We are grateful to John Stephens for continuing to fine-tune the superb website and document-production system that he created, and to Brett Barkley, Ryan Daza, and Paul Mueller for occasional service to the journal. We are grateful to the authors who contribute material, especially David Colander of Middlebury College for serving as overseeing referee on the September 2013 issue, the twelve laureate economists who responded to a questionnaire for that issue, and to readers for their interest and feedback.

For friendship and vital sponsorship over the past two years, we are grateful to donors, especially the Earhart Foundation, the Charles G. Koch Foundation, the Mercatus Center at George Mason University, the John William Pope Foundation, Gerry Ohrstrom, and Robert and Susan Finocchio for their support.

We are grateful to the Atlas Economic Research Foundation for their friendship and in-kind support in housing EJW within their organization, especially Kelly Ream, Romulo Lopez, and Brad Lips.

We thank the Mercatus Center at George Mason University for co-organizing and sponsoring the debt crisis symposium appearing in the January 2012 issue, especially Tyler Cowen (who co-edited the symposium) and Rob Raffety, and for partnering with us on the Milton Friedman symposium appearing in the May 2013 issue.

We thank the following individuals for helping provide intellectual accountability to EJW:

Terry L. Anderson | Hoover Institution, Stanford University |

Jim Bessen | Boston University |

Olav Bjerkholt | University of Oslo |

Karol Boudreaux | Mercatus Center, George Mason University |

Dennis Coates | University of Maryland, Baltimore County |

David Colander | Middlebury College |

Tyler Cowen | George Mason University (multiple times) |

David O. Cushman | Westminster College (multiple times) |

Francesco Daveri | University of Parma |

Douglas Den Uyl | Liberty Fund |

Brian Doherty | Reason magazine |

Chris Doucouliagos | Deakin University |

Ross B. Emmett | James Madison College, Michigan State University |

Tom Engsted | Aarhus University |

Rodney Fort | University of Michigan |

Mark Freeland | Centers for Medicare & Medicaid Services |

Warren Gibson | San Jose State University (multiple times) |

Robin Grier | University of Oklahoma |

Robert Higgs | The Independent Review |

Jeffrey R. Hummel | San Jose State University |

Douglas Irwin | Dartmouth College |

Garett Jones | George Mason University (prior to co-editorship; multiple times) |

Niels Kærgård | University of Copenhagen |

Arnold Kling | Mercatus Center, George Mason University (multiple times) |

Jan Tore Klovland | Norwegian School of Economics |

Edward Leamer | University of California, Los Angeles |

Keith Lewin | University of Sussex |

Bruce McCullough | Drexel University |

Joseph McGarrity | University of Central Arkansas |

Joseph McLaughlin | International Epidemiology Institute |

Roger Meiners | University of Texas, Arlington |

Stephen C. Miller | Western Carolina University |

James Otteson | Wake Forest University |

Martin Paldam | Aarhus University |

Sam Peltzman | University of Chicago |

Mark Pennington | King’s College London |

Bhaven Sampat | Columbia University |

Edward M. Scahill | University of Scranton |

Kurt Schuler | U.S. Department of Treasury |

Jane Shaw | John William Pope Foundation |

Aris Spanos | Virginia Polytechnic Institute and State University |

Thomas Stanley | Hendrix College |

Guido Tabellini | Bocconi University |

Robert Tarone | International Epidemiology Institute |

Robert Whaples | Wake Forest University |

Abhay Aneja | Stanford University |

Frank Boons | Erasmus University, Rotterdam |

John J. Donohue III | Stanford University |

Eric D. Gould | Hebrew University |

Todd R. Kaplan | University of Haifa |

Marc T. Law | University of Vermont |

Mindy S. Marks | University of California, Riverside |

Thomas Mayer | University of California, Davis |

Deirdre N. McCloskey | University of Illinois, Chicago |

Robert Muñoz, Jr. | Portland State University |

Christine Meisner Rosen | University of California, Berkeley |

Alexandria Zhang | Johns Hopkins University |

Stephen T. Ziliak | Roosevelt University |

John Blundell | Institute of Economic Affairs, London |

David Colander | Middlebury College |

Tyler Cowen | George Mason University |

Richard A. Epstein | New York University |

James K. Galbraith | University of Texas, Austin |

J. Daniel Hammond | Wake Forest University |

David R. Henderson | Naval Postgraduate School |

Daniel Houser | George Mason University |

Jeffrey Rogers Hummel | San Jose State University |

Garett Jones | George Mason University |

Arnold Kling | Mercatus Center, George Mason University |

Steven G. Medema | University of Colorado, Denver |

Joseph J. Minarik | Committee for Economic Development |

Sam Peltzman | University of Chicago |

Richard A. Posner | University of Chicago |

Robert Solow | Massachusetts Institute of Technology |

Peter J. Wallison | American Enterprise Institute |

MTL are interested in the “Post-Study Probability (*PSP*),” which is the probability that a research finding that is statistically significant is true (MTL 2014, 284). Their equation (1), reproduced here as my equation (1), gives a formula for *PSP*:

$\mathrm{PSP}=\frac{\left(1-\mathit{\beta}\right)\mathit{\pi}}{\left(1-\mathit{\beta}\right)\mathit{\pi}+\alpha \left(1-\mathit{\pi}\right)}$ (1)

Interpretations of the expression’s terms are as follows:

- α =
*P*(test wrong|*H*_{0}), the probability that the test statistic rejects*H*_{0}(i.e., erroneously favors*H*_{1}) when*H*_{0}is true, - 1 −
*β*=*P*(test correct|*H*_{1}), the probability that a research hypothesis is found significant when it is true, *π*=*P*(*H*_{1}), the unconditional probability that*H*_{1}is true.Hence α denotes the probability of a type 1 error,*β*denotes the probability of type 2 error, and 1 −*β*is the power of the test. In repeated random sampling α and*β*are the long-run frequencies of type 1 and type 2 errors.

Alternatively, we can write an expression for *PSP* in terms of the probability that the null hypothesis *H*_{0} is true given that the data *D* provides support for the alternative hypothesis *H*_{1}. The probability that a research finding that is statistically significant is false is

$P\left({H}_{0}\text{|}D\right)=\frac{P(\mathrm{test\; wrong}|{H}_{0})\cdot P({H}_{0})}{P(\mathrm{test\; wrong}|{H}_{0})\cdot P({H}_{0})+P(\mathrm{test\; correct}|{H}_{1})\cdot P({H}_{1})}=1-PSP$ (2)

Note the use of Bayes’ theorem.A more sophisticated approach would require the specification of a prior distribution and not only the prior probability. The approach represented in equation (2) is widely applied in medical and psychiatric diagnosis, where all of the terms in right-hand side of the equation are presumably known, including *P*(*H*_{0}), which would be the unconditional probability of the prevalence of a disease in the population. Calculating the *PSP*, therefore, is of great value and provides information on how likely it is that a patient who is given a positive diagnosis actually has a disease.

