3.1.1. Identification assumptions

To understand the logic behind instrumental variables, let us consider our initial toy example about pills and headaches. However, let us now assume that researchers cannot randomise individuals to actually ingest the pill, but that they can only encourage subjects to do so (i.e. a ‘randomised encouragement design’; Holland, Reference Holland1988; Keele, Reference Keele2015). For instance, researchers might send a daily reminder to treated subjects to take the pill (cf. Hirano et al., Reference Hirano, Imbens, Rubin and Zhou2000). In this setting, it is ultimately each subject's decision whether or not to take the medical treatment, yet the encouragement they receive acts as a random push to take the pill. As such, the pill → headache relationship is confounded, but both the encouragement → pill and the encouragement → headache ones are not. Thus, if the researchers are ready to assume that the encouragement affects the outcome of the study (e.g. the felt headache of a person) only via the intake of the treatment (i.e. actually ingesting the pill), then the random encouragement can be seen as a prototypical instrumental variable, also called ‘instrument’.

This example lacks cultural or evolutionary subtlety, yet hints at the power of instrumental variable estimation for cultural evolutionary scholars. The intuition is as follows. While it is usually impossible to randomise culture directly, it might be feasible to find a (conditionally) random variable that causes culture. This variable – the instrument – can be thought of as the initiator of a causal chain that ‘de-confounds’ the effect of a cultural trait of interest (Angrist & Pischke, Reference Angrist and Pischke2009). To produce such a powerful result, instruments need to satisfy three assumptions (Angrist & Pischke, Reference Angrist and Pischke2014, see Figure 3 for an intuitive representation):

1. 1. Relevance. Relevance means that the instrument should be associated with the treatment (e.g. the cultural trait of interest).

2. 2. Independence. Independence is similar to unconfoundedness and requires the instrument (but not the treatment) to be at least as good as random.

3. 3. Exclusion. Exclusion means that the instrument should affect the outcome solely via the treatment (e.g. the cultural trait of interest) and not via any other unmeasured variable. Readers familiar with statistical mediation literature might intuitively think about exclusion as the assumption that requires the treatment to mediate fully (rather than partially) the instrument–outcome relationship (cf. Baron & Kenny, Reference Baron and Kenny1986).

Figure 3.

Instrumental variables (see Huntington-Klein, Reference Huntington-Klein2021).

Note: All panels display the relationship between a valid or invalid instrument Z_i, a cultural trait D_i, an outcome Y_i and two potentially omitted common causes, Q_i and C_i.

Of these three assumptions, only relevance can be directly tested by measuring the empirical association between instrument and treatment (for details, see, e.g. Andrews et al., Reference Andrews, Stock and Sun2019). Independence – like unconfoundedness – is untestable but can be assumed as valid when the instrument is randomised (Angrist & Pischke, Reference Angrist and Pischke2009). The exclusion assumption is also untestable, yet it is not assured to hold even in a randomised experiment, as the randomised instrument might affect the outcome through a channel different from the (endogenous) treatment.

Note that these assumptions are enough to characterise an instrumental variable in a scenario with homogeneous effects, a simplifying assumption describing a world where the effect of the cultural trait on the outcome of interest is identical for all units in the population. However, an additional assumption called ‘monotonicity’ (or ‘no-defiers’) is usually required when focusing on a more general heterogeneous effects scenario (for details, see Angrist et al., Reference Angrist, Imbens and Rubin1996, or Technical box 3). Monotonicity boils down to assuming that no unit does the contrary of what its instrument level would imply, also allowing us to clarify the interpretation of the instrumental variable parameter as a local average treatment effect, that is, the effect of the treatment among the units that respond to the instrument.

