Engineering in political science

Why so little?

Note: The post below got a little out of hand, so here is a quick summary. Economics has a thriving field of engineering (often called mechanism or market design) where scholars work at creating novel economic and sometimes political institutions. A few exceptions aside, it is hard to see an equally thriving field of engineering in political science. Why is that? I speculate that it has to do with theoretical proclivities that make us suspicious of such engineering, methodological tendencies that make some sorts of engineering harder, and habits of mind that make us skeptical of remaking existing institutions. However the gains of political engineering are potentially large and so I propose a number of ways of encouraging political scientists to take the engineering approach more seriously.

The recent Nobel Prize awarded to Paul Milgrom and Robert Wilson is another success for economics in the field that is known as mechanism or market design. It follows similar Nobels for William Vickrey, Al Roth, Michael Kremer, Roger Myerson, Eric Maskin, and Leonid Hurwicz. And to these could be added popular and influential works in the same field by Glen Weyl (with law professor Eric Posner) on radical markets, Richard Thaler (with law professor Cass Sunstein) on nudges, Robin Hanson on futarchy, Paul Romer on charter cities, and Ian Ayres (with law professor Bruce Ackerman) on voting with dollars.

In the relevant work of all of these scholars, the aim is not just to understand the economy (or politics), but to engineer it - to create new sorts of markets or political and economic structures that will increase human welfare. And the success of some of these inventions seems to prove their veracity. The real world use of Milgrom and Wilson’s work in the very profitable FCC spectrum auctions or the application of Roth’s work to medical residency placements looks like real progress (though see Alexandrovna and Northcott for an argument that this progress is more practical than theoretical).

The question I have here is why political scientists do not have a similarly fruitful subfield focused on political engineering. While there has been productive work done on what Sartori has called constitutional engineering, most of this theorizing focuses on the effects of existing institutions or interactions between institutions rather than deriving new institutions. By my admittedly cursory assessment, relatively few political scientists have tried to invent new institutions - I discuss some of the exceptions below - and this despite the fact that one can find many works in the engineering mode among the classics of political theory and despite the fact that several economists have taken a stab at engineering political institutions. 

In this post, I suggest a number of speculative reasons why political scientists have not played a large role in this area. They include theoretical proclivities that make us suspicious of such engineering, methodological tendencies that make some sorts of engineering harder, and habits of mind that make us loath to completely remake existing institutions. However the gains of political engineering are potentially large and so I propose a number of ways of encouraging political scientists to take the engineering approach more seriously.

The case for an engineering approach to political science

Political scientists tend to do two types of things. First, they try to understand how the political world works by searching for causal connections between phenomena. Second, they, and here I am thinking mostly of political theorists, ask how the political world should work, what is just and right. Empirical work and normative thinking are at the center of political science.

The engineering approach differs somewhat from these two visions. The idea is to create or engineer new political institutions that did not exist before in the hope that they produce better outcomes and improve human welfare. I’m thinking of things like new kinds of electoral rules or new ways of soliciting the opinions of citizens. These new institutions should be grounded in the real world. As the name implies, the engineering approach is not concerned with ideal theory or utopias. The idea is to build things.

Political engineering is not exactly empirical or normative work even though it relies on both - empirical methods to see if the new institution works as we expect and normative theory to determine what we want the institution to achieve. Engineering, however, goes beyond them by focusing on the act of creation and coming up with currently non-existent institutions rather than testing the effects of already existing institutions or asking where those institutions fall short.

Robin Hanson has a good description of the distinctive mode of thinking of the engineer. He puts it like this:

A scientist (or at least a caricature of one) insists on saying “I do not know” about a theory until it has robust empirical support, or has clear theoretical support from a well‐supported theory. A scientist thus bases policy recommendations only on relatively direct data, or on well‐supported theory, and so stays quiet about radical new forms of governance, which cannot possibly have direct empirical support, and which are too complex for direct theoretical application.

An engineer, on the other hand, is happy to work on a concept with a five percent chance of success, if success pays thirty times the cost of trying. An engineer first uses analogies and theory‐informed intuitions to consider a wide range of design issues, and then seeks modular design concepts that seem, relative to the status quo, likely to reduce more problems than they worsen. Promising design concepts progress to increasingly realistic proof‐of‐concept prototypes, from simulations, to wind tunnel models, to field tests. While scientists have little use for prototypes, prototypes make engineers' worlds go round.

