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Trial Title
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Electoral Rules vs. Voter Psychology: Fiscal Accountability in Theory and Experiment
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Fiscal Accountability: Institutional Discipline and Behavioral Frictions
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Trial Status
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completed
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on_going
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Abstract
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We develop and test a model of fiscal accountability in which parties compete over a full fiscal platform: taxes, public goods, and political rents. Our theory predicts that disproportional electoral rules, by raising the stakes of winning, discipline politicians and lead to higher provision of public goods and lower corruption and taxes in equilibrium. We tested this mechanism in a laboratory experiment with human subjects as candidates and voters. The results provide causal evidence for this core mechanism in our experiment, where disproportional rules significantly reduce corruption and increase public goods. However, this institutional discipline is attenuated by two behavioral frictions. First, a partisan shield allows voters to tolerate high corruption from ideologically aligned candidates. Second, candidates learn to execute a public–good gambit, compensating voters for high rents with increased public spending funded by higher taxes. Our integrated approach shows that while electoral rules are a powerful discipline tool, their effectiveness is fundamentally constrained by the psychological trade-offs voters are willing to make.
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After
We study fiscal accountability in a laboratory election environment in which candidates compete over a full fiscal platform consisting of a budget and its allocation between a public good and private rents. The theory predicts that more disproportional power-sharing rules raise the electoral stakes of winning and therefore discipline rent extraction. The experiment is designed to test five hypotheses. First, greater power-sharing disproportionality should reduce corruption, increase public-good provision, and improve aggregate voter welfare. Second, if voters behave fully rationally, human voters should not differ from automated utility-maximizing voters. Third, explicit disclosure of rents should not matter when voters can infer rents from the budget constraint. Fourth, greater disproportionality should weaken the rent-increasing effect of stronger partisanship. Fifth, away from equilibrium, a candidate may sustain higher rents by bundling them with higher public-good provision when the benchmark platform provides too little of the public good relative to the socially efficient benchmark. We implement seven laboratory treatments at Tianjin University with 346 student subjects. Main outcomes are candidate policy choices, vote choice and vote share, and aggregate voter welfare.
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Trial Start Date
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October 29, 2024
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October 15, 2024
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Trial End Date
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December 19, 2024
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May 15, 2026
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JEL Code(s)
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C90, D72, D73.
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C91; D72; H11; H41
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Last Published
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August 18, 2025 06:40 AM
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April 15, 2026 09:36 AM
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Intervention (Public)
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The treatments were designed to address distinct dimensions of the model: the relationship between electoral outcomes and power-sharing, the role of transparency in fiscal policy, and the implications of voter behavior. Specifically, the first treatment implemented a proportional power-sharing rule, where policy-making power was directly proportional to the vote shares received by each candidate.
The second treatment replicated the proportional rule of the first treatment but replaced human voters with automated algorithms, aligning with the methodology commonly used in the experimental literature on electoral competition. This allowed for a closer comparison with existing studies, which often focuses exclusively on candidates' decisions, while isolating the effects of automated versus human decision-making on electoral outcomes.
The third treatment, like the first, used a proportional rule but added full transparency by explicitly informing voters about all elements of fiscal policy, including allocations to both public goods and rents. This treatment was designed to investigate how transparency affects voter accountability and candidate behavior. In the other three treatments only partial information about taxes and public good was released to the electorate in each round, leaving voters to infer corruption levels from the budget constraint.
Finally, the fourth treatment was identical in most respects to the first, but with a key modification: policy-making power responded more than proportionally to vote shares, particularly for the candidate receiving a majority of votes. This allowed us to examine how changes in the payoff structure influenced candidates' strategic behavior and voters' decisions.
The selection of these four treatments strikes a balance between theoretical relevance and empirical feasibility. While the theoretical model generates a wide array of hypotheses, these four treatments were chosen to focus on the most salient aspects of the research exercise and to address gaps in the existing literature. They capture critical mechanisms such as power allocation, transparency, and voter behavior, all while ensuring the experimental design remains practical in terms of complexity and session length.
