Setting.

Similar to many developing countries, Uganda holds elections that are not free and fair and suffers from corruption and poor governance, especially locally (21, 22). Although there is competition, the electoral playing field favors the ruling National Resistance Movement (NRM) party. Moreover, the NRM restricts what media can report, particularly around elections (ref. 22, pp. 96–101). This setting creates severe challenges for electoral accountability.

We focus on council elections for district offices, analogous to provinces or states in other countries. District councils (also known as LC Vs or LC5) are comprised of chairs and directly elected councillors that represent smaller constituencies. In our sample, 85% of elections for district chairs were contested, though the NRM won 77% of these elections.

District councils have primary responsibility for local public services such as health, roads, and education. They write legislation, monitor contracts, supervise public-service staff, formulate local development programs, and plan and oversee public budgets (23, 24). Chairs have significant responsibilities in these areas in both law and practice. However, when citizens observe shoddy services and mismanaged funds, councillors are often a first point of contact (23, 25). According to one study, two-thirds of councillors believe their efforts at monitoring public services and spending affect public-service quality (24). Yet the influence of bureaucrats and higher level officials clearly constrains councillors’ ability to manage budgets (26).

Many Ugandans lack knowledge about district councils, which further hinders their ability to hold local officials accountable (ref. 27, p. 16). This dynamic contributes to what the Ugandan Auditor General has called poor local government performance (ref. 28, pp. 13–14). In our sample, 47% of subjects said they would be “not surprised” or “not too surprised” to learn about corruption in their district. Scandals of financial fraud have frequently implicated both chairs and councillors. We thus hypothesized that budget information delivered privately on mobile phones could help overcome more systemic barriers to gaining information about politicians’ performance.

Experimental Treatment.

District councils must submit to an annual audit by the internationally respected Ugandan Auditor General. The audit tracks whether councils followed procurement rules, completed projects as specified, and accounted for expenditures properly. The Auditor General presents its reports to parliament and posts them online. However, the reports are not widely known to the public or discussed. Respondents indicated limited knowledge of their contents; less than 25% correctly ranked their council’s budget performance.

We used the audits to create district ratings for fraud and mismanagement. This information was salient: More than 80% of respondents in our sample indicated that good budget management was important in deciding how to vote for district officials. We made the audit information more accessible and meaningful by simplifying it and adding comparisons. For example, we explained how the percentage of unaccounted-for funds in a citizen’s district compared with other districts. Additionally, to make the information more tangible, we sent two messages with local examples of budget performance that aligned with the treatment. Examples messages sent to treated subjects in a “much worse” district on day 2 of the experiment are

• i) In your LC5, the auditor found issues with 120 million UGX from its budget of 19 billion UGX. This is much worse than in other districts.

• ii) This means that 6.3 out of 1,000 UGX in your LC5 budget had issues. In most LC5s, 2.2 out of 1,000 UGX had issues. Your LC5 did much worse than average.

• iii) One reason your LC5 did much worse than average is that a bid for borehole construction included unexplained expenditures.

Subjects not assigned to the treatment received placebo messages about the value of good personal financial management. This placebo design helped us isolate the effect of novel information from any increased salience of budgeting. Providing useful placebo information also helped avoid unequal attrition across conditions (see SI Appendix, Tables S8 and S9). Examples messages sent to control subjects in a “much worse” district on day 2 of the experiment are

• i) Research suggests that households which open a savings account are better able to save for school books and fees.

• ii) When youth learn to save and manage their money well, they often have higher savings and income later on in life.

Additional examples and screenshots are provided in SI Appendix, Fig. S1 and Table S1.

The study was logistically complex, nationally representative, and a significant increase in scale from most prior studies on information and accountability. Just before district elections, we sent a total of 207,940 text messages in 11 languages to 16,083 subjects in 762 villages dispersed among 27 districts. Because both chairs and councillors share budget-management responsibilities, the texts appeared relevant for voter evaluations.*

To understand subjects’ experiences with the text messages, we designed an additional survey and recontacted a random sample of 100 treated respondents after end line. Eighty-seven percent remembered receiving the texts, of whom 64% reported reading them fully and 33% in part. Seventy-four percent found them easy to understand and distinguish from other messages.