As Hanson intimates, this way of thinking can arguably have large benefits in creating new solutions to real political problems. Indeed, all political institutions that we have today were once design concepts and prototypes that some political actor or actors decided to put into practice. Of course, as political scientists like to point out and as I discuss below, many of these institutions were not designed from scratch or work according to plan as the engineering mindset seems to assume. Borrowing, adaption, layering, and drift tend to be our watchwords in thinking about institutions, though it is similarly possible to find examples of blueprint institutions, a few of which I mention below.

There is a definitional difficulty here - where is the line between engineering and gradual change or reform of existing institutions? Any change, say, in ballot design or legislative rules could be considered engineering. To take a recent example, there are a number of extant proposals for altering selection and terms of SCOTUS, but most are well-known in other countries.

I have tried to reserve the term engineering for changes that are both more novel and wide-ranging, but I admit that the line is fuzzy. I might not classify 16-year staggered terms for SCOTUS justices as original engineering - because it simply altered an existing variable - but storable votes (which might be used for SCOTUS) would count - because it is a very different form of voting. But this line is debatable. If we expand engineering to include all changes to institutions, then political scientists would have much more to contribute, though it would be harder to isolate those contributions.

Regardless of the merits of newly engineered institutions, the engineering approach can also enrich political science theorizing itself, producing knowledge for its own sake. By creating and then potentially testing the effects of radically different institutions, we expand political science. These institutions introduce new variables and new contexts that could potentially lead us to revise or delimit existing theories. At worst, engineering allows us to more accurately map the space of potential political institutions and discover potential dead ends. At best, it provides us with improvements that make all (or most) of us better off.

A brief history of engineering in political science

Though the engineering approach may not be prominent in political science today, especially compared to economics, it does have deep roots in political science, even if they are not always elevated as a distinct tradition. 

The founding work of Western political science, Plato’s Republic, is a wholly original design for a political order (though there are debates about how literally Plato intended it to be taken). Aristotle was similarly concerned with building the best constitution and studied the varied constitutions of Greek city states in search of models. 

Later scholars continued along this path. Montesquieu saw politics as an engineering problem and provided his own solutions to it, some of which influenced the framers of the US constitution who used them to invent the modern system of presidentialism. A considerable number of political theorists even took their hand at actually writing or helping to write original constitutions including Rousseau, Bentham, and Weber.

While the engineering vision has deep roots, it is less prominent in modern political science.  There have been political innovations over the past century and a half, concurrent with modern political science, but they have come more frequently from thinkers operating outside of political science proper. 

Thus, the idea of proportional representation and its many instantiations were invented by a variety of thinkers in the 19th century, typically lawyers or mathematicians. Their names – Hare, d’Hondt, Sainte-Laguë, not to mention Lewis Carroll – have often been applied to the rules that they devised. The position of the ombudsman meanwhile was a conscious creation of the Swedish government and the semi-presidential system arose thanks to de Gaulle and his supporters. The 20th century saw politicians and bureaucrats creating new supranational institutions like the League of Nations, the United Nations, and the European Union, among others.

As we noted earlier, economists (and law professors) have taken the lead recently. The economist Thomas Schelling was one of those responsible for the hotline between Moscow and Washington, while Richard Thaler along with other behavioral economists has helped invent and popularize a number of policy nudges. It even appears that Romer’s idea of a charter city may officially get off the ground. And this is in addition to plans that remain on the drawing board by the likes of Ayres on voting with dollars, Hanson on futarchy, Weyl on quadratic voting (among other reforms), or McAdams on paying rewards to terrorists.

One might object that political science has recently devoted itself to constitutional engineering, the effort to create new constitutions for democratizing countries (Sartori 1994). As Figure 1 shows, use of the phrase “constitutional engineering” took off after the fall of communism as nations behind the iron curtain adopted new constitutions en masse. The University of Chicago set up a Center for the Study of Constitutionalism and the European Community created the Venice Commission to help advise countries on new constitutions and constitutional amendments. These organizations sent advisors to countries in the postcommunist region to help them assemble their constitutions.

Figure 1: Google ngram for “constitutional engineering” in English books.

However most of the work of these constitutional engineers involves the empirical vision of political science – the assessment of how different constitutional forms function, how they interact with each other, and how they mix with domestic cultures. To my knowledge, relatively little work in this vein has attempted to create brand-new institutions. Much more common was an attempt to correctly match existing institutions to the circumstances first of the postcommunist region and more recently to places like Iraq and Afghanistan. In the next section, however, I will discuss the works of two scholars who might be placed in this group, though they predated it.