MTL remind us that the probability of rejecting *H*_{0} when *H*_{0} is true (i.e., the probability of committing type 1 error) is not equal to the probability that the hypothesis *H*_{0} is true when *H*_{0} is rejected. Table 2 in MTL (2014, 286) shows, for example, that if *P*(*H*_{0}) is known and equals 0.99, and *P*(test wrong|*H*_{0}) = 0.05, and *P*(test correct|*H*_{1}) = 0.80, then Bayes’ theorem allows us to calculate the conditional probability $P\left({H}_{0}\text{|}D\right)=\frac{(0.05)\cdot (0.99)}{\left(0.05)\cdot (0.99\right)+\left(0.80)\cdot (0.01\right)}=0.86$, which is the posterior probability that the null is true when the researcher rejects the null. Hence, the *PSP* states that there is only a 14 percent chance, given a statistically significant finding at the 5% level, that there is a true association. Moreover, this estimate is still far from the worst case that is presented. MTL calculate several *PSP*s under the assumption that the priors are in the interval 0.45 < *P*(*H*_{0}) < 0.99. Based on the general impression from these calculations, MTL conclude that “it is not unlikely that the *PSP* after the initial study is less than 0.5, as several plausible parameter combinations yield this result” (2014, 287). That is to say, the conjecture is that *P*(*H*_{0}|*D*) is higher than 0.5. As mentioned, MTL (2014) suggest that a decision about whether to call an experimental finding noteworthy, or deserving of great attention, should be based on the Bayesian post-study probability since the Classical procedure is shown to have problems.

It follows immediately from Bayes’ theorem that *P*(*D*|*H*_{0}) ≠ *P*(*H*_{0}|*D*). About 20 years ago, in American Psychologist, Jacob Cohen (1994) raised this issue in the context of null hypothesis significance testing. Cohen made the point that there could be a chance as low as 40 percent that the statistically significant finding represented a true association even though *P*(test wrong|*H*_{0}) = 0.05, i.e., at a 5% significance level. In the same journal, Galen Baril and Timothy Cannon (1995) replied that, instead of using fabricated data to illustrate how different the probabilities can be, that is, that *P*(*D*|*H*_{0}) ≠ *P*(*H*_{0}|*D*), it would be more informative to estimate how large the gap between the conditional and reversed conditional probabilities is *likely* to be. In his reply Cohen (1995) made clear that his example was not intended to model null hypothesis significance testing as used “in the real world” but rather to demonstrate how wrong one can be when the logic of null hypothesis significance testing is violated. In light of the claims in MTL (2014), there is a need to revisit the results in Baril and Cannon (1995).

The starting point in Baril and Cannon (1995) is that statistical power cannot be sufficiently good to detect all effect sizes. Assuming that the effect sizes follow a standard normal distribution centered at zero and that scientists only detect and consider effect sizes |*d*| > 0.2 as relevant (*d* is what is known as Cohen’s effect size, i.e., it is the difference between means divided by the standard deviation), approximately 16 percent could be considered as equivalent to *H*_{0} being true.The point that economists *should* consider economic significance together with statistical significance is raised by McCloskey (1985). In case absolute substantive significance is hard to corroborate, Cohen’s *d* statistic offers a relative measure that facilitates sample size planning and power analysis. Baril and Cannon make use of an estimate from Joseph Rossi (1990) that the average statistical power for moderate effect sizes (i.e., *d* > 0.2) is 0.57. Finally, the conventional *P*(test wrong|*H*_{0}) = 0.05 is applied. Using Bayes’ theorem, we now have: $P\left({H}_{0}\text{|}D\right)=\frac{(0.05)\cdot (0.16)}{\left(0.05)\cdot (0.16\right)+\left(0.57)\cdot (0.84\right)}=0.016$, that is, the *PSP* states that there is a 98.4 percent chance that the statistically significant finding will represent a true association. Such a statement would mean that the probability of *H*_{0} being true given a significant test is 0.016, which is not very different from 0.05 which is, in turn, the probability of a significant test given that *H*_{0} is true. Clearly, 0.016 ≠ 0.05, but still the conditional and reversed conditional probabilities are shown to be not very different once a parameter space different from that adopted in MTL (2014) is adopted. The example also shows that the Classical significance test can be even more conservative than realized. Although it is possible that estimates (e.g., statistical power) are different in economic experiments compared to psychological experiments, using estimates from a related field can still be useful as a first approximation. Also note that even if we assume that the statistical power takes a considerably lower value of 0.20, the *PSP* then equals 0.95 which means that there is a 95 percent chance that the statistically significant finding will represent a true association. More crucial to our results is that we assumed that scientists are willing to consider economic significance instead of hunting only for statistical significance, such assumption affirming a norm about how to apply classical statistics.To understand the need of such norm, consider an economic experiment with a control and an experimental treatment. As soon as the experimental treatment has a non-zero percent of subjects that behave differently in the experimental treatment, retrieving a statistically significant result is only a matter of choosing the right sample size. A non-zero threshold, e.g., |*d*| > 0.2, adds a constraint on substantive significance. Choosing an appropriate threshold is of course a non-trivial task.

Remember that MTL assumed priors in the range of 0.45 < *P*(*H*_{0}) < 0.99 to calculate *PSP*, a range that is obviously far off from the neighborhood of *P*(*H*_{0}) ≈ 0.16, and they show that there, even in the absence of other biases such as research competition and research misconduct, the Classical framework leads to an “excessive number of false positives” (2014, 278) compared to what is stated in the significance level.MTL’s conclusion that Classical statistics leads to an “excessive number of false positives” is reached under the definition that the benchmark probability of false positives is the probability that *H*_{0} is true when *H*_{0} is rejected. The significance level in Classical statistics on the other hand measures the probability to reject *H*_{0} when *H*_{0} is true (i.e., error of the first kind). Hence the claim that Classical statistics leads to an “excessive number of false positives” is another way to claim that there is a positive difference between the conditional and reversed conditional probabilities. Importantly, there is no “excessive number of false positives” if we apply the standard definition in Classical statistics that the probability of false positives is the probability of error of the first kind. But MTL’s conclusion that we should embrace the Bayesian framework seems exaggerated. The conclusion is based on this selective empirical support that only considers 0.45 < *P*(*H*_{0}) < 0.99 and excludes the neighborhood of *P*(*H*_{0}) ≈ 0.16, a neighborhood that is appreciated to be a more realistic estimate and that would change their main result.

At this point we have not even taken into account that the prior could be biased but instead we have postulated that it is a known, a postulation that is in line with the simulation in MTL (2014). But this should not go uncommented, because therein lies the real rub. Postulating that the unconditional probability is known facilitates assessment of the probability that a research hypothesis that is statistically significant is true. But this probability is feasible only in the Bayesian framework.

