Do We Have Too Much Theory in International Relations or Do We Need Less? Waltz Was Wrong, Tetlock Was Right
Summary and Keywords
The field of international relations has developed the notion that world politics is made up of dyads, a thing that no one has actually ever seen. This notion is referred to as a theory by many scholars. Both the notion that world politics is dyadic as well as the idea that this is a theory need to be jettisoned from our scholarship. They have deleterious effects on what we can learn about the world.
What Is Empirical Theory in International Relations?
I don’t know. This may compromise my ability to convince you that we need less of it. Doubtless many other contributors will spell out clearly what theory is, why it’s become so rare/distorted/atrophied/glorious in recent times, and tell you why we need more of it. Whatever it is. Along with others I will find these treasured insights upon reading the other articles. Maybe you have already read those articles and are now convinced that theory is such a good thing that we need more and better theory. If so, you may not actually want to continue reading mine, which makes the simple point that we don’t need more theory, we need less. Since I don’t really believe much in theory—but am a strong believer in science—I’ll limit my discussion to how I typically see the term used in published articles, books, and graduate syllabi. I’ll focus on my antediluvian point: We need less theory. The concept of theory has been confusing social scientists for decades.
There is little agreement about what constitutes strong versus weak theory in the social sciences, but there is more consensus that references, data, variables, diagrams, and hypotheses are not theory. Despite this consensus, however, authors routinely use these five elements in lieu of theory (Sutton & Staw, 1995, p. 371).
Indeed, it is the premise of this article that the word “theory” is used in so many different ways in international relations that is has become meaningless. This would not be problematic in and of itself, but the deleterious consequences of the worship of theory as a reification are severe and range from isolating one field of inquiry from another, through a closing of ranks against criticism, on to the use of theory-as-a-reified-thing to criticize a wide variety of scholarly efforts. In short, the use of literature, hypotheses, and totems as theory in our discipline remains widespread.
What is good theory? No one knows. However, everyone thinks they know. One definition is “something that explains, predicts, and delights” (Weick, 1995). For a definition of theory, many rely on the ideas of Kaplan (1964) and Merton (1968) that theory is about the why. This is what many are taught in graduate school; I was. But in my opinion, this promotes a confusion between how and why. Feynman explained this in the following way. If you rub your hands together repeatedly, they will get warmer. How does this happen can be explained by friction, which generates heat when things are brought together. This can be explained even more precisely at the molecular, and even the atomic level, as essentially one type of energy (work) is converted into another (heat). By why does this occur is an ontological question that cannot easily be answered. No one knows why the world is organized in this fashion. The universe could be different. Or, different parts of the universe could be different—say on a non-spherical planet rotating in a different direction in a different part of the universe. We can never know why at a fundamental level. The search for answers to the question of why are misguided. And, demands of ourself and others to unravel the answer to the question of why are misguided. The question of how something occurs is more approachable and useful. Warm hands are generated by converting kinetic energy to heat. That is an explanation, but is it a theory? Why social scientists often seem to expect more from theory is, to me puzzling. Even more puzzling is what many refer to when they ask for theory.
How is theory used in international relations? Well, I’ll do what most do when ask about theory. I’ll provide a long list of references, in this case to scholarship that uses theory (Agnew, 1994; Brown, 2006; Cederman & Daase, 2003; Checkel, 1998; Clarke & Primo, 2007, 2012; Deibert, 1997; Hopf, 1998; Jackson, 2008; Jørgensen, 2000; Keohane, 1989a; Lapid & Kratochwil, 1996; Osiander, 1998; Roberts, 2006; Sørensen, 1998; Thomson, 1995; Williams, 2005). But it may be better to look at some more specific examples. I briefly explore five recent examples. These are taken from recent (2016) issues of the International Studies Quarterly, International Organization, American Journal of Political Science, American Political Science Review, and World Politics, arguably among the most prominent social science journals publishing research in the field of international relations, foreign policy, and world politics. Each of these journals has a very low acceptance rate, typically around 10%. Each of the chosen articles is a laudable piece of research that has been vetted by the harshest and most demanding professional reviewers.