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This is a laboratory experiment implementing a three-stage election game. In each of 25 periods, two candidates simultaneously propose a fiscal platform. The platform consists of a budget or tax rate and an allocation of that budget between a public good that benefits all voters and a private good interpreted as political rents. Five voters then observe the platforms and vote for candidate A or candidate B. The electoral outcome determines political influence through a power-sharing rule.
The design includes seven treatments:
Treatment T1 (Baseline) implements the model with a proportional power-sharing rule, low partisan intensity, human voters, and partial fiscal transparency, where voters observe only the proposed tax and public good levels and must infer corruption from the budget constraint.
Treatment T2 (Automated Voters) is identical to the baseline, except that the five human voters are replaced by five automated agents programmed to vote sincerely for the party offering them the highest utility. Comparison between T1 and T2 tests Hypothesis 2.
Treatment T3 (Transparency) is identical to the baseline, except that voters are explicitly shown the level of rents proposed by each candidate. Comparison between T1 and T3 tests Hypothesis 3.
Treatment T4 (Disproportional Rule) is identical to the baseline, except that it implements a more disproportional power-sharing rule. The comparison between T1 and T4 provides a direct test of Hypothesis 1.
Treatments T5--T6 (Disproportionality--Partisanship Interaction) replicate the proportional and disproportional power-sharing rules under stronger partisan intensity. Together with T1 and T4, they form a two-by-two factorial design that varies the electoral rule and the strength of partisan bias, providing a direct test of Hypothesis 4.
Treatment T7 (Public-Good Gambit) is a scripted-candidate election treatment in which the candidates' platforms are pre-programmed by the computer. In each round, five human voters observe the two platforms under full transparency and cast their votes, so the electoral outcome continues to depend on aggregate voter support. The scripted platform pairs are organized around two benchmark environments: one in which the benchmark platform provides the socially efficient amount of the public good, and one in which the benchmark platform provides too little of the public good. In each environment, the opposing scripted platform combines a fixed increase in rents with different amounts of additional public-good provision.
The experiment uses a common theoretical calibration in which both private consumption and public-good benefits are valued with diminishing marginal returns, there is no office rent or valence advantage built into the candidates, income is fixed across participants, and partisan bias is introduced through an individual-specific predisposition toward one of the candidates. Some treatments use weaker partisan bias and others use stronger partisan bias.
Hypothesis 1 (H1):Greater power-sharing disproportionality is expected to promote stronger fiscal discipline. Under the disproportional rule treatment, relative to the proportional baseline, we predict that candidates will propose lower levels of corruption, greater provision of public goods, and, as a result, higher aggregate voter welfare.
Hypothesis 2 (H2): Policy payoffs lead voters to electorally punish rent-seeking behavior and reward public-good provision. Under the assumption of voter rationality, we predict no significant differences between a treatment with automated utility-maximizing voters and a baseline with human voters.
Hypothesis 3 (H3): Greater fiscal transparency does not necessarily improve voter accountability. Under the assumption of voter rationality, we predict that equilibrium policy will be similar in a treatment where political rent levels are explicitly disclosed to voters and in a baseline where corruption must be inferred from the budget constraint.
Hypothesis 4 (H4): Greater disproportionality weakens the rent-increasing effect of stronger partisanship. When the electoral rule and partisan intensity are varied independently, we predict that the increase in corruption caused by stronger partisanship will be smaller under the disproportional rule than under the proportional baseline.
Hypothesis 5 (H5): The electoral viability of the public-good gambit depends on whether public-good provision at the benchmark platform is already socially efficient. Comparing candidate vote shares across scripted platform pairs, we predict that combining higher rents with additional public goods should not improve electoral support when the benchmark platform already provides the efficient amount of the public good, but can improve support when the benchmark platform provides too little of the public good and the increase in public-good provision is large enough.
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Intervention Start Date
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October 29, 2024
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October 15, 2024
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Intervention End Date
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December 19, 2024
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May 15, 2026
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Primary Outcomes (End Points)
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Corruption level, Public good level, Tax level.