In medicine the aim is to find the conditional probability that an individual patient who is given a positive diagnosis actually has the disease, and the unconditional probability, that is, prevalence in the population, is considered to be known or available. For economic hypotheses, the unconditional probability *P*(*H*_{0}) is hardly ever known. Bayesian statistics cope with this problem by assuming that the prior probability is a subjective belief, possibly mistaken, and subject to revisions.

This assumption, that the prior probability *P*(*H*_{0}) is a possibly mistaken belief, facilitates a move from the Classical to a Bayesian framework, even when the prior is unknown. What is worth emphasizing is that based on a single experiment and using prior beliefs we do not necessarily estimate the unbiased *P*(*H*_{0}|*D*) in the Bayesian framework. Going back to the example of Baril and Cannon (1995), remember that the conditional probability was calculated to be $P\left({H}_{0}\text{|}D\right)=\frac{(0.05)\cdot (0.16)}{\left(0.05)\cdot (0.16\right)+\left(0.57)\cdot (0.84\right)}=0.016$, and it was assumed that the unconditional probability is known and equals 0.160. Let us instead assume that the unconditional probability is unknown and that the subjective beliefs are that the prior corresponds to *P*(*H*_{0}) = 0.99. In this case, *P*(*H*_{0}|*D*) = $\frac{(0.05)\cdot (0.99)}{\left(0.05)\cdot (0.99\right)+\left(0.57)\cdot (0.01\right)}=0.897$. Hence, although *P*(*D*|*H*_{0}) = 0.05 is close to the correct benchmark of *P*(*H*_{0}|*D*) = 0.016, the conditional probability based on subjective beliefs is considerably higher, namely at *P*(*H*_{0}|*D*) = 0.897. The example demonstrates that it is easy to come up with counterexamples to MTL’s (2014) simulation and thereby show that the Bayesian framework does not necessarily perform better than the Classical framework, and might even perform worse, in estimating *P*(*H*_{0}|*D*). In the example above, the *PSP* calculation underestimates the probability that a statistically significant research finding is true.By incorporating subjective beliefs into the inference process, the risk of introducing errors or biases that would not otherwise be present is inevitable. On the other hand, the Bayesian approach is particularly useful when one has strong prior knowledge of a situation and wants to summarize the accumulated evidence.

The conceptual difference between the Classical and Bayesian frameworks regarding prior beliefs about *P*(*H*_{0}) also deserves to be mentioned. In Classical statistics a probability is the long-run relative frequency, while in the Bayesian framework a probability is the degree of the belief. Although posterior *P*(*H*_{0}|*D*) undeniably has an appealing interpretation, it is only available through Bayes’ theorem, which R. A. Fisher rejected with the motivation that it requires one to “regard mathematical probability not as an objective quantity measured by observable frequencies, but as measuring merely psychological tendencies, theorems respecting which are useless for scientific purposes” (Fisher 1937, 7). Although Fisher’s position may be perceived as extreme, I mention it to place the difference between the Classical and Bayesian approach in an historical context.

Based on what is presented in Maniadis, Tufano, and List (2014), the conclusion that only a Bayesian analysis provides “proper inference” seems exaggerated. The assumption that the unconditional probability *P*(*H*_{0}) is knownWhile MTL (2014) make use of different values of *P*(*H*_{0}) to calculate the difference between conditional and reversed conditional probabilities, in each calculation it is assumed that *P*(*H*_{0}) is known (unbiased), which makes the Bayesian approach into the benchmark from which any observed deviations under the Classical approach are interpreted as bias. implies that the Bayesian approach can only be better but never worse than the Classical approach in their simulation. Once we relax this assumption by allowing for subjective beliefs, it is no longer trivial to decide whether the Classical or the Bayesian framework is better. MTL combined the assumption that the unconditional probability is known with a selective empirical setup that also favors the Bayesian framework by excluding many instances where the problems of the Classical approach are small. Such moves do, of course, make the simulation in MTL (2014) great for demonstrating the pitfalls of the Classical framework.

First, if

P(H_{0}) is unknown, as is often the case with economic applications, the post-study probability can lead to even worse inference than the Classical significance test, depending on the quality of the prior. Second, the simulation in Maniadis et al. (2014) ignores previous assessments ofP(H_{0}) and instead utilizes a selective empirical setup that favors the use of post-study probabilities. … [Third,] contrary to what Maniadis et al. (2014) argue, their results do not allow for drawing general recommendations about which approach is the most appropriate. (Kataria 2014, abs.)

We believe that our work might have been misunderstood by Kataria. Moreover, it seems that some of his claims are not supported by relevant empirical evidence.

In Maniadis, Tufano, and List (2014), our basic aim is to draw on the general problem of the credibility crisis in disciplines other than economics (Ioannidis 2005; Bettis 2012; Jennions and Moller 2002), and to convey the disquieting news to economists by relying on insights and tools from the life sciences literature. While conveying the troubling news, we also emphasize the good news that usually it takes only a few independent replications to advance considerably the credibility of empirical exercises. We wish to understand how confident one should be in the published empirical findings in economics. Simply put, we are not discarding classical significance testing, just arguing that we should be interpreting it accurately. For an educated assessment of the empirical evidence we need to know not just whether tests were significant but also the value of key variables such as research priors and statistical power. Admittedly, these variables are not easy to estimate, and in economics it is often, even typically, the case that there is not much relevant evidence. But this is exactly our point: We wished to show that if we wish to assess how confident we are in our findings, evidence is lacking in critical dimensions. Given the recent evidence pointing to non-replicability in several life sciences (Ioannidis 2012), such lack of evidence may cause serious questions to be raised about economics as well (see Ioannidis and Doucouliagos 2013; Alexander 2013).

Whereas Kataria claims that “for economic hypotheses, the unconditional probability *P*(*H*_{0}) is hardly ever known” (Kataria 2014, 8), we suggest that the issue of such knowledge accumulation needs to be regarded as endogenous. If the investigator’s frame of analysis disregards the variable *P*(*H*_{0}), there is no need to estimate it. Other disciplines have developed meta-analytic methods that can be fruitfully employed in economics for estimating the relevant variables (Cooper, Hedges, and Valentine 2009). Replication has a key role in these methods.

To encourage such a structured approach, we illustrated with Tables 2 and 3, using Bayesian language, the fact that we should be cautious of new evidence and—as we argue later in Maniadis, Tufano, and List (2014)—that we should also increase our efforts to replicate original studies. We clearly note in the paper that the combinations of parameter values used in Tables 2 and 3 should be thought of as applying to novel and surprising findings (Maniadis, Tufano, and List 2014, 278, 286 n. 27). So these combinations were *truly selected* to illustrate what happens in the case of such findings. Moreover, we acknowledged the difficulty of pinpointing those combinations exactly (ibid., 286). Essentially, the degree to which our discipline is characterized by such combinations of priors and power is an empirical question. We hope that the message of the tables itself will encourage work on this underexplored question. Once more, we view as one of our key messages that we lack sufficient evidence to evaluate the credibility of much work in our field. We join others in prompting economists to grapple with such questions as: What is a reasonable estimate for the typical prior in each subfield of economic research? What is the typical power of a research study? How common is replication in economics and how common should it be?

