Journal of Political Risk, Vol. 7, No. 12, December 2019
Alicia N. Ellis, PhD, Arizona State University
This report assesses the state of the academic literature on political risk and evaluates its contribution to understanding and mitigating risk for both business and political professionals. This assessment concludes that policy-relevant research has been in some cases limited and, in most cases, ineffectively communicated. Several major problems contribute to the persistent disconnect between policy, industry, and academia. Political scientists do not approach their research questions in a communicable way, nor do they often take the necessary step of connecting their research to an end use. Risk rating organizations have become overly reliant on cross-national aggregate models. Mixed methods research has been applied inappropriately and thus, ineffectively. Systematic biases have been introduced to models at a structural level, and conceptual difficulties plague some of the most basic questions for risk analysts.
Despite these problems, opportunities do exist for bridging the gap between research and practice, and producing policy-relevant research. This article proposes some recommendations for moving forward. Research questions must be structured in new ways to reflect the needs of end consumers that include non-academic professionals. Several research agendas in need of a practical-minded researcher are put forth, including the rise of China and what it means for global trade patterns, the ‘buy local’ movement spreading across the United States, and the problem of democratic consolidation. For each problem identified, the article makes suggestions for how we might reframe the questions in a way that produces more useful research on political risk.
Political risk is typically understood as risks to business, investment, or financial assets that stem either from some form of government intervention or social/political instability (such as armed conflict or civil strife). It concerns itself with understanding the source, likelihood, and impact of such events. It doesn’t have to be limited to conflict or obvious interventions such as nationalizations and state expropriation. It can include government measures such as regulatory changes, selective enforcement or favorable treatment to favored firms, complex rules governing hiring practices, profit repatriation, permitting and licensing requirements, et cetera. It can also cover informal practices such as corruption or clientelistic bureaucratic structures that branch into local economies. When it is expanded to include these issues, the concept of political risk has great salience not just to multinational firms, but to domestic firms trying to operate in an increasingly complex regulatory environment.
Surprisingly, it remains one of the most understudied and little understood “niche” areas of political science. Part of the reason it remains in relative obscurity is that it sits at the crux of political science and economics, neither field taking full ownership. Scholarly research in the field of economics tends to focus on mathematical models and market forces; few economists study geopolitical tensions or religious divisions in some obscure part of the world. Understandable though that is, it is also regrettable, given that geopolitical competition has historically been a frequent driver of global trade patterns, and it seems to be making a resurgence today. Moreover, with foreign investments spread all over the world, it is not hard to imagine that renewed conflict in South Sudan could bankrupt a Texas oil company, or that a revival in pirate activity off the coast of Somalia might interrupt crucial international transportation networks.
Problems of this nature do not just have relevance to industry and finance, but to state policymakers. The primary task of research on political risk is to understand what causes political upheavals and predict what the impact will be; this is valuable information to a policy analyst or decision maker. The likelihood that conflict could break out in country x, given current conditions and the occurrence of a (hopefully foreseen) possible catalyst is information policymakers need. What that might mean for the business community is information at least as valuable to the prudent statesman, given the interconnectedness of the global economy with its sprawling supply chains and integrated finance system.
Yet political scientists aren’t really covering political risk either. Most of the academic research on political risk converges around one of two questions: how regime type affects investment behavior, or how a state’s political risk rating affects investment behavior. Few look at the issue from the standpoint of the practitioner. Were they considering that perspective, it would change the questions that are being asked: not how does regime type affect the level of investment, but how does the nature of the regime affect the value of an investment, the predictability of the business environment, or the viability of an emerging market? Not just how does the given risk rating affect investment levels, but what environmental factors increase or decrease risk? What catalysts, combined with the right conditions, tend to generate instability? Which areas are ripe for political or social change? These types of questions would tell the end users of information much more about political risk from just the people who should be studying it: political scientists.
Paradoxically, most mainstream scholars in political science are doing some form of research on political risk without explicitly using the term. Anyone who publishes a paper on the causes of civil war, the drivers of regime change, the politics of nationalization, global or regional patterns in agricultural policy, the dynamics of clientelism, corruption, repression, or a host of other common topics, is making a contribution to our understanding of political risk. They just aren’t saying that’s what they’re doing. Everyone is staying in their lane. The scholars who write about political risk aren’t asking the right questions; the scholars who cover the host of topics that collectively make up political risk aren’t phrasing the answers in a way that is digestible and relevant. This persistent disconnect between policy, industry, and academia is plugging the flow of necessary information like the stove-piped intelligence community before 9/11.