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Candidate policy choices: proposed political rents or corruption, proposed public-good provision, and proposed budget or tax rate. Electoral outcomes: candidate vote share and individual voter choice. Aggregate voter welfare. In the scripted-candidate treatment, vote share and individual support for the deviating platform.
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Primary Outcomes (Explanation)
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The primary outcomes map directly to the five hypotheses in the paper. Candidate policy choices test whether institutional rules affect rent extraction, public-good provision, and budget size. Vote choice and vote share test voter accountability, the effects of transparency, the comparison between human and automated voters, and the electoral viability of the public-good gambit. Aggregate voter welfare tests whether the disproportional rule improves welfare relative to the baseline.
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Experimental Design (Public)
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Before
Each experimental treatment consisted of two independent sessions, each lasting 25 periods. Each period simulated an election involving two candidates (labelled A and B) and five voters (denoted as 1, 2, 3, 4, and 5). While longer sessions with 50 or 60 periods are common in experimental studies on elections, we opted for shorter sessions due to the inclusion of human voters instead of computer algorithms.
Human voters increased the time required for each election, as candidates made their decisions first, followed by the voting process, during which all five voters cast their votes independently. To manage session length while ensuring robust data collection, we maintained the smallest meaningful number of voters per election. This constraint was relaxed in treatment 2, where voters were replaced by computer algorithms, allowing a more streamlined process focused on candidates’ behavior.
At the start of each session, 28 participants were randomly and anonymously assigned the role of either ``candidate'' or ``voter.'' These roles remained fixed throughout all 25 elections. Participants were informed of their own roles but not the identities of others they were matched with. In treatment 2, the number of participants was reduced, as voters were automated, and only 8 human subjects were assigned the roles of candidates A and B (see Table~\ref{tab-lab_overview} for further details).
Within each election, participants were randomly assigned to one of four groups, each consisting of seven members. Although group composition changed between elections, the initial role (candidate or voter) of each participant remained fixed. For instance, a participant assigned the role of candidate A in group 1 during the first election might be candidate A in group 3 in the second election, and so forth. The same applied to voters, except in treatment 2, where the electorate was automated. Group re-matching was implemented in each period to mitigate potential collusion among candidates and voters.
The experimental design employed neutral language to avoid introducing unintended positive or negative connotations unrelated to the incentive structure. For example, participants assigned the role of candidates were instructed to make two decisions in each election: (a) a budget, representing a percentage (a number between 1 and 99) of the total voter income, set at 100 Experimental Currency Units (ECUs); and (b) an allocation of the collected income between good 1, which benefits all voters equally, and good 2, which benefits only the candidates.
Voters observed the budget and proposed spending on good 1 from each candidate before independently voting for their preferred candidate (A or B). In treatment 3, voters were also explicitly informed about the spending on good 2. This variation in the information setting enabled an assessment of how voters respond differently to scenarios where fiscal misuse is explicitly disclosed compared to cases where they infer such misuse indirectly from other fiscal policy components. This comparison highlights the role of transparency in fostering accountability and the challenges voters face in less transparent settings.
Participants were informed about their payoff structure at the beginning of the session. Candidates’ payoffs depended on the number of votes their proposed budget and allocation received, which determined their ``share of power.'' Power directly influenced their earnings from the amount allocated to good 2. In most treatments, power was proportional to the number of votes received. For instance, if a candidate received three votes out of five, their power share was 0.6. However, in treatment 4, power increased disproportionately with the percentage of votes received, allowing us to examine how non-linear returns affect candidates’ strategic decisions and competition for voter support.
Voters’ payoffs were determined by their net income, the benefit derived from good 1, and their candidate bias. Initial incomes were randomly assigned, with voters 1–4 receiving values between 18 and 25 ECUs, and voter 5 receiving the remainder of the group’s total income (100 ECUs). A candidate’s proposed budget affected voters’ net incomes. For instance, if a voter’s initial income was 25 ECUs and a candidate proposed a budget of 32\%, the voter’s net income would be \( (100-32)\% \times 25 = 17 \) ECUs. Candidate bias, a randomly assigned value between \([-0.25, 0.25]\), influenced voters’ payoffs by favouring one candidate over the other, independent of policy proposals.