Given the scarcity of relevant empirical studies, we find the particular configurations suggested by Kataria (2014) somewhat unsupported by the evidence. In particular, there seems to be no empirical foundation for the claims that “effect sizes follow a standard normal distribution centered at zero and…scientists only detect and consider effect sizes |*d*| > 0.2 as relevant” (Kataria 2014, 6). Despite this, Kataria claims that “the neighborhood of *P*(*H*_{0}) ≈ 0.16 … is appreciated to be a more realistic estimate” (ibid., 7). Estimating *P*(*H*_{0}) is a difficult empirical question that would require much more research. With respect to power, Kataria mentions evidence from the related field of psychology, namely Joseph Rossi (1990), who estimated that the average power for medium effect sizes is equal to 0.57. However, it is not clear on which evidence the assumption of medium effect sizes is based. Furthermore, more recent evidence reveals that typical power in psychology is about 0.35, even if we assume that the average effect size |*d*| is equal to 0.5 (Bakker, van Dijk, and Wicherts 2012).

The spirit of our paper is to encourage work such as the very recent paper by Le Zhang and Andreas Ortman (2013). They retrospectively estimated the power of several experimental designs reported in Christoph Engel’s meta-analysis of dictator games (Engel 2011), and they found that the median level of power was less than 0.25. It is important to note the critical role of meta-analysis for generating this piece of new evidence. The point is not to argue in the absence of evidence but to try to accumulate the necessary evidence. As economists, we hope that our field is very credible, but we need to provide empirical evidence using the relevant tools.

At this point we need to acknowledge the important issue of “previous assessments of *P*(*H*_{0}),” although Kataria mentioned it without justification. As we said in Maniadis, Tufano, and List (2014), we aimed to make a claim about novel, surprising results. We do believe that many types of economic research are more grounded in theory than research in other social sciences, so for them “surprising” results may not be as important for publication. In fact, Brad DeLong and Kevin Lang (1992) found that *P*(*H*_{0}) is very close to zero for a set of hypotheses published in top economic journals in the 1980s. If their interpretation—that the referee process somehow manages to filter true associations—is correct, that would be reassuring for the credibility of the economics profession. As DeLong and Lang (1992) acknowledge, however, there are alternative interpretations for their findings, such as the existence of selection issues and data mining in the discipline, so their optimistic interpretation should be taken with caution. There is a need for further research on the matter, following the seminal analysis of DeLong and Lang (1992). We are particularly interested in the field of experimental economics, where we worry that “surprising” findings might be more frequently published.We would welcome more empirical evidence on this and related issues.

From the previous arguments it should be clear that in Maniadis, Tufano, and List (2014) we did not put forward any general recommendation about which inference approach, Classical or Bayesian, is the most appropriate. In fact, in the context of the current “publish or perish” culture (see, e.g., Fanelli 2010) and the related structure and incentives of the economics knowledge system (Oswald 2007; Glaeser 2008; Young, Ioannidis, and Al-Ubaydli 2008), we merely resort to Bayesian language to argue in favor of a much more careful interpretation of Classical inference.

Summing up, we believe that studying systematically the factors that affect the credibility of empirical findings might have an important role to play in economics. Meta-analysis and Bayesian tools are of central importance for conceptualizing the problem and quantifying key variables, and should not be ignored by economists. Our point was not to argue in favor of a specific configuration of parameter values, but to show that we cannot ignore factors such as priors and power, because if we do, something can go very wrong with economic research.

]]>The modernization hypothesis, understood as political development, is investigated in several papers by Daron Acemoglu, Simon Johnson, James Robinson, and Pierre Yared (2005; 2008; 2009), a team of authors hereafter referred to as AJRY. Using mainly panels of countries spanning the period 1960–2000, they find no correlation between income and democracy after controlling for country specific factors and world trends, that is, after allowing for country and time effects, and likewise for education and democracy. AJRY (2009) interpret their country fixed effects results as being consistent with the critical junctures hypothesis.Exponents of the critical junctures hypothesis are Moore (1966) and O’Donnell (1973). The fixed effects, AJRY say, are “capturing the impact of time-invariant, historical variables simultaneously affecting the evolution of income and democracy” (AJRY 2009, 1057). Put differently, fixed effects proxy for country-specific differences in institutional quality that ultimately account for the observed correlation between income and democracy.

Econometric specifications used in the 2008 and 2009 papers by AJRY always include among the independent variables income and a proxy for democracy, both lagged, and in the 2005 paper they always include education and democracy, also both lagged. The democracy variable measures quality of *political* institutions, but AJRY do not control for *economic* institutions. More specifically, AJRY do not include a variable to control for the level of inclusiveness of economic institutions.

Income is at least to some extent a result of the interplay between economic and political institutions. In our view, economies tend to grow if political and economic institutions induce a stable environment where private property of the vast majority of the population is protected, creating incentives to work, innovate, invest, and allocate resources efficiently.Jong-A-Pin and De Haan (2008; 2011) report episodes of growth acceleration which are preceded by economic liberalizations. Additional evidence supportive of a beneficial effect of democratic institutions on growth is uncovered by Mobarak (2005), who finds that democracies enhance growth through the channel of reduced volatility given the inverse relation between political development and volatility. See also Persson and Tabellini (2009) for the role of democratic capital in stimulating growth by enhancing democracies’ stability. We strive to incorporate such mechanisms in comparative political development research by including, in addition to democracy and income, an index of economic freedom as a proxy for capitalist institutions which are crucial for development along with human capital.For recent supportive evidence see Ashraf and Galor (2013), and for a fresh summary of the literature on deep determinants of economic development and the role of institutions see Spolaore and Wacziarg (2013). A central indicator of economic freedom is quality of the legal infrastructure, in particular extent of the rule of law and independence of the judiciary, both of which can in the spirit of Lipset be interpreted as proxies for some social requisites for political development.

AJRY’s basic results hinge on specifications which control for lagged democracy and country and time fixed effects, and in this context of limited residual variability they attempt to assess if income exerts an independent effect on democracy, and likewise for education.To better appreciate the issue of reduced variability left to be explained by income, see Benhabib, Corvalan, and Spiegel (2011), who document that in democracy regressions using country five-year panels, the inclusion of lagged democracy along with country and time fixed effects accounts for 81% of total variation of the democracy variable, leaving little variability to be explained by income. A similar point is made by Paldam and Gundlach (2012, 164 n. 21): “This empirical model [referring to the specification used by AJRY (2008)] leaves virtually nothing to be explained by income, and consequently the effect of income becomes insignificant, and is declared spurious.” Needless to say this problem of little variance of democracy left to be explained by income or education is not mitigated and can be aggravated by the inclusion of economic institutions to the extent that economic freedom impacts democracy.Indeed, components of economic freedom such as rule of law can promote democratization.