Four main problems in the political risk research are contributing to this blockage. The first is mentioned above. Asking policy-relevant questions is the first step in producing policy-relevant research. This goes beyond justifying a given research project as relevant merely because it is related to some topic that has something to do with a policy issue sometimes. It is more than adding a paragraph at the end of an article with a vague suggestion of policy relevance as an afterthought. It means starting out by asking the question the way a policymaker would. Considering this at the outset would substantially reduce the amount of explanation needed to bridge the gap; the relevance to the practitioner would become obvious.
Taken one step further, research should tell the audience what it means for them. There are two pieces to political risk. First, the event or possible event in question (instability, regime change, conflict, policy change, et cetera). Second, the impact on whatever entity is interested in the event. Typically, when we speak about political risk, we’re thinking of firms or industries, but the interested party could also be governments. Regardless of the audience, the event itself and the related research is the same; only the second question regarding impact changes based on who is interested in the information.
Questions that address the second piece would include how might instability in country x potentially impact the bottom line on the influx of investments that recently took root in neighboring country y? Is there a certain point on the political risk scale at which a country becomes much more likely to experience event a, and what is the potential fallout from that? These are answers policymakers are interested in, and on which political scientists are well positioned to offer new ideas and insights. A lot of the work on the causes and likelihood of certain events is already being done, if sometimes implicitly; the work on how those events impact firms, industry, other states, or even the global system, is the missing link that makes that work relevant.
Scholars are understandably wary of offering prediction, preferring instead to draw insights from the past; from knowledge, not guesswork. But good predictions come from a solid understanding of the past. This knowledge allows one to comprehend the relationship between events that may at first glance seem unrelated, and to recognize when something may be changing. Even if one takes the view that political science is intended to pursue knowledge for the sake of knowledge and should not be driven by the policy concerns of the day, the subfield of political risk is the exception. By its very definition, it is concerned with contemporary problems as they relate to practical needs; its purpose is to look ahead.
The remaining problems with political risk research are less issues within academia than with the industry, where most research on political risk is actually taking place. Most firms and organizations in the industry produce some version of a global risk rating system. This is the staple of the political risk industry, even though the target consumers of that information are not finding it overly helpful. The gap between research and practice is evidenced by the extreme mismatch between investor priorities and actual behavior. Several studies have surveyed management in multinational firms, and all have rated political risk as a major concern, citing in particular concerns over property rights and rule of law. Yet most studies of the relationship between political risk ratings and FDI flows find little to no relationship between the two. This may be explained by the finding that despite their vocalized concerns, few firms are undertaking a “rigorous and systematic assessment of political environments and their potential impact on the firm.” Kobrin found that even large multinational corporations tend to rely on an overly generalized feel for the political environment, and end up sticking to investments in the same handful of countries they already perceive as stable. Political risk models offer little help, since they don’t tell a firm anything about how the general ratings are applicable to industries. Instead, they employ the repetitive aggregate cross-national database, even though most of the risk posed by politics is “markedly affected by industry, firm, and even project-specific factors.”
Some organizations, such as the Political Instability Task Force, have found more traction in the policy community, where the country-based focus is more appropriate to their needs. All the risk models, however, share one common problem: they are confusing risk with uncertainty. This was a natural casualty of the quest to quantify everything. Numbers imply some degree of certainty, so they’re more comfortable for the consumer of information. Political science can deliver on that, since better access to data and more sophisticated modeling software has facilitated the trend toward data-driven research. The problem is that it conveys a sort of certainty that isn’t really there when you’re dealing with politics. Most of the political world lies in the realm of uncertainty, not risk. Few social problems are narrow enough in scope to operate with very high degrees of certainty. Most have a wide range of possibilities; many have infinite futures; all at least have multiple possible paths they can take. If there are a limited number of possibilities, or at least likely possibilities, you can, to some extent, transform uncertainty into risk. It is possible to define the scope of possibilities and quantify the relative likelihoods based on further information, so long as you are honest about the degree of uncertainty still embedded. But this requires going beyond the statistical model to gather contextual information. This requires more detective than mathematical skill. Data systems are, of course, valuable tools in risk management. They facilitate a systematic approach to assessing and mitigating risk, though it is just one of many possible systematic approaches.
