Income, Democracy, and Leader Turnover

While some believe that economic development prompts democratization, others contend that both result from distant historical causes. Using the most comprehensive estimates of national income available, I show that development is associated with more democratic government—but mostly in the medium run (10 to 20 years). This is because higher income tends to induce breakthroughs to more democratic politics only after an incumbent dictator leaves office. And in the short run, faster economic growth increases the ruler's survival odds. Leader turnover appears to matter because of selection: In authoritarian states, reformist leaders tend to either democratize or lose power relatively quickly, so long-serving leaders are rarely reformers. Autocrats also become less activist after their first year in office. This logic helps explain why dictators, concerned only to prolong their rule, often inadvertently prepare their countries for jumps to democracy after they leave the scene


Calculating cumulative impact of variables in models with lagged dependent variables and interaction terms:
In a model with a lagged dependent variable:   Sources: see Table A18. Note: (A)-(D) estimated by OLS with country and year fixed effects; "t-1" refers to previous panel period. Robust standard errors, clustered by country, in parentheses; * p < .10, ** p < .05, *** p < .01. "Fisher p level": probability level at which one can reject H0: residuals are I(1), from Fisher test of residuals. Cumulative effects calculated as on p.1. (E): Year fixed effects included in 10-20 year panels; could not compute with year fixed effects in 1 and 5 year panels. (F): Arellano-Bond regressions, democracy and Ln GDP per capita instrumented with second lags. Table A2 shows that results are similar to those in Table 2, panel C, if one focuses on transitions to democracy (using the Boix-Miller-Rosato dichotomous measure or just upward movements on the Polity2 scale, as in Table A1) or excludes interpolated income data. On use of linear probability model in (A), see note to Table A1.   5 OLS with fixed effects and a lagged dependent variable can yield biased estimates because the lagged dependent variable is mechanically correlated with the error terms for earlier periods. Table A3 shows results are also similar if the lagged dependent variable is dropped (at the cost of autocorrelation and less precise estimates; clustered standard errors, nevertheless, remain consistent).  Table A18. Note: All regressions estimated by OLS with country and year fixed effects; "t-1" refers to previous panel period. Robust standard errors, clustered by country, in parentheses; * p < .10, ** p < .05, *** p < .01. "Fisher p level": probability level at which one can reject H0: residuals are I (1) Estimating the relationship with a panel error correction model I argue that there is an equilibrium relationship between income and democracy, but that reequilibration occurs only in periods after leader turnover. Thus, the system alternates between two states that depend on whether turnover has recently occurred. One can capture this with the following model, estimated on annual data: where lt is a dummy coded 1 in years when the leader exited, 0 otherwise. The first part of the right-hand side models the dynamics in years after leader exit, the second part captures those in other years. If the estimates for  and  are significant and have opposite signs, that suggests there is a positive equilibrium relationship between income and democracy that is visible in periods after leader turnover. From this, we can derive the speed at which equilibration occurs during the post-turnover period. Note that we do not expect  and  to both be significant (there is no equilibrium relationship detectable in years when leader exit has not occurred). Nor do we expect the coefficients on the growth terms,  and  , necessarily to be significant-although they may-because of the opposite effects growth has, simultaneously raising the income level (favoring democracy) and entrenching the incumbent (obstructing change). I allow the fixed effects to differ between the two types of period.