To assist participants in evaluating their decisions, an `expected payoff calculator' was provided on the decision screen. This tool allowed subjects to experiment with different combinations of their own and others’ choices to observe the resulting per-period payoffs. Participants could use the calculator as many times as needed before making their decisions. A log-sheet was also provided for participants to track their earnings throughout the experiment, helping them better understand how different decisions impacted their payoffs in previous rounds.
Control questions were administered at the start of each session to ensure participants understood the instructions. After the final election period, and before receiving payment, participants completed a post-experiment survey. The survey included questions about their experience during the experiment, their decision-making process, and related factors. Responses were anonymized and did not affect participants' per-period payments.\footnote{A copy of the lab instructions, the control questions, and the post-experiment survey are available from the authors upon request.}
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The experiment implements the election game from the model over 25 repeated periods. Treatments T1 through T6 involve two candidates and five voters in each electoral interaction, except that T2 replaces the five human voters with automated voting agents. In T1 and T3 through T6, subjects are randomly re-matched each period into groups of seven, consisting of two candidates and five voters. In T2, each group consists of two human candidates paired with five computer algorithms. In T7, subjects are randomly re-matched each period into groups of five voters, while the two candidates' platforms are scripted by the computer. The election environment is preserved in T7 because aggregate voter support still determines the electoral outcome between the scripted platforms.
The treatment structure is designed to identify the effect of a disproportional versus proportional power-sharing rule, the difference between human and automated voters, the effect of explicit rent disclosure, the interaction between disproportionality and partisanship, and the off-equilibrium public-good gambit.
The design combines between-treatment variation with repeated within-subject play and random rematching across periods. The main comparison for institutional discipline is between T1 and T4. The comparison between T1 and T2 tests voter rationality. The comparison between T1 and T3 tests transparency. Treatments T1, T4, T5, and T6 form a two-by-two factorial design in the power-sharing rule and partisan intensity. T7 isolates voter responses to scripted platform pairs in a fully transparent environment.
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Randomization Method
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Randomization by computer
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Computerized randomization. Within treatments, participants are randomly re-matched across periods by the experimental software. Treatment assignment should be recorded at the session level to avoid contamination across treatments; if the current registry already lists the exact session-level procedure, retain that wording.
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Randomization Unit
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Individual level
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Primary treatment variation: experimental session. Within-session rematching: group composition is randomized each period. In T7, scripted platform pairs are assigned by the computer across rounds.
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Planned Number of Clusters
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32 groups
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56 groups
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Planned Number of Observations
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800 observation at the candidates level, and 4000 observation at the voter level.
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1200 observations at the candidate's level, and 6250 observations at the voter level.
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Sample size (or number of clusters) by treatment arms
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200 candidate-level elections, and 1000 voter-level in the control treatment; 600 candidate-level and 3000 voter-level in the other three treatments.
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Each treatment has at least two sessions with 56 subjects (16 candidates and 40 voters) and 25 rounds. Therefore, the minimum sample size is (8*25*6=)1200 (winners of the elections) for the candidate analysis and (20*25*10+25*25*2=)6250 for the voting analysis.
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Keyword(s)
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Electoral
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Electoral, Governance
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Secondary Outcomes (End Points)
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Responsiveness of voting to utility differences and to differences in rents, public-good provision, and taxes. Interaction between partisan bias and policy responsiveness, which captures the partisan-shield mechanism. Treatment interactions between disproportionality and partisan intensity. Time trends and learning in candidate policy choices across rounds.
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Secondary Outcomes (Explanation)
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These outcomes are used to study behavioral frictions that mediate accountability, including whether human voters are less punitive toward corruption than automated voters, whether transparency changes the weight voters place on policy differences, whether stronger partisanship weakens accountability, and whether candidates learn over time to adjust the composition of the budget.
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