In the wake of the Great Recession, economists faced tough questions: How could they have missed the imminent collapse of the world economy? Of what use were all their intricate models if they couldn’t predict such a huge systemic crisis?
Just as economists failed to predict the Great Recession, so political scientists failed to predict a series of momentous political upsets. The most obvious is the dizzying rise of Donald Trump. But the story is bigger than that: In recent years, political scientists have overestimated the forces of stability time and again, failing to foresee Brexit, the chaos wrought in the Philippines by Rodrigo Duterte, and the serious threat posed to Polish democracy by its populist government, among other developments.
To be sure, it would be too much to ask political scientists to have predicted each of those twists and turns. For one, academics aren’t in the forecasting business. For another, there is such a thing as contingency: When the unlikely comes to pass, even correct models of the social world fail to see around the next historical corner.
With the finish line in sight for the presidential campaign of 2016, we decided to devote our pages to essays that examine and challenge the way we think about politics, democracy, and the American electorate. Why do voters make the choices that they do? How could political scientists have failed to foresee this year’s tectonic political shifts? And what aftershocks can we expect in the wake of Donald Trump? We tackle these and other questions in this special issue of The Chronicle Review.
And yet it would be a mistake to quibble away the failure of scholars to recognize that, say, one of the most seismic American political events in a half-century might be on the horizon. A year ago, most political scientists would simply have dismissed the suggestion that somebody like Trump could win the Republican nomination and prove competitive in the general election. Worse still, the dominant theories in the field actually seemed to predict just about the opposite of what eventually happened.
In one of the most respected recent works on presidential nominations, for example, Marty Cohen and his co-authors argue that The Party Decides. In their view, party elites use endorsements and campaign contributions to help favored politicians in primaries, effectively preselecting approved candidates. And yet an outsider with virtually no institutional backing put up stiff resistance against Hillary Clinton in the Democratic primaries, and an even greater outsider with even less institutional backing swept the competition aside to become the Republican nominee for the presidency of the United States. In short, reality upended what we thought we knew even in areas where dominant theories did seem to make clear predictions.
How could this have happened?
Over the last three decades, political scientists have made impressive strides in understanding how the political world functions, especially in periods of relative stability. American politics is a good case in point. Scholars of the judiciary have shown to what degree the past ideological alignment of Supreme Court justices predicts their decisions in future cases. Scholars of Congress, meanwhile, can anticipate with great accuracy how representatives are going to vote on a pending bill by looking to such factors as their party ID, their past votes, or their biggest donors.
Three interlocking methodological shifts account for much of that progress.
First, political scientists were once interested in describing, interpreting, and explaining important aspects of the political world, from particular events of great significance like the French Revolution to specific milieus like the legislature or local trade unions. Today, by contrast, their explicit hope is to focus primarily on causality, inferring general regularities about political life. To describe facts, most political scientists now believe, is the task of journalists. To explain a particular event, they insist, is the task of historians. To speculate about extreme changes that might befall a polity tomorrow, they warn, is the task of pundits. Political scientists primarily seek to uncover how variables like income or education influence outcomes like voting behavior.
Second, political science was once dominated by scholars with a proudly qualitative approach. Steeped both in history and the intricacies of current affairs, they gathered their empirical evidence from archives, interviews with politicians and policy makers, or ethnographic studies of particular organizations and neighborhoods. Today, by contrast, political scientists predominantly use quantitative methods. Most of them spend the bulk of their time on constructing data sets and using statistical techniques to identify how a particular set of factors is associated with — or, preferably, causes — the outcomes in which they are interested.
In recent years, political scientists have overestimated the forces of stability time and again.
Third, political scientists once defined their field of study by a central canon of important questions about politics: How do social revolutions come about? Under what circumstances is democracy secure? Today, by contrast, they define their discipline by a set of methods. To count as political science, it is no longer enough that a piece of work should provide the best available answer to an important political question; rather, it now has to clear an inflexible methodological bar.
While that methodological turn has borne rich fruit in understanding how the world works in normal times, the overreliance on quantitative data, the narrow focus on uncovering general regularities, and the methodological bar also make it very difficult to think systematically about what would happen if times ceased being normal. For that reason, the failure to foresee the emergence of Trump wasn’t a lacuna in the enterprise of contemporary political science that might easily be addressed. On the contrary, it was a direct result of its core commitments.
If I record the point at which the water in my kettle boils here in Cambridge, Mass., I will reliably get a measurement of about 100 degrees Celsius. If I go on to repeat the same procedure in Chicago or in Washington or in San Francisco, I will keep getting the same result. Before long, I might have hundreds or thousands of observations. All of them would seemingly confirm the obvious and unchanging truth I learned in grade school: Water boils at 100 degrees.
And yet, the truth is much less obvious and unchanging than that. If I took my trusty kettle to La Paz, Bolivia, the water would boil well before it reached 90 degrees. If I somehow managed to schlep it all the way up Mount Everest, it would boil at about 70 degrees.
General regularities, whether in the natural or the social sciences, have “scope conditions.” They accurately describe the world while certain background conditions — in this case, air pressure — hold. When those background conditions change, the supposed laws have to be refined, circumscribed, or jettisoned.
This point is of course well known to social scientists. But while we fully understand the importance of scope conditions in the abstract, we rarely think seriously about how they might invalidate a lot of our key assumptions — and systematically blind us to history’s rare yet incredibly important turning points.
