Government Turnover and the Effects of Regime Type

Abstract

Incumbents voluntarily leaving office after losing elections is a hallmark of democracy. Hence, the most prominent binary democracy measure (Democracy–Dictatorship/Alvarez–Cheibub–Limongi–Przeworski [DD/ACLP]) requires observed alternation in power to score regimes democratic. Such “alternation rules” may, however, lead to underestimating democracy’s effect on economic growth. As strong economic performance reduces the probability of incumbents losing democratic elections, young democracies with high growth may falsely be coded dictatorships; their popular governments have yet to lose an election. We identify the expected bias using different tests, for example, when following Przeworski et al.’s advice to re-estimate relationships after re-coding multi-party regimes without alternation as democratic, or when employing differences in information about alternation from different time points to contrast original DD estimates with our “real-time” DD estimates. We present resembling arguments on how alternation rules may bias democracy’s estimated relationships with civil war onsets and coups, but find fewer empirical indications of biases here.

Keywords

democratization and regime change politics of growth/development non-democratic regimes political economy political regimes

Introduction

Numerous democracy measures exist, drawing on different conceptualizations of democracy and using different indicators and aggregation methods (see, for example, Coppedge et al., 2011; Munck & Verkuilen, 2002). Although most measures correlate highly, choosing one over another can affect conclusions drawn in empirical work. Applying the Polity, Freedom House, and Vanhanen’s Polyarchy indices, Casper and Tufis (2003) report that only three of nine investigated determinants of democracy are robust. Cheibub, Gandhi, and Vreeland (2010) show that choice of measure also matters for estimates on how democracy affects economic growth (see also, for example, Krieckhaus, 2004) and civil war onset (see also, for example, Vreeland, 2008). In this study, we caution against the uncritical use of measures applying observed government alternations to identify democracy when turnover is endogenous to the outcome (or determinant) of democracy under study. We focus on the widely used Democracy–Dictatorship (DD)—or Alvarez–Cheibub–Limongi–Przeworski (ACLP)—measure. Identifying whether elections exist, and whether they are contested, are critical coding tasks, and the original DD coding scheme requires that regimes are scored as democratic only if at least one alternation in power (after an incumbent election loss) has occurred. We argue that this requirement—the alternation rule, henceforth—may induce particular biases when investigating effects of democracy, focusing on how it underestimates the effect on economic growth.

ACLP/DD was introduced in Alvarez, Cheibub, Limongi, and Przeworski (1996) and elaborated on in Przeworski, Alvarez, Cheibub, and Limongi (2000) and in Cheibub et al. (2010), who also provided updated data. Numerous high-profile publications use it to investigate, for example, how income inequality (Houle, 2009), oil resources (Haber & Menaldo, 2011), and Islam (Potrafke, 2012) impact on democracy, or how democracy affects, for example, states’ credit access and credit ratings (Beaulieu, Gary, & Saiegh, 2012), transparency (Hollyer, Rosendorff, & Vreeland, 2011), and gender inequality in education (Cooray & Potrafke, 2011). Highlighting the importance of using objective and minimalist measures, Cheibub et al. make a convincing case for DD. The clear coding rules leave little room for subjective judgments, and thus unsystematic errors, giving DD a reliability-edge over measures such as Polity and Freedom House. Furthermore, Polity and Freedom House involve multiple components and indicators, whereas DD draws on a minimalist democracy concept centering on contested elections. DD has been central in the study of links between income and democracy. In their seminal study, Przeworski et al. use DD to investigate how democracy affects growth, reporting little or no effect. Although several later contributions using different measures report a positive relationship (e.g., Baum & Lake, 2003; Gerring, Bond, Barndt, & Moreno, 2005; Papaioannou & Siourounis, 2008), the results in Przeworski et al. remain widely acknowledged. One reason is skepticism toward employing “maximalist measures”; factors like executive constraints (dominant component of Polity) or low corruption (indicator in Freedom House) may drive correlations with growth, and there is no consensus on whether they are part of the democracy concept.

Below, we show how the alternation rule embedded in DD may induce biases when estimating how democracy affects growth. In doing this, we highlight how high growth helps incumbents remain in power in young democracies. As the economic voting literature indicates (see Lewis-Beck & Stegmaier, 2000), democratic governments are less likely tossed out by voters when growth is high. Hence, fairly young democracies may fail to pass the alternation rule not because they are autocratic but because they have economically well-performing governments. Young democracies presiding over very high growth are therefore at particular risk of being falsely classified as dictatorships.

We first describe DD, focusing on the alternation rule. Thereafter, we discuss why this rule may lead to biased results on democracy and growth, first considering the case of Botswana before presenting the general argument. Thereafter, we design different tests to evaluate the expected bias. For example, we follow the advice of the authors of DD, and re-estimate the democracy–growth relationship using DD but relaxing the alternation rule. We also compare DD-based results with results generated by another minimalist democracy measure (Boix, Miller, & Rosato, 2013) not relying (solely) on alternation for coding contested elections. Furthermore, we investigate the bias by re-coding DD, using all original coding rules but varying the (hypothetical) year of measurement: We compare estimates from regressions based on data from, say, 1946-1990 using “real-time” coded DD (using government alternation information available in 1990) with regressions on identical observations but applying current information. This allows us to investigate how estimates change as history unfolds and we learn about the true nature of regimes, with errors in DD being corrected; all new democracies start out as being coded dictatorships because it, inevitably, takes time before government alternations occur. These and other analyses indicate the baseline DD measure may underestimate the effect on growth. We also discuss and test whether resembling biases affect estimates of democracy’s impact on coups d’état and civil war onsets, finding only inconclusive evidence for these relationships.

Contestation and the Alternation Rule

DD explicitly draws on a minimalist democracy concept with contestation as the only component. Contested multi-party elections is the (necessary and sufficient) institutional requirement for being considered democratic. Przeworski et al. (2000) define democracy simply as a regime where “those who govern are selected through contested elections,” which are repeated elections characterized by “ex-ante uncertainty” and “ex-post irreversibility” (pp. 15-16). Different researchers have criticized such minimalist definitions, contending that democracy is a multi-faceted concept (see, for example, Munck & Verkuilen, 2002). Yet, its proponents argue in favor of a minimalist, procedural definition, in part, because of its implications for reliable operationalization. As highlighted by Cheibub et al. (2010), democracy indices relying on more complex multi-dimensional concepts run into problems of “subjectiveness and arbitrariness” (p. 75). The benefits of a minimalist definition relates to precision and stringency, enabling “objective” measurement.¹

The logical structure of DD is uncomplicated: A regime classifies as democratic if and only if it passes four rules. The first rule is “[t]he chief executive must be elected,” and the second is “[t]he legislature must be elected” (Przeworski et al., 2000, p. 15). The third is “[t]here must be more than one party,” and this is extended to consider whether governments subsequently established no-party or one-party rule, or permanent electoral domination (Przeworski et al., 2000, pp. 20-22).