Voters may be more politically engaged when they are able to coordinate within social networks (29, 30). As a second experimental treatment, we therefore varied treatment density at 80% and 20% between village-pair blocks with at least 15 subjects. In the high-density condition, we also informed voters that many others in their village had received the treatment. We expected to observe stronger treatment effects and evidence of information sharing in the high-density condition.

Sample.

We used a nationally representative sample of 27 out of 111 district councils, selected for a concurrent education audit by Twaweza. Within each sampled district, Twaweza chose 30 villages randomly in proportion to population, except Kampala, where 60 villages were chosen to account for greater population. In 762 accessible sample villages, enumerators recruited 31,310 individuals using gatherings and door-to-door visits. Recruitment involved substantial on-the-ground effort, since preexisting contact lists were unavailable. We were able to recontact 16,083 subjects via phone to confirm participation and administer a baseline survey. These subjects formed our experimental sample. SI Appendix contains a detailed description of sampling procedures, reasons for exclusion, a CONSORT diagram (SI Appendix, Fig. S3), a map of the sample (SI Appendix, Fig. S2), and subjects’ characteristics (SI Appendix, Tables S6 and S7 and Figs. S10 and S11).

We used the 2015 Afrobarometer survey to compare our experimental sample to the Ugandan population. In both samples, the median age was 33. However, our recruitment of people with mobile phones skewed the sample toward men and better educated individuals (31). If well-educated subjects are also more politically sophisticated, it may be more difficult to change their minds and our treatment effects may reflect lower bounds on population effects. However, better educated subjects might more easily understand new information, implying that these effects might not scale fully to voters without mobile phones.

Outcome of Interest.

We measure vote choice using answers to questions from an endline survey. Self-reported voting measures may introduce biases, such as those related to social desirability and strategic misrepresentation. To combat such biases, previous studies have randomly assigned interventions at the level of precincts and measured aggregate support for given candidates using official returns (e.g., ref. 3).

We instead used a postelection survey for multiple reasons. First, given ethical considerations, we wished to avoid affecting election outcomes. Thus, we treated at a low density within constituencies, preventing the detection of effects in aggregate returns. Second, we valued the ability to account for individual characteristics like priors in our analysis, and this aligns with the goals of the Metaketa I initiative of which this study was a part (9). Third, studying aggregate-level outcomes necessitates cluster-randomized designs, which would dramatically decrease statistical power to identify the relatively small anticipated effects. Fourth, reports indicated that precinct-level results for district offices might not be released or might be unreliable. Fifth, survey-based data are often used to study vote choice in both experimental and observational studies (32, 33). Nevertheless, relying on reported vote choice introduced the possibility that subjects did not truthfully report behavior. Although the results from our endline survey correlate well with the official returns (see SI Appendix, Fig. S5), we used multiple approaches to detect possible misreporting.

First, we asked respondents about the basin color in their polling station and checked for internal consistency of responses.^† Second, due to social desirability, respondents may have overreported voting for incumbents who performed well on budgets and underreported voting for incumbents who performed poorly. Yet this possibility is inconsistent with our finding that information affected reported votes for councillors but not for chairs. Moreover, under the reasonable assumption that the treatment and placebo groups were equally likely to overreport votes for the ruling party, this dynamic would not have altered estimated effects. Our check for reporting bias toward the election winner did not show any differences between responses conducted before and after the release of official results (SI Appendix, Fig. S4). Additional checks show that reported vote choice is not conditional on perceptions of our partner (SI Appendix, Table S2) or expectations about privacy (SI Appendix, Table S3).

Turnout.

The treatment could have influenced which citizens reported voting (3, 11), so we first consider how information affected reported turnout. The treatment had no detectable average effect on turnout (SI Appendix, Table S10). We further show that treatment effects reported below on votes for the incumbent are robust to including a lack of turnout as a nonpositive outcome (SI Appendix, Table S11). Further explanation is in SI Appendix, Turnout and Estimates of Vote Choice.

Vote Choice.

We expected that when citizens received good (bad) news about politician performance, they would be more (less) likely to vote for incumbents. Like other Metaketa I studies (9), we examine the effects of receiving good news and bad news separately. The subsets of subjects are defined by whether the information that voters were eligible to receive was better or worse than what they believed at baseline or, if the budget information matched their pretreatment beliefs, whether it was above or below the median district performance (see SI Appendix, Table S5 for analysis without priors). A detailed accounting of the match between this analysis and our preanalysis plan is in SI Appendix, Pre-Registration.