This leads to the third problem in political risk research: inappropriate use of mixed methods. I’ll start with an example. One of the common approaches to building political risk models using “mixed methods” is the expert survey. They attempt to incorporate area experts with their deep knowledge of a smaller area into a database that aggregates information on a global scale. One such firm sends survey materials to academics focusing on particular countries or regions, asking them to weigh the possibility of various events in a given time frame. The risk of a coup that deposes the sitting regime in the next year, for instance. The experts fill in the requested information, send it back, and the data is entered into the model, presumably along with opinions from other experts, allowing them to average it out as well. A colleague of mine, who focuses on Asian affairs, responded (correctly) to one of these surveys that the likelihood of a coup in Thailand in the next few years was very high. A week later, the news spread: “U.S. FIRM PREDICTS COUP IN THAILAND.” What their model didn’t account for was that this was the typical means of regime change in Thailand, and was no more an indicator of instability than a change in party leadership in the United States.
At worst, this type of misunderstanding could create unnecessary economic instability if it’s widely consumed by investors unfamiliar with Thai politics. At best, this wasn’t exactly headline news and it surely didn’t contribute to an aura of expertise on the part of the political risk firm. The problem was that they were trying to transform qualitative, contextual knowledge into quantitative data. They were trying to force one type of data to be something it wasn’t. This isn’t mixed methods research, this is just survey research. A better application of mixed methods would have been to let them both do what they do best, come to separate conclusions, and then red team the question. This takes more time, more effort, more money, and more personnel; but it produces higher quality information.
Both quantitative and qualitative research methods have something to contribute to political risk analysis. Sophisticated data modeling advances almost constantly and has become relatively adept at locating environmental factors that suggest a risk of instability. A good quantitative predictive model can be up to 85 percent accurate; the model run by the Political Instability Task Force is able to achieve that kind of accuracy in predicting how likely a state is to experience civil conflict with only a handful of the most salient variables, all of which are relatively easy to measure. This is valuable information, and vastly simplifies the universe for a busy decisionmaker, but the flow of information from quantitative models stops here. It doesn’t suggest a causal theory about why, so it doesn’t leave the analyst any means for identifying when those factors might be on the verge of change. It makes sense, then, that this type of modeling is notoriously better at predicting stability (including the stability of instability) than it is at foreseeing change.
Quantitative models are also better at identifying environmental factors than they are at uncovering the triggers or catalysts that will set new events into motion. For this, you need focused, in-depth research that is more limited in scope. To be fair, the track record of subject matter experts at foreseeing political change is no better. They are subject to human bias in the same blind spot being experienced by the computer data: it’s biased toward historical patterns, and prone to overlook change. Identifying patterns in the past, which is what political science is accustomed to, is in many ways, the easy part. Predicting change is an even more inexact science. It requires imaginative thinking, scenario planning, recognizing patterns and correctly interpreting the meaning of outlying information, knowing the context, perceiving the interaction of structure and actor (and understanding the relevant actors), and most of all, comfort in the gray area. This doesn’t necessarily require subject matter expertise in each specific geographic or topical area; what it asks of the analyst is to know where and how to look.
Quantitative models also tend to be global in scope, which limits the degree to which an analyst can grasp the nuance from which the unexpected usually arises. Global models serve a purpose in risk research, an important one. They can tell us where to look, give the user a starting point if they have none, and provide a comparative frame of reference. They cannot, however, substitute for a thorough risk assessment. The more defined and narrower the scope, the better a risk assessment will be; all a global database can tell you is how the topic or area of interest to you compares to others on specific data points.
The fourth problem in political risk research is the tendency to inject value-laden concepts into objective assessments. The most egregious error is the bias toward democracy. The assumption is that democracies offer better long-term investment environments. Institutions such as free speech, elections, and constitutional procedures not only constrain the state, but also contribute to overall stability since people have an outlet for expressing social, political, and economic frustrations. Research linking democracy to political risk ratings has revealed that democracies do tend to score significantly better, but no systematic attempt at validating the argument that they should score better has been undertaken.
Most rating systems are not public, so it is unclear whether states are being scored higher simply for having democratic institutions or whether democracies are performing better on political risk measures because they are actually less risky environments. The fact that one study of the impact of political risk on FDI substituted democracy as a measure of political risk in the absence of better data suggests that there is some implicit bias at work. This is problematic because the question of whether democratic or autocratic governments offer better environments for investment is unresolved in the literature.