However, observing de facto contestation is difficult. Several autocracies hold multi-party elections that are neither free nor fair, where the opposition has little chance of obtaining power (e.g., Levitsky & Way, 2010; Schedler, 2006). Trying to combine coding rules that are “objective,” and thus reliable, with the difficulties of observing contestation leads to the fourth DD rule: “[A]n alternation in power under electoral rules identical to the ones that brought the incumbent to office must have taken place” (Cheibub et al., 2010, p. 69).² The underlying logic of this rule is that regimes—or should one perhaps say governments—must prove they are democratic through accepting an election loss and stepping down. Although many governments publicly state they are democratically minded, observers cannot know this before they are forced to reveal their preferences through losing an election. If a regime observes post-electoral alternation, DD provides the democracy score retrospectively for all years operating under the current set of electoral rules. This leads Cheibub et al. (2010) to re-code the original Alvarez et al. (1996) score for Bangladesh for 1986-1990, not because they use different rules but because they have obtained new information (government alternation in 1996).

Scoring whether elections are contested or not may thus lead to “Type I errors”—coding non-democracies as democracies—and “Type II errors”—coding democracies as non-democracies. The alternation rule is explicitly constructed to minimize Type I errors, thereby also increasing chances of Type II errors. Alvarez et al. (1996) and Cheibub et al. (2010) are clear that the alternation rule may lead to errors by assigning the dictatorship-label to democracies with governments that have yet to lose elections.³ Still, given that the counter-factual (What would the government have done had it lost an election?) is unobservable, they consider it preferable to be cautious with assigning the democracy label. This leads, for instance, to Botswana and South Africa being coded as dictatorships by (baseline) DD, because the Botswana Democratic Party (BDP) and the African National Congress (ANC), respectively, have yet to lose elections. Furthermore, if DD had been coded in, say, the late 1980s, Japan would have been scored as dictatorial, due to the Liberal Democratic Party’s (LDP) electoral dominance until 1993. In Western Germany, it took until 1969 for the Christian Democratic Union (CDU) led government to lose power through election. Hence, DD may sometimes classify genuine democracies as dictatorships simply because their governments remain undefeated in (truly contested) elections. Although this has long been recognized, we argue it is more consequential than previously supposed.

One beneficial property of DD and the alternation rule is that we know in which direction measurement errors likely are; potential Type II cases are even identified in the original data sets. Furthermore, the DD data set provides disaggregated indicators for individual components. This not only allows re-coding the measure according to ones preference, as explicitly suggested by Alvarez et al. (1996) and Cheibub et al. (2010), but also to analyze the consequences of particular errors. Unfortunately, few researchers have followed the advice from the authors of ACLP/DD in checking whether re-coding potential Type II regimes matters. Below, we elaborate on when and why this is crucial, and propose novel ways to test for “alternation-rule-induced” biases.

Why the Alternation Rule May Yield Biased Estimates of Democracy’s Effect on Growth

The probability of making Type II errors may be endogenous to the correlates of democracy we are interested in studying. We show how this applies to economic growth, and how the alternation rule can therefore lead to underestimating the effect of democracy. First, we consider a particularly illustrative case.

Botswana

Przeworski et al. (2000) report that among all regimes with data, the current Botswanaian presided over the fastest growing economy; from 1966 to 1990, Botswana’s annual gross domestic product (GDP) growth was 9.6%. Using data from Maddison (2007), Botswana’s (per capita [p.c.]) income increased more than 10-fold from 1966 to 2008, from US$473 to US$4,769 (1990 US$, purchasing power parity [PPP]–adjusted). Although its diamond reserves are often considered an enabling condition, abundance of diamonds has not contributed to high growth in countries such as Sierra Leone and the Democratic Republic of the Congo (World Bank, 2003). In line with analysis of the institutional contingencies of the “Resource Curse” (Mehlum, Moene, & Torvik, 2006), Botswana’s benevolent institutional framework was arguably crucial in transforming resource abundance into productive investments and high growth (e.g., Acemoglu, Johnson, & Robinson, 2001). Case studies describe how its institutions incentivized politicians to pursue growth-enhancing policies, from prudent macroeconomic policies to productivity-enhancing public investment in education, health, and infrastructure (e.g., Danevad, 1995; Leith, 2005; Tsie, 1996).

The literature also highlights Botswana’s political successes, with free and fair multi-party elections and decent protection of civil liberties since independence. By many observers, Botswana was long considered one of few democracies in Sub-Saharan Africa (e.g., Bratton & Van de Walle, 1997; Lindberg, 2006). As of 2014, it remained one of eight African countries rated “Free” by Freedom House, and had a democratic Polity score (+8 in 2010). Botswana’s elections are single-constituency plurality elections, which reduce effective parties and promote single-party governments (G. B. Powell, 2000). The BDP has held a majority of parliamentary seats and votes in all elections since 1969, although its vote share has recently declined. Therefore, Botswana fails to pass the alternation rule, and is scored as dictatorial by DD. However, Botswana is explicitly highlighted as a potential Type II error—a genuine democracy misclassified as autocratic—by Alvarez et al. (1996). Case studies of Botswanaian politics then also indicate that the multi-party elections and wider political system have “induced the Government to be responsive to the interests of various segments of Botswana society” (Danevad, 1995, p. 401). Furthermore, there is “no constraints on the opposition, little visible repression, [and] no apparent fraud” (Alvarez et al., 1996, p. 10). Granted, the various BDP leaderships have never been forced to reveal their intentions on accepting election defeat, and one could speculate “whether elections are not held in Botswana only because the ruling party is certain to win them and whether the ruling party would yield office if it ever lost” (Alvarez et al., 1996, p. 10). Yet, few observers have questioned the freeness and fairness of Botswana’s elections, or its democratic credentials on other dimensions.

Thus, the BDP may consistently win elections—with the consequence that Botswana is scored as autocratic by DD—simply because it is popular among voters. Indeed, BDP’s popularity may stem, in large part, from the apt handling of economic policies, and resulting high growth. If there counterfactually would have been turnovers in Botswana, should the BDP have been less popular and lost an election, also the authors of DD would agree that Botswana is erroneously classified as dictatorial from de-colonization onward (and retrospectively re-code it as democratic). Hence, Botswana’s high growth may have contributed to it being falsely put in DD’s dictatorship category from 1966. Although Botswana is an extreme case, the suggested mechanism could work also in other countries failing the alternation rule, such as Montenegro, Namibia, and The Seychelles. Hence, analyses using (baseline) DD may underestimate the effect of democracy on growth: Some high-growing, young democracies are scored as dictatorial because their successful governments are too popular to lose elections. Indeed, had DD been coded some decades ago, several fast-growing post–World War II (WWII) democracies would have been coded as dictatorships. In Western Germany and Japan, post-war governments stayed in office for a long time, arguably in part because of popular economic policies and high growth.

Economic Voting and Government Alternation

Before returning to a general (and formal) version of our argument below, let us elaborate on one aspect indicated by the above story: Voters tend to re-elect governments when the economy performs well, and otherwise throw them out (see, for example, Duch & Stevenson, 2005; Hibbs, 1982, 2000; Lewis-Beck & Stegmaier, 2000; Pacek & Radcliff, 1995; G. B. Powell & Whitten, 1993).⁴ As noted in a survey of the field,

Economic conditions shape election outcomes in the worlds democracies. Good times keep parties in office, bad times cast them out. This proposition is robust, as the voluminous body of research reviewed here demonstrates. The strong findings at the macro level are founded on the economic voter, who holds the government responsible for economic performance, rewarding or punishing it at the ballot box. Although voters do not look exclusively at economic issues, they generally weigh those more heavily than any others, regardless of the democracy they vote in. (Lewis-Beck & Stegmaier, 2000, p. 183)

This result may stem from different mechanisms. First, retrospective voting—where voters use their votes to reward or punish politicians (e.g., Ferejohn, 1986)—may generate the observed correlation. Under this description, voters are past-oriented, receiving utility from either “throwing the rascals out” or signaling approval of incumbent performance without regarding how this affects future performance. A somewhat different explanation is that voters—who want to improve growth to increase future incomes—are future-oriented, using past performance as an information signal on the competencies of those in power (e.g., Besley, 2006). Assessing how competent governments are on economic policy is difficult. Despite numerous other shocks affecting the economy, voters should, however, generally anticipate a positive correlation between “competent economic governing” and outcomes such as growth—drawing inferences from prior performance may constitute one of few available heuristics for voters.