3.1.2. Estimation: Basic notions

The most intuitive way to think about instrumental variable estimation in the homogeneous effect case is via an estimation procedure called ‘two-stage least squares’ (Angrist & Pischke, Reference Angrist and Pischke2014). Two-stage least squares relies quite literally on the causal chain implied by an instrumental variable and estimates two different equations. The first stage usually takes this form:

(9)$$D_i = \alpha _1 + \gamma Z_i + u_i$$

and is estimated via an ordinary least squares estimator, wherein D_i is the cultural trait of interest explained by the instrument Z_i, by a constant term, α ₁, and by a disturbance, u_i. Intuitively, the value of D_i predicted by this regression equation can be thought of as the unconfounded variation in the cultural trait that is driven only by those units who responded to the instrument. The second stage requires regressing the outcome Y_i on the values of D_i predicted by Equation (9), thus obtaining an estimate of the effect of culture ‘purged’ of confounding if the identifying assumptions of instrumental variable estimation hold.

3.1.3. Where to find instruments and how to argue for their validity?

In the context of culture as cause, a valid instrument is a variable that is (as good as) randomly assigned, but that strongly predicts culture and causes the outcome of interest only through its effect on culture. This is a demanding and rather distinctive set of characteristics, making it difficult to even think about an instrumental variable in many applied scenarios. Indeed, as succinctly put by Cunningham (Reference Cunningham2021), ‘[g]ood instruments should feel weird’ (chapter 7.2.2). So, where to look for such surrogate random assignment to treatment when studying culture as a cause? Aside from relying on the physical random assignment typical of actual experiments, researchers might look for as-if random variation that emerges naturally in the field. We now discuss some examples related to culture that clarify this logic.

The effect of collectivism on economic development. In a series of studies, Gorodnichenko and Roland examine one of the most studied psychological differences across societies: collectivism vs. individualism (Gorodnichenko & Roland, Reference Gorodnichenko and Roland2011a, Reference Gorodnichenko and Roland2011b, Reference Gorodnichenko and Roland2017, Reference Gorodnichenko and Roland2021). This psychological continuum measures whether members of society attribute greater importance to individual goals and personal freedom (i.e. individualism) or group goals and conformity (i.e. collectivism, Hofstede, Reference Hofstede2001). At the country level, the collectivism–individualism continuum shows a remarkable correlation with economic development, but is this relationship causally interpretable or is it just driven by unobserved confounding?

Technical box 3:

Instrumental variable estimation

Following the notation of Angrist and Pischke (Reference Angrist and Pischke2009), consider an instrument, Z_i, that can take two values, z ∈ {0, 1}, and that affects a cultural trait, D_i, which can also take two values d ∈ {0, 1}. To formalise the logic of instrumental variable estimation, we need to augment the potential outcome notation. Specifically, we can think of the cultural trait as a potential outcome in terms of the instrument, D_i(Z_i). Similarly, we can think about the potential outcome for our outcome of interest as dependent both on the cultural trait and on the instrument, Y_i(D_i(Z_i), Z_i). Assuming that consistency and no-interference hold, we can define the instrument Z_i as a variable that satisfies (Angrist et al., Reference Angrist, Imbens and Rubin1996):

• • Independence: {Y_i(D_i(1), 1), Y_i(D_i(0), 0), D_i(1), D_i(0)} $\perp\!\!\!\perp$ Z_i.

• • Exclusion: Y_i(d, 0) = Y_i(d, 1) for d ∈ {0, 1}.

• • Relevance: E[D_i|Z_i = 1] − E[D_i|Z_i = 0] ≠ 0.

Under these assumptions, we can define an instrumental variable parameter as

(10)$$\displaystyle{{E[ Y_i\vert Z_i = 1] -E[ Y_i\vert Z_i = 0] } \over {E[ D_i\vert Z_i = 1] -E[ D_i\vert Z_i = 0] }}$$

which, if the treatment effect does not vary across units, is equivalent to the two-stage least square parameter described in the main text

(11)$$\displaystyle{{Cov( {Z_i, \;Y_i} ) } \over {Cov( Z_i, \;D_i) }}$$

Note, the numerator of Equation (10) (i.e. the effect of the instrument on the outcome, E[Y_i|Z_i = 1]−E[Y_i|Z_i = 0]) is often referred to as ‘reduced form’ or ‘intention to treat’, and it requires only the unconfoundedness of Z_i vis-à-vis the outcome Y_i to be interpreted causally.

