International relations has a problem with the future

Then, so does everything else

[Johann Baptist Homann - Planiglobii Terrestris Mappa Universalis, courtesy of the Met]

I’ve a new piece in the Robert Jervis International Security Studies Forum “Chaos Unleashed” series of papers on the second Trump administration and the crisis in global affairs. My own paper is moderately obnoxious, in the ways that academic papers sometimes are, but it comes by its obnoxiousness honestly.

Robert Jervis, whom the forum was named after, was a genuinely great thinker (also: not a notably good writer). I’ve thought for a long while that there is enormous value in his book, System Effects, which tries to bring complexity science together with the study of international affairs, but it is buried deep. For years, I’ve wanted to write something that extracts the core ideas of this book (as I understand them) and explains why they are important to understanding where we are today. That is what I do in this essay, although I jump to conclusions that Jervis almost certainly would not have shared. The key argument:

The conventional approach would be to test … various futures against each other. Yet this is a hopeless endeavor in the early stages of a possible transition. The feedback loops that drive system change are both “highly destabilizing and difficult to predict.”

Perhaps the most useful role that the discipline of International Relations may play is not in testing possible futures, beyond the minimum required to ensure that they are not obviously wrong or self-contradictory. Instead, it may usefully play a role as a generator of largely untestable and incompatible claims that can then help inform policy systems that are better adapted to work with many possible futures. Specifically, International Relations can build on complex systems approaches, which look to model just such processes of change and stability as are currently under debate.

This hangs on the notion that we are in a period of relatively unpredictable change, in which certain positive feedback loops (things feeding on themselves) are liable to destabilize the existing system, whereas negative feedback loops (when things inspire dampening counter-reactions) will likely have the opposite consequence. In a moment when no-one has any idea what is going to happen next in international affairs, structured accounts of possible futures may end up being quite useful. So too for other big areas where we have no very strong sense of what is likely to happen next, such as the energy transition (see this great discussion between Dave Roberts and Jane Flegal, which I will return to in the final part of this post). The essay is calculated to annoy pretty well every existing faction in the discipline of international relations - but only because I think that we should be doing things very differently than we are, if we want to be useful right now. More below the fold.

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Some background for those who have not studied international relations (IR). Even by academic standards, IR is a field that is riven by many lively controversies, some of which are rather magniloquently styled by certain IR scholars as the “great debates” (characteristically, they fail to agree on what does or does not belong on this list). Two disputes are relevant to this post.

The first is the long-standing fight between what IR people call the three “isms,” which still dominated discussions when I was a grad student.¹ Each “ism” is, or can be made to sound like,² a grand theory of how global politics works. Realism sees the world as a brutish tragedy where states strive for power and survival because they have to, liberalism is more optimistic about the prospects for inter-state cooperation, especially where states have economic interests in common, and constructivism, which elbowed its way into the debate later, argues that we should think about international politics as involving norms, identities and other concepts from sociology and social psychology. These differences used to result in remarkably bitter disagreements, where people who were particularly attached to the one approach or the other would take on all comers. Now things are calmer, although John Mearsheimer’s lively approach to discussion with his peers gives some sense of what things used to be like back in the day.

The second is the fight between all those attached to different grand theories of international politics, and those who instead opt for a more data driven understanding (this sort-of overlaps with the first fight, but in weird ways). A series of articles in the early 2000s poured scorn on the aspirations of grand theorists, and their hopelessly unscientific approach to international politics. Critics of the great debate approach argued that instead of constructing sweeping narratives, scholars of international relations ought all be constructing our accounts of international politics from the ground up, building theories about “mid-range” relationships on the basis of statistical or similarly reliable evidence. Liberals very often accepted this more modest approach to understanding international politics (the critics were mostly liberals, and the approach fit well with the liberal world view). Realists typically did not, and mounted a ferocious counter-attack, blasting statistically inclined international relations scholars for writing abstruse research pieces that were stuffed with incomprehensible quantitative mumbo-jumbo, and entirely useless to actual policy makers who needed to understand what to do in a complex world.

Today, these feuds are sputtering, and are conducted in funereal garb. Many liberals are in despair at the collapse of what seemed to them like an international order that in large part reflected their values. Realists’ attitude to the collapse of the liberal international order often (though not always) involves some combination of (a) I told you so, and (b) it never really existed anyway. But many realists too are distressed by how the second Trump administration’s policy making appears to be the most stupid possible caricature of their ideas imaginable. Every time a Trump official utters the two words ‘flexible realism’ (which stand in for the proposition that whatever the United States wants, it gets), the rotational velocity of the late Hans Morgenthau’s cadaver increases by another few centimeters per second.