In Table A4, I show results for this model. As expected, lagged income and democracy are significant, with opposite signs, in the case of leader exit. This suggests an equilibrium relationship between the two such that a one ln unit increase in income is associated with around a .26 points increase in the rescaled Polity2 score (or equivalently, a doubling of GDP per capita is associated with a .17 point Polity2 increase). 2 I graph the equilibrium relationship in Figure A2. In the noexit years, only lagged democracy is significant (with a negative coefficient), suggesting reversion to the mean, but no impact of income. The growth rate is not significant at all if the leader did not exit. If he did exit, it is significant at p <.10, with a positive sign. 2 The long run multiplier between Ln income and democracy is equal to Sources: see Table A18. Note: Estimated by OLS with full sets of country and year fixed effects, interacted with indicator for leader turnover in previous year. Robust standard errors, clustered by country, in parentheses; * p < .10, ** p < .05, *** p < .01. "Fisher p level": probability level at which one can reject H0: residuals are I(1), from Fisher test of residuals. ≈ $300 ≈ $15,500

Other possible estimation strategies
Another approach would be to use annual data and estimate the effect of income conditional on leader turnover over multiyear periods by including multiple lags of income, leader turnover, and their interaction: where it l is a dummy taking the value 1 if leader turnover occurred in period t. There are two problems with this. Most important, the argument in this paper contrasts the effect of income during k-year periods in which at least one leader turnover occurred with the effect of income in k-year periods in which the same leader remained in power throughout. However, A2 does not estimate this. Instead, it estimates the effect of income if leader turnover occurred in precisely year t-k (while controlling for income and leader turnover in the intervening years of the k-year period). And it is not obvious how one could recover the effect of income given at least one leader turnover from the regression results. The most direct way to estimate the effect of at least one leader turnover is to use a dummy for at least one leader turnover, as in Equation 1 in the paper and adjust so as to avoid attributing increases in Polity2 to leader turnover that did not precede the regime change. The second problem is that, even if one could recover the relevant effect, the high correlation between consecutive lags of it y and it it ly would produce severe multicollinearity, resulting in imprecise estimates. One might also think of estimating versions of A2 with the intervening lags dropped: However, again, this would not estimate the effect of income conditional on at least one leader change. In addition, the estimates of it k   and it k   would suffer from omitted variable bias because of the omission of the intervening lags. Finally, one might estimate: that is using a dummy for whether there was at least one leader turnover in the k-year period.
(One must now adjust to avoid picking up any relationship between increases in Polity2 and simultaneous or subsequent leader turnover.) This is quite close to the Equation 1 model estimated in the paper. Running such regressions, I get significant results for the interaction between income and leader turnover at all values of k, consistent with the paper's message. The main disadvantage of A4 is that it counts each instance of leader turnover multiple times (for k = 20, each leader turnover will show up in 20 consecutive values of it k   ). Thus, the errors will-by construction-be strongly autocorrelated since consecutive values of it k   will contain a lot of the same information (not to mention the high autocorrelation in income). For k = 20, the correlation between it u and 1 it u  resulting from regressing A4 on this paper's dataset is r = .92. Clustering the standard errors by country adjusts for this. Still, it seems preferable to choose an estimation strategy in which autocorrelation is less extreme.

Could it be that the Polity coders simply take leadership change as a sign of democratization? In this case, the association between leader exit and democratization would be trivial.
In fact, this is clearly not the case. Among the country-years for which the coders recorded an increase in the Polity2 score, more than half (403) occurred with no leader change that year and 43 percent (311) occurred with no leader change either that year or the previous year. Conversely, of all country-years in which leader change occurred, only 15 percent were coded as years in which democracy increased. Evidently, the coders do not equate the two.

Are there too few cases of democratization without any prior leader change to estimate the relationship between income and democratization in such circumstances?
The proportion of cases of democratization without any prior leader change naturally falls as the panel interval increases. If the number fell too low, that could make it hard to estimate the effect of income in cases without leader turnover. This might explain why the significance of Ln GDP per capita is not higher in the 20-year panel ( Table 2, column 15). Among non-democracies whose Polity2 score rose in a given year, only 11 percent (69 cases) had experienced no leader change in the preceding 20 years.
It is much less of an issue in the lower-interval panels. Among non-democracies whose Polity2 score rose in a given year, 15 percent (98 cases) had experienced no leader change in the previous 15 years, 24 percent (155 cases) in the previous 10 years, 41 percent (262) in the previous 5 years, and 76 percent (552 cases) in the previous year. Without leader turnover, income is not just insignificant in the 20-year panel-it is insignificant in all the others as well (Table 2, columns 11-14). Table A7, column 1, repeats the basic model from Table 2, column 11, to facilitate comparison.

Robustness checks
Whether a country democratizes may depend on the extent of democracy in other countries, especially those nearby (Gleditsch andWard 2006, Gleditsch andChoung 2004). Column 2 controls for this using a measure of "foreign democratic capital"-essentially, the average level of democracy in other countries, weighted by their distanceconstructed by Persson and Tabellini (2009): ( , where i and j index countries, t indexes year, a equals 1 for autocracies and 0 for democracies, ij  measures the distance between i and j, and ρ operationalizes a geographical limit beyond which influence falls to zero, which they, in fact, estimate from the data. To capture the "resource curse," column 4 includes the logged income per capita earned from the country's sales of oil and gas, from Michael Ross's database. Autocracies that use pseudo-or partly-democratic institutions such as elected legislatures and executive elections to coopt opposition may be more stable (Gandhi and Przeworski 2007), while non-regime parties may weaken the regime (Wright and Escribà-Folch 2012). Column 5 controls for these.