Choi (2016) reexamines the so-called democratic-peace theory. This theory was introduced by an article published by Dean Babst in an arcane sociological newsletter (Babst, 1964). Russett (1993) resurrected this ideal, and it has been studied by many others with considerable success (Dafoe, 2011; Dafoe et al., 2013; Leeds, 1999; Oneal & Russett, 1999a, 1999b; Russett & Oneal, 2001; Russett, Oneal, & Berbaum, 2003). It has also been criticized on a number of fronts (Gartzke & Weisiger, 2013, 2014; Gibler, 2012; Ward, Siverson, & Cao, 2007). Choi sets about to show that the articles by Gartzke and Weisiger contain a mistake, which leads to their rejection of findings that support the democratic-peace theory. Democratic peace is an important topic in international relations. It even has its own Wikipedia page explaining that it is a theory that suggests that democracies do not engage in armed conflict with other democracies. Many scholars take this notion back to the early work of Immanuel Kant in his essay on Perpetual Peace, written in the late 18th century. The use of theory in this literature is basically the empirical hypothesis that was begun with Babst, and followed extensively by others. It is fairly general, applying to all countries over all time spans, but it only applies to violent, directly militarized conflict initiated by the state. A summary characterization of this theory is that it is really a hypothesis, based on an empirical observation of correlation.
Wucherpfennig, Hunziker, and Cederman (2016) examine the claims found in the broad literature on civil war that there is an endogeneity; namely, that political inequality is endogenously part of what creates a civil war. They find that by comparing within-country variation between French and British colonies, it is possible to conclude that there is substantial support for the inequality violence link, despite endogeneity. This suggests that post-conflict power sharing is more effective in diffusing conflict than partition or other approaches. The role of theory in this article is in reference to the broad arguments found in the literature on inequality, grievances, and conflict, not any specific theory. Indeed they refer to theory only twice: First they note that “in terms of theory, these findings suggest that the grievance skeptics have been right about endogeneity” (p. 883) and then note that “[t]he final section draws conclusions for theory and policy” (p. 883). Herein, the term “theory” is reserved for a general body of literature.
Johns and Wellhausen (2016) recently studied whether supply chains could create protections for foreign investors in host countries that have weak protection of property rights. Using a variety of cross-national aggregate information, detailed surveys, and case studies they find that outsourcing via supply chains can create a protective network that anneals property rights in weak states. They first introduce three hypotheses, the first of which is that a “host government is less likely to break its contract with a firm if the firm purchases more goods in the host country” (p. 39). Very quickly these hypotheses become “theory,” as in “Our theory suggests that the coefficient for the dummy variable Joint venture with Russian entity should be negative” (p. 43). Subsequently, “These weaker results correspond with a key element of our theory: firms face a collective action problem when they must jointly protect the property rights of other firms” (p. 44). This is a compelling study, but elevating a hypothesis or even a few of them to the status of theory is commonly found in political science articles, but it doesn’t meet many definitions of what a theory is. This is a theory as hypothesis. Or, vice versa.
David Cunningham (2016) argues that international military interventions can forestall the outbreak of civil war. He argues that since a motivation toward violence is necessary for dissidents to engage in civil wars, and further that the dissidents have to assume that they can further their goals by using violence. If they anticipate that a foreign power will intervene, they will be less motivated to use violence, and in spite of increasing grievances will tend to choose less violence strategies to try to achieve their goals. He notes the following:
I argue that this provision of order means that potential rebels anticipate that the United States will intervene in a civil war. Consistent with the expectations of the theory, I find that states in more hierarchical relationships with the United States are more repressive, more prone to terrorist attacks, more likely to experience nonviolent campaigns, and less likely to experience civil wars.