Still, academic research has a lot to offer here. Several scholars have devoted resources to learning what type of regime offers better conditions for investment, though they disagree on the answer. Supporting the thesis that democracies offer better investment environments, Olson (1993) cites the role of individual rights and regular elections as forms of constraint, which Jensen (2008) argues is the linchpin of democratic favorability. My own research suggests that constraint is critical to stable democratic governance, but that not all democracies are necessarily good at this. This would mean that Jensen’s argument about the importance of executive constraint may be sound, but this does not necessarily mean that democracy = constraint, at least not in the most recent century.
Other scholars disagree that democratic governance offers a relative advantage at all, arguing that because of their degree of control, authoritarian governments are better positioned to make guarantees to investors. The question of whether democratic or autocratic governments are more stable environments is not settled, in part due to this disagreement in the literature on regime type. More to the point, these studies aren’t measuring the actual impact of regime type on political stability or any other form of riskiness; by focusing on FDI flows as the dependent variable, they are really measuring the impact of regime type on investor perceptions that the environment is riskier.
Political risk is most often about instability, not about the quality of governance (except insofar as that might affect stability). The assumption that democratic governance is necessarily more favorable is embedded in many risk models, even though in the past several decades, at least as many democracies have overturned the political order as the other way around. Despite their assumed favorability toward private property rights, democracies have also proven entirely capable of expropriating property, which has often been electorally popular. Adding to the confusion is the difficulty of classifying the many hybrid regimes that characterize the 21st century globe.
Classification systems fall far behind the curve needed to develop accurate models for use in political risk forecasting. Democracies that experience authoritarian backsliding or even full reversals often exhibit democratic traits to the casual observer right up until the eve of disaster. It is only after peeling back a few layers of surface institutions that the analyst discovers how politics really works in the area under investigation. That requires in-depth and ongoing investigative knowledge of each case. To be useful to industry or policy, it needs to be done well before instability emerges, not during or after. The literature tries to deal with this by breaking categories down into full and partial democracies and autocracies. It seems to have reached as close to a consensus as it can that full democracies and full autocracies are both relatively stable, while partials or hybrids are more prone to civil war, violent regime change, and other forms of political instability.
A related theory posits that the level of economic development is the intervening variable. O’Neal differentiates between developed and underdeveloped states and improves the value of the research agenda by directly measuring returns on investment (RTI), rather than just levels of FDI. After testing RTI against regime type at various levels of investment, he finds that it is highest in developed democracies, but lowest in peripheral democracies, which were far outperformed by autocratic states. This suggests that economic development is more important than democracy when it comes to sound investment decision making. However, it should be noted that the peripheral states he classifies as underdeveloped also tend to be the less stable democracies. Not only does this make it difficult to determine whether it is level of development or simply political stability that makes the investment environment favorable, it is also likely that these two phenomena are themselves related to one another. Furthermore, the research on democratic consolidation is in early stages. Though it’s clear that wealthy democracies are more stable, we still don’t know what the causal mechanisms for consolidation are. Political scientists are working on that question. The answers can tell risk analysts a lot about the key risk factors for major political reversals.
There are many opportunities for overlap between academic work and practitioners, whether it be policymakers, business leaders, or other decision makers who operate in the international space. Scholars interested in making their work policy relevant need to think about research problems in a different light. Start by choosing questions that are timely. Watch for developing trends without jumping on the bandwagon of whatever issue everyone else is talking about at the moment. For example, globalization has been a popular theme for at least a decade. Experts argue it’s a force that can’t be stopped or rolled back. Fewer policymakers at the top level are paying the same degree of attention to the reverse current.
All over the country, “buy local” is becoming increasingly trendy. It’s picking up steam with consumers and producers are responding to it. Large chain grocery stores and major retailers are actively looking for local producers of food and other goods to create entire sections of locally-produced items in their state and regional markets. This new wave of localization of markets that have spent the last century becoming increasingly trans-local may be a signal of changes on the horizon. It might remain a niche phenomenon, given how complex and integrated the economy is today and how difficult that makes it for a small producer to enter even her own local market. Or not. Economic growth can also reach a point where the connected services a local producer needs (storage, transportation, distribution, processing, etc.) can all be found at the local level. What would have been impossible to create in a given area a century ago is now possible, especially with the backing of large retailers.
Not all sign posts point clearly in one direction, which is typical of predictive research. The tide of globalization has for years created business interests that are by nature supranational. In his book Special Providence, Walter Mead points out that through much of history, support for U.S. business interests was a mainstay of U.S. foreign policy. Likewise, the business community has been part and parcel of the American nation; during the Cold War, it played an active role in isolating the Soviet economy from the western world. In his book, Mead questions the future of that alliance as U.S. firms become increasingly international. Globalization in this sense eventually means the erosion of national identities, if not for the average citizen, at least for the business community.