Column 6 includes whether the head of state was a military officer or a monarch, as recorded by Banks (2007). Column 7 uses the more fine-grained classifications of Geddes, Wright, and Frantz (2012: GWF), who distinguish military, monarchical, one-party, and personalistic regimes (but only since WWII). (I use "miscellaneous" for regimes that GWF do not consider non-democracies but which have a Polity2 score less than six; the excluded category is military regime.) A country's history of democracy and autocracy may affect its current regime. In column 8, I include Persson and Tabellini's measure of accumulated democratic experience, which they call "domestic democratic capital." They assume this accrues at a fixed rate in each year a country is democratic (Polity2 > 0) and depreciates geometrically in years of autocracy: (1 ) year, a equals 1 for autocracies and 0 for democracies, and δ is a discount rate that they estimate from the data. As a second check, column 9 contains a variable based on that used by Epstein et al. (2006) to capture the legacy of past democratic failures. Epstein et al. used the absolute value of the sum of a country's total downward movements on the Polity scale since 1960. I use the total since the start of the data, and normalize by the number of years.
To control for political instability, column 10 includes the percentage of previous leader changes in the country (since the start of the data) that were "irregular," according to the Archigos codings.
Perhaps it is not leader turnover that prompts democratization, but war that overthrows both leaders and regime. Column 11 controls for whether the country had been in a war or civil war the previous year, and whether the government won or lost such wars. (I exclude military defeats that resulted in foreign occupation or imposition of a leader, since obviously occupation by a democratic power could result in democracy.) Democratization was more likely if a civil war had been underway. But this had little effect on the leader turnover and income results.
In the same regressions run on 10-year panels (not shown), the interaction of income with leader change is sometimes less significant (probably due to the large drop in observations due to problems of data availability), but the cumulative impact of income after leader exit is almost always significant.   Table A18. Note: All regressions estimated by OLS with country and year fixed effects. Robust standard errors, clustered by country, in parentheses; * p < .10, ** p < .05, *** p < .01. "Fisher p level": probability level at which one can reject H0: residuals are I(1), from Fisher test of residuals. I assume that if a country enters the Ross data set with 0 oil and gas income, it also earned 0 income from oil and gas in preceding years. This reduces the loss of data due to fact that Ross data start only in 1930s. "Lost interstate war" excludes cases where foreign power occupied territory within following 10 years or imposed a leader. Table 3 While the timing of death by natural causes is unlikely to be affected by democratization, leader deaths in office may be more likely to occur in some settings than in others. We need to check that such contextual factors do not, in fact, account for the income-democracy relationship in the aftermath of a leader's natural death. Table A8 establishes that, among non-democracies, years in which a leader died of natural causes are distributed similarly to years without any leader death with regard to countries' income levels, Polity2 scores, and the time period. Such leader exits do occur slightly more often in South Asia and less often in Sub-Saharan Africa and Latin America than elsewhere. And, as one might expect, leaders that die in office tend to be older and to have served for longer. Table A9, therefore, repeats the top line of Table 3, but controlling for region of the world, (previous) leader's tenure, and (previous) leader's age.  1875-89 1890-1904 1905-19 1920-34 1935-49 1950-64 1965-79 -leader Table 2, column 11, for comparison. Subsequent columns control for the average rate of leader turnover in the previous 20, 10, and 5 years, and the interactions of this rate with lagged income and leader exit in year t -1. The cumulative impact of income conditional on exit in the previous year is hardly changed at all. What activates the link between income and democracy is not leader instability in general but the fact that a leader has actually just exited.  Table A18 in Appendix.

Identification in
Note: All regressions estimated by OLS with country and year fixed effects. Robust standard errors, clustered by country, in parentheses; * p < .10, ** p < .05, *** p < .01. "Fisher p level": probability level at which one can reject H0: residuals are I(1), from Fisher test of residuals.