He further notes that “If this theory is correct, external interventions producing extreme asymmetry should only occur when the other side does not anticipate them,” (p. 314) and concludes that “[c]onsistent with the predictions of the theory, nonviolent campaigns were significantly (at the 0.1 level) more likely in Warsaw Pact countries” (p. 331). Finally, he notes that “Its consistency with the predictions of the theory across different variables measuring four outcomes—civil war, state repression, nonviolent campaigns, and terrorist attacks—is strong evidence for the theoretical argument” (p. 332).
This is a fairly limited domain for any theory. Imagine each sentence that replaces the word theory with the word idea, or strikes it altogether. Would the meaning be changed? This is a theory in the sense that it presents an argument, but not based on any general assumptions.
Jo and Simmons (2016) examine the impact of the International Criminal Court (ICC) as it relates to the control or diminution of violence. The ICC has the goal of creating peace and security, along with justice in societies around the globe. Yet, it has a limited ability to do so insofar as it can affect a limited set of the stakeholders in any situation, typically the leaders of governments and opposing forces. They offer a “Theory of the ICC’s Conditional Impact” (p. 446), which suggests that prosecutorial deterrence works as an expected value, raising and lowering the risks of prosecution and the costs of punishment. Thus it raises the risk of punishment and the cost of conviction. At the same time a social deterrence is described as well. The combination of social and prosecutorial deference comprises one aspect. But these features are incorporated into and affect the strategic thinking on all sides in a potential conflict. They note the following:
[W]e have theorized two broad and mutually reinforcing channels of potential deterrence—prosecutorial and social deterrence—and specified the conditions under which we might expect them to hold. We have argued that the ICC contributes directly to prosecutorial deterrence by investigating and prosecuting international crimes on its own authority. It also encourages member states to improve their capacity to reduce, detect, and prosecute such crimes domestically. Indeed, ratifying states are much more likely than nonratifiers to do so.
In short their basic idea is that the ICC can raise the potential costs of violations of international law, and in so doing will deter some, but not all, potential offenders. If this is a theory, it is at best a middle-range theory in the sense that its scope is very narrow. But compared to all the other examples, even if limited, it does take a small set of assumptions and deduces from the logically consistent hypotheses that could be examined, and which, in turn, could provide evidence against the theory. In so far as I can see, this is the only example that would meet Merton’s or Kaplan’s notion of a social science theory. It posits assumptions, logically deduces implications from these assumptions, and from there generates testable implications. However, it is by far the exception in the IR literature. Hypothesis, entire bodies of printed literature, a hunch, or observed correlations more often than not are described as theory.
Maybe Theory Is Bad? Not Just Bad Theory, But an Undesirable Thing-Itself?
Everyone wants to have theoretical rigor. But maybe it is so poorly understood, contextually specified, and vaguely interpreted that it simply has become a totem to either worship or use to intimidate? If one argues that my theory is underdeveloped (ahem, reviewer number 3) that my theory is wanting, what does this mean? Does it mean I haven’t cited the relevant literature? Does it mean I haven’t couched things as a hypothesis that is based on some assumptions I have presented? Does it mean that there are many plausible other explanations that easily come to mind that are not mentioned? Does it mean that there is no causal explanation of how something occurs? Does it mean that my idea is so far off the beaten path that no one else has ever published it? It is not clear what it means. Some treat theory, model, framework, and even explanations as synonyms. Others do not.
Maybe instead of theory we need more analytical studies of a wider range of cases? In response to the claim that case studies were not theoretical, some scholars developed the analytical narrative approach (Bates, Greif, & Levi, 2000; Bates, Greif, Levi, & Rosenthal, 1998). Analytic narratives provide a framework that gives structure to case studies. That structure is based on a puzzle or problem, much like suggested in the field of IR by Zinnes (1980). By undertaking a detailed account focusing on both the context and the historical process under investigation, this approach embraces uniqueness while seeking to identify generalizable, causal mechanisms. The analytical narrative approach focuses on identifying the stakeholders, their motivations, decision points, and the rules (in a game theoretic sense) of the “game” that they are presumed to be playing. The historical episode is sequenced over time through this framework, and the comparative statics of the game analyzed, along with any empirically testable implications. This approach aims at a casual explanation that is formal, but at the same time it tries to focus insight toward a small number of factors. This approach is also often described as theoretical, but the main thrust is the structured analysis of a narrative case study. Many practitioners of this approach consider their work theoretical (Rodrick, 2003) at least in so far as game theorists consider their work theoretical.
