Experimental Design Details
We will work in the Pikine and Guediawaye departments of peri-urban Dakar, Senegal. This area is home to approximately 1.2 million individuals, and roughly 80% of households in the area are not connected to the city's sewage network; each household is responsible for deciding how to dispose of its own waste. This area is also poorer than the rest of Dakar. Many areas in Pikine and Guediawaye are far from the waste treatment plants or less directly accessible, so mechanized desludging is expensive. Collusion among desludging service providers also seems to contribute to high prices. These facts mean that adoption of mechanized desludging is particularly low relative to the rest of Dakar. We will measure the following direct social effects on the treated households.
Social pressure and incoming reciprocity: We have randomly assigned discounts of 4% or 32% to each household, sharing the distribution of these discounts with 'public' clusters and not sharing this information in 'private' clusters. Households that have been assigned the high discount in 'public' clusters will face stronger social pressure to purchase the sanitation service than households that have been assigned the same discount in the ‘private’ clusters. We offer only two levels of subsidies in order to increase the social pressure felt by households drawing the high subsidy and in order to avoid small sample problems when estimating the impact of the subsidies.
The public-private treatment is randomized at the cluster level. There are 400 clusters, each with 10 households. In this treatment we will compare the overall use of mechanized desludging versus manual desludging. We estimate the necessary sample size assuming a standardized effect size of 0.2 and an intra-cluster correlation coefficient of 0.2, based on desludging data from a related study in Dakar. With 10 households per cluster, the cluster-corrected power calculation suggests that we need at least 364 clusters. This corresponds to a power level of 95% and confidence level of 5%. We have selected 400 project clusters.
We will also evaluate the effect of this treatment on the follow-through rate for those who commit to mechanized desludging. Because this outcome can only be measured for participants who sign up for a subsidized desludging through the project, there will be fewer participants per cluster. We adjust the power calculation assuming only 4 households per cluster. We expect a greater standardized effect size for this group of 0.25. Keeping the same power and confidence levels, we need at least 333 clusters.
Learning-by-Doing: People may be more likely to continue mechanized desludging after they experience it. Households are given discounts for the first two desludgings during the 9 months following their subscription, while the price for the third desludging, or any desludging after the 9-month period, will no longer be subsidized.
Learning-from-others, coordination, and outgoing reciprocity: People may be more likely to sign up for mechanized desludging after they have seen their neighbors do it. Some of the neighborhoods (200 clusters of 10 households) will be randomly divided into two halves when surveying. In the second half, we will provide information about the first five households' desludging decisions to the last five participants. We will notify the last five of how many of their first five neighbors have signed up for a desludging subscription, with half of the treated group learning only the number of neighbors and half also learning the names of subscribing neighbors. We will then compare the takeup and follow-through rates of the first fives with the last fives, and also of the number-only treatment group with the names treatment group.
Within a cluster, the assignment of households to the first five or last five is randomized at the individual level. In order to detect a standardized effect size of 0.2 for the learning from others treatment, we will need a sample size of at least 1300 households for a 5% confidence level with 95% power. Conducting this experiment with 2000 households is therefore sufficient. We will be able to compare the 1000 last five households with control groups from the 1000 first five households, as well as with the 2000 households not included in this experiment, giving a total of 1000 treated and 3000 control.
We will also compare the two treated groups – whether the households are told how many or who among their neighbors sign up for a mechanized desludging. These treatments are randomized at the cluster level, with 5 treated households per cluster. Because this intervention is logistically difficult and costly, we are not able to increase the sample beyond 100 clusters (500 households) per treatment arm. Still, this sample size will be sufficient to detect a standardized effect of 0.25 with 82% power, or a standardized effect of 0.3 with 94% power.
Incoming reciprocity: People may sign up for desludging in order to reap future benefits from their reciprocal neighbors. We will carry out baseline and endline social network surveys to test this. In addition to the RCT, we will also play an economic game. During the survey, we will run a variant of a dictator game measuring incoming reciprocity. Each individual is given 500 CFA. He will choose how much to keep and how much to distribute anonymously to each of the other households. Any money sent to others will be doubled. This game will be played again during the endline survey. We will compare transfers to households that purchased the desludging service with those who did not.
Payment mechanisms: We will also separately measure the effects of payment mechanisms on the willingness to pay for desludging services. There are several different payment types that we are testing: frequency of payments, the requirement of a deposit in addition to payment at the time of service, and the availability of savings accounts for general purposes in addition to the savings account earmarked for desludging.
Frequency of payments: Households receive reminders to save for their desludgings, and the frequency with which they are asked to pay in the reminders varies between at will, monthly, and payment at the time of service.
Earmarking: The earmarking treatment will compare those who received a single savings account earmarked for desludging with those who received both a desludging account and a normal savings account. Because not all participants will opt into the payment plan, we have adjusted our sample size to account for an estimated 40% expected takeup (hence 1600 participants in the earmarking experiment). For the earmarking experiment, our outcomes of interest are both total levels of savings and final use of the desludging services. We will compare the proportion of households who follow through with mechanical desludging after signing up for a subscription plan.
We estimate that use of the desludging services (follow-through rate) will be about 70% for those with one account. In order to detect an increase to 80% or higher, we require a sample size of at least 962. We therefore believe our sample size of 1600 should be conservative for the earmarking treatment arms.
In terms of the savings level outcome for the earmarking experiment, we expect a standardized effect size of at least 0.2, which suggests that we need a sample size of at least 1300.
Deposit: About 3500 households will be asked to pay a deposit toward a subsidized desludging at the time of the decider survey, and 500 will be offered a subsidized desludging with no deposit. We will compare the proportion of households who follow through with mechanical desludging among those who left a deposit and those who did not. This sample size is sufficient to detect a 0.2 standardized effect size at 5% confidence with over 98% power.
Note that this treatment is cross-randomized with the payment plans. Half of each deposit treatment arm will receive a subscription payment plan. We expect the effect of the commitment deposit treatment to be similar across the different subsidy levels.
Spillovers: Two households (out of 12) within each cluster will not receive any treatment in order to measure spillover effects. We estimate the sample size necessary in order to have 95% power to calculate an effect that is statistically different from 0 at a 5% level of confidence, and still adjust for likely intra-cluster correlation of the two households.
Using a similar framework in estimating the effect of learning on adoption of mosquito nets, Dupas (2010) finds a standardized effect size of having all neighbors receive the maximum subsidy of 0.44. (The coefficient on the share of households with the maximum subsidy within 500 meters is 0.215, and the standard deviation of adoption is 0.489.) We estimate the necessary sample size assuming a more conservative standardized effect size of 0.2 and an intra-cluster correlation coefficient of 0.2. With 2 households per cluster, the cluster-corrected power calculation suggests that we need 780 spillover households to compare with 3900 participant households. We will therefore use all 400 of our project clusters, for a total of 800 spillover households.