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This helps elucidate why the propositions of my paper will likely annoy those on all sides of these fights, to the extent that any of them take notice. If you are one of the remaining stalwarts battling it out on behalf of either realism or liberalism (constructivism perhaps too, but to a much lesser extent), you are liable to take exception when I argue that your perspective on the world largely boils down to a few notions about feedback loops. And if you are a proponent of mid-range theory, you will object to my implication that clever causal identification strategies are not likely to be enormously helpful right now, since any regularities they identify are under siege.

But as I say, I come by my obnoxiousness honestly. My arguments stem from three basic propositions. First, that we do seem to be in a moment of system change in international politics. What I mean by that is that the standard assumptions on which international politics are conducted are up for grabs. Perhaps we will move to some new system that orders international politics. Perhaps the existing sources of order in international politics will reassert themselves in some form, so that we continue in something that is recognizably a version of what we have had before, albeit likely with significant changes. Perhaps (as Adam Tooze has suggested in various places) we will not move from one system to another, but instead see the emergence of collapse and self-sustaining disorder. More generally, as Adam puts it:

A world at “loose ends with itself” might be precisely the kind of conceptualization we need to grasp out current moment as “a giant non-linear outcome generator with wicked convexities. In plain English, there is no mean, there is no average, there is no return to normal. It’s one way traffic into the unknown.”

Second, that existing grand approaches to international relations are badly suited to explaining system change. Liberalism and realism rest on arguments about how the existing system sustains itself, while constructivists typically either don’t ask about system change, or suggest that the system is moving towards some kind of immanent proto-Hegelian destination.

Third, that the best set of tools close to hand for thinking about system change come from the study of complexity. This is where Jervis’ work comes in. System Effects is the most comprehensive effort I know of to think through complexity in the context of international politics, and Jervis talks about how core propositions in realism rest on propositions about feedback loops. I build on this idea to talk about how liberal claims about the ‘liberal international order’ too involved arguments about feedback loops between domestic politics and international politics. Liberals believed that liberal societies and economies structured international rules in ways that reflected their values, further reinforcing liberalism within countries that were already liberal and inexorably pulling non-liberal societies such as the People’s Republic of China within their logic. This did not, obviously, work out as they expected.

The notorious problem with complexity scholarship is that it has poor predictive capacities. It suggests that even moderately complex structures of interaction can become rapidly unpredictable. We have made advances in studying some complex phenomena (see Ben Recht on weather forecasting) although our ability to predict breaks down after some period, as the coarse graining-based modeling drifts away from the phenomena being modeled. Others, we can’t do much with (see also: Ben on earthquake prediction). So the obvious rejoinder to complex systems arguments, especially those without lots of fine grained data and many past examples of the events you might want to predict in future, is that they are more descriptive than usefully explanatory. Saying that a system is complex doesn’t tell you much about how it will behave.

The counter-rejoinder to this in the social sciences is that even if we don’t know much about how the system will behave, we have some sense of which kinds of knowledge helps you to better map the rough shape of the system and adapt as it shifts in unforeseeable ways. Scholars like Hong and Page argue that groups with highly diverse viewpoints are better able to capture the contours of complex systems than groups with greater expertise but more similarity across their members’ understanding. Decades earlier, the cybernetician Ross Ashby argued that any successful regulator of a system needed to contain as much variety as the system that it purported to regulate.

That, then, translates into the claim that standard social scientific approaches (which assume a lot of stability) are likely to be less helpful in moments of possible transition. That is not to claim that they are completely unhelpful - even while many important things change, others may remain the same - but the value of standard social science approaches, which attempt to discover long term regularities, is likely to depreciate in relative terms until the system settles down again. Mid-range theories are probably not going to provide the kinds of knowledge that they set out to provide.

Equally, both mid-range and grand theories can be helpful collectively rather than individually. The theories we have point to many possible futures. It is impossible to predict which of these futures will come to pass. But having many possible futures provides a highly valuable source of diversity across expertise in Hong and Page’s sense, and variety in Ashby’s.

If I thought I could get away with calling this article “Generating and Organizing Variety in the Social Sciences,” I probably would have. Equally, I understand why scholars who have made broad claims about international politics would prefer not to have their ideas and research treated as resources from which useful variety can be mined. The reason one writes an article, or a book, defending some set of claims, is not that you think that they add to the grand tapestry of variety, but because you believe that you are right, dammit, and the world ought recognize as much.

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I of course myself think that I am right, dammit, as, more importantly, are the people whose ideas I am relying on (in addition to those mentioned directly: Dan Davies, Brian Eno; the late Stafford Beer). Whether I am or not, these questions and problems extend far beyond the field of international relations. And that brings us back to the conversation about energy politics that I linked to right at the beginning.

In that conversation, Jane notes that it is really hard to figure out in advance what paths will lead us to an economy that relies less on fossil fuels.

I really do think that climate change is an incredibly complex challenge that has multiple dimensions, where uncertainty is often quite high, and the stakes of decision-making are quite high.