Theories seek to be general, and provide precise explanations of how things happen irrespective of context. This is the sense in which all theories are demonstrably false in some context. Most will agree that to be evaluated the first stage is to determine that a theory is logically consistent with itself. Often theories that are constructed from a series of ad hoc hypotheses will not be logically consistent. Theories should not have internal contradictions. Subsequent to that test, theories must be contextualized to be further evaluated. This is true because theories also assume that the world is homogeneous, and we know it is not. Thus to be useful, generalizable statements qua theories, whatever they are, need to be contextualized. The bulk of political geography has established that the world is not homogeneous. Different areas have different endowments, different histories, and causal processes—at least as considered from a geography perspective—do not operate in the same way in different places. For political geographers, the context, often local context, matters more substantially than does the general proposition. As a result, explanations may be so contextualized that some have argued that social science should give up on wide-ranging generalizations. As a result, a class of models and approaches have built up to take into account these contexts (Ward & O’Loughlin, 2002).1 If context is king, what is theory?
Many worry that we need experiments, not theory (Cook, Campbell, & Day, 1979). The quasi-experimental movement began decades ago, moved ahead by the ideas of Donald T. Campbell and Tom Cook, among others. In political science this was first introduced by Caporaso and Pelowski (1971) and Caporaso, Roos, and Bohner (1973). Recently, the experimental thread has become legion in political science (Druckman, Green, Kuklinski, & Lupia, 2011). The basic argument is two-fold, in my view. First, much of political science is based on observational data. Experimentalists do not believe that most observational data can resolve causal questions. As a result they have moved toward a different methodology that is in essence anti-theoretical. The basic argument is that we don’t have enough information to generate theories in part because the evidentiary base doesn’t exist.
Experiments may help to identify instances of causal change, and those are necessary to begin causal thinking. This approach argues that some fields may not yet be ready for theory development, whatever that is.
In short, it could be that calls for more theory are often misguided, especially when they come from a foundation that is weak to begin with. There are so many meanings to theory that are rarely clear to what is desired in any case. Theory is often a meaningless term that serves to identify good or bad research.
How Is Theory Used in International Relations Research Using Dyads?
This article focuses on the use of theory in dyadic IR research. Dyads as a framework gained considerable prominence with the introduction of the notion of dangerous dyads by Stuart A. Bremer (1992). At the same time, the dyadic format of the militarized interstate dispute database from the Correlates of War project also emphasized the importance of dyads (Gochman & Maoz, 1984). There is a recent special issue on the use of dyadic data in the Journal of Conflict Resolution (Beardsley & McQuinn, 2009; Cederman & Gleditsch, 2009; Cederman, Buhaug, & Rd, 2009; Cunningham, Gleditsch, & Salehyan, 2009; Hegre, Østby, & Raleigh, 2009; Weidmann, 2009). Additionally, a recent issue of the International Studies Quarterly also focuses on the role of dyads.
A recent survey (Mitchell, 2017) shows that very few articles that would be (self)-described as empirical qua theoretical articles in international relations also can be criticized as ignoring the deep dependencies in typical data on dyads, be it conflict, trade, or other types of transactions. Since Bremer’s 1992 piece there are myriad studies that assert—but do not test—the independence of dyads: Asal and Beardsley (2007); Bennett and Stam (2003); Colaresi and Thompson (2002); Diehl and Goertz (2000); Diehl, Goertz, and Jones (2005); Dixon (1994); Gibler (2007, 2008, 2010); Gibler, Rider, and Hutchison (2005); Goertz, Diehl, and Balas (2016); Hebron, James, and Rudy (2007); Hensel (1996); Hensel and Mitchell (2005); Kadera (2001); Leeds (2003); Lemke (2002); Lemke and Reed (2001); Mitchell (2002); Mitchell and Prins (1999, 2004); Mitchell and Thyne (2010); Senese and Vasquez (2008); Toft (2003); Vasquez (1995); Vasquez and Henehan (2001).
