1. Global Workshop on Development Impact Evaluation in Finance and Private Sector Rio de Janeiro, June 6-10, 2011 Using Randomized Evaluations to Improve Policy Isabel Beltran

2. Objective  To Identify the True Effect of a Program separate the impact of the program from other factors >> What is the causal effect of a program?  Need to find out what would have happened without the program Cannot observe the same person with and without the program >> Rely on counterfactual analysis (control group) 2

3. Correlation is not causation Higher profits Credit Use OR ? 2) ? 1) Higher profits Business Skills Credit Question: Does providing credit increase firm profits? Suppose we observe that firms with more credit also earn higher profits.

4. 4 (+6) increase in gross operating margin Illustration: Credit Program (1) A credit program was offered in 2008. Why did operating margin increase?

5. 5 (+) Impact of the program (+) Impact of other (external) factors Illustration: Credit Program (2)

6. 6 (+) BIASED Measure of the program impact Illustration: Credit Program (Before-After)

7. Motivation  Hard to distinguish causation from correlation from statistical analysis of existing data However complex the statistics can only see that X (credit program) goes with Y (operating margin) Hard to correct for unobserved characteristics, like motivation/ability Motivation/ability may be the most important things to correct for  Selection bias a major issue for impact evaluation Projects started at specific times and places for particular reasons Participants may be selected or self-select into programs (eligibility criteria)  People who have access to credit are likely to be very different from the average entrepreneur, looking at their profits will give you a misleading impression of the benefits of credit 7

8. Motivation  Retrospective impact evaluation: Collecting data after the event you don’t know how participants and nonparticipants compared before the program started Have to try and disentangle why the project was implemented where and when it was, after the event  Prospective evaluation allows you to design the evaluation to answer the question you need to answer  Allows you to collect the data you will need 8

9. Experimental Design  All those in the study have the same chance of being in the treatment or comparison group  By design treatment and comparison have the same characteristics (observed and unobserved), on average Only difference is treatment  With large sample, all characteristics average out  Unbiased impact estimates 9

10. Options for Randomization Lottery (only some get the program) Random phase-in  Everyone gets it eventually Variation in treatment  Full coverage but with different options Encouragement design (when partial take up)  Everyone can get it, some encouraged to get it 10

11. Example in Private Sector Development  Lottery Lottery to receive new loans  Random phase-in (everyone gets it eventually) Some groups or individuals get credit each year  Variation in treatment Some get matching grant, others get credit, others get business development services etc.  Encouragement design Some entrepreneurs get home visit to explain loan product, others do not 11

12. Lottery among the qualified Must get the program Not suitable for the program Randomize who gets the program

13. Opportunities for Randomization (1)  Budget constraints  prevent full coverage Random assignment (lottery) is fair and transparent  Limited implementation capacity Randomized phase-in gives all the same chance to go first  No evidence on which alternative is best Random assignment to alternatives with equal ex ante chance of success 13

14. Opportunities for Randomization (2)  Take up of existing program is not complete Provide information or incentive for some to sign up (Randomize encouragement)  Pilot a new program Good opportunity to test design before scaling up  Operational changes to ongoing programs Good opportunity to test changes before scaling them up 14

15. Different levels you can randomize at Individual (firm owner) Firm Business Association Village level Regulatory jurisdiction/ administrative district 15 Women’s association Youth groups School level

16. Group or individual randomization?  If a program impacts a whole group usually randomize whole group to treatment or comparison  Easier to get big enough sample if randomize individuals Individual randomizationGroup randomization

17. Unit of Randomization  Randomizing at higher level sometimes necessary: Political constraints on differential treatment within community Practical constraints—confusing for one person to implement different versions Spillover effects may require higher level randomization  Randomizing at group level requires many groups because of within community correlation 17

18. Elements of an experimental design 18 Random assignment Treatment GroupControl Group Participants  Drop-outs Evaluation sample Potential participants TailorsFurniture Manufacturers Target population SMEs