If the latter mechanism operates, past economic performance could yield particularly strong impetuses to vote for incumbents in young democracies without alternation. Voters in these regimes can only speculate what growth would look like under alternative governments, and thus have limited information for inferring how appropriate the oppositions proposed economic policies are. This might also make government “scare tactics” harder to disprove, leading voters to accept claims that the (inexperienced) opposition endangers the economy. Likewise, promoting the “experienced and proven” incumbent as a safe bet for voters becomes easier. One recent example comes from Botswana, where—following a surge in the opposition’s popularity—one BDP spokesman referred to the opposition party Umbrella for Democratic Change (UDC) as a “newborn baby,” while remarking the BDP had “been in the marathon for too long and results of our good governance are there for all to see” (Moyo, 2012). Similar rhetoric was, for example, also employed by the LDP in Japan. In high growth periods, “the LDP seemed a good bet for many Japanese to entrust their government to” (Krauss & Pekkanen, 2010, p. 7)—the LDP only lost power after the economy started tanking in the early 1990s. Thus, where the opposition has never ruled and the economy is performing well, risk-averse voters may heed incumbents’ advice not to vote for the incompetent opposition. Young democracies with few previous alternations may therefore display a particularly strong relation between past growth and incumbent success. Consistent with this, Brender and Drazen (2008) finds that the positive effects of growth on incumbent re-election prospects are particularly strong in new (and less developed) democracies.

We now return to our broader argument, concerning how such economic voting mechanisms contribute to us underestimating democracy’s effect on growth when using regime measures with alternation rules.

Modeling the Bias

To more precisely illustrate how the alternation rule may induce biased inferences on democracy and growth, we present a formal model. We let φ designate regime type characteristics. Following DD, we model φ as dichotomous. When φ = 0, we have a dictatorship where the ruler is intensely motivated by staying in power or where the institutional environment induces low costs of manipulating elections. When φ = 1, the regime is democratic; elections are freely and fairly conducted and the ruler will not or cannot stay in power after an election loss.

Furthermore, our regime measure $\bar{ϕ}$ is a function of actual regime type, φ, but also observed government alternation, a. Regime measures, such as DD, where both existence of democratic institutions (φ = 1) and alternation of government (a = 1) are necessary conditions for being scored as democratic ( $\bar{ϕ} = 1$ ) can be modeled multiplicatively (Goertz, 2005):

\bar{ϕ} = ϕ \cdot a .

We model growth, η, as a function of (actual) regime type, without making assumptions on the sign of $\partial η / \partial ϕ$ . To keep the model simple, we parameterize by using the linear specification,

η = b_{0} + b_{1} ϕ .

Finally, we model the determinants of government alternation, a. In practice, post-election alternation may occur in all electoral regimes; even manipulated elections inevitably carry some elements of uncertainty (see, for example, Levitsky & Way, 2010). Likewise, lack of alternation may occur even in democracies, as the opposition is never guaranteed a victory even when elections are perfectly free and fair. Nevertheless, we assume that $\partial a / \partial ϕ > 0$ . Still, a is a function also of growth, η, one core performance indicator for economic voting (Lewis-Beck & Stegmaier, 2000). Opposition parties have a harder time winning elections over incumbents perceived as economically competent in democracies, but also in dictatorships (see Magaloni, 2006). Hence, a = a(φ, η) and $\partial a / \partial η < 0$ . Again, we employ a linear specification and simplify by letting alternation happen whenever the probability of it exceeds a critical threshold c.⁵

\begin{matrix} a = 1 \Leftrightarrow β_{0} + β_{1} ϕ - β_{2} η \geq c \\ a = 0 \Leftrightarrow β_{0} + β_{1} ϕ - β_{2} η < c \end{matrix}

To explore how growth is affected by changes in the regime measure—that is, investigating $\partial η / \partial \bar{ϕ}$ —and how this differs from the actual effect—that is, $\partial η / \partial ϕ = b_{1}$ , we first rearrange Equation 2 so that $ϕ = (η - b_{0}) / b_{1}$ and insert this into Equations 1 and 3, before inserting the expression for a into Equation 1:

\bar{ϕ} = (\frac{η - b_{0}}{b_{1}}) \cdot (β_{0} + β_{1} (\frac{η - b_{0}}{b_{1}}) - β_{2} η) .

We algebraically manipulate this (see online appendix) before applying implicit derivation on the subsequent expression, considering η as a function of $\bar{ϕ}$ . The resulting expression for $\partial η / \partial \bar{ϕ}$ is

\frac{\partial η}{\partial \bar{ϕ}} = \frac{b_{1}^{2}}{(β_{1} + β_{2} b_{1}) \cdot 2 η + β_{0} b_{1} - 2 β_{1} b_{0} + β_{2} b_{0} b_{1}} .

From Equation 2, we know that the first derivative of growth with respect to (actual) regime type is b₁. When comparing this with the first derivative of growth with respect to the alternation-based regime measure from Equation 5, these are equivalent only when b₁ = 0—only then, regressions using $\bar{ϕ}$ to measure φ (on average) estimate the true effect on growth, namely, zero. If b₁ ≠ 0, regressions using $\bar{ϕ}$ yield biased estimates. We cannot even determine the sign of $\partial η / \partial \bar{ϕ}$ , a priori, even if b₁ > 0.⁶ Hence, regression models using alternation-based measures might estimate that democracy reduces growth even if democracy actually enhances growth. For other parameter values, $\bar{ϕ}$ would provide a positive, but downward biased, estimate. Nevertheless, we obtain a precise expression of the alternation-induced bias by subtracting the actual regime effect on growth (b₁) from the expression in Equation 5:

Bias = \frac{\partial η}{\partial \bar{ϕ}} - \frac{\partial η}{\partial ϕ} = \frac{b_{1}^{2}}{(β_{1} + β_{2} b_{1}) \cdot 2 η + β_{0} b_{1} - 2 β_{1} b_{0} + β_{2} b_{0} b_{1}} - b_{1} .

From this, we see that when η is very high, $\partial η / \partial \bar{ϕ}$ decreases, provided that b₁ > 0. Hence, when there is an actual positive effect of democracy, high growth rates lead us to underestimate this effect when using $\bar{ϕ}$ . One interpretation is that alternation will often not occur in true democracies with high growth rates, leading them to be miscoded as dictatorships. This, in turn, leads us to underestimate the effect of democracy on growth. Equation 6 shows that the alternation-induced bias also depends on the strengths of the relationship between regime type and alternation (β₁), the impact of growth on prospects for alternation (β₂), and democracy’s true effect on growth (b₁).