Cranmer and Desmarais (2016) examine what they describe as “theoretical claims” and “statistical problems” of dyadic IR scholarship. They argue that most dyadic IR research assumes that (1) dyads are independent of other dyads, and (2) that there are no confounding variables that affect dyads differently. They further suggest that much dyadic research is weakened by ignoring the simple fact that dyads are demonstrably not empirically independent of one another. Examples of work that suffers from this criticism are the norm in the discipline, not the exception (among many others, see, for example: Ellis, Mitchell, & Prins, 2011; Gowa, 1994, 1995, 1999; Maoz & Russett, 1993; Oneal & Russett, 1999b; Peceny & with Shannon Sanchez-Terry, 2002; Rasler & Thompson, 2011). This point is well established, at least since Ward, Hoff, and Lofdahl (2003) and Hoff and Ward (2004) and applied in the same exact domain in Ward et al. (2007). Being transparent, or well established, doesn’t mean that everyone agrees. Over the past decade these norms have changed very little in empirical IR research.
For Cranmer and Desmarais, theory is important. But at the same time, theory has a broad range of meanings, largely focused on what other scholars (mostly implicitly) assert that it means. Cranmer and Desmarais note that “[w]hen testing hypotheses empirically, the statistical model must be a careful operationalization of the theory under consideration.” Relational social theory such as found in Tilly (2003) and White (2002) uses a network-oriented perspective on social relations. That perspective must be included in empirical manifestations such as models and data if the theory is to be adequately represented. They further demark dyadic theory, which they describe as “thinking dyadically,” whatever that means (p. 2). Moreover, model and theory are considered separate, but interrelated entities. They, note that theoretical criticisms are often implied by statistical models in dyadic and network-oriented research. Thus “. . . [w]e do believe that theoretical problems . . . are endemic to the study of international politics. They represent a serious challenge to the development of sound, consistent, and complete theoretical explanations for a range of important international phenomena” (p. 2). Those problems are (1) omitting variables from (casual) models result in models that are incorrectly specified and thus deliver incorrect and biased inferences; (2) the assertion that dyads exist in a vacuum and are unrelated to one another; (3) the Procrustean transformation of all explanatory factors into a dyadic format (the well-known non-sequitur dyadic democracy); and (4) an incoherent treatment of multilateral phenomena such as the consideration of the Iraq wars as being a collection of dyadic actions, without multilateral dependence or coordination. These criticisms are all, in my opinion, correct. But they are not problems with theory, because there is no theory. They are problems with generating coherent models that usefully capture some aspect of the world.
The upshot of Cranmer and Desmarais’s article is that much empirical IR research is wrong or misleading because it assumes that the correct theory and thereby the correct model of international politics is based on dyads, not on a network. By analogy, prior to Bremer, much work in the field was monadic—considering only the characteristics of countries. This missed the dyadic aspects of the world, which are now believed to be paramount (see Diehl & Wright, 2016, for example). In the same way, the network perspective promoted by Cranmer and Desmarais is suggesting that the dyadic approach is similarly truncated.