Consider these hypotheses: Senior members of American political parties get to pick their nominees. Extreme candidates who attack basic democratic norms do not gain mass support among members of the American (or Polish or Swedish) public. If a wealthy country has experienced at least two turnovers of government by free and fair elections, liberal democracy is there to stay. Each of these has been confirmed by subtle and extensive empirical evidence drawn from the last 50 years. And yet all of these hypotheses might be subject to scope conditions that are invisible to our eyes because they have held true for the last half-century — and are now giving way.
Do parties still retain the same influence over primary voters once public trust in politicians has plummeted to record lows? Do voters still shun extremist candidates at a time when they are less and less invested in the idea of democracy? And will wealthy liberal democracies continue to be stable when, for the first time since their founding, the living standards of average citizens have barely increased in a generation?
Natural scientists can, to some degree, test the scope conditions of their findings in a systematic manner. If there is some theoretical reason to suspect that air pressure might influence the boiling point of water, and if it is impractical to carry out experiments atop Mount Everest, they can artificially lower the air pressure in their laboratory. Political scientists have far fewer tools at their disposal. Even if they realize that there is some theoretical reason to suspect that liberal democracy might prove less stable when living standards no longer rise, they cannot run an artificial experiment that confirms the scope conditions of their theory.
The obvious takeaway is that political scientists need to be less confident about the general applicability of their findings. The less-obvious takeaway is even more radical: In a field in which we can never systematically determine the scope conditions of our theories, the discovery of general regularities may have less value than meets the eye. To discover that a high GDP boosts the stability of liberal democracy under some unknowable set of scope conditions, for example, is ultimately not very helpful: It neither gives a full explanation for why democracy has historically been firmly established in the United States, nor does it tell us under what circumstances American democracy might fail.
There is another problem. The use of statistical tools and the focus on causal explanation have allowed political science to expand its explanatory reach and to make its findings less prone to preconceptions. And yet they also risk narrowing our field of vision and biasing social-scientific findings.
It is easier to amass high-quality data, and therefore to make “rigorous” causal claims, about the economy than about culture; in part for that reason, the social sciences now favor economic over cultural modes of explanation. Similarly, it is easier to amass high-quality data, and to test causal hypotheses, about frequent events that are easy to count and categorize, like votes in Congress, than about rare and intractable events, like political revolutions; in part for that reason, the social sciences now tend to focus more on the business-as-usual of the recent past than on the great turning points of more distant times.
Liberal democracy is entering a deep crisis. Our most urgent task is to understand why.
All methods have their strengths and weaknesses. The current approach lends itself better to studying periods of relative stability than to understanding times of relative instability. It is bitterly ironic that the methodological turn in political science has taken place at the very moment when the new set of tools it mandates is especially likely to blind us to the radical transformations going on around us.
In Athens, in Seoul, in Stockholm, and in Washington, political systems that had seemed very stable a few short years ago suddenly appear to be under great strain. Countries in which moderate parties held all the power until recently have witnessed the sudden rise of populist forces that seek to challenge some of the core tenets of liberal democracy. Across the globe, liberal democracy is entering a deep crisis.
It would seem to follow that the most urgent task for political science now is to understand this crisis, and perhaps to point the way to potential remedies. And yet, the current methodological orthodoxy makes this task especially difficult. If our only way of understanding a particular political moment is to use statistics to make broad causal claims, then we need to have data drawn from similar developments in the past in order to describe the forces at work. But this makes it virtually impossible to say something about developments that don’t have a real precedent: There is, by definition, no past data that can explain their causes or consequences.
What kind of damage would Trump do to the American republic? Under what circumstances might the past stability of liberal democracy cease — and a deep challenge to our political system emerge?
By the current methodological standards, those questions have essentially been defined out of existence.
The inability to speak to large, inherently speculative questions might be a price worth paying in normal times, when the political world is relatively calm, and the recent past provides a reasonable guide to the immediate future. But it is now becoming increasingly clear that we are living in times that are far from normal, and that the future may turn out to be very different from the recent past.
Political scientists now face a stark choice: We can stick to our current methodological prescriptions and remain silent as the fate of liberal democracy hangs in the balance. Or we can try to understand what caused liberal democracy’s current crisis and how that crisis might be overcome.
I do not mean to pretend that this will be easy. Understanding the world in uncertain times is a fraught undertaking. But we do have a lot of tools at our disposal that are largely going unused: We can pay a lot more attention to history, including the times in the past when democracy found itself in deep trouble or regime forms that had been stable for many centuries suddenly started to crumble. We can spend a lot more time getting to know the voters disaffected with the political system, or the new crop of populists conquering our capitals. We can pay more attention to the dogs that didn’t bark, studying how looming disasters were averted in the past.
Irrespective of the particular methods we choose, we need to make it our priority to answer the most pressing political questions of the age as best we can — rather than retreating to the comfort of proving general regularities that are, at best, of secondary importance. With the benefit of hindsight, some of the theories we will come up with using this broader set of methods will turn out to be wrong, especially if we hazard a prediction from time to time. But if we are to have any real relevance, it is better for us to be wrong, or even to cry wolf, from time to time than to stay in a bubble that insulates us from the increasingly scary events unfolding all around us.
Yascha Mounk is a lecturer on political theory at Harvard University and a postdoctoral fellow at the Transatlantic Academy of the German Marshall Fund. He is the author of The Age of Responsibility: Luck, Choice, and the Welfare State, forthcoming from Harvard University Press, and he is now working on a book about the crisis of liberal democracy.
