This paper surveys the extensive literature that seeks to estimate the effect of the initiative and referendum on public policy. The evidence on the referendum uniformly finds that requiring voter approval for new spending (or new debt) results in lower spending (or lower debt). The initiative process is associated with lower spending and taxes in American states and Swiss cantons, but with higher spending in cities. The initiative is consistently associated with more conservative social policies. Policies are more likely to be congruent with majority opinion in states with the initiative process than states without the initiative, suggesting that direct democracy allows the majority to counteract the power of special interests in policy making.
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Cross-county data are from Kaufman et al. (2010).
Following standard practice, and the Oxford English Dictionary, I use referendums as the plural rather than referenda.
Also called “compulsory” and “obligatory” referendum.
Also called “optional” or “popular” or “veto” referendum.
And at least 10 other states have flat limits on the aggregate amount of debt, meaning that exceeding the debt limit requires popular approval in the form of a constitutional amendment.
Summary information from Initiative and Referendum Institute (2017).
Numbers are from the Direct Democracy Database maintained by the International Institute for Democracy and Electoral Assistance, available at https://www.idea.int/data-tools/data/direct-democracy.
There are many reasons why median voter outcomes might not prevail: The pressure group models of Stigler (1971) and Peltzman (1976) show how policy responds more to preferences of organized groups; the Downsian model fails to produce convergence to the median when the issue space is multidimensional, there are more than two candidates, candidates are policy motivated, or there is a valence dimension; and the shirking models of Barro (1973) and Ferejohn (1986) show that elections put pressure on representatives to follow voter preferences, but not enough to cause them to entirely forego their own policy preferences.
Note that a mandatory referendum on spending cuts would have the opposite effect—leading to higher spending.
For example, Case 2a might represent a tax increase, and Case 2b might represent an increase in the minimum wage.
Matsusaka (2014) develops an empirical strategy to quantify the sizes of the direct and indirect effects, and finds evidence suggesting that the direct effect is larger than the indirect effect, at least for American states.
Matsusaka and Ozbas (2017) show how this property emerges under fairly general conditions.
Specifically: First, for the most part I have excluded working papers, on the principle that their findings have not yet undergone peer review. This is with regret, since some of these studies employ interesting and reasonably convincing methods of causal identification. Second, I have excluded studies that compare mean policy outcomes between jurisdictions without any control variables, because theory strongly suggests that controls for preferences need to be included. Third, I have excluded studies that estimate the effect of the initiative using interaction terms, but do not present estimates of the net effect of the initiative, or do not provide enough evidence to infer the net effect. Fourth, I omitted studies that rely entirely on a direct democracy index because it is not possible to separate initiative and referendum effects and thus lack theoretical coherence, as discussed in Sect. 4. Finally, I have excluded a small number of studies with findings that are known to be spurious based on subsequent research or that employ methods that are problematic.
To be precise, Asatryan (2016) uses the signature requirement as an instrument for the use of initiatives. For the purposes of this survey, I interpret those findings to be based on variation in signature requirements, although those specific results are not reported in the article.
The two papers in Panel C of Table 4 using international evidence provide somewhat contradictory evidence, but the papers contain little basis for determining whether the differences are explained by different sample periods, different definitions of initiatives, or something else. These papers also contain fairly weak controls for citizen ideology, culture, and similar factors that might generate spurious correlations, so it does not seem productive to speculate at length about those findings.
For example, the large literature on fiscal externalities argues that legislators prefer excessive spending because pork-barrel projects provide concentrated benefits to their constituents, while the costs are spread over the taxpayers at large (Buchanan and Tullock 1962; Weingast et al. 1981; Gilligan and Matsusaka 1995, 2001; Bradbury and Crain 2001; Baqir 2002). The bureaucratic budget-maximizing model of Niskanen (1971) also implies a propensity for government to spend more than voters prefer.
Fiscal data from State and Local Government Finances, published by the Census.
Following the literature, I omit Alaska and Wyoming, which are outliers because of significant severance tax revenue.
While hazard models have their virtues, the underlying assumption that policy making is a one-way trip—all states eventually adopt a policy and never reverse themselves—is contrary to fact. For example, there have been numerous reversals in death penalty and same-sex marriage policies over time.
The lack of statistical significance for English-only stands in contrast to the findings of Schildkraut (2001). The sample periods differ, but given the much larger number of observations in Schildkraut (\(N = 630\)), my estimates are insignificant probably because of the small sample size (\(N = 50\)).
Theodore Roosevelt, “A Charter for Democracy,” speech to the Ohio State Constitutional Convention, February 21, 1912.
This pattern holds whether initiative states are defined if they allow (1) constitutional amendment initiatives, or (2) constitutional amendment or statutory initiatives. Following the literature, I classify Illinois as a non-initiative state (its initiative process is limited so that it cannot be used to address any of the policy issues in the dataset); Illinois’ classification does not change the results.
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This appendix explains why the congruence of jurisdictions with and without direct democracy cannot be compared from regressions of the form of Eq. (3). The discussion is adapted from Matsusaka (2001); see also Achen (1977) and Golder and Stramski (2010).
In a slight change in notation from the text, define congruence as
where x i is the policy outcome that prevails in jurisdiction i, and x * i is the policy outcome that the voter would like to prevail (in the text V = x *). The preferred policy x * could be the median voter’s ideal point, the majority position, or some other measure.
Now suppose that x * cannot be observed, but that the researcher has access to a public opinion variable P that is correlated with x * according to x * = f(P), where f is an increasing function. For example, the policy is the income tax rate and P is an ideology index or a vector of demographic variables. Critically, while we know that x * and P are correlated, we do not know the precise functional form of f. Because P and x are measured on different scales (5) cannot be implemented. Consider instead a regression of the form
where a and b are coefficients to be estimated. The coefficient on the proxy for constituent preferences, b, is sometimes referred to as “responsiveness” in the literature. The question is: what is the formal connection between responsiveness b and congruence? The answer is: none, in general.
Consider Fig. 8. In a perfectly congruent world, the policy would be x = x *, and all observations would lie on the f function: x = f(P). In such a case, there would be a positive relation between outcomes and the preference proxy, and regression (6) would yield b > 0.
Now consider comparisons of congruence between jurisdictions with and without direct democracy. Denote the two groups we would like to compare as G DD and G 0. We would like to measure the mean of CONG = − |x − f(P)| for each group, but f is not observable. Suppose instead that equation (6) is estimated separately for each group, producing responsiveness coefficients b DD and b 0 (or, as is more common in practice, a single regression is estimated with an interaction term that allows the coefficient on preferences to vary by group). What can we learn about relative congruence from a comparison of the two coefficients?
Figure 8 shows a hypothetical case. The cluster of points G DD represents opinion-outcome observations for one group and the cluster labeled G 0 represents observations for the other group. Note that in this example, (1) the policy outcomes for group G 0 are less congruent (more distant) with public preferences than the outcomes for group G DD , but (2) if regression (6) is estimated separately for the two groups, we would find b DD < b 0 (or, in an interaction framework with G 0 as the null and G DD as the interaction, we would find a negative coefficient on the interaction term). In this case, the regression estimates of b are inversely related to congruence. It is straightforward to construct examples in which the regression estimates of b are positively correlated with congruence. The implication is that the coefficient b is not an indicator of congruence, and therefore regressions (6) do not permit comparison of congruence between the two groups.
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Matsusaka, J.G. Public policy and the initiative and referendum: a survey with some new evidence. Public Choice 174, 107–143 (2018). https://doi.org/10.1007/s11127-017-0486-0