This development is evidenced by the increasing divergence of U.S. business interests and U.S. geostrategic interests. Firms need new markets to keep growing. With its burgeoning middle class, opportunities for upward mobility, and increasing demand for higher quality products, China offers one of the most promising markets for multinational firms. Elements of the business community have reacted in different ways to their difficulties breaking into that market. Several Wall Street bankers and hedge fund managers are circumventing U.S. policymakers to engage directly with China in an effort to pressure the United States into making a deal that meets their needs. Others have attempted to gain market entry through firm-to-firm relationships but are often unable to gain access without also moving production overseas. For some industries, especially food production, it stops there when Chinese production facilities don’t meet quality control standards. These firms were counting on the TPP to open some of those doors but were disappointed at the meager attempt to gain market access for U.S. firms. U.S. policy must meet these needs if it wants to align the long-term interests of the business community with its political objectives.
However, more recent developments point to a convergence of interests on the horizon. Enlivening the industrial and manufacturing sectors is seen by the current U.S. administration as not only an economic benefit, but a critical pillar of national security. Businesses in those sectors have obvious interests in increasing activity, production, and profit. Now they also find a place in national grand strategy. This also points to the reversal of some aspects of globalization. The multinational nature of critical supply chains is increasingly viewed as a national security problem. This doesn’t apply only to defense-oriented industries, but also those involved in communication, energy, and food production. The more power becomes globally dispersed, the more wary the U.S. is of becoming reliant on foreign entities to uphold the structural integrity of supply systems. U.S. policymakers need an alignment of political and business interests over this point in order to meets its long-term national security goals. The Trump administration is responding to this by paying attention to policies that lower the cost of doing business in the United States. By doing so, he meets a critical need of U.S. firms and increases the appeal of keeping production within national borders; but it needs to be combined with attention to market growth.
There is, of course, no guarantee that this is the direction it will take. Some observers go so far as to predict that the increasing influence of non-government interests combined with the rise of international and non-governmental organizations points to the eventual decline of the nation-state as the primary building block of the global system. Others point especially to the influence of large multinational corporations, arguing that they have become powerful enough to drive policy or if they so choose, ignore it. Both do happen: trade policy is often a reflection of the most powerful business interests, the effect of which has been to relocate jobs to areas where lower wages and no benefits are the norm. Google refused to hand over data on its users to the Chinese government; Apple declined to unlock the iPhone of a terrorist suspect without a warrant. Not that these are all necessarily undesirable events, but they do indicate that the state is not automatically sovereign in all matters. Still, this overlooks the mutual need that does exist between government and business and the “trump” cards (so to speak) that are held by the political side.
Firms still need the support and protection of the U.S. government in their international endeavors, perhaps now more than ever. Throughout the globe, and not limited to the developing world, firms are at risk of losing value in their investments. Often, it doesn’t come through direct expropriation or even political violence, but through less headline-grabbing events such as policy changes, contract reneging, favorable treatment toward competing state-owned enterprises, currency manipulation, limits on profit repatriation, inconsistent regulatory enforcement, or simply power shifts among important players in the host country. There is little a firm can do about some of these, other than think ahead about the potential risk factors and have contingency plans for minimizing exposure. But many of these measures do trespass on international laws and treaties that govern investments. The only real insurance policy a firm has against this type of political risk is the power of the U.S. government and the world institutions backed by that power. The international business community may have interests that supersede the national security or diplomatic prerogatives of its home country, but it also has an interest in maintaining the economic power that gives the U.S. so much international clout.
In the context of these contrary trends, there has been somewhat of a resurgence in great power rivalries. The rise of China has been a hot topic for some time. China’s rise on its own isn’t necessarily a negative development for the U.S. (with whom China has had a cooperative relationship for much of the past century), but it does mean uncertainty because it means changes in the global power structure. The three-way dynamic between the U.S., China, and Russia has again taken a prominent role in world politics that hasn’t had such relevance since the end of the Cold War. The sometimes-adversarial, sometimes-cooperative relationship between the U.S. and China has a real and lasting impact on economic development beyond the two countries and on overall global stability. Leaders in both are acutely aware of this, and managing it is a constant balancing act.