Diehl and Wright essentially reject the arguments against dyadic research by essentially ignoring them. First they claim that in contradistinction to the argument made in Cranmer and Desmarias, “Indeed, depending on the question and theory, dyadic approaches may be the most appropriate simplification of reality for scholars of international studies” (abstract). This assertion is conditional on the theory, so it is interesting to see what they mean by theory. It is truly unclear. But they defend the dyad-only approach in three ways. First, they argue that it might be that the dyad-only approach is the right level of analysis. They further assert that IR scholarship is conventionally divided into four levels of analysis: subnational, national, dyadic, and systemic. Since dyadic is one of those levels, having appropriate measurement at this level is posited to be justified. With some nuance, Dielh and Wright essentially argue that some scholars might be willing to have different levels included in the same analysis, but that early scions (Singer, 1961) in the field did not and that this is the current state of the art, given that many scholars have followed it. Despite this, cross-level linkages have been prominent since the 1970s (Keohane & Nye, 1977). Diehl and Wright are aware of many different approaches, but fall back on theory to justify dyad-only designs: “. . . but our central point here is that the dyadic level of analysis is a consequence of the research question asked and its utility is a function of the value of that question for theory [emphasis added] and policy.” But to my knowledge no actual theory requires dyad-only interactions and no others. Even studies of reciprocity found that the bilateral, dyad-only approach was misleading (Goldstein & Freeman, 1990, 1991; Rajmaira & Ward, 1990).
Secondly, Diehl and Wright reject the idea that important things are lost by the dyad-only approach. They essentially assert that in some arena most things are dyadic, and therefore a network perspective is not required. They note:
Employing the militarized interstate dispute (MID, hereafter) data (Palmer, d’Orazio, Kenwick, & Lane, 2015), identifies interstate conflicts ranging from the threat of military force by one state against another to full-scale war (1,000 or more battle-deaths), we counted the number of dyadic and multilateral disputes between these rivals. Through 2010, only four of the fourteen MIDs in which Jordan clashed with Israel also involved Syria and Egypt. Four other MIDs find Egypt and Syria only on the same side against Israel. Still, the number of common disputes for Egypt and Syria are a minority of all their disputes with rival Israel, 8 of 39 for Egypt and 8 of 56 for Syria, respectively. Of Egypt’s 39 total MIDs with Israel, 27 are dyadic while 38 of Syria’s 56 total MIDs with Israel are exclusively between those two states.
While some might read this as acceptance of the notion that dyad-only research leaves a lot out, they do not and argue instead that the bulk of these disputes are dyad-only and therefore, dyad-only is an appropriate strategy most of the time.
This totally misses the point. Consider a different type of relations: bilateral investment treaties, which have been the focus of much dyad-only research (Allee & Peinhardt, 2010; Büthe & Milner, 2009; Elkins, Guzman, & Simmons, 2006; Kerner, 2009; Neumayer & Spess, 2005). Minhas (2016) has argued that the system of bilateral investment treaties in the international system should be conceptualized as a network, in which a country’s decision to form a BIT is endogenous to the network of existing investment agreements. Thus, the likelihood of an agreement between a pair of countries is influenced by extant linkages of each signatory with third parties. There is scant empirical evidence to support the notion of credible commitment or competition for capital once the network is considered. The haphazard way in which BITs have proliferated political rather than economic dimensions are helpful. This is another example—like the study of militarized disputes—of why the dyad-only approach does a disservice, even when the dominant literature is based on it.
Finally, Diehl and Wright make the specious argument that we have a long history of insights that have come from using the dyad-only approach. They note that “[s]ome of the most influential theoretical ideas and empirical findings in international conflict research have come from adopting a dyadic perspective” (p. 4). They include (wrongly it seems to me) the systemic power transition model as well as the line of research about hegemony transitions. This is the same type of argumentation used by the Catholic Church against non-earth centric ideas about planetary movements: It works really well. But it doesn’t. It is true we can benefit from previous research and insights, but that doesn’t mean to benefit we need to continue with ancient technologies when new approaches abound.
A symposium was conducted discussing the Cranmer and Desmarais as well as the Diehl and Wright articles in the special issue, along with the article by Paul Poast. It is interesting to survey the responses.
• William Kindred Winecoff agrees with Cranmer and Desmarais, but suggests that sometimes we have to use what is available to us.
• Toby Rider argues that scholars have good reasons to pursue dyadic theory and shouldn’t be deterred by criticism.
• Patrick J. McDonald notes that dyadic approaches magnify the state-based bias of country years, and replace them with two country years.
• Brandon J. Kinne notes that dyadic models are the norm in empirical international relations, but that using dyads does not necessarily mean only using dyads.