Exceptions: Current examples of engineering in political science

One can find a number of political scientists (and others) who do engage in the task of original engineering. Here I will call attention to a number of areas where political scientists have attempted to engineer new forms of politics. It is not clear whether any of these ideas will lead to optimal outcomes or are politically feasible. I will bracket that question for the moment. The aim is merely to show that some engineering in the sense of novel, wide-ranging, and realistic proposals does take place. However, even in these cases, the engineering innovations are not always so central.

1. Deliberative polling

Political science has demonstrated that most citizens are woefully uninformed and often misinformed about politics. Though there is debate about the policy significance of this ignorance, most would agree that producing a more informed and less misinformed public is a good thing.

James Fishkin’s (2009) deliberative polling is an attempt to fix this problem. It begins with an issue of public concern about which the organizers conduct a representative poll of the community. Those who have been polled are then invited to a weekend retreat. In advance of the meeting, they are provided with packets of information about the issue. When they arrive they are introduced to experts and participate in plenary and small group sessions to discuss and debate the issue. At the end of the weekend, they are polled again to determine how their beliefs have changed.

Fishkin has conducted this exercise over 40 times at the local, national, and international level. Each time participants significantly changed their perspective and always in the direction of more informed and enlightened views. So that the benefits of the exercise are not confined to the participants, the discussions can be filmed and shown on television. The group of deliberators may even be delegated to make decisions on behalf of the polity. Alternatively, Ackerman and Fishkin (2004) have proposed a national deliberation day to generalize the benefits of this sort of exercise.

The engineering innovation here could be seen as the attempt to scale down the problem of deliberation in a large polity to a smaller, randomly chosen group, who can deliberate on behalf of all us.

2. Ethnic Conflict

Ethnic conflict may be one of the most intractable political problems. Though it is not as common as one might expect – consider the large number of ethnicities who could be fighting each other – ethnic conflicts that progress to violence tend to be destructive and long-lasting. While solutions like international intervention or war crimes tribunals are often proposed, a more long-lasting solution would put in place institutions that lead to peaceful cooperation between ethnic groups.

Political scientists have developed two sets of institutions that might do this. Both start with the presumption that majority rule is unlikely to work because one group may then dominate. One solution, termed consociationalism and outlined by Arend Lijphart (1977), goes to the opposite extreme. It attempts to give each group protection against majority rule. It does this by mandating grand coalition governments, mutual vetoes over important policies, and federalism with each group governing its own people. Lijphart’s inspiration for this system was his native Netherlands, but his scheme also goes beyond real-world cases to articulate a more general model.

An alternative solution, proposed by Donald Horowitz (1985), instead tries to promote cooperation and hopes to reduce the salience of ethnicity. Called the integrative approach, it consists of electoral systems like the alternative vote that give candidates an incentive to appeal to other groups and a federal system with more heterogeneous small units where cooperation can emerge from the ground up. While neither of these solutions appears to be a cure-all, there is some evidence that each can work under the right conditions (Reynolds 2010).

In each case, the engineering innovation is less in the creation of new institutional forms than in the combination of existing institutions and their application to appropriate contexts.

3. Analogic Perspective Taking

Prejudice and intolerance are long-standing problems for all polities, but original and practicable solutions are less common. Broockman and Kalla (2016, 2020) have proposed the technique of analogic perspective as a way to reduce prejudice. The idea is that trained canvassers spend ten minutes talking with citizens and encouraging them to remember and speak about a time when they were judged negatively. This simple intervention appears to have long-lasting effects in reducing prejudice. In the cases they have analyzed, it increases tolerance towards transgender individuals and undocumented migrants. 

Here the engineering innovation is to build on principles of social psychology to generate scalable and actionable interventions.

4. Israeli-Palestinian Conflict

Solutions to political problems do not have to be aimed at the general level. Equally useful would be to consider the context of a particular problem and tailor the solution to that place. This seems to apply in spades to the Israeli-Palestinian conflict where the devil resides in the myriad details.

Bruce Buena de Mesquita (2009) proposes an original idea to resolve the conflict. His insight is to create incentives so that both sides gain from peace and lose from conflict. He proposes that tourism revenues from the region be divided between the two sides, so that Palestinians would lose in their pocketbooks if they deterred tourists through attacks. He claims that this is superior to solutions that depend on trust – for obvious reasons in short supply – or trade land for peace – which suffer from credible commitment problems. He argues that his solution is self-enforcing since it depends on the self-interest of each side.

