Academics and policymakers enthusiastically endorse “evidence-based” policymaking, for obvious reasons. (After all, what is the alternative? Faith? Popularity contests?) But while evidence—including quantitative evidence—is often helpful, we must be mindful of the limits on what empirical analysis can tell us about important topics. Take the regulation of transnational bribery. Scholars and policymakers would like to know if the current regime—laws like the U.S. Foreign Corrupt Practices Act (FCPA) and U.K. Bribery Act, and international instruments like the OECD Anti-Bribery Convention—has “worked.” That is, have these instruments reduced bribery by the firms that they cover? And did those laws have additional, possibly undesirable collateral consequences, for example reducing investment in countries perceived to be corrupt?
The most sophisticated efforts to answer these questions (see, for example, here and here and here) essentially rely on what social scientists call “natural experiments.” First, the intervention (the law or policy change) of interest, which (in a borrowing from medical terminology) researchers call the “treatment.” Next, one must identify the population of interest—say, firms or countries—and an outcome of interest (such as the frequency of bribery or the level of investment). Then, the researcher identifies the subset of those entities that are affected by the intervention (for example, the firms that fall under the jurisdiction of the new anti-bribery law); this is the “treatment group.” The researcher also identifies another subset of entities—the “control group”—that appears otherwise similar to the treatment group, but did not receive the treatment (for example, a group of firms that are outside the jurisdiction of the new law). The big difference between a “controlled experiment” and a “natural experiment” is that in a controlled experiment the researcher can randomly choose which members of the population receive the treatment (for example by randomly selecting some patients to get a new drug and giving the other patients a placebo), but in a natural experiment, the assignment of the treatment is done not by the researcher, but by some “natural” process in the world. In trying to figure out the effect of an anti-corruption law, it generally is not feasible to conduct a controlled experiment: researchers can’t decide that these firms but not those firms, selected at random, will fall under the jurisdiction of an anti-bribery law. So the best that researchers can do is to rely on natural experiments and try to account as best they can for possible differences between the control group and the treatment group by including additional control variables in a multivariate regression.
Unfortunately, when it comes to studying the effects of transnational anti-bribery laws, these sorts of studies face several fundamental challenges, which are all too often overlooked or understated.
- First, as with just about all studies that rely on natural experiments, there is a deep problem with attributing differences in outcomes to the treatment, as opposed to other differences between the treatment and control group. It’s impossible to control for everything, especially since some of the variables that might affect both selection into the treatment group and the outcome of interest may not be the sorts of things researchers can observe.
- Second, in this context many of the outcomes of interest are difficult to measure—particularly illicit activity like bribery. Data from surveys of experiences are available for many countries and there have been some interesting methodological advances in recent years (for discussions see here and here). However, those surveys rarely provide enough information about respondents to determine which foreign laws apply to them. And even some outcomes of interest that might seem easier to measure sometimes prove challenging. For example, a common question in this area is whether anti-bribery laws have discouraged investment in countries perceived as corrupt. These studies are hampered by the limited availability of data on aggregate bilateral investment flows—the popular UNCTAD dataset only provides figures up to 2012. Meanwhile, country-specific firm-level data on foreign direct investment generally are only available for publicly traded firms, and the reported flows often are aggregated across multiple countries.
- Third, it is often challenging to figure out which subjects belong in the treatment group. Take the example of comparing firms that are subject to anti-bribery laws like the FCPA to otherwise similar firms that are not subject to those laws. The FCPA’s anti-bribery provisions clearly apply to any firm incorporated or headquartered in the U.S., and they also apply, with qualifications, to firms listed in the U.S. However, as many European firms have learned the hard way, the FCPA’s anti-bribery provisions also apply to firms that participate in bribery schemes that are partly conceived or implemented in U.S. territory or through the U.S. financial system. There is no straightforward way to identify firms affected in this way. Moreover, the mere fact that a particular firm is subject to the FCPA does not mean the statute applies to misconduct committed by that firm’s parent or subsidiary or affiliates.
- A variant on that problem arises when the main comparison is over time—that is, when the treatment and control groups are not different entities, but the same entities before and after the intervention. If the treatment is something like the adoption of a new law, the timing of the treatment isn’t so hard to determine. But what if the treatment is something like increased enforcement, which is presumably associated with perceptions of increases in either the probability or the magnitude of sanctions? For example, there was a well-documented increase in FCPA enforcement in the years after the OECD Convention came into force. Suppose we want to evaluate the effect of this increased enforcement, by doing a before-and-after comparison. When did the level of enforcement change, and when was that change perceived by firms? Was the relevant date 2005, when we saw an uptick in the number of settlements? Or a few years earlier, when the investigations that led to those settlements were initiated? Or earlier still, when other countries joined the OECD Convention and firms anticipated that this would make it easier for US enforcement agencies to secure cooperation in transnational investigations? Or perhaps as late as 2008, when corporate directors around the world read newspaper articles about the mega-settlement with Siemens?
Given these obstacles, what is to be done? The standard academic response is to advocate for the collection of better data. In meantime, for policymakers in the real world, the only possible response is to muddle along with what we’ve got—less than perfect evidence and theories that draw upon as broad a range of perspectives as possible combined with a commitment to reconsideration and revision in the face of new evidence or insights. The kind of evidence favored by proponents of evidence-based analysis is generally difficult to come by in connection with illicit transnational activity. Consequently, we must of necessity explore alternatives to evidence-based policymaking.