19. External and Internal Validity (1)  External validity The sample is representative of the total population The results in the sample represent the results in the population We can apply the lessons to the whole population  Internal validity The estimated effect of the intervention/program on the evaluated population reflects the real impact on that population i.e. the intervention and comparison groups are comparable 19

20. External and Internal Validity (2)  An evaluation can have internal validity without external validity Example: a randomized evaluation of encouraging informal firms to register in urban area may not tell you much about impact of a similar program in rural areas.  An evaluation without internal validity, can’t have external validity If you don’t know whether a program works in one place, then you have learnt nothing about whether it works elsewhere. 20

21. Internal AND external validity 21 Randomization National Population Samples National Population

22. Internal validity ONLY 22 Stratification (some sub- group of the population) Randomization (treatment and control) Population Population stratum Samples of Population Stratum

23. 23 Representative but biased: useless National Population Biased assignment USELESS! Randomization

24. Example: Credit Program, internal validity 24 Random assignment Sample of female entrepreneurs

25. Example: Credit program Basic sequence of tasks for the evaluation  Listing eligible firms ▪ E.g. SMEs with turnover below a certain threshold  Baseline data of firms  Random assignment to different treatments or to treatment and control  Project implementation  Follow-up survey 25

26. Efficacy & Effectiveness  Efficacy Proof of concept Smaller scale Pilot in ideal conditions  Effectiveness At scale Prevailing implementation arrangements -- “real life”  Higher or lower impact?  Higher or lower costs? 26

27. Advantages of “experiments” Clear and precise causal impact Relative to other methods:  Much easier to analyze  Cheaper (smaller sample sizes)  Easier to explain  More convincing to policymakers  Methodologically uncontroversial 27

28. What if there are constraints on randomization?  Budget constraints: randomize among the most in need  Roll-out capacity constraints: randomize who receives first… (or next, if you have already started)  Randomly promote the program to some and not to others …(participants make their own choices about adoption) 28

29.  Those who get/receive promotion or marketing are more likely to enroll  But who got promotion or marketing was determined randomly, so not correlated with other observables or non-observables Compare average outcomes of two groups: promoted/not promoted Effect of offering the encouragement (Intent-To- Treat) Effect of the intervention on the complier population (Local Average Treatment Effect) ▪ LATE= effect of offering program (ITT)/proportion of those who took it up

30. Assigned to treatment Assigned to control DifferenceImpact: Average treatment effect on the treated Non-treated Treated Proportion treated 100%0%100% Impact of assignment 100% Mean outcome1038023 Intent-to-treat estimate 23/100%=23 Average treatment on the treated

31. EncouragedNot encouraged DifferenceImpact: Average treatment effect on compliers Non-treated (did not take up program) Treated (did take up program) Proportion treated 70%30%40% Impact of encouragement 100% Outcome100928 Intent-to-treat estimate 8/40%=20 Average treatment on the compliers

32. Common pitfalls to avoid Calculating sample size incorrectly Randomizing one district to treatment and one district to control and calculating sample size on number of people you interview Collecting data in treatment and control differently Counting those assigned to treatment who do not take up program as control—don’t undo your randomization!! 32

33. When is it really not possible?  The treatment already assigned and announced and no possibility for expansion of treatment  The program is over (retrospective)  Universal take-up already  Program is national and non excludable Freedom of the press, exchange rate policy (sometimes some components can be randomized)  Sample size is too small to make it worth it 33

34. Thank you Financial support from: Bank Netherlands Partnership Program (BNPP), Bovespa, CVM, Gender Action Plan (GAP), Belgium & Luxemburg Poverty Reduction Partnerships (BPRP/LPRP), Knowledge for Change Program (KCP), Russia Financial Literacy and Education Trust Fund (RTF), and the Trust Fund for Environmentally & Socially Sustainable Development (TFESSD), is gratefully acknowledged.