Empirical Analysis: The Alternation Rule and the Democracy–Growth Relationship

Przeworski et al. (2000) report no clear effect of democracy, as measured by DD, on growth.⁷ Several later studies using different regime measures—not relying as heavily on an alternation rule—have reported a positive relationship. Online Appendix Table A.1 reports characteristics, including regime measure used, of three widely cited such studies (namely, Baum & Lake, 2003; Gerring et al., 2005; Papaioannou & Siourounis, 2008). Yet, these studies differ from Przeworski et al. also on many other accounts than choice of regime measure. Providing a more controlled comparison, at least three studies (Cheibub et al., 2010; Knutsen, 2011b; Krieckhaus, 2004) have employed both DD/ACLP and other regime measures for otherwise similar specifications. As Table A.1 indicates, they generally report that models using DD provide less indications of a positive relationship between democracy and growth.

It could thus be that democracy actually enhances growth, and that estimates from regime measures relying on government alternation may be downward biased. We design different tests to check for this bias. Most notably, we use DD’s own coding criteria to create “real-time DD” measures, allowing us to investigate changes to estimates when potential Type II errors (democracies falsely coded dictatorships) are corrected by new historical information. Before that, we run other tests to provide indications on whether the above-theorized bias exists.

Preliminary Tests: Re-Coding Type II Regimes and Employing Different Democracy Measures

First, we simply investigate whether there are differences in average growth between the regime categories. Figure 1 shows that average GDP p.c. growth is 1.8 for all country-year observations classified as autocracies by DD and 2.5 for regimes coded as democracies. As expected, Type II regimes passing the three first DD rules, but failing the alternation rule, have a high average growth rate (3.0). Hence, these regimes, constituting $> 1 / 5$ of DD-coded dictatorships, have growth rates more similar to DD-coded democracies than other DD-coded dictatorships (1.6). Indeed, these regimes, on average, grow 0.5% faster than DD-coded democracies. If many Type II regimes are actually democratic—which they certainly need not be—(baseline) DD estimates will understate democracy’s effect on growth. Yet, Type II regimes may grow faster because of other characteristics conducive to high growth, and we therefore investigate the proposed bias by running regression models.

Figure 1.

Average GDP p.c. growth for country-year observations from different regime categories: 1946-2008.

Our baseline is an ordinary least squares (OLS) model adjusting for panel-level heteroskedasticity, panel-specific first-order autoregressive (AR(1)) autocorrelation, and contemporaneous correlation. There is no consensus on how to specify models investigating the effect of democracy on growth (see Doucouliagos & Ulubasoglu, 2008). We present a fairly parsimonious specification, but the findings relevant for our argument—on the direction and size of the alternation-rule-induced bias—are fairly robust to control variable and lag-length specifications.⁸ GDP p.c. growth in percent is the dependent variable. We include Ln GDP p.c. (level) to control for convergence effects (Barro & Sala-i Martin, 2004), and that income may affect democratization and democratic stability (e.g., Przeworski et al., 2000). Second, we include Ln population, because population size may affect market specialization and economies of scale, and thus growth (Romer, 1990), and possibly regime type (Dahl & Tufte, 1973). Income and population data are from Maddison (2007). Third, high ethnic fractionalization may depress not only growth (Easterly & Levine, 1997) but also democratization prospects and democratic durability (Alesina, Devleeschauwer, Easterly, Kurlat, & Wacziarg, 2003). Hence, we add Alesina et al.’s Ethnic Fractionalization Index, ranging from 0 to 1. Fourth, we include region dummies, because geographic, cultural, and political-historical factors related to specific regions may impact on both regime type and growth (see, for example, Acemoglu, Johnson, Robinson, & Yared, 2008). Finally, we add decade dummies; different decades have been associated with varying global growth rates (Maddison, 2007) and varying democratization patterns (Huntington, 1991).

We lag the independent variables 5 years to account for likely delays in effects on growth. Although the exact lag length is unknown, Papaioannou and Siourounis (2008) report that the growth effect from democratization experiences peak and stabilize after 3 years, whereas Clague, Keefer, Knack, and Olson (1996) and Rock (2009) indicate even longer lags for effects on property rights protection and corruption, respectively. Hence, we suspect the traditional 1-year lag is too short to capture substantive effects. Yet, effects could manifest in less than 5 years, leading us to effectively mix, for example, observations from young democracies with those from autocracies. Thus, we also test models with 1- and 3-year lags.

Model I in Table 1 runs this baseline specification, with DD as regime measure, on 6,873 observations distributed over 156 countries and maximum time series (on dependent variable) from 1951 to 2008. The DD coefficient is only 0.18—suggesting that GDP p.c., on net, grows 0.18% faster in democracies than in dictatorships, holding the controls constant. However, democracy is not systematically related to growth in this regression (t = 0.8). Model II is similar to Model I except for coding all regimes passing the three first DD rules as democracies; some Type II regimes may be democracies that have yet to observe alternation due to popular incumbent governments presiding over high growth. Indeed, Model II using re-coded DD reports an estimate almost 4 times the size of that in Model I (0.69 vs. 0.18). Furthermore, the coefficient turns highly significant (t = 3.4), although we should remind that the high estimate, in this model, could stem both from high-growing electoral authoritarian regimes being falsely coded as democracies (Type I errors), and from the correction of Type II errors. Nevertheless, we highlighted Botswana as one notable high-growing Type II regime. When re-running our baseline Model I, and re-coding only the Botswanaian regime as democratic (Model III), DD increases by 60% (from 0.18 to 0.29) and the t value from 0.8 to 1.4.

Table 1.

Testing for Alternation-Rule Bias in the Estimated Effect of Democracy on Growth.

	Model I	Model II	Model III	Model IV	Model V
	Baseline DD	Re-coded DD: All Type II democratic	Re-coded DD: Botswana democratic	Baseline DD on BMR sample	BMR regime measure
	b/(t)	b/(t)	b/(t)	b/(t)	b/(t)
Democracy	0.175	0.693****	0.287	0.219	0.441**
Democracy	(0.81)	(3.36)	(1.35)	(1.02)	(2.18)
Ln GDP p.c.	−.0343	−0.409*	−0.356	−0.326	−0.349
Ln GDP p.c.	(−1.43)	(−1.78)	(−1.49)	(−1.37)	(−1.47)
Ln population	0.035	0.013	0.029	0.051	0.044
Ln population	(0.61)	(0.21)	(0.50)	(0.85)	(0.74)
Ethnic fractionalization	−1.742****	−1.676****	−1.719****	−1.808****	−1.795****
Ethnic fractionalization	(−4.36)	(−4.20)	(–4.31)	(−4.43)	(−4.39)
East Europe–ex-Soviet	1.057**	1.243***	1.113**	0.958**	1.089**
East Europe–ex-Soviet	(2.29)	(2.72)	(2.42)	(2.05)	(2.32)
Sub-Saharan Africa	−1.508**	−1.407**	−1.455**	−1.405**	−1.283**
Sub-Saharan Africa	(−2.42)	(−2.33)	(−2.34)	(−2.25)	(−2.06)
Asia	0.027	0.177	0.073	0.076	0.182
Asia	(0.04)	(0.29)	(0.12)	(0.12)	(0.29)
Middle East–North Africa	−0.464	−0.169	−0.387	−0.402	−0.230
Middle East–North Africa	(−1.03)	(−0.38)	(−0.87)	(−0.89)	(−0.51)
Latin America	−1.115***	−1.118***	−1.100**	−1.085**	−1.029**
Latin America	(−2.58)	(−2.63)	(−2.55)	(−2.51)	(−2.39)
n	6,873	6,873	6,873	6,730	6,730
Countries	156	156	156	154	154
Observations re-coded		796	38		242
Countries re-coded		55	1		46

Models are OLS PCSE, adjusting for panel-level heteroskedasticity, panel-specific first-order autoregressive (AR(1)) autocorrelation, and contemporaneous correlation. Independent variables are lagged 5 years. Maximum time series is 1951-2008 on dependent variable, GDP p.c. growth (in %). Decade dummies and constant are omitted from the table. DD = Democracy–Dictatorship; BMR = Boix–Miller–Rosato; GDP p.c. = gross domestic product per capita; OLS = ordinary least squares; PCSE = panel corrected standard errors.

p < .10. **p < .05. ***p < .01. ****p < .001.