Moreover, economic freedom and income are highly correlated, as are economic freedom and education. The collinearities between income and economic freedom and between education and economic freedom, like the inclusion of economic freedom, reduce the likelihood of uncovering a statistically significant impact of income and/or education on democracy. Thus we are stacking the cards against the modernization hypothesis, and in this sense our tests are more demanding than those performed by AJRY.

A final reason for including economic freedom is that a research strand in the economics literature argues that economic freedom is a necessary condition for political freedom.Among early proponents of this research strand are Friedman (1962) and Hayek (1944). The view has found recent empirical support in Lawson and Clark (2010). Economic freedom may be an important channel in explaining democracy that has gone missing in the modernization literature.

Another trait that distinguishes this paper from those of AJRY is methodological. Part of our empirical strategy is the application to our sample of the System Generalized Method of Moments estimator developed by Richard Blundell and Stephen Bond (1998). The System GMM estimator is particularly suited for identification tasks where the variables are highly persistent, which is the case with income, education, and democracy.

We apply System GMM techniques to an unbalanced panel of countries spanning the 1970–2010 sample period,Thus, similar to AJRY, we focus on a recent sample. using quinquennial data and after controlling for economic freedom and democracy. We find that education and income predict democracy. Also, applying OLS to our data set and using a specification that captures long-run changes in democracy, we obtain results that support the modernization hypothesis.

The research in this paper is related to a number of recent studies, some of them motivated by the papers by AJRY (2005; 2008; 2009). First and perhaps the closest to ours, is a paper by Benedikt Heid, Julian Langer, and Mario Larch (2011), which finds support for the modernization hypothesis using the System GMM technique. But unlike Heid, Langer, and March (2011), we control for economic institutions and address the role of education as a driver of modernization.

Jess Benhabib, Alejandro Corvalan, and Mark Spiegel (2011) report evidence favorable to the modernization hypothesis after employing panel nonlinear estimation methods that account for censored democracy data. As previously mentioned we find support for the modernization hypothesis using linear estimation methods, also used by AJRY (2005; 2008; 2009). However, our results rely on the Blundell-Bond System GMM estimator which is employed by neither AJRY (2005; 2008; 2009) nor Benhabib, Corvalan, and Spiegel (2011). Further, education is treated by Benhabib et al. (2011) as another covariate in addition to income in their main specification. We also perform regressions displaying horse races between income and education. In line with Lipset (1959; 1960) we attempt to evaluate education’s predictive power of democracy independently of income.Lipset (1959) viewed education as a necessary condition for democracy. Consequently, we present regression specifications containing income but excluding education and, symmetrically, specifications that include education and exclude income.*See* Glaeser, Ponzetto, and Shleifer (2007) for a theoretical development in which education is modeled as having a causal impact on democracy.

Carles Boix (2011) argues that AJRY’s results are partly driven by the post-WWII sample period in which the effect of income on democracy is particularly weak. He finds support for modernization in long-run panels that use fixed effects spanning eighty or more years. By contrast, we find support for the Lipset hypothesis using a sample that focuses on recent decades commencing in 1970 and ending in 2010.

Eric Gundlach and Martin Paldam (2009) employ the Polity index as a proxy for democracy and use a sample that spans the period from 1820 to 2003. Estimating OLS and Two-Stage Least Squares cross-country regressions for each of the 184 years intervening between 1820 and 2003, Gundlach and Paldam find evidence that buttresses the democratic transition view. These scholars use this long-run procedure because in their view five-year panels offer a horizon too short to test the democratic transition hypothesis. Gundlach and Paldam write: “The Grand Transition view and the Democratic Transition hypothesis are about long-run trends that can be best handled by pure cross-section estimates, not by a combination of fixed effects and lagged adjustment over a short time horizon” (2009, 349-350).A similar argument is articulated by Paldam and Gundlach (2012, 152), who interpret their Granger causality test results as revealing “that the short to medium run is probably not well suited to identifying the main direction of causality between income and democracy.” Nonetheless and as previously indicated, we find support for the modernization thesis using panels with a five-year frequency.

Paldam and Gundlach (2012) use the Gastil index as a proxy for democracy. They apply country and time fixed effects in a balanced panel of countries spanning the 1972–2008 period with frequencies of 18, 12, and five years. They find support for the modernization hypothesis using five-year panels and restricting the sample to the pre-1989 period.Unfortunately, Paldam and Gundlach (2012) do not indicate if the estimated standard errors used to assess the statistical significance of regression coefficients are robust to the presence of arbitrary heteroskedasticity and/or autocorrelation, or are clustered by countries. Reporting the type of standard error is relevant because the significance test may be invalid and the estimated p-value may change depending on the type of standard error used. Like Gundlach and Paldam (2009), Paldam and Gundlach (2012) do not control for economic institutions,*See* Gundlach and Paldam (2009) for a justification of institutions-free analyses of democratic transition. and they do not use dynamic specifications such as were employed by AJRY. Nonetheless, after applying OLS and IV methods to long-run cross-country specifications, both papers report strong support for the modernization hypothesis.

Daniel Treisman (2012) provides evidence which suggests that the impact of development on democracy takes place over a 10- to 20-year time span. The finding is particularly strong after 19th-century data is included. Treisman writes: “The new point I emphasize here is that the link between income and democracy is clearest and strongest *in the medium to long run*—i.e. panels of 10 to 20 years” (2012, 7, emphasis in original). Moreover, similar to Boix (2011) and to AJRY, Treisman (2012) reports that over the 1960–2000 period income does not predict democracy in panels of one-, five-, 10-, 15- and 20-year frequencies. However, Treisman does not apply Blundell-Bond methods to any sample period.

Ghada Fayad, Robert Bates, and Anke Hoeffler (2012) applied a Pooled Mean Group estimator (PMG), augmented with averages of all variables in the model to proxy for time-common factors, to a sample of countries with observations that commence in 1955 and end in 2007.The PMG estimator does not allow for year fixed effects because parameters are estimated separately for each country. To correct for this shortcoming of the PMG methodology, the Fayad et al. (2012) model is augmented with world income and democracy. They find that income is negatively and significantly related to democracy. Parameter estimates associated with world income and world democracy enter positively and significantly, predicting greater democratization at the country level. Figure 1 in Fayad, Bates, and Hoeffler (2012, 5) graphs world democracy and world per capita income starting in 1960 and ending in 2008 for a sample of 105 countries. World income mostly rises over the sample period whereas the democracy index falls during 15 consecutive years from 1960 through 1975. Yet, over the following 33 years the world democracy index rises along with income. Thus the Fayad, Bates, and Hoeffler (2012) Figure 1 is generally consistent with the modernization hypothesis.