This solution is closer in spirit to the mechanism design work taking place in economics as it is rooted in game theoretic thinking, though it has more of a political science flavor in its grounding in a specific situation.


I may be missing other examples of engineering in contemporary political science. In particular, I have mostly avoided proposals from political theory as they tend to be grounded in more idealistic or utopian theorizing and are rarely the subject of empirical testing. And, as I mentioned earlier, I excluded minor changes to existing institutions. I am happy to update this section as I discover more examples.

I would note that these examples differ somewhat from economics in how political scientists conduct engineering. Work on mechanism design in economics tends to be based on game theoretic models, a key concept being incentive compatibility. At the risk of generalizing from a very small sample, engineering-style work in political science appears more inductive - starting with existing institutions and considering ways to recombine and rescale them - and psychologically based. There are economists who take these approaches as well - for example, Romer on charter cities or behavioral economics and nudges, but I think more typical are proposals like quadratic voting or new forms of auctions.

Why so little engineering in political science?

While there is no definitive means to determine how much energy political science devotes to attempts at engineering, I think the difficulty of identifying examples of this approach in political science and the ease of doing so in economics suggest that it has not been widely adopted. Again, I would be happy to be proven wrong.

I can think of a number of reasons why the engineering tradition is so weak within political science even as it has found a welcoming home in economics.

  • Context dependence. Political scientists tend to study the details of places and eras. Indeed, much of our work is qualitative and until recently emphasized description. As a result, there is considerable suspicion, even in a field like constitutional engineering, of the idea that there would be one-size-fits-all solutions to political problems. For this reason, our focus is more on the details of specific situations rather than engineering general structures. Noteworthy is that a recent critique of Posner and Weyl’s Radical Markets argues that it fails precisely by not being attentive to the details of these situations.

  • Historical institutionalism. This prominent approach to political science has been skeptical of the possibility of getting new institutions to work according to plan. Pierson (2004), drawing on earlier work, has pointed to persistent gaps between designs and their implementation. These arise from cognitive limitations, the necessity of political compromises, the attempts by losers to change the winning institutions, and the effect of time itself. Mahoney and Thelen (2010) have further developed a theory of institutional change that emphasizes mechanisms like layering, drift, and conversion. This school of thought tends to embed engineering in larger power struggles rather than seeing it as a technocratic exercise.

  • Diversity of motivations. Political science entertains a variety of motivations for action as opposed to the economic focus on self-interest and rational choice. As a result, political scientists may be less prone to believe that outcomes can be read off of institutional designs as actors may interact with them in a variety of ways, which are hard to predict a priori. The historical institutionalist approach in fact posits that institutions shape preferences. For these reasons, political scientists may be more comfortable with studying institutions in situ than creating blueprints for institutions.

  • Lack of technical tools. Much of the work in market or mechanism design in economics is built on game theoretic foundations, particularly the prize-winning work. In a piece on economic engineering, Roth (2002) argues that three tools are necessary for evaluating designs: game theory, experiments, and computational simulation. While all three are used in political science, they are not as common as in economics, especially at the research frontiers occupied by the Nobel prize winners. Of course, some economic proposals are less technical in this sense, for example, Romer on charter cities, Hanson on futarchy, or Ackerman (a lawyer) and Ayres on voting with dollars.

  • Publishing difficulties. Many of these tendencies mean that political scientists may see few opportunities to publish engineering proposals. Pure theoretical exercises are not in vogue and the effort required to combine theoretical innovation and the sort of empirical testing necessary to satisfy reviewers concerned with causal inference may be unacceptably high. 

  • Skepticism. I can imagine that political scientists are greater skeptics of big changes than economists. To give a taste of the engineering mindset, Ezra Klein describes his conversations with tech and VC entrepreneurs who look at politics from the outside and come up with 20 interesting ideas. As he puts it, “Nineteen of them are probably quite wrong, not even a little wrong, like very wrong. But that last one might be great, really important, and if you could just figure out which one it is...” Just in terms of mental habits, political scientists (with the possible exception of political theorists) tend not to think in this way. They are taught to try to figure out why the system works the way it does instead of imagining a radically different system.