The point estimate in Model II resembles those of recent studies employing more comprehensive democracy measures (see, for example, Acemoglu, Naidu, Restrepo, & Robinson, 2014; Gerring et al., 2005; Gerring, Maguire, & Skaaning, 2013; Knutsen, 2011b; Papaioannou & Siourounis, 2008). Although it has been noted that DD yields different estimates on growth than, for example, Polity or Freedom House (Cheibub et al., 2010; Knutsen, 2011b; Krieckhaus, 2004), the common interpretation has been that this stems from the latter incorporating additional regime dimensions such as executive constraints or civil liberties. Hence, proponents of a minimalist democracy concept have had reason to consider the results in Przeworski et al. (2000)—suggesting little or no effect—to provide more reasonable estimates of democracy’s impact on growth. Our results, however, suggest that differences in estimates—at least in single-equation regression models—could, in part, stem from a bias generated by one particular coding rule of DD. Even “minimalist democracy” might be associated with growth.

However, a simple re-coding of DD as in Model II likely counts several competitive authoritarian regimes as democratic. Thus, it may be better to compare with estimates based on the Boix et al. (2013) measure. Boix–Miller–Rosato (BMR) is also minimalist and dichotomous, but instead of coding contestation solely by an alternation rule, BMR takes “any instance of electoral executive turnover to an opposition party as a strong indicator of free and fair elections. However, the presence of electoral turnover is neither necessary nor sufficient” (pp. 1530-1531).⁹ Hence, BMR

checked the history of those cases with no electoral turnover for a sufficiently long period of time (over two electoral terms) to examine whether internal coups, external interventions, abuses of state power, or reports of fraud could explain the prolonged control of the executive by the same party. If there were none and we observed contested elections, we coded the period as having free and fair elections. If a peaceful governmental turnover was observed, we applied the same check to determine how far back in time the condition of free and fair elections applied. (p. 1531)

Alternation of government is but one noisy signal of whether elections are contested; by including different types of information BMR may better mitigate Type II errors.¹⁰ We therefore compare how BMR and DD relates to growth; if the above-hypothesized bias exists, BMR should produce a stronger positive correlation. To properly compare DD and BMR estimates, we do so for identical observations. We therefore first run Model IV, which is identical to Model I except for only including the 6,730 observations with data also on BMR. The DD coefficient in this model is 0.22, and far from statistically significant (t = 1.0). In contrast, Model V using BMR reports a democracy coefficient twice the size (0.44) and significant at 5% (t = 2.2). We also re-ran Model IV using the original DD coding, but re-coding (only) the 108 non-democratic regime-years considered democratic by BMR. This increases DD from 0.18 to 0.32 and the t value from 0.8 to 1.6.

In several regimes, governments were initially selected via contested multi-party elections—including pre-independence elections in many African countries (see Geddes, Wright, & Frantz, 2014b)—but some years later cracked down on opposition and violated the regime rules under which they were selected. One could argue that these regimes were initially democratic, and turned autocratic only after the observed violation of regime rules. This contrasts with the extended coding of the third DD rule, considering regimes as dictatorial from when the violating government was elected. Although proponents of DD may argue these regimes were non-democratic from their governments’ election—they simply did not have to reveal non-democratic practices before—we check whether also this coding decision matters: Perhaps only governments initially overseeing high growth accumulate sufficient resources to consolidate their position and, subsequently, succeed with auto-coups, thereby selecting high-growing democracies out of the sample. We test this by utilizing differences in democracy scoring between DD and Geddes, Wright, and Frantz (2014a); somewhat simplified, the latter codes regimes as autocratic only from the year “autocratic behavior” is observed. We thus re-code DD as democratic for 156 GWF (Geddes, Wright, and Frantz)–democracy observations. This increases the estimated effect of democracy on growth, although not by much and the effect remains insignificant (see Online Appendix Table A.17).

Returning to our main tests, the differences reported in Table 1 are retained for various specification choices (see online appendix). Also in random- and fixed-effects models, the estimated effect of democracy increases when going from Model I to II and from IV to V—although BMR is no longer statistically significant. Changing the lag-time on the independent variables to 1 or 3 years barely changes the results from Table 1. The overall picture is also retained when adding controls such as population growth, oil and gas income, plurality religion dummies, regime duration, and lagged growth. A further worry is that the results might be affected by including several observations (mostly coded as non-democratic) that arguably constitute neither democratic nor autocratic regimes, for example, because the country is under foreign occupation or because no central authority controls much territory. GWF separate foreign-occupied, non-independent, provisional, and “warlord” observations from both democracies and autocracies (see Geddes et al., 2014b, pp. 17-19). Excluding these regimes does not alter our conclusion, however, although all democracy coefficients are reduced by about 0.1. Still, there is another specification issue that should be discussed and investigated.

Does the Alternation Rule Affect Results in Models Treating Democracy as Endogenous?

Unlike most studies investigating democracy and growth, Przeworski et al. (2000) were explicitly attentive to potential endogeneity biases associated with single-equation growth regressions, and presented models adjusting for the “selection of democracy.” Although not their explicit intention—which rather related to modeling real-world processes behind why some regimes turn (and stay) democratic—employing selection models may actually also mitigate some of the coding bias highlighted here. The first stages of such selection models, in practice, model factors that explain why some countries are coded as democracies and others as dictatorships—and later adjust for these when producing second-stage estimates of democracy’s effect on growth. Thus, selection models may also adjust for sources of systematic errors in the regime coding. For instance, if prior growth enters the first stage, and high growth predicts that some democracies will be coded as dictatorial, the selection model will register high past growth as a determinant of (being coded as) dictatorship, and subsequently adjust for this selection. Even if past growth is not in the first-stage regression, but this regression contains a valid instrument, employing only the exogenous variation in democracy may contribute to reducing overall measurement error. Consequently, selection models may mitigate the above-theorized bias that we found indications of in single-equation models.

We ran Heckman Treatment-Effects versions of the models in Table 1, employing WAVE from Knutsen (2011a) as instrument. WAVE captures exogenous sources of variation in democracy—from geo-political factors generating international-political “regime trends,” and from spillover effects from regime changes in neighboring countries—by scoring whether a regime originated within one of Huntington’s (1991) reverse waves of democratization. Knutsen (2011b) finds that it is both a strong instrument for democracy and that it satisfies the exclusion restriction in IV models with growth as dependent variable. The first-stage estimates are reported in Online Appendix Table A.18.