• Sarah E. Croco states that “I am not fully convinced that the call to abandon the dyad in favor of a more networked approach is the best course of action” because she believes that the interdependence bias is not as pernicious as portrayed and that she doubts that ERGM is as she puts it “a silver bullet.”
• Kathleen Gallagher Cunningham points out that network models haven’t solved side switching and faces challenges dealing with multiplex networks.
• Allison Carnegie and Tarara Slough oppose abandoning dyadic models because gravity models in trade are prominent.
• Cassy Dorff (a co-author) noted that much of the debate about the dyadic framework and use of networks ignores the fact that advanced methods for assessing relational data do exist and have been widely adopted in other fields.
Thus, the use of theory in dyadic research parallels its use in IR more broadly, as we might expect. Theory is used in a fairly vague way to argue against different perspectives without really confronting directly the points of contention. Theory is a type of delusional that shows beauty and virtue only upon reflection. My arguments are right because they have theoretical status, even if yours may be more logical or more supported by empirical research. Wherein empirics support my ideas, they are correct. Wherein they do not, the methods are not correctly aligned to my theory. One is reminded of Chan’s research on the democratic peace (Chan, 1984).
How Might We Actually Use Dyads in Empirical International Relations Scholarship?
Network analysis provides a framework to study “dyadic data,” that is, data with characteristics beyond the monadic level. But network analysis is not a dyad-only approach, even if it uses dyadic information. Data that extend beyond the monadic level are the norm in many parts of international relations, including trade, conflict, and international institutional collaboration, such as treaties. The dominant paradigm in international relations for dealing with these kinds of data is what I will call the text it dyad-only approach. In this approach dyads (pairs of countries) are viewed as independent of other pairs of countries.2
This perspective implies not only that all dyads involving the United States, for example, will be correlated because they all share the United States, but also that dyads such as the United States→North Korea will be uncorrelated with other dyads, such as that between Japan→South Korea. Maoz, Kuperman, Terris, and Talmud (2006); Ward et al. (2007); and Minhas, Hoff, and Ward (2016b) each note the importance of taking into account network dynamics in the study of interstate conflict. Yet, the dyad-only approach is still widespread. But it cannot be denied that interdependence among observations, whether they are dyads or monads, poses a strong challenge to standard approaches to empirical studies in IR.3
There are many types of dependencies. Reciprocity is one form of interdependency that has long been observed in international relations (Brandt, Colaresi, & Freeman, 2008; Choucri & North, 1972; Goldstein & Freeman, 1991; Keohane, 1989b; Rajmaira & Ward, 1990; Richardson, 1960). First- and second-order dependencies have been long studied in psychology, but only recently in political science. Warner, Kenny, and Stoto (1979) developed what is now known as the social relational model (SRM). Dorff and Ward (2013) introduce this framework and Dorff and Minhas (2016) apply this approach to studying reciprocal behavior in economic sanctions. SRM decomposes the row and column variance in an adjacency matrix. Wong (1982) and Li and Loken (2002) provide a random effects representation of the SRM. Hoff (2005) shows that the SRM covariance structure can be incorporated into the systematic component of a general linear model via a mixed effects model. This approach incorporates first- and second-order dependence in a straightforward regression framework with additive random effects accommodating variances and covariances of relational data. It can be used to study binomial, ordinal, and continuous data.
Third-order effects concern interactions among sets of countries. Zinnes (1967) explored such dependencies in terms of balance of power systems. It has been argued that balanced sub-graphs are more stable than unbalanced ones and as a result actors try to balance their negative relations with positive ones. Stochastic equivalence is another third-order dependence pattern that captures the place and role that a particular country may play in the network. If two countries play the same role, they are perfect substitutes for one another—in a network sense—and can be considered equivalent. Manger, Pickup, and Snijders (2012) explore stochastic equivalence structure to explain the formation of preferential trade agreements (PTAs) and demonstrate the broader point; namely, that the behavior of countries in a network is partially determined by local network dynamics.