Furthermore, the heterogeneous PMG estimator used by Fayad, Bates, and Hoeffler (2012) estimates individual country coefficients thus requiring long time series for each country included and excluding countries with a time-invariant dependent variable.In other words, regression coefficients are calculated for every country in the sample, as opposed to, say, OLS, which estimates one slope coefficient for all the countries. The PMG estimator by design eliminates time-invariant dependent variables. This is not so extraordinary (e.g., the fixed-effect methods employed by AJRY also by design discard time-invariant variables, which appear frequently among explanatory variables). Due to this long time series requirement, countries that transition to democracy such as the Czech Republic, Estonia, Latvia, Lithuania, and Slovak Republic are not included in the sample. Among the time-invariant consistent democracies excluded are Australia, Austria, Belgium, Canada, Denmark, Finland, Ireland, Italy, Japan, Netherlands, New Zealand, Norway, Sweden, Switzerland, United Kingdom, and United States. Among the consistent autocracies excluded are Cuba, Libya, and Vietnam. Fayad, Bates, and Hoeffler (2012, 14) write: “Both the sample choice and the methodology thus led us to our results.” In other words, the methodology constrains the sample, leaving out potential important sources of information.

Additionally, Fayad, Bates, and Hoeffler show in Table 2 (2012, 11) that, both for their sample of 105 countries and for AJRY’s sample, OLS fixed effects estimates of income per capita are insignificant only when conditioning on year fixed effects. As previously mentioned, the PMG estimator does not allow for year effects.

The OLS Pooled Error Correction Model (PECM) admits controls for country and time fixed effects, however. The results of Fayad, Bates, and Hoeffler’s main sample using OLS (PECM) are shown in their Table 5 (2012, 14). In three out four different lag structure models, income per capita at the country level enters significantly negative, albeit only at a 10% significance level. They write: “However, estimating the pooled error correction model while using the AJRY (bigger) sample yields long-run coefficients on income per capita that are insignificant, regardless of the number of lags” (ibid., 13).

Interestingly, when Fayad, Bates, and Hoeffler apply the PMG estimator without accounting for their proxies for time effects, “the coefficient on income per capita is instead positive and significant” (2012, 12 n. 11). Overall, this evidence they offer may lead one to suspect that their results are also sensitive to the methodological procedure due to the technical impossibility of controlling for year effects using annual dummies when the PMG method is employed.

In light of the findings of Treisman (2012) and particularly Boix (2011), a potentially interesting robustness check of the Fayad, Bates, and Hoeffler (2012) findings may be to expand the sample coverage to earlier periods. This extension may alleviate sample attrition containing relevant information.A recent paper that addresses the relation between education and governmental quality and, indirectly, the relation between education and democracy is Botero, Ponce, and Shleifer (2013). As they write: “Most studies find that education and development lead to improved government (e.g., Barro 1999, Glaeser et al. 2004, Bobba and Coviello 2007, Castello-Climent 2008, Murtin and Wacziarg 2011), although some disagree (Acemoglu et al. 2005). In this paper, we ask *why* the quality of government improves with education and development, assuming that it does” (Botero et al. 2013, 2).

Our sample period comprises the years 1970 through 2010. In this regard our paper follows a common practice in the democratization literature of using data less afflicted by measurement problems than data prior to the Second World War.

We pool cross-section data with time series data in order to exploit the time dimension of the data, allowing us to investigate the impact over time of variables which proxy for socio-economic development, such as real income and human capital, on democracy. Specifically, exploiting the within-country variation in the data permits us to evaluate whether, as a country becomes more socio-economically developed, relative to its mean, it also turns out to be relatively more democratic.

Our dependent variable and proxy for democracy measures is the Index of Political Rights from Freedom House published in 2010. In the Index, “political rights” include the existence of free and fair elections, competitive parties, an opposition that plays an important role in the political process, and whether those who are elected rule, among others. “Political rights are rights to participate meaningfully in the political process. In a democracy this means the right of all adults to vote and compete for public office, and for elected representatives to have a decisive vote on public policies” (Gastil 1991, 7).The late Raymond Gastil directed Freedom House from 1977 to 1988 and made a decisive contribution to its indexes on political rights and civil rights, which are now published yearly. The Index of Political Rights goes from one to seven, where one indicates most politically free and seven least free.

Our independent variables are lagged democracy, log of real income per capita, human capital, and the Economic Freedom of the World (EFW) index. Real income per capita is provided by the World Development Indicators published in 2010 by World Bank. Human capital is provided by Robert Barro and Jong-Wha Lee (2010)This metric of human capital updates the Barro and Lee (2000) data set and corrects for measurement errors in educational attainment and takes account of criticisms made by Cohen and Soto (2007). and measures average years of education of the population 25 years and older. The EFW index—inspired by Milton Friedman, built over the years since 1997 by James D. Gwartney and Robert Lawson, and published by the Fraser Institute—is our proxy for capitalism. The EFW index contains the following areas: (1) “Size of Government: Expenditures, Taxes, and Enterprises”; (2) “Legal Structure and Security of Property Rights”; (3) “Access to Sound Money”; (4) “Freedom to Trade Internationally”; and (5) “Regulation of Credit, Labor, and Business” (Gwartney, Lawson, and Hall 2011). Thus the index controls for trade, inflation, regulation, government spending, taxes, rule of law, and quality of the judiciary. The ratings for the components of the EFW index range from zero to ten with higher ratings indicating more economic freedom. The summary ratings are an aggregation of the five area ratings, and they almost always fall within a range between three and nine.

Using quinquennial panels and an unbalanced panel of countries from 1975 to 2010 we estimate the following regression model:This functional form is used by Glaeser, La Porta, Lopez-de-Silanes, and Shleifer (2004).

${\mathit{PF}}_{i,t}-{\mathit{PF}}_{i,t-1}=\alpha \cdot {\mathit{PF}}_{i,t-1}+\mathit{\beta}\cdot {\mathit{EFW}}_{i,t-1}+\mathit{\theta}\cdot {Y}_{i,t-1}+\mathit{\tau}\cdot {\mathit{HK}}_{i,t-1}+{\mathit{\delta}}_{i}+{\mathit{\mu}}_{i}+{\mathit{\epsilon}}_{it}$ (1)

where change in political rights*PF*_{i,t} stands for level of political rights in country *i* at year *t*. is regressed against lagged political rights to capture persistence in democracy and also potentially mean-reverting dynamics. The main parameters of interest are *θ* associated with initial-period income, and *τ* associated with initial-period human capital. Specification (1) allows for country fixed effect dummies, with *δ _{i}* to control for country idiosyncratic time-constant factors, and for time period dummies, with

Results shown in Table A indicate that, applying fixed-effects OLS over non-overlapping five-year periods comprising thirty-five years, initial-period (lagged) political rights (in columns 1 and 2) enter negative and statistically significant at a 1% level, suggesting the presence of mean reversion. Controlling for income (column 1) and human capital (column 2), the regression coefficient associated with economic freedom is negative and significant at a 5% level, consistent with the view that higher levels of economic freedom induce more democratic change. Income (column 1) enters significantly though with a positive sign, inconsistent with the modernization hypothesis implying that development leads to less democracy, whereas human capital (in column 2) does not predict democracy at a 5% significance level.