The results, presented in Table 2, are more mixed and weaker for these specifications. Notably, the difference between the DD and BMR estimates disappears, and flipping Botswana does not move the estimate in the expected direction; the selection-adjustment might thus alleviate much of the bias. However, we still identify differences between Model I, using original DD, and Model II, scoring all Type II regimes as democracies. The point estimate from Model I is actually larger, indicating that democracy increases growth rates by, on average, 2.4 percentage points. However, the standard error is extremely large, and DD thus remains statistically insignificant (t = 0.8). In contrast, Model II yields a positive effect on growth (about 1.4 percentage points) significant at 5%. This effect is retained, for instance, in models with 1-year lags and when also controlling for log regime duration. Interestingly, Przeworski et al. (2000) also conducted robustness tests of their Heckman models after re-coding Type II regimes as democratic. They found that this did “alter the results slightly in favor of democracy” (Przeworski et al., 2000, p. 184), but not enough to change their conclusion that democracy is an insignificant determinant of GDP growth. However, they only had time series extending to 1990, whereas our growth data extend to 2008. Indeed, when re-running Model II on the 1946-1990 time series, the t value of the democracy measure drops from 2.2 to 1.7.

Table 2.

The Second Stage of Heckman Treatment-Effects Models—Regime Type Modeled as Endogenous.

	Model I	Model II	Model III	Model IV	Model V
	Baseline DD	Re-coded DD: All Type II democratic	Re-coded DD: Botswana democratic	Baseline DD on BMR sample	BMR regime measure
	b/(t)	b/(t)	b/(t)	b/(t)	b/(t)
Democracy	2.383	1.358**	0.335	2.340	1.323
Democracy	(0.82)	(2.18)	(0.15)	(0.78)	(0.20)
Ln GDP p.c.	−0.492	−0.410*	−0.230	−0.477	−0.362
Ln GDP p.c.	(−1.08)	(−1.77)	(−0.58)	(−1.02)	(−0.37)
Ln population	−0.077	−0.078	−0.044	−0.067	−0.052
Ln population	(−0.56)	(−0.70)	(−0.41)	(−0.49)	(−0.34)
Ethnic fractionalization	−1.409**	−1.465**	−1.620**	−1.447**	−1.595*
Ethnic fractionalization	(−2.02)	(−2.34)	(−2.09)	(−2.03)	(−1.71)
East Europe–ex-Soviet	2.253	1.533***	1.233	2.163	1.690
East Europe–ex-Soviet	(1.52)	(2.96)	(1.09)	(1.43)	(0.50)
Sub-Saharan Africa	−0.206	−1.101	−1.157	−0.196	−0.716
Sub-Saharan Africa	(−0.14)	(−1.54)	(−1.18)	(−0.13)	(−0.27)
Asia	1.348	0.719	0.588	1.361	0.978
Asia	(1.04)	(1.06)	(0.63)	(1.02)	(0.40)
Middle East–North Africa	0.922	0.070	−0.401	0.917	0.293
Middle East–North Africa	(0.47)	(0.13)	(−0.28)	(0.46)	(0.07)
Latin America	−0.644	−1.079***	−1.030**	−0.646	−0.821
Latin America	(−1.04)	(−2.91)	(−2.28)	(−1.02)	(−0.64)
n	6,701	6,701	6,701	6,593	6,593
Countries	154	154	154	152	152
Observations re-coded		784	38		242
Countries re-coded		53	1		46

Independent variables are lagged with 5 years. WAVE from Knutsen (2011a) is used as instrument. Decade dummies and constant are omitted from the table. Maximum length of time series is 1951-2008 on dependent variable, GDP p.c. growth (in %). See Online Appendix Table A.18 for first-stage equations. DD = Democracy–Dictatorship; BMR = Boix–Miller–Rosato; GDP p.c. = Gross domestic product per capita.

p < .10. **p < .05. ***p < .01. ****p < .001.

Regarding the much weaker evidence for the proposed bias in the Heckman Treatment-Effects models, we speculate that this might be a side-benefit from modeling regime type (coding) as endogenous. We therefore cautiously propose selection models as one potential “fix,” although they are far from a cure-all. These models have their own problems related to inefficiency (the standard errors from Table 2 are large) and

[s]election models turn out to be exceedingly sensitive: minor modifications of the equation that specifies how regimes survive can affect the signs in the equations that explain growth. Standard regression techniques yield biased (and inconsistent) inferences, but selection models are not robust. (Przeworski & Limongi, 1993, p. 64)

Independent of how one considers the relative advantages and disadvantages of single-equation and selection models, most contributions on regime type and growth have relied on single-equation models. In their Meta-Regression Analysis of democracy and growth—including 483 estimates from 84 studies—Doucouliagos and Ulubasoglu (2008) count that 90% of estimates were produced assuming that democracy is exogenous (p. 71). Hence, our single-equation results from Table 1 are of relevance for the scholarly community, even if selection models should alleviate much of the bias in practice. We therefore return to single-equation OLS models when providing another test for whether our proposed bias operates.

Re-Coding DD and Comparing Estimates Using Information Available at Different Points in Time

Although the above regressions provide indications that DD’s alternation rule generates a bias in the estimated democracy–growth relationship, a skeptic might suspect the results in, for example, Model V, Table 1 to be wrong because of the subjective judgments introduced in BMR. Furthermore, simply flipping Type II regimes does not tell us whether increased growth estimates stem from misclassified electoral authoritarian regimes or previously misclassified democracies. We therefore propose a more stringent and less controversial method for assessing the potential bias, which avoids subjective judgments and is “Type I-error proof.” To this end, we exploit the practical feature that DD can be disaggregated into its individual components: We only use DD’s coding rules, the observable information Cheibub et al. had in 2010 (remember that DD employs retrospective coding), and the historical information concerning government alternation available at particular previous points in time. We then construct “real-time DD scores” based (only) on the historical information (on alternation) available in a given year (t). Hence, we code what DD would have looked like had it been coded in, for example, 1990, 1980, or 1970.

Indeed, all democracies have at some point been Type II regimes; it takes time from competitive elections are planned until a country observes its first election-induced government alternation. The current Japanese regime was in place fairly shortly after WWII, but the first alternation occurred only in 1993 when the LDP failed to retain its majority in the Diet Lower House elections. In post-war Western Germany, it took until 1969 for the CDU-led government to cede power after an election loss to Willy Brandt and the Social Democratic Party (SPD). Had DD been coded in 1968, Japan and Western Germany would have been scored as dictatorships.

At t + 1 some regimes that were falsely coded as dictatorships at t are corrected because of observed government alternations. In 1994, for instance, we knew the post-war Japanese and German regimes were truly competitive, and these Type II errors were corrected. Even better, the actual DD measure coded by Cheibub et al. is based on historical information available in 2010; Type II errors identified by more recent alternations (e.g., South Korea-1997, Taiwan-2000) are thus also corrected. Therefore, we can assess the bias—or at least its direction—by running pairs of regression on identical samples (e.g., 1946-1980) using real-time DD and original DD from Cheibub et al. If the above-hypothesized bias exists, we should observe a more positive/less negative effect on growth after correcting Type II errors. We therefore expect regressions using real-time DD to provide lower estimates of democracy’s effect on growth than regressions using original DD.

We run growth regressions on time series from 1946 to t, letting t vary between 1965 (to ensure decent time series) and 2003 (last year of data because independent variables are lagged 5 years).¹¹ Table 3 presents these pairs of regression models for t = 1970, 1980, and 1990. As expected, original/Cheibub et al. DD—which has removed some Type II errors because of the passage of time—provides higher point estimates than real-time DD for all years.¹² For 1980, real-time DD is negative (−0.36), whereas original DD is positive (0.16); the difference in estimated effects totals half a percent GDP p.c. growth. For 1990, both DD coefficients are positive, and the difference is smaller. Yet, original DD yields a weakly significant effect (t = 1.81), whereas real-time DD does not (t = 0.89), further illustrating that the above-described bias may matter for our conclusions on the consequences of democracy.