If the treatment effect varies across units and an assumption known as monotonicity holds (i.e. no unit does the opposite of its instrument assignment: D_i(1) ≥ D_i(0), ∀i), then Equation (10) can be interpreted as

(12)$$E[ Y_i( 1 ) -Y_i( 0 ) \vert D_i( 1 ) > D_i( 0 ) ]$$

Equation (12) defines a local average treatment effect, that is, the effect of the cultural trait on the units that responded to the instrument Z_i. This is an important – although not necessarily positive – result, which implies that instrumental variable estimation (under the four assumptions) identifies an average treatment effect only on a specific subpopulation of units (Angrist et al., Reference Angrist, Imbens and Rubin1996).

To answer this question, Gorodnichenko and Roland (Reference Gorodnichenko and Roland2017) rely on instrumental variable estimation. Among the various instruments used by the authors, for the sake of brevity, here we focus only on two of them: historical pathogen prevalence (Murray & Schaller, Reference Murray and Schaller2010) and a genetic marker based on Cavalli-Sforza et al.'s (Reference Cavalli-Sforza, Menozzi and Piazza1994) data measuring the Mahalanobis distance between the frequency of blood types in a given country and the frequency of blood types in the UK (one the most individualistic country in their sample). The rationale behind the pathogen prevalence instrument echoes a functional view of culture (cf. Nettle et al., Reference Nettle, Gibson, Lawson and Sear2013), which suggests that collectivism might be a cultural adaptation to a pathogen-ridden ecology. Where pathogens abound, norms of out-group discrimination, limitations to individual behaviours and internalisation of group interests could favour individual-level survival chances. Different from the pathogen prevalence measure, the genetic instrument hinges on a purely cultural transmission argument. The intuition is as follows. Parents transmit their blood type to their children, but they also spread their culture, individualism included. As such, blood type and culture (or, at least, the vertically culturally transmitted portion of it) should correlate. That is, the argument is not that blood types cause culture, but rather that distance between the frequency of blood types across countries can serve as a proxy for differences in cultural traits across countries.

Overall, the results of Gorodnichenko and Roland (Reference Gorodnichenko and Roland2017) suggest that individualism causes economic development, as measured by the logarithm of income per worker. However, can we trust these results? Both instruments predict Hofstede's individualism–collectivism index well, so they both meet the relevance condition. Concerning the independence assumption, more circumspection is required, as neither instrument is directly assigned at random by the researcher. As-if randomness might be plausible for the genetic instrument, to the extent that it is hard to imagine a specific omitted common cause that could jointly cause blood type, individualism and economic development. Yet independence is perhaps less clearly met for pathogen prevalence, as unobserved geo-climatic variables might act as confounders (e.g. humidity, distance from the equator, temperature). It is, thus, reassuring that the instrumental variable results of Gorodnichenko and Roland (Reference Gorodnichenko and Roland2017) survive the inclusion of absolute latitude and longitude, thus providing some tentative evidence for (conditional) independence. Let us now consider exclusion. While a direct effect of the genetic-based instrument and of pathogens on current economic outcomes might be far-fetched, exclusion could also be violated if, for instance, either instrument causes economic development via some causal channels different from individualism–collectivism, like institutional quality or some alternative cultural traits (see, e.g. Acemoglu et al., Reference Acemoglu, Johnson and Robinson2001; Nash & Patel, Reference Nash and Patel2019). Again, the authors control for several suspicious covariates, thus providing some confidence that the main results are not explained away by alternative causal channels like the percentage of the population practising different religions or institutional quality.

Finally, and irrespective of the validity of the instruments, it should be noted that the results of Gorodnichenko and Roland (Reference Gorodnichenko and Roland2017) do not directly address issues related to the cultural relatedness of different countries (see Mace et al., Reference Mace, Pagel, Bowen, Gupta, Otterbein, Ridley and Voland1994). The issue is