Column (3) presents our first horse race results between income and education. Human capital does not predict democracy. Income, however, enters significantly predicting *less* democracy.

According to AJRY, conditioning on fixed effects captures the spirit of the critical junctures hypothesis to the extent that it accounts for the effect of unobserved heterogeneity associated with time-invariant historical factors impacting both political and economic development. In their sample, income loses significance controlling for fixed country effects and time dummies, which is consistent with the critical juncture hypothesis. However, our results indicate that economic freedom predicts more democracy and income predicts less democracy. This evidence suggests that their democracy-income effects are sensitive to the presence of economic freedom in the model.In our sample and using our functional form that regresses changes in democracy over five-year periods against initial-period democracy and income, and also allowing for time and country fixed effects but not controlling for economic freedom, income enters significantly at a 5% level predicting *less* democracy. These results, which are available upon request, are also at odds with the tenets of the modernization hypothesis.

While fixed-effects estimation methods correct for biases induced by the omission of a complete list of country-specific unobserved heterogeneity variables correlated with the independent variables, parameter estimates are inconsistent if time-varying independent variables correlated with explanatory variables are omitted, violating consequently the strict exogeneity assumption. Moreover, fixed-effects estimates in dynamic specifications are biased, and in short time-period panels inconsistent,However, these estimates become consistent as country time observations increase. More precisely, the fixed-effect estimator is consistent as T increases assuming both that there is no other source of correlation between lagged democracy and the error term and that remaining regressors are strictly exogenous (see Wooldridge 2002). due to the correlation between the transformed lagged dependent variable and the transformed unsystematic error term *ε*_{i,t} inherent to the time-demeaned transformation. To overcome inconsistency of the fixed-effect estimator, and following AJRY, we apply the Difference Generalized Method of Moments (GMM) estimator proposed by Manuel Arellano and Stephen Bond (1991). In addition, we also apply the System GMM estimator introduced by Blundell and Bond (1998) to the following dynamic specification:The estimating equations (1) and (2) are equivalent. Specification (1) is obtained subtracting lagged democracy on both sides of (2).

${\mathit{PF}}_{i,t}=\alpha $′$\cdot {\mathit{PF}}_{i,t-1}+\mathit{\beta}\cdot {\mathit{EFW}}_{i,t-1}+\mathit{\theta}\cdot {Y}_{i,t-1}+\mathit{\tau}\cdot {\mathit{HK}}_{i,t-1}+{\mathit{\delta}}_{i}+{\mathit{\mu}}_{i}+{\mathit{\epsilon}}_{it}$ (2)

where the dependent variable is the level of political rights for country *i* in period *t*.

Columns (4) through (9) of Table A present Arellano-Bond estimates. Economic freedom enters significantly and negative in column (4), whereas income enters significant at a 10% level and positive, thus with a sign at odds with Lipset’s hypothesis. In column (5) controlling for time effects, economic freedom loses significance, the p-value being 0.103, and income again enters significantly at a 5% level but with the ‘wrong’ sign. In columns (6) and (7) we substitute human capital for income, and only lagged political freedom enters significantly. Horse race results between human capital and income using Arellano-Bond are presented in column (8) not controlling for time effects and in column (9) controlling for time effects. Lagged income enters significantly at a 10% level in column (8) and at a 5% level in column (9). However, in both cases income predicts less democracy. Human capital again does not predict democracy at conventional levels of significance.

Moreover, Sargan tests suggest that none of the models that apply Arellano-Bond methods are correctly specified. These results are qualitatively similar to those obtained by AJRY (2005; 2008; 2009) in that predictors of the modernization hypothesis, education and income, either enter not significantly or, if significantly, show up with associated regression coefficients bearing the wrong sign.

The Arellano-Bond estimator is based on the following moment conditions: E(*PF*_{i,t−s}Δε_{it}) = 0 for *t* ≥ 3 and s ≥ 2. It is well known, however, that democracy, education and income are highly persistent variables,See, for example, Glaeser, Ponzetto, and Shleifer (2007) and Bobba and Coviello (2007). and therefore instruments in levels are poorly correlated with first differences.To understand the poor correlation between the instrument in levels and subsequent differences when the series is highly persistent, consider a simple autoregressive process of order one (AR(1)), e.g., *PF*_{it} = α*PF*_{i,t−1} + ε_{it}. Subtracting *PF*_{i,t−1} from both sides, to transform this process in differences, yields Δ*PF*_{it} = (α − 1)*PF*_{i,t−1} + ε_{it}. The closer the value of α to 1 (the higher the persistence), the lower the correlation between Δ*PF*_{it} and *PF*_{i,t−1}, that is, between the difference and the level. This low correlation originates a weak-instrument problem aggravating finite sample biases. To enhance precision of the point estimates, the Blundell-Bond System GMM estimator employs simultaneously the equation in levels and the equation in first differences, conforming to a system of equations which uses lagged differences as internal instruments for the equations in levels and lagged levels as instruments for the equation in differences. Thus, the procedure allows us to exploit additional overidentifying moment restrictions that may contribute to overcome the weak-instrument problem. These additional moment restrictions use internal instruments in differences which are assumed to be orthogonal to the country fixed effect plus the zero mean error term.This is not to say that the Blundell-Bond estimation technique cannot be afflicted by weak instruments; see Bazzi and Clemens (2013) for cases in the economic growth literature. Alas, extant econometric methods do not provide standard tests to detect weak instruments in dynamic panel GMM settings.

In Table A, the Columns (10), (11), and (12) report Blundell-Bond estimates. The parameter estimate associated with income in column (10) is significant at a 5% level, with a p-value of 0.018, and the estimate is negative, suggesting that development predicts democracy. According to column (11) the point estimate of education is also negative and significant at a 5% level with a p-value of 0.018, indicating that education predicts democracy. Both specifications, used in columns (10) and (11), condition on time effects and in neither do the regression coefficients associated with economic freedom enter significantly. Further, according to the Hansen over identification test and second order autocorrelated disturbances in the first differences equations, AR (2), we fail to reject the Hansen test’s null hypothesis that the instruments are valid and also the null hypothesis of no second-order autocorrelation.Interestingly, when applying Blundell-Bond methods to specifications that do not control for economic freedom, income does not predict democracy, which underscores the appropriateness of our basic specification that includes economic freedom. These results are available from the authors upon request.

Column (12) contains results of the horse race between income and education. Neither income nor education enters significantly. In fact, only the coefficient estimate of lagged democracy, the autoregressive variable, enters significantly.