And so I try to push for both epistemic humility in the face of that. You know, I think we need to, rather than trying to pick one path that is optimal and blast it through, given all the things that have to happen for us to achieve our goals, I sort of adopt more of a risk management frame around, like, how do we adopt plural perspectives? How do we move forward to address climate in a way that mitigates the risk of failure, which in my view is like trying to pursue one optimized path that some engineer cooked up in a lab or whatever, or a model.

What she is saying is very much the same as me, unless I’m misinterpreting: if we are dealing with a complex transition, we can’t start with some single simplifying framework. Equally, in stark contrast to my own piece, Jane talks intelligently about the practicalities from the point of view of a policy practitioner rather than that of an airy theorist:

you will find in most of the kind of academic or theoretical literature around the rationale for just, like, pricing the externality of climate change assumes that you can actually do that effectively in the real world, which of course confronts all sorts of real challenges that I know you’ve talked to Danny Cullenward and David Victor, who’ve done a great job sort of describing all of the ways in which that fails when it hits reality.

So there is … a practical argument about this. But I also think one of the original sins in my view about the way that we came to understand climate change as a problem was that. … we had all this great success with the Montreal Protocol and HFCs ... Which was a certain kind of problem, a relatively well-bounded one in a couple of discrete geographies with a handful of producers where we had cheap substitutes, or at least rapidly becoming cheap substitutes. And so the mechanism for managing that was kind of a conventional pollution control program … That is not, though, the same shape of problem as climate change. Carbon, unlike these other pollutants, is embedded deeply everywhere in the economy. And so the expectation that price signals alone are gonna move it is, I think basically incorrect. [HF - regular phatics of real life conversation removed for easier reading]

To actually shift the system, you need to figure out how to generate a “green spiral”:

a positive feedback loop where investment, often government investment, though not only, makes clean technologies cheap enough to deploy at scale. That deployment then creates industries and jobs, and those industries become a powerful political constituency with real power to demand more climate action.

That broad approach - building a positive feedback loop for what you want to happen- seems absolutely right. Equally, doing it is hard, and intensely political. You are probably going to discover that what you thought might get the spiral going won’t work. If it does work initially, it probably won’t be self-sustaining without further adjustments, which you are likely going to have to wing. And if that all works out, it will certainly have all sorts of unexpected side effects and consequences, some of which may be good (awesome!) and others of which will create their own self-ramifying problems. That is why you need “plural perspectives”: to figure out as much of the complexity that you are dealing with as you possibly can, both as you begin and as you go on.

But that’s not all you need. You also need institutions that are capable not simply of building in those perspectives and taking advantage of them, but responding flexibly, and changing approach when what you are doing turns out not to have the expected results. And you need to generate political legitimacy. Our existing institutions are not particularly well suited to do any of that, to the extent that they even exist in the US. Creating institutional forms that can incorporate diversity and respond flexibly to a changing environment while maintaining legitimacy in the eyes of citizens is the fundamental project of state capacity that faces us. My version of this, as stated in the paper is that:

scholars should consider how to engage more directly with problems of institutional design. An extensive existing literature examines how expertise, experience, and other such factors contribute to good foreign policy decision making. This literature could be welded together with complex systems analysis to map out the kinds of institutions that are likely best fitted to dealing with systems change, by processing variety in ways that can map out onto the variety in the complex international environment that they seek to model and control. At a minimum, this implies internal governmental institutions that can work across silos so that policy makers with different subject-matter expertise are exposed to each other. More broadly, it suggests that institutions that are more capable of applying and testing variety through experimentation and consequent policy reform will be better capable of adapting to unanticipated change.

but I know very well that the most serious problems are practical rather than theoretical.

So like many academic papers, mine at best helps to identify a problem, rather than offering practical solutions to solve it. Those solutions plausibly involve large scale changes to the institutions through which we filter ideas about the world, make policy decisions on the basis of those ideas, and revise and update the ideas and the policies depending on how they work out. I do think that we are at an inflection point for both the social and natural sciences through which we try to discover things, for the institutions through which we try to shape things, and, most importantly, for the world that we are trying to shape. We don’t know what kind of future we are heading into, and we need to contemplate various possible ones, building approaches that are robust across as many as possible, and capable of updating quickly. That is a hard problem in international relations, in climate and energy, and in other spaces too. But it is the one that we need most urgently to confront.

1. Not, as it happens, a grad student in international relations. My real introduction to international relations theory happened when I was an assistant professor, and was asked to co-teach the introductory seminar for IR students at the University of Toronto. I had never myself taken a Ph.D. level class in international relations in my life. It was a proper baptism of fire.

2. Constructivism is not a grand theory in the same way as the other two, being notably eclectic in most of its formulations, but regularly gets shoehorned in as an ‘ism’ nonetheless.