Table 3.

Correcting Historical Type II Errors in DD and Investigating Bias in Estimated Effect of Democracy on Growth.

	1946-1970	1946-1970	1946-1980	1946-1980	1946-1990	1946-1990
	Real-time DD	Original DD	Real-time DD	Original DD	Real-time DD	Original DD
	b/(t)	b/(t)	b/(t)	b/(t)	b/(t)	b/(t)
Democracy	−0.430	−0.182	−0.356	0.159	0.231	0.523*
Democracy	(−1.50)	(−0.56)	(−1.22)	(0.50)	(0.89)	(1.81)
Ln GDP p.c.	−0.261	−0.280	−0.818**	−0.879**	−0.514*	−0.548*
Ln GDP p.c.	(−0.91)	(−0.97)	(−2.26)	(−2.40)	(−1.79)	(−1.93)
Ln population	−0.044	−0.033	−0.051	−0.058	−0.005	−0.016
Ln population	(−0.53)	(−0.40)	(−0.62)	(−0.73)	(−0.07)	(−0.23)
Ethnic fractionalization	−0.706	−0.639	−1.762****	−1.694****	−1.843****	−1.827****
Ethnic fractionalization	(−1.20)	(−1.07)	(−3.73)	(−3.58)	(−3.91)	(−3.87)
East Europe–ex-Soviet	0.379	0.516	−0.430	−0.087	−0.348	−0.079
East Europe–ex-Soviet	(0.63)	(0.86)	(−0.84)	(−0.17)	(−0.58)	(−0.13)
Sub-Saharan Africa	−2.788***	−2.658***	−3.471****	−3.253****	−2.267***	−2.072***
Sub-Saharan Africa	(−3.04)	(−2.97)	(−4.10)	(−3.83)	(−3.27)	(−2.92)
Asia	−1.386**	−1.282*	−1.910***	−1.718**	−0.887	−0.760
Asia	(−2.02)	(−1.88)	(−2.58)	(−2.30)	(−1.28)	(−1.09)
Middle East–North Africa	−0.459	−0.353	−1.317**	−1.058*	−1.011*	−0.783
Middle East–North Africa	(−0.78)	(−0.57)	(−2.31)	(−1.80)	(−1.93)	(−1.45)
Latin America	−1.771****	−1.611****	−2.373****	−2.199****	−1.512***	−1.472***
Latin America	(−3.41)	(−3.31)	(−4.57)	(−4.25)	(−3.20)	(−3.14)
n	2,223	2,223	3,519	3,519	4,855	4,855
Countries	121	121	134	134	136	136
Observations re-coded		409		524		654
Countries re-coded		11		14		18

Models are OLS with PCSE, adjusting for panel-level heteroskedasticity, panel-specific first-order autoregressive (AR(1)) autocorrelation, and contemporaneous correlation. Independent variables are lagged 5 years. Maximum time series is given in top row (for independent variables). Real-time DD is calculated using historical information on alternations available at last year of sample (and does not invoke “Cheibub-Gandhi-Vreeland (CGV) override rule”; cf. Online Appendix Table A.23). Original DD is from Cheibub, Gandhi, and Vreeland (2010). Decade dummies and constant are omitted from the table. DD = Democracy–Dictatorship; GDP p.c. = Gross domestic product per capita; OLS = ordinary least squares; PCSE = panel corrected standard errors.

p < .10. **p < .05. ***p < .01. ****p < .001.

Figure 2 shows that the expected bias not only materializes for the particular years (1970, 1980, 1990) demarcating the end of the time series in Table 3. The original DD estimates systematically yield higher estimated effects than the real-time estimates. For several years, original DD is outside the 90% confidence interval of real-time DD. When approaching the last years of our sample, the difference between real-time information about regime alternations and the information Cheibub et al. possessed in 2010 dwindles, and the two estimates converge. In sum, this exercise shows that correcting (some) Type II errors yields more “optimistic” results regarding how democracy affects growth—at least in OLS models. And, we should remember that other potential Type II errors, such as—most likely—Botswana, have yet to be corrected also in the Cheibub et al. coding.

Figure 2.

Estimated effect of democracy according to (original) DD as coded by Cheibub, Gandhi, and Vreeland (2010) and real-time DD (with 90% CIs) from OLS PCSE regressions, specified as in Table 3, for samples from 1946 to year given by x axis.

Another interesting trend is observable from Figure 2: The effect of democracy on growth seems to change over time, as including more recent observations—at least until the early 1990s—generates a clearer positive effect. Already in 1993, Przeworski and Limongi noted that older regression studies on democracy and growth often arrived at more “skeptical” conclusions. Furthermore, Krieckhaus (2004) finds that sample-period matters, reporting a negative effect of democracy on growth in the 1960s and a positive effect in the 1980s. Knutsen (2011c) argues that there are good theoretical reasons for why the effect has become stronger, positive in more recent decades. Notably, particular production-technology changes may have amplified the economic benefits of democracy—as human capital–based economies favor democracies with their mass-education systems (e.g., Baum & Lake, 2003). Simultaneously, changes to the international economy may have reduced democracy’s economic drawbacks—as increased foreign direct investment (FDI) flows mitigate the investment advantage dictatorships have from higher savings rates (Przeworski & Limongi, 1993). Employing Chow tests and the Polity index, Knutsen (2011c) finds a systematically larger, positive effect after 1980 than before. Figure 2 shows that also regressions using DD indicates the correlation between democracy and growth has increased after 1980, at least when compared with the two decades prior. This is also congruent with the Heckman results above, where the relationship turned clearer positive when extending the time series from 1990 up to 2008.

Does the Alternation Rule Induce Bias for Other Relationships?

Our reasoning can be applied beyond the democracy–growth relationship; resembling biases may affect estimates on other (causes and) consequences of democracy, if alternation in young democracies is correlated with these factors. Below, we briefly discuss and test for biases in estimated effects of democracy on civil war onsets and attempted coups d’état.

First, alternation in power—or, rather, the lack of it—may affect civil war risk. In particular, democratic systems where government alternation prospects are lower could be more conflict-prone than other democracies: Groups expecting to be “permanent minorities” have stronger incentives to take up arms, which constitutes a (costly) alternative channel for achieving their preferred policies (through obtaining power or winning negotiated concessions). This logic is clearly spelled out in Przeworski (1991); groups will only accept peaceful political competition when they have a real chance of winning the next election. Whereas permanently accepting opposition status is more costly than resorting to arms, temporarily accepting such status is less costly. Alternatively, armed rebellion may be less a rational response, and more an expression of group grievances stemming from the frustration of never having a say in day-to-day democratic decision making (see, for example, Cederman, Gleditsch, & Buhaug, 2013; Gurr, 1970). Several cases might reflect this. In the Chiapas conflict in Mexico during the 1990s, the grievances of the Zapatistas were partly fueled by political exclusion from a system dominated by the PRI (see, for example, Harvey, 1998). Other examples of political uprisings by minorities in (real-time) Type II regimes are the Mohajiir rebellion in 1990s Pakistan, the Maoist rebellion in 1996-Nepal, and the revolutionary leftist rebellions in 1965-Peru. More generally, in certain democracies—particularly those with dominant parties—different minority groups may perceive future prospects of obtaining power through elections to be low, inducing armed rebellion. This is consistent with evidence that exclusion from political power increases the risk of ethnic groups rebelling (Cederman et al., 2013; Cederman, Wimmer, & Min, 2010). Consequently, the original DD measure may underestimate the propensity of civil war in democracies, as the possibly most conflict-prone democratic systems—democracies with disgruntled “permanent minorities” that have yet to observe post-election government alternation—might falsely be coded as dictatorships.