The Banks data on opposition mobilization are compiled from newspapers, which raises the concern that reports might be censored in countries with less freedom of the press. In fact, using Freedom House's index of press freedom, I show that the number of reported mobilizations is usually significantly higher in countries with less freedom of the press. It might be that the measures would be higher still if journalists could report more freely, but the variation does not seem to be driven by restrictions on the press. I use the natural log of the number of mobilizations since the distribution for each variable is right-skewed.  Table A18. Notes: All variables averages for 1994-2008, the years for which Freedom of Press index available. Natural logs of dependent variables used because distributions of all are right skewed. I have reversed the scale on Freedom House's index of press freedom so that higher values indicate more freedom. Robust standard errors in parentheses: p < .10, ** p < .05, *** p < .01.
In Table A12, the dependent variable is a dummy for leader exit. Here, but only here, leader exit excludes exit due to death from natural causes, suicide, or retirement due to poor health, because these are not likely to be influenced by economic growth, defeat in wars, or the other factors. Rather than restricting attention to nondemocracies, I include all countries and model the difference in the effects in democracies and nondemocracies using interaction terms.
One concern is that regressions of leader replacement on economic growth might pick up the opposite causal process: more leadership change might, by creating uncertainty for investors, inhibit growth. To address this, column 2 estimates a model instrumenting for the growth rate with the average growth rate in other countries, weighted by their trade shares with the given country in the previous year:  (2003); since these data end in 1992, I use the trade weights from 1992 for the years 1993-2008. (This instrument is similar to one AJRY (2008) use for per capita income. I tried to instrument for income using an instrument corresponding to theirs, but in the dataset used here the instruments were too weakly correlated with income to serve adequately.) To satisfy the exclusion restriction, the instrument should be unrelated to leader turnover by any path other than via growth. It is possible that economic performance in other countries affects the incidence of war, which, if it involves the given country, could influence leader change there. I therefore control here for interstate war. I use the test devised by Stock and Yogo (2005) to check that the instrument is not weak. This test consists of comparing the Cragg-Donald statistic to a set of critical values. We can reject the hypothesis of weak instruments with high confidence. Some papers have analyzed leader turnover using leader-year data with hazard models (e.g., Chiozza and Goemans 2004). These have a number of attractive features. For instance, besides gauging the impact of independent variables, one can calculate a hazard rate at which leaders are replaced on average, other things equal. As in Bueno de Mesquita and Smith (2010), I fit a Weibull hazard model in column 4 for growth and military defeat, which allows the hazard rate to change over time; how it changes depends on an "ancillary parameter," p, which is estimated from the data. I model this parameter as a function of whether the country is a democracy (Polity2 greater than 5).
The main conclusions from this analysis are that: 1) low growth, military defeat, high and increasing opposition mobilization, civil war, and major government crises are all associated with higher odds of leader exit in nondemocracies, and the effect of low growth may well be causal; 2) in nondemocracies, older leaders are more likely to leave office, but longer tenure reduces the odds; 3) low growth, major government crisis, and maybe the leader's old age are associated with higher odds of exit in democracies; 4) among nondemocracies, military regimes experience more leader turnover along with personalist regimes; one-party regimes and monarchies experience less.
Archigos distinguishes several ways leaders leave office. Besides dying from natural causes, committing suicide, retiring due to poor health, or being deposed by a foreign force, they may be replaced in a "regular" or an "irregular" manner. "Regular" replacements occur "according to the prevailing rules, provisions, conventions, and norms of the country" (Goemans et al. 2009, p.272). Although such turnovers are the rule in democracies, they also occur in authoritarian regimes, as, for instance, when a new leader takes over in a faked election or a monarch abdicates in favor of his son. "Irregular" replacements occur amid abnormal events such as military coups or popular revolts.
I show regressions in which each type of leader exit is interacted with income. In models 1-5, the dependent variable is the level of Polity2. Models 6-10 use the Boix-Miller-Rosato binary measure of democracy, and include only non-democracies, so the regressions measure the probability of transition to democracy. For why it is necessary to estimate models 6-10 with a linear probability model, see footnote on p.2.
