other data collection activities • Results from randomized evaluations can be quite different from those drawn from retrospective evaluations • NGOs are well-suited to conduct randomized evaluations in collaboration with academics and external funders

  30. Lessons randomized experiments While randomization is a powerful tool: • Internal validity can be questionable if we do not allow properly for selective compliance with the randomized assignment. • Not always feasible beyond pilot projects, which raises concerns about external validity. • Contextual factors influence outcomes; scaled up program may work differently.

  31. Matching Method Example :Piped water and child health in rural India • Is a child less vulnerable to diarrhea if he/she lives in a household with piped water? • Do children in poor, or poorly educated, households realize the same health gains from piped water as others? • Does income matter independently of parental education?

  32. The evaluation problem • There are observable differences between those households with piped water and those without it. •  And these differences probably also matter to child health.

  33. Naïve comparisons can be deceptive • Common practice: compare villages with piped water, or some other infrastructure facility, and those without. • Failure to control for differences in village characteristics that influence infrastructure placement can severely bias such comparisons.

  34. Model for the propensity scores for piped water placement in India • Village variables: agricultural modernization, educational and social infrastructure. • Household variables: demographics, education, religion, ethnicity, assets, housing conditions, and state dummy variables.

  35. More likely to have piped water if: • Household lives in a larger village, with a high school, a pucca road, a bus stop, a telephone, a bank, and a market; • it is not a member of a scheduled tribe; • it is a Christian household; • it rents rather than owns the home; this is not a perverse wealth effect, but is related to the fact that rental housing tends to be better equipped; • it is female-headed; • it owns more land.

  36. Impacts of piped water on child health • The results for mean impact indicate that access to piped water significantly reduces diarrhea incidence and duration. • Disease incidence amongst those with piped water would be 21% higher without it. Illness duration would be 29% higher.

  37. Stratifying by income per capita: • No significant child-health gains amongst the poorest 40% (roughly corresponding to the poor in India). • Very significant impacts for the upper 60% • Without piped water there would be no difference in infant diarrhea incidence between the poorest quintile and the richest.

  38. When we stratify by both income and education: • For the poor, the education of female members matters greatly to achieving the child-health benefits from piped water. • Even in the poorest 40%, women’s schooling results in lower incidence and duration of diarrhea among children from piped water. • Women’s education matters much less for upper income groups.

  39. Lessons on matching methods • When neither randomization nor a baseline survey are feasible, careful matching to control for observable heterogeneity is crucial. • This requires good data, to capture the factors relevant to participation. • Look for heterogeneity in impact; average impact may hide important differences in the characteristics of those who gain or lose from the intervention.

  40. Tracking participants and non-participants over time 1. Single-difference matching can still be contaminated by selection bias Latent heterogeneity in factors relevant to participation 2. Tracking individuals over time allows a double difference This eliminates all time-invariant additive selection bias 3. Combining double difference with matching: This allows us to eliminate observable heterogeneity in factors relevant to subsequent changes over time

  41. Improving Evaluation Practice When there is an impact evaluation: • Build in evaluation ex-ante • Make a quality evaluation a primary responsibility of the manager of the program • Allocate the necessary resources • Encourage randomization whenever feasible (education, health, micro-finance, governance, not monetary policy…)

  42. Practical suggestions • Not every project needs impact evaluation: select projects in priority areas, where knowledge needed • Take advantage of budget constraints and phase-in • Require pilot project before large scale project • Finance pilot projects and evaluations with grants • Collaborate with others: • Academics (e.g. Evaluation Based Policy Fund in UK) • NGOs

  43. Evaluation: An Opportunity • Creating hard evidence of success will • spend future resources more effectively • influence other policymakers • build public support