The R package amen provides for the estimation of these kinds of network models using a Bayesian framework. The main function assumes that no multiplicative effects are necessary, but these can also be estimated.
The latent factor model incorporates these components in a flexible way. An early iteration is found in Hoff (2005) and Hoff and Ward (2004), more recent specifications are found in Hoff (2015) as well as Minhas, Hoff, and Ward (2016a, 2016b). In sum, additive effects networks are described by the SRM and the multiplicative effects captured by latent factors. Together, these constitute a general linear modeling approach that is widely familiar, yet it has the benefit of being of incorporating interdependencies in relational, dyadic data that vary over time. This permits the study of dyads, but not in a dyad-only way that ignores important dependencies.
This network approach to understanding international interdependencies can be undertaken with a somewhat complicated version of a general regression framework. There are few reasons to avoid investigating these potent interdependencies. We study international relations because of the relationships, so we should stop avoiding these interdependencies—they are what drew us to the field in the first place.
What About Just Doing Inference?
Nobel Laureate (2005) Thomas Schelling firmly believed that rationality was a useful framework to understand individual and collective human behavior. His most important works (1960, 1966, 1978) focused on using rationality to explain conflicts among nation-states, among other issues. He also worked on a variety of other problems, including the individual level reasoning needed to overcome addictions such as smoking. Many would argue that Thomas Schelling was perhaps the best theorist of his generation. But this reasoning found in Schelling’s works is exactly the kind of thinking that is useful and could serve as a goal for many aspiring to make a theoretical contribution. Schelling rarely used the word theory. When he did it was in the context of game theory—which was a direct target of much of his work. Schelling didn’t call his work theory. But he is a paragon for many social scientists who aspire to be theoretical. Merely calling something a theory does not increase its theoretical content.
Arguing about theory may resolve some important issues. But my assessment is that we still have no single, intersubjectively shared idea of what theory in international relations might be. Further, I don’t think many agree on a useful definition of theory. Yet like pornography, every thinks they know it when they see it. Remember that at the West of England Fat Stock and Poultry Exhibition at Plymouth in the early 1900s, 787 individuals guessed the dressed weight of a living ox was (an average of) 1207 pounds, while the actual weight was 1198 pounds (Galton, 1907). Maybe the most important thing is not to worry about which of the 787 theories was right (or wrong), but to get on with predicting features about our oxen.
I recently wrote about prediction in world politics (Ward, 2016). Therein, I wrote about the Antikythera Mechanism that was discovered in a shipwreck in 1901 in a bay of the Greek island Antikythera. Examining this bronze mechanism, Greek scholars at the National Museum of Archeology in Athens dated it to about 150 BCE, but ignored it for essentially six decades. By 2014 it was established that the mechanism dated back to about 250 BCE. This device was shown to be an elementary computer able to calculate and display celestial cycles, including phases of the moon and a solar calendar. It was also able to predict eclipses accurately. Thus, the main purpose of the Antikythera Mechanism was to generate accurate predictions without a detailed theoretical knowledge. Perhaps a self-correcting science of making predictions about international relations is one path forward. We would know definitively when we were wrong. Debates about theory would be less central if our goal was to generate accurate predictions about the world and how important organizations such as countries behaved toward one another. We might even gain guidance about which theory could be easily jettisoned. We could be agnostic on whether theory was useful, focusing instead on whether our predictions were accurate. In such a conception, it is clear that we would benefit not just from information about those organizations, but also about their interactions. It is further plausible that we would benefit further by looking at the dependencies among those relationships. In such a conception, one in which we are interested in international relations, it is clear that we need to focus on the network of dependencies that exist in the world. We now have replete information about those interactions, as well as a principled way to study them.
Waltz was wrong; Tetlock was right. We don’t need theory to make progress, we need progress to make progress.
Thanks to William R. Thompson for provoking me, and to Shahryar Minhas for helping me better understand networks. Along the way, Will Moore provoked me more, for which I am grateful.
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