  • Humility. Relatedly, political scientists may arguably be more humble in their sense of what can be achieved. Lilla’s (2003) survey of the attempts of political thinkers to put their ideas into practice is a story of failure. The leitmotif of his book is Plato’s journey to Syracuse to advise the king on setting up a better political system. The episode ends in tyranny, which Lilla argues is paradigmatic. These lessons might be better known to political scientists than to economists. At least in my area of Eastern Europe and Russia, the failure of communist-inspired engineering has bred considerable skepticism.

Interestingly, I think some of the objections to the engineering approach that might be best known to economists are not as widespread among political scientists. Conservatively-inclined thinkers like Burke or Oakeshott argue that social institutions are too complex to be engineered. For them, institutions encompass the accumulated wisdom of our ancestors and we throw aside this wisdom at our peril. According to Hayek (1945), a better alternative is to decentralize institution building so that institutions are built out of independent individual actions. His idea of spontaneous order contrasts with the engineering vision (which he terms rationalist constructivism). In his view, planners lack the information required to foresee the results of their proposed plans. A more recent claim is that selection pressures help institutions to evolve in more efficient directions (Posner 1973). It is possible that current institutions have thus evolved to be good fits for a society and we unfit (or engineer) them at our peril. While the informational and evolutionary arguments against engineering are likely to be more salient to economists, it has not prevented them from pursuing engineering.

Paths forward

What might political scientists contribute to the task of engineering and how could we encourage such research? 

The comparative advantage of political scientists lies in their knowledge of places and eras, not to mention their skills in fieldwork. Building on these traditional strengths, one opportunity would be the closer study of existing or previously existing institutions to find forms of government that have mostly been ignored. Some of these may be found in the past. Thus, Jon Elster (1999) points to the unusual forms of political accountability in ancient Athens like graphe paranomon where citizens could be punished for putting forward an unconstitutional proposal or euthynai where magistrates were automatically audited at the end of their term. Even in the present, there are forms of government that have been ignored. Consider the work of Elinor Ostrom (1990, 2005) who investigated ways that communities solved common-pool resource problems and discovered previously invisible forms of self-government. In all these ways, we might discover or rediscover engineering solutions.

The same detailed knowledge should also allow political scientists to produce better engineered institutions than those with less knowledge of politics. Some of the analytic strategies used in the field of constitutional engineering could be used to explore the politics behind adopting engineered institutions (the endogeneity of institutions), the interaction between the engineered institution and other institutions, and the way that the engineered institutions function in different contexts. In short, political scientists should be well-situated to add value to the field of mechanism design even if they do not follow in the theoretical footsteps of economists.

A way to start down this path is to create venues and support for this sort of research. The current trend in political science is to privilege causal identification in empirical work. This is a positive step for empirical research. But there should still be space for new ideas that are difficult to test precisely because they do not exist. Economists have gotten around this problem because formal theory has considerable prestige and new institutions can be framed as works of pure theory. Lab experiments are one way to connect the empirical and the engineering vision. A simple fix would be to provide more journal space for contributions that take an engineering approach even without empirical testing - a sort of Journal of New Ideas.

Besides changing our appreciation of work in the engineering vein, awards or prizes might help to encourage more research on these ideas. The Grawemeyer Award currently exists to support “ideas improving world order”, though a glance at their awards indicates that most if not all are for scholars who empirically show the costs or benefits of existing solutions. It would not be difficult to offer prizes for original solutions to more specific problems.

Which concrete areas of politics deserve more attention from political engineers? Recent research has pointed to the problems of citizens and their ability to make democracy work (Achen and Bartels 2016). One can imagine engineering-style work on ways to improve the informedness of citizens or limit the spread of misinformation or combat myopia. Broockman and Kalla’s (2016, 2020) work described above fits this bill. One could put the varieties of fact-checking here as well. Original ways to combat corruption might be another area where creative solutions could help. Consider the use of zero-rupee bills in India. In terms of government institutions, recent work on electoral laws shows that scholars still have not mapped the universe of possible rules.

A final question for the engineering perspective is how far we should go. In many respects, we have figured out what a good political system looks like. Francis Fukuyama, for example, terms the goal of political development as “getting to Denmark”. We should thus be cautious about trying to reinvent the wheel. Current political and economic institutions may be as close to optimal as we are likely to get. On the other hand, there are problems that we are not solving and some evidence that current institutions have not kept up with social and technological changes. No matter the case, exploring the entire space of political institutions is worthwhile simply for the sake of knowledge and can show whether we have reached a local maximum or if we can go even higher.