What does rivalry between the world’s largest economies juxtaposed with an increasing demand for nationally, and even locally, produced goods mean for global trade trends? Where will the secondary powers likely fall in new trade patterns, and how will those economic realities shift the global balance of power? Will the international business community follow suit where national policy leads, or will it diverge? These are questions with immediate practical relevance, phrased in the language decision makers speak. These are the kind of questions that exist in the realm of uncertainty, but they are not without direction. They help clarify the meaning of current events and open possible pathways to likely futures. They hold information that both business and political decision makers want to know. They’re the type of questions policy-relevant research needs to be asking.
Alicia Ellis received her PhD in Political Science from Arizona State University. Her research specialties include comparative political economy, political risk, and political instability. She published her doctoral dissertation on how the development of the agriculture sector drives the setup and durability of political institutions. Alicia was appointed as a Presidential Management Fellow in 2012, serving as a State Department Policy Analyst and Department of Treasury Management Analyst. A former U.S. Air Force officer, she is a veteran of Operation Enduring Freedom and Operation Iraqi Freedom.
 Stephen J. Kobrin, “Political Risk: A Review and Reconsideration,” Journal of International Business Studies Vol 10, No 1 (1979): 74. For a more recent study, see also Glen Biglaiser and Joseph L. Staats, “Do Political Institutions Affect Foreign Direct Investment? A Survey of U.S. Corporations in Latin America,” Political Research Quarterly Vol 63, No 3 (September 2010): 508-522.
 Kobrin, 74
 Though this point seems to have been lost in the intervening years, I’m not the first to point this out. See also Dan Haendel, Gerald T. West, and Robert G. Meadow, “Overseas Investment and Political Risk,” Foreign Policy Research Institute, 1975. See also Kobrin, 68-69. See also Franklin R. Root, “Analyzing Political Risks in International Business,” in Multinational Enterprise in Transition, eds. A. Kapoor and Philip D. Grub (Princeton: Darwin Press, 1972), 354-365.
 Name of firm withheld.
 Philip A. Schrodt, “Technical Forecasting of Political Conflict,” (presentation given Arizona State University, Tempe, February 10, 2017).
 Krishna Chaitanya Vadlamannati, “Impact of Political Risk on FDI Revisited—An Aggregate Firm-Level Analysis,” International Interactions 38 (2012): 111–139.
 Olson (1993). Mancur Olson, “Dictatorship, Democracy, and Development,” American Political Science Review
Vol 87, No 3 (September 1993): 567-576. Nathan Jensen, “Political Risk, Democratic Institutions, and Foreign Direct Investment,” Journal of Politics Vol 70, no 4 (October 2008): 1040-1052.
 Alicia N. Ellis, “The Decline of Democracy: How the State Uses Control of Food Production to Undermine Free Society,” (PhD Diss., Arizona State University, 2019).
 A number of scholars have written that authoritarian regimes receive more favorable treatment by investors than new democracies. See John R. O’Neal, “The Affinity of Foreign Investors for Authoritarian Regimes”, Political Research Quarterly Vol 47, No 3 (September 1994): 565-588. See also Adam L. Resnick, “Investors, Turbulence, and Transition: Democratic Transition and Foreign Direct Investment in Nineteen Developing Countries,” International Interactions 27 (2001): 381-398. See also Quan Li and Adam Resnick, “Reversal of Fortunes: Democratic Institutions and Foreign Direct Investment Inflows to Developing Countries,” International Organization Vol 57, No 1 (Winter 2003): 175-211.
 Jack A. Goldstone, Robert H. Bates, David L. Epstein, Ted Robert Gurr, Michael B. Lustik, Monty G. Marshall, Jay Ulfelder, and Mark Woodward, “A Global Model for Forecasting Political Instability,” American Journal of Political Science Vol 54, No 1 (January 2010): 190-208.
 Much has been written about what causes democratic reversals/regime overturn, but Svolik notes that the causers of democratization, the causes of democratic reversal, and the causes of democratic consolidation, are different, and there is no way to directly observe the last, which helps explain the literature’s perpetual state of infancy on consolidation. See Milan Svolik, “Authoritarian Reversals and Democratic Consolidation,” American Political Science Review Vol 102, No 2 (May 2008): 153-168.
 Walter Russell Mead, Special Providence: American Foreign Policy and How it Changed the World (Routledge: New York, 2002).
 Peter Navarro, “Economic Security as National Security” (speech, Washington, D.C. November 9, 2018), Center for Strategic and International Studies, https://csis-prod.s3.amazonaws.com/s3fs-public/event/181109_Economic_Security_National_Security.pdf <accessed 8 Sep 2019>