A Market-Equilibrium Approach to Reduce the Incidence of Vote-Buying

We intend to study the impacts of a large anti-vote buying campaign conducted across 53 districts in Uganda in January and February 2016. The campaign was designed and implemented by a coalition of 17 local civil society organizations, the Alliance for Election Campaign Finance Monitoring (ACFIM), and coordinated and funded by an international NGO, the National Democratic Institute (NDI). Their approach seeks to foster collective commitments in a village not to sell any votes.

The intervention took place during the two months leading up to the election, and involved several stages in each selected village:

1. Each household received a leaflet approved by the Electoral Commission explaining in simple terms the costs and risks of vote-buying to the community.

2. Three community-wide meetings were organized to discuss the vote-buying issue, facilitated by a local ACFIM activist.

3. At the end of the third meeting, ACFIM activists invited the community to collectively commit to refuse offers of gifts or money in exchange for votes.

4. ACFIM activists then placed posters through the village indicating the village is a "no vote-buying village."

5. Prior to the presidential and MP election (February 18, 2016), individuals that attended the village meetings received automatized phone calls (robo-calls) recorded by prominent religious figures reminding them to abide by the collective guidelines agreed upon in community meetings.

2016-01-04

2016-02-18

Our primary outcome of interest is a standardized index of vote-buying. The details of the computation of this index are provided in the Pre-Analysis Plan.

Our experimental sample includes 2,796 villages across 53 Ugandan districts, 110 parliamentary constituencies, and 918 parishes. Among these, 1,427 villages across 611 parishes were selected for treatment. The remaining 307 parishes were allocated a pure control group with no village treated. An additional 1,399 villages located in the same 918 parishes were added to the endline survey sample to look for spillovers (we oversampled villages in parishes with a higher treatment saturation).

The intervention uses a randomized saturation design, along the lines of Baird et al. (2014), varying the level of saturation of treatment at the parish level. (Parishes are the geographic unit just above village and generally consist of 3-10 villages.) Based on our qualitative work, we understand that most vote-buying is organized at this level. We have allocated parishes to one of three cells: a pure control cell (no treatment), a partial-saturation treatment cell (50% of eligible villages are treated), and a high-saturation cell (100% of eligible villages are treated). On average, across all parishes with at least one eligible village, 40% of registered voters in a parish live in eligible villages.

This design will allow us to recover the spillover effect on the non-treated and the total (general equilibrium) causal effect of the intervention, in addition to standard intent-to-treat estimates, as well as how those estimates vary with treatment intensity. We believe that the treatment effect could be quite different if more nearby villages are treated, since the more villages resist vote-buying, the more political candidates will be forced to change tactics by making policy promises instead. If only one village opposes vote-buying, we believe that candidates may instead simply buy more votes in nearby villages, showing the importance of a widespread campaign in order to discipline candidate behavior.

The randomization was conducted remotely in Cambridge, MA, using Stata. The do-file used for the randomization will be posted under the "Materials" section.

Treatment status was allocated across 918 parishes eligible to receive the campaign. A parish was eligible if at least one village in the parish had baseline ACFIM presence. The parish definitions were taken from the March edition of the Electoral Commission's assignment of villages to polling stations.

Each parish was allocated to one of three cells: a pure control cell (no treatment), a partial-saturation treatment cell (50% of eligible villages are treated), and a high-saturation cell (100% of eligible villages are treated). In the "pure control" parishes, the ACFIM campaign did not take place. In the "high saturation" parishes, all eligible villages (all villages with ACFIM presence at baseline) received the campaign. In the partial-saturation parishes, a random subset of villages was treated, as described below. The parish-level randomization was stratified along baseline measures of partner presence (defined in terms of the number of voters covered), parish-level voter population, and support for the incumbent political party in the previous national election. Specifically, a stratum was defined by the three-way interaction of quartile of partner presence, quartile of voter population, and quartile of NRM support (63 strata in total).

A second layer of randomization was then conducted exclusively in the partial-saturation treatment cells. In these cells, randomization was conducted at the polling station level. Polling stations were randomly allocated to treatment or spillover status. All villages falling under "treatment" polling stations were selected to receive the ACFIM campaign. None of the villages falling under "spillover" polling stations were selected to receive the campaign. If only one polling station was eligible in a partial-saturation treatment cell, it was either fully treated (with 50% probability) or a full control (with 50% probability).

Yes

918 parishes.

Approximately 25,200 individuals without attrition (6 individual surveys across 4,200 villages).

The 918 parishes were randomly allocated as follows: 307 "pure control" parishes, 305 "partial saturation" parishes, and 306 "high saturation" parishes. In total, 1,453 villages were randomly selected for the ACFIM campaign (including 941 villages in the "high saturation" parishes and 486 in the "partial saturation" parishes).

Due to the complex design of the study, which layers a randomized saturation design on top of endogenous gateways of varying sizes (different numbers of campaign eligible villages in each parish), it was not feasible to calculate MDEs analytically. Instead, we simulated many different effect sizes and calculated the probability of detecting an effect of each magnitude. We used Afrobarometer data from Uganda on prior experiences with vote selling as our source for data. We first calculated district averages in vote buying experience from Afrobarometer. Subsequently, we calculated differences in village averages from the district mean for each village in the Afrobarometer data. Then, for each village in our data, we simulated its degree of vote selling by assigning it the relevant district average (if available) or a randomly selected district average (held constant for all villages in the same district) plus a village-level shock drawn randomly from the distribution of calculated differences in village averages. All draws were with replacement. Thus, for control villages, their average degree of vote selling was: (district average level + random village deviation), censored below at 0 and above at 1. For treatment villages, we added a set of effects for being treated in terms of a direct treatment effect and a slope effect that rises with the percent of voters in the same parish who are subject to the treatment. For spillover villages - villages in parishes where at least one village is treated, but which are not themselves treated - we added a direct spillover effect plus a slope effect that rises with the percent of voters in the same parish who are subject to the treatment. Then we estimated an ITT equation with an indicator for being a treatment village and an indicator for being a spillover village plus a set of stratum FEs. We clustered at the parish level. We are powered at approximately 80% to detect an ITT direct effect of approximately -0.15 standard deviations and an ITT spillover slope effect (holding the intercept at 0) of about 0.35 standard deviations (that is to say, an effect that is 0 when there is 0% saturation and which rises linearly to 0.35 standard deviations as the percent of voters in a parish who are treated rises to 100%). Since average potential saturation is 45% and average saturation conditional on any treatment is 39%, this equates to a spillover ITT effect of 0.137 standard deviations. Previous studies, e.g. Vicente (2014) have found effects of 0.4 standard deviations, so we feel we are well-powered to measure relevant effects. We expect that there will be several important differences between our power calculations and the end results. First, our measured outcomes will differ from those used by Afrobarometer. Second, the number of individuals sampled per village differs from Afrobarometer. Third, the assignment of additional spillover villages will differ slightly from the process used for power calculations.