Summing up the results of our horse races using high-frequency panels: parameter estimates associated with education do not enter significantly, and in the cases where income parameter estimates entered significantly they show up with the ‘wrong’ sign. Similarly non-instructive results are reported by AJRY (2005, 46) in their Table 1. This lack of meaningful results should not be surprising given the aforementioned low residual variability to be explained by income or education. The lowness of the residual variability stems from the inclusion of lagged democracy, economic freedom, time and fixed effects (see footnote 10). This problem is exacerbated by the simultaneous inclusion of both of the democracy predictors, education and income, which are highly positively correlated.

Finally, columns (13), (14), and (15) of Table A evaluate the predictive power of income, human capital, and economic freedom on political rights over a longer time span and using traditional OLS methods. We use a specification where the dependent variable is the change in political freedom over 35 years from 1975 to 2010 and the independent variables are the initial values of political rights, economic freedom, income, and/or human capital.

Economic freedom in 1975 does not predict a change in political rights over the long run controlling for income (column 9) and human capital (column 10) in the year of 1975. By contrast, parameter estimates associated with income and human capital show up as highly significant in columns (9) and (10) respectively. Regression coefficient estimates are precisely estimated and appear with the hypothesized sign. The negative sign of 1975 political rights suggests the presence of mean reversion.

These findings are reassuring because they suggest that our results based on shorter time spans are not driven by sample characteristics. Indeed, the evidence is consistent with prior findings on the long-run effects of income and education on democracy.

Lipset’s renowned quotation (1959, 75) suggests a gradual democratization process associated with greater socio-economic development. Thus, the empirical strategy of panel data with fixed effects, which assesses the within-country variation between relative wealth or education and democracy, captures econometrically the spirit of Lipset’s hypothesis.

Applying fixed-effects OLS and Arellano-Bond methods to our post-World War II data set, using five-year high-frequency panels and conditioning on a proxy for capitalism, we obtain results qualitatively similar to those of AJRY to the extent that increasing both income and education do not induce greater political development. However, to account for weak instruments and endogeneity bias, we use a System GMM estimator advanced by Blundell and Bond, and we find that income and education predict democracy in five-year panels conditioning on economic freedom. Intuitively, as countries become relatively wealthier and their populations relatively more educated, the likelihood of these countries becoming relatively more democratic increases. We also find using OLS that democracy changes over a 35 year period are predicted by income and human capital in 1975. Thus, using our sample and the frequently used method of OLS, we corroborate prior evidence that was consistent with the modernization theory.

Finally, given the complex interplay between development, capitalism and democracy, we conjecture that one causation channel goes from institutions, such as economic freedom and human capital, to development, and that another channel leads from development to democracy. Thus economic freedom becomes an indirect catalyst of democracy through its impact on development.James Gwartney (2013) in a personal communication states a similar view: “Finally, there is strong evidence that increases in economic freedom promote subsequent increases in income levels. With time, these higher income levels will also promote democracy. Thus, acting through income, increases in economic freedom will also tend to promote democracy. But, the lags between both (a) increases in economic freedom and higher income levels and (b) increases in income and moves toward democracy will be long and variable. Thus, when analyzed across time periods of even a decade or two, the economic freedom–democracy linkage will be quite weak.” This of course is not a fully resolved issue and is part of an ongoing research agenda.For some of the evidence on the link between economic freedom and development see Dawson (1998); Faria and Montesinos-Yufa (2009); Gwartney, Holcombe, and Lawson (2006); Hall, Sobel, and Crowley (2010); Rode and Coll (2012); and Bennett, Faria, Gwartney, and Morales (2013). On the relation between capitalism and democracy see Aixala and Fabro (2009); De Haan and Sturm (2003); Lundstrom (2005); Rode and Gwartney (2012); and Giuliano, Mishra, and Spilimbergo (2013).

Short-run fixed effects | Arellano-Bond | Blundell-Bond | Long-run OLS | ||||||||||||

Independent variables | (1) | (2) | (3) | (4) | (5) | (6) | (7) | (8) | (9) | (10) | (11) | (12) | (13) | (14) | (15) |

Initial political rights | −0.692 (0.000) | −0.665 (0.000) | −0.673 (0.000) | 0.349 (0.000) | 0.327 (0.000) | 0.447 (0.000) | 0.438 (0.000) | 0.413 (0.000) | 0.391 (0.000) | 0.817 (0.000) | 0.765 (0.000) | 0.788 (0.000) | −0.735 (0.000) | −0.764 (0.000) | −0.821 (0.000) |

Initial economic freedom | −0.199 (0.064) | −0.164 (0.106) | −0.204 (0.060) | −0.203 (0.006) | −0.141 (0.103) | −0.090 (0.258) | −0.082 (0.328) | −0.135 (0.111) | −0.124 (0.152) | 0.078 (0.504) | 0.006 (0.947) | 0.017 (0.867) | −0.058 (0.770) | 0.081 (0.621) | 0.029 (0.875) |

Initial income | 0.407 (0.045) | 0.418 (0.043) | 0.514 (0.055) | 0.638 (0.028) | 0.570 (0.052) | 0.744 (0.012) | −0.176 (0.018) | −0.071 (0.411) | −0.536 (0.001) | −0.110 (0.677) | |||||

Initial human capital | 0.123 (0.138) | 0.115 (0.167) | −0.013 (0.831) | 0.058 (0.614) | −0.049 (0.438) | 0.118 (0.301) | −0.081 (0.018) | −0.055 (0.159) | −0.374 (0.000) | −0.352 (0.008) | |||||

Time effects | yes (0.008) | yes (0.047) | yes (0.028) | no | yes (0.674) | no | yes (0.798) | no | yes (0.677) | yes (0.465) | yes (0.006) | yes (0.176) | |||

Number of observations | 785 | 758 | 741 | 527 | 527 | 521 | 521 | 504 | 504 | 785 | 758 | 741 | 85 | 94 | 83 |

Residual AR(2) test | (0.174) | (0.170) | (0.601) | (0.643) | (0.536) | (0.589) | (0.302) | (0.740) | (0.731) | ||||||

Hansen OIR test | (0.117) | (0.235) | (0.979) | ||||||||||||

Sargan OIR test | (0.005) | (0.004) | (0.003) | (0.001) | (0.011) | (0.005) | |||||||||

Dependent variables are: for columns (1) to (3), change in political rights between t−1 and t; for columns (4) to (12), level of political rights at t; for columns (13) to (15), change in political rights between 1975 and 2010. Sample periods are: for columns (1) to (12), the eight five-year periods 1970–2010; for columns (13) to (15), the one 35-year period 1975–2010. An “initial” variable is the value of the variable at time t−1. A “change” in a variable is its value at time t minus its value at time t−1. P-values are in parentheses. Estimated coefficients are above p-values. Fixed effects p-values are calculated using clustered standard error by country. Arellano-Bond and Blundell-Bond p-values are calculated using robust standard errors. |

Data and code files used in this research can be downloaded from the Econ Journal Watch website (link).

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