In the multiyear panels, when more than one change of leader occurs within the period, I focus on the final mode of leader exit. (If a regular turnover is followed by a revolution that sweeps away the old leader, one would expect the revolution to affect the type of regime at the end of the period more than the earlier turnover.) As before, I also adjust so that a leader exit is coded zero if it comes in a period when there was net increase in Polity2 but none of the net increase in Polity2 came after the leader change. This is to avoid attributing liberalization to leader change that did not precede the liberalization.
Note that these panel regressions are a far less efficient way of estimating the impact of death by natural causes than the comparison of means in Table 3. There, I examine all 10-year periods after a leader's natural death.
Here, I examine each 10 year panel-period that contains a leader's natural death-whether the death occurred in the first, the last, or some other year of the panel. If the effect is actually felt 5 years after the leader's death, the regressions will not capture this for the cases where the leader died less than 5 years before the end of the panel.  Table A18. Note: All estimations by OLS with country and year fixed effects. Robust standard errors, clustered by country, in parentheses; * p<.10, ** p<.05, *** p<.01. "Fisher p level" is probability level at which one can reject H0: residuals are I(1), from Fisher test of residuals. "BMR": Boix-Miller-Rosato dichotomous measure. Too few cases of leader suicide to estimate effects. If more than one leader turnover during the panel interval, type of turnover refers to last one. Data adjusted so leader turnover not coded 1 if Polity2 increased during panel period but there was no net increase after the leader exit.  (2007), Archigos. Note: From regressions controlling for country and year fixed effects . Antigovernment demonstration: "Any peaceful public gathering of at least 100 people for the primary purpose of displaying or voicing their opposition to government policies or authority, excluding demonstrations of a distinctly anti-foreign nature." General strike: "Any strike of 1,000 or more industrial or service workers that involves more than one employer and that is aimed at national government policies or authority."Attempted revolution: "Any illegal or forced change in the top government elite, any attempt at such a change, or any successful or unsuccessful armed rebellion whose aim is independence from the central government." Riot: "Any violent demonstration or clash of more than 100 citizens involving the use of physical force." The following graphs present marginal (short run) effects from estimation of an OLS regression of the country's Polity2 score on its lagged Polity2 score and all elements and interactions of: the leader's total term, a set of dummies for the leader's current year in office, Ln GDP per capita in the previous year. The regression is run on non-democracies (Polity2 in previous year < 6) and includes full sets of country and year fixed effects; standard errors are robust and clustered by country. Since the many interactions are cumbersome to list, I summarize the results graphically.   Table A18; 95% confidence intervals. Leader's current year in office Source: See Table A18; 95% confidence intervals. The goal of Table A16 is to test whether certain fixed characteristics of leaders and regimes, on which selection might operate, do in fact catalyze the effect of income on liberalization. Column 1 shows that leaders who have graduated from college tend to liberalize more when in countries with relatively high income. Column 2 shows that when the country's current income is high, those leaders who grew up at a time when the country was relatively developed tend to liberalize much more than those who grew up when it was still poor. This is consistent with the argument that those who came of age in more modern periods were socialized into values more favorable towards democracy and are therefore more likely to reform in response to the pressures for liberalization generated by development. Column 3 shows that military regimes tend to democratize more than other subtypes of nondemocracy, and that the estimated effect is higher in more developed countries. Thus, these characteristics are associated with greater liberalization in more developed countries. Cumulative effect of leader's college degree when income is: -$1,000 .02 (.05) -$5,000 .18** (.08) -$10,000 .25** (.12) Cumulative effect of prodemocratic values (proxied by Ln GDP p.c. when leader was 20), when current income is: -$1,000 .06 (.10) -$5,000 .27** (.11) -$10,000 .35*** (.13) Cumulative effect of military regime, when income is: -$1,000 .30** (.13) -$5,000 .45*** (.14) -$10,000 .52*** (. Sources: see Table A18. Note: All estimations by OLS with country and year fixed effects. Robust standard errors, clustered by country, in parentheses; * p < .10, ** p < .05, *** p < .01. "Fisher p level" is probability level at which one can reject H0: residuals are I (1) Table A18. Note: All estimations by OLS, with full sets of country and year dummies. Annual data. Standard errors in parentheses; * p < .10, ** p < .05, *** p < .01. a years in which state does not initiate a MID but continues one it previously initiated are excluded. Cases where lagged Polity2 score equals 10 (-10) excluded in column 1 (2) to adjust for fact that countries cannot move beyond the limit of the scale.