Political institutions and academic freedom: evidence from across the world

We consider the following definition from The Lima Declaration on Academic Freedom and Autonomy of Institutions of Higher Education (Fernando, 1989, p. 50) to be useful: “‘Academic freedom’ means the freedom of members of the academic community, individually or collectively, in the pursuit, development and transmission of knowledge, through research, study, discussion, documentation, production, creation, teaching, lecturing and writing”. For more on the history and concept of academic freedom, see, e.g., Machlup (1955), Altbach (2001) and Karran (2009).

For more on how academic freedom can be justified, see, e.g., Moodie (1996) and Karran (2009).

The existing literature on factors influencing academic freedom mainly comprises qualitative discussions or limited studies of particular cases or countries. For example, vommercial academic-industry relationships do not seem to reduce academic freedom (Behrens & Gray, 2001; Streiffer, 2006); government research assessments appear to have detrimental effects on academic freedom (Martin-Sardesai et al., 2017); communism has impeded academic freedom in Polish sociology (Kwasniewicz, 1994); and the authoritarian cultures of many Muslim-majority countries has been detrimental for academic freedom (Kraince, 2008).

Political institutions have been shown to affect outcomes other than academic freedom – for overviews, see Persson and Tabellini (2003), Kurrild-Klitgaard and Berggren (2004) and Voigt (2020).

Leighton and López (2014) show how academics often can influence reform paths by providing alternatives to the prevailing ideas that are available to political decision-makers at critical junctures.

The conclusion applies to scholars whose work is relevant for politics, in particular those in the social sciences and humanities, and not so much to scholars in the natural sciences. Hence, political decision-makers can champion academic freedom for the latter, while at the same time wanting to restrict, or actually restrict, the academic freedom of those who are seen as threats to their position of power or their ideological goals. Unfortunately, the data do not specify how academic freedom varies between academic disciplines, so we cannot test for such differential effects in our empirical analyses.

Evidence has been reported that fair and free elections can discipline political decision-makers when it comes to economic policy matters, arguably having those decisions conform more to the public interest (Collier & Hoeffler, 2015), if it were possible to identify what that may be.

Effects of (changes in) political institutions can be of a short- and a long-term kind: the former reflecting “immediate” adjustments and the latter incorporating settled equilibrium effects. We do not have particular theoretically based expectations about the temporal or dynamic character of how political institutions influence academic freedom but consider it an important issue to study empirically, and we do so below. Moreover, the effects can also differ within democracies and within autocracies, as well as between them, which is why we also report interactions between the system of government and a number of political institutions below.

The V-Dem indicators are based on expert assessments. Other measures of academic freedom are available, including one focusing on legal protections of institutional autonomy and tenure within EU countries (Karran, 2007; Karran et al., 2017); survey data on how academics themselves perceive academic freedom at UK universities (Karran & Millinson, 2019); and an expert-assessment indicator by Freedom House (2020). Limitations of the last dataset are a primary focus on political expression (and not only in higher education), and omission of a measure of the freedom to do research (rather than teaching).

See Spannagel et al. (2020, pp. 7–10) for detailed descriptions of the five indicators. In addition, V-Dem contains data on two other indicators of academic freedom that capture the de jure status of academic freedom: “Constitutional Protection of Academic Freedom”, and “International Legal Commitment to Academic Freedom Under ICESCR [International Covenant on Economic, Social and Cultural Rights].” However, we do not consider them in our study.

The freedom of expression index, which was suggested to us by a reviewer, is the average of V-Dem’s indicators of government censorship efforts, harassment of journalists, media self-censorship, freedom of discussion, media bias, critical media, entry and exit of civil society organizations, and repression of such organizations, on a 0–1 scale.

As a way of illustrating the magnitudes of the correlations, they are quite similar to the standard correlations found between income per capita and measures of property rights protection, corruption and general governance quality. Those correlations generally are thought to reflect overall, long-run transition processes rather than any conceptual or practical identity between income and institutions (cf. Paldam 2021). Additionally, it may be worth noting that in approximately 10% of all country-year observations within our sample, assessments of academic freedom and overall freedom of expression move in opposite directions.

Error-correction models offer a good solution to some of the potential problems, but they are not perfect solutions to problems of endogeneity and simultaneity bias. While they do yield relatively unbiased long-run estimates if the exact sequence of events operates in a Granger-causal way, they remain sensitive to bias owing to anticipation effects and measurement problems, although such problems can lead to both positive and negative biases. When, for example, coders are conservative and change their assessments of academic freedom only after observing a stable change, error-correction models will underestimate short-run effects. Conversely, if coders rely on clues from other institutional changes – for example, if they expect democratization eventually to lead to more academic freedom – such changes will be coded too early and tend to overestimate short-run effects. As we have no way of solving these problems because finding instruments for all possible changes is impossible and the application of GMM estimators is practically problematic with variables that change episodically and remain stable between episodes, we caution against interpreting the results without due care.

More specifically, according to Cheibub et al. (2010, p. 69): “A regime is classified as a democracy if it meets the requirements stipulated in all of the following four rules: 1. The chief executive must be chosen by popular election or by a body that was itself popularly elected. 2. The legislature must be popularly elected. 3. There must be more than one party competing in the elections. 4. An alternation in power under electoral rules identical to the ones that brought the incumbent to office must have taken place.”.

To illustrate that our dichotomous democracy indicator does not by definition entail academic freedom, we note that undemocratic Burkina Faso and Togo have had academic freedom scores of 0.85 and 0.75, respectively, in recent years, which is equivalent to or substantially higher than democracies such as Ecuador (at 0.75) and Guinea (0.56).

As noted in previous research using the ideology data, we often code some parties defining themselves as “right-wing” at different positions than determined by their official ideological locations. Examples include the French Rassemblement National, which we code as reformed socialist based on its economic policy preferences, and the Danish People’s Party, which we code as social democratic.

We tried entering education, measured as either the average years of schooling or the share of the population with at least a secondary education, in the regressions, but the coefficient always is virtually zero and statistically insignificant. Similarly, we have experimented with separating non-democracies into civilian and military types instead of single- and multi-party autocracies, but we find no clear differences between the two.

A parallel problem applies to GMM estimators for addressing causality. In situations in which changes in the dependent variable are distinct events while the regime remains stable over long periods of time between those events, lagged levels of regime status tend to be statistically strong predictors of levels, while lagged changes in the independent variables provide very little information about the events. In practice, the particular structure of our data invalidates the use of GMM estimators.

The only clear example in Fig. 4 of academic freedom increasing prior to a regime transition is with transition from a single-party regime to full democracy. Those transitions essentially all are post-communist transitions in Central and Eastern Europe and the Caucasus. A complication with the regime data in those specific cases is that a number of the countries – most clearly in the Baltic region – started their transitions to effective independence prior to holding their first democratic elections as independent nations. The Bjørnskov-Rode dataset counts them as democratic only after a democratic election that results in a change of government control; hence, in a real sense our data source locates the democratic transition one or 2 years later than the de facto transition occurred.

In an additional test, we also distinguish the effects of judicial accountability in autocracies and democracies. However, although the difference is statistically significant and judicial accountability is more important in democracies, the difference is quite small.