A resembling bias may apply to coups. In countries where—in spite of free and fair elections—being in permanent minority is more likely, regime opponents have stronger incentives to engage in the risky business of staging a coup. Such concerns have arguably been prevalent, for example, in coup attempts against popularly elected governments in Latin America. The 1962 coup attempt in Venezuela was inspired by a communist opposition left on the sidelines after the dominant party (Acción Democrática) won the 1958 election, and set up a coalition government. Another example is the 1949 coup attempt in Guatemala. This was instigated by rightist groups who saw the center-left government, which had come to power through elections and initiated several social reforms, as foreshadowing a permanent socialist revolution.

In sum, when prospects for turnovers through elections are bleak, groups not occupying power may use extra-constitutional means to obtain the government they like. This may lead to the DD autocracy category comprising both autocracies and those democracies that are particularly coup- and civil-war prone. This, in turn, indicates that (original) DD may exaggerate the extent to which democracies are peaceful and stable polities. Both for civil wars and coups, we thus expect a less “pacifying” effect of democracy when (a) counting Type II regimes as democratic rather than autocratic, (b) using BMR rather than DD, and (c) correcting Type II errors in DD using updated historical information.

We explore these implications conducting similar tests to those in Tables 1 and 3 for growth. For the regime type–civil war relationship, we employ and adjust (e.g., add ethnic fractionalization and economic growth as controls) the main model in Cederman, Hug, and Krebs (2010). However—despite the intriguing theoretical argument—we do not find systematic evidence of alternation-rule-induced bias on civil war onsets. This is true when flipping all potential Type II regimes to the democratic column—where our results rather point in the opposite direction—when comparing DD to BMR estimates (see Online Appendix Table A.29) or when comparing original DD results with real-time DD results (see Figure 3). Hence, employing the alternation rule does seemingly not lead to overstating the pacifying effect of democracy on civil war onsets.

Figure 3.

Simulated probability of experiencing civil war onsets (left) and coup attempts (right) for originally coded DD democracies and real-time DD democracies, for samples from 1946 to year given by x axis (t).

Regarding coups, we employ the coup attempts model in Powell (2012) as point of departure. We find that real-time DD is negatively and significantly linked to coup risk, while the (retrospectively coded) original DD has a weaker negative effect (see Figure 3 for estimated probabilities of coup attempts). This follows our expectation; the estimated effect that democracy has on reducing coup risk is modified when we correct Type II errors. Where the incumbent’s willingness to cede power after an election defeat is fairly certain and recently proven (as in the real-time DD cases), regime opponents might find electoral competition to be preferable to the risky business of staging a coup. However, we do not find support for our other expectations (see Online Appendix Table A.31), and the evidence is thus not unequivocally supporting our suspicion that the alternation rule falsely amplifies the effect democracy has on mitigating coup risk.

Conclusion

Using subjective indicators to code democracy may generate various problems, and democracy measures such as Polity and Freedom House are likely associated with substantial unsystematic measurement errors. Hence, Alvarez et al. (1996), Przeworski et al. (2000), and Cheibub et al. (2010) put a high prize on objective coding rules, ensuring that their DD measure scores high on inter-coder reliability. However, all coders may be systematically wrong when in unison following objective rules that use limited information. Although the DD measure is rightly praised for its beneficial properties (e.g., Clark, Golder, & Golder, 2012; Munck & Verkuilen, 2002), its alternation rule may yield problems for empirical studies on the correlates of democracy. Already Alvarez et al. pointed out that some democracies are likely falsely coded dictatorships for their baseline measure. Hence, we should at least expect some attenuation bias—meaning that coefficients are drawn toward zero—when using DD to, for instance, estimate democracy’s impact on growth or coup attempts; we are comparing a subset of the world’s democracies to a set comprising both democracies and dictatorships.

Yet, we argued that the bias may sometimes be more severe than what we would expect from simply misclassifying democracies as dictatorships at random. We elaborate on how high economic growth contributes to bolster the position of incumbents—perhaps particularly in young democracies where voters have yet to learn about the economic policies and competencies of the opposition. Hence, misclassified democracies are, expectedly, often (young) democracies with above-normal economic performance: If voters systematically reward competent governments, and punish governments that fail to perform, governments in high-growing democracies are less likely to face election losses. This, in turn, disallows the regime in question to pass the alternation rule. Thereby, we may actually be comparing old democracies and young democracies with low growth, on one hand, with dictatorships and young democracies with high growth, on the other. Using different tests, we find indications of the expected bias for the effect on growth.

Which regime measure we use may alter what we believe about the substantial effects of democracy. As different measures often tap very different concepts of democracy (e.g., Munck & Verkuilen, 2002)—procedural and substantive, uni- and multi-dimensional—this general point is uncontroversial. However, our analysis shows that also when considering only minimalist democracy measures, the specific operationalization matters. Even changing one particular coding rule—the alternation rule—might induce different conclusions, for instance, on how democracy relates to growth. The scholars producing the ACLP and DD data sets explicitly noted that the alternation rule may miscode some democracies as dictatorships, and urged users of their data to conduct robustness tests by re-coding these regimes. However, few users have heeded this advice. Based on our analysis, we re-iterate the importance of robustness testing results on the (causes and) effects of democracy when using regime measures, like DD/ACLP, that rely on alternation rules. Our analysis further suggests that we should not be content simply with robustness testing and registering whether results differ or not. Thinking carefully through what the coding rules of a particular measure imply, and how they—through different channels—relate to the other variables of interest, may lead to intriguing theoretical explanations for why different measures produce different estimates.

Footnotes

Acknowledgements

The authors are thankful for comments and suggestions from three anonymous referees and participants and discussants at the following venues: The Annual EPSA Conference, June 2014, Edinburgh; The NOPSA Conference, August 2014, Gothenburg; ESOP Lunch Seminar at the Dept. of Economics, University of Oslo; Tuesday Seminar at the Dept. of Political Science, University of Oslo; Department Seminar at the Dept. of Political Science, Trinity College Dublin.

Author’s Note

Data Replication Materials are available at

Declaration of Conflicting Interests

The authors declared no potential conflicts of interest with respect to the research, authorship, and/or publication of this article.

Funding

The author(s) disclosed receipt of the following financial support for the research, authorship, and/or publication of this article: The authors received partial funding for the work on this article from Research Council of Norway project 204454/V10.

Notes

Author Biographies

Carl Henrik Knutsen is a professor at the Department of Political Science, University of Oslo. His research interests include the economic consequences of political institutions and the determinants of regime change. His publications include articles in the American Journal of Political Science, Electoral Studies, Journal of Development Studies, and World Development.

Tore Wig is research fellow and Phd candidate at the Department of Political Science, University of Oslo. His research interests include the institutional determinants of civil conflict, and how institutions in autocracies impact on regime survival.

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