Fig. 1 displays the core results on reported vote choice and confidence intervals on the estimated treatment effects among subjects who reported turning out and who voted in elections without party switching or redistricting. This is to minimize ambiguities to the definition of incumbency (see SI Appendix, Tables S18–S21 for robustness).

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Fig. 1.

Treatment effects of budget disclosures by news type. The figure displays estimated treatment effects for all subjects and for respondents who reported seeing messages in the endline survey. Subgroup sample sizes and control group means are printed at right. All estimates exclude uncontested elections, elections with party-switching incumbents, and redistricted constituencies. Thick and thin bars show 90% and 95% confidence intervals, respectively. Full results are in SI Appendix, Tables S14 and S15.

For subjects eligible for good news, treated subjects were no more likely to report voting for the incumbent chair than placebo subjects. In contrast, treated subjects were ∼3% points more likely to report voting for the incumbent councillor than the placebo subjects.^‡ Likewise in the other direction, treated subjects eligible for bad news were not less likely to report voting for the incumbent chair, but they were around 3% points less likely to report voting for the incumbent councillor. In an augmented analysis, we find the effects were larger among verified respondents—subjects who said that they had seen our messages—and in the range of 5–6% points. SI Appendix, Tables S12 and S13 show the treatment effect by party and voter–incumbent alignment.

Information might not have affected votes for chairs because they represent larger constituencies and, unlike councillors, are not the primary contacts for constituents. Incentives for performance-based voting are often greatest in small constituencies because voters can more easily coordinate (2). Councillors’ smaller constituencies and their role as primary contacts at the district level might be the reason why citizens hold councillors responsible for budget management, despite chairs’ greater role in principle. Thus, our findings on citizens’ reward or punishment of councillors are consistent with literature on attribution in consolidated democracies (34, 35).

Additionally, elections for chair involve higher profile campaigns that disseminate information via rallies, flyers, and public media. Indeed, independent audits assess chairs as communicating better with their constituents than councillors (25). This dynamic could decrease voters’ likelihood of reacting to new budget information and increase chairs’ ability to diffuse responsibility for budget mismanagement. Also, chairs evince more stable tenure, perhaps due to increased resources for vote buying. Voters may thus feel less able to impact chairs’ elections and be more likely to rely on ethnicity or party as a coordination device. Our treatments may therefore have been too weak to overcome barriers to coordination or to compete with other sources of information in the chairs’ campaigns.

Treatment Density.

We expected larger treatment effects among those in high-density villages compared with low-density villages. Yet as Fig. 2 shows, we did not find evidence inconsistent with the null hypothesis for treatment density.

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Fig. 2.

The treatment effect of higher treatment density among treated subjects. The figure displays estimated treatment effects of being assigned to a high-density village among treated subjects. Subgroup sample sizes and control group mean are printed at right. All estimates exclude uncontested elections, elections with party-switching incumbents, and redistricted constituencies. Thick and thin bars show 90% and 95% confidence intervals, respectively. Full results are in Table 1.

There is, however, some evidence of information spillover. Table 1 shows the crossed impacts of the density treatment and the budget information treatment combined into one indicator with four levels. The baseline condition is a placebo subject in a low-density village. For placebo subjects in high-density villages, there is some evidence of negative spillover in the bad news condition, since they are less likely to vote for the incumbent than placebo subjects in the corresponding low-density villages. The treatment effects of bad news are similarly sized within low- and high-density subgroups. Given the indications of spillover to the placebo subjects, these results indicate that a 9% reduction in votes for the incumbent is the upper bound on the treatment effect of bad news disseminated at high density. These results provide some support for our hypothesis that higher treatment density encourages communication and coordination. The good news subgroup, however, does not yield results that are inconsistent with the null hypothesis.

The mixed effects of encouraging common knowledge to overcome coordination problems are largely consistent with the findings of related experiments. An experiment in Kenya showed that privately disseminated information about children’s education outcomes did not affect parents’ private or public actions, and the researchers hypothesized that publicly disseminated information would have also yielded null effects unless it raised expectations of collective action (7). Another study found an impact of information on vote choice only when many others were receiving the same information and when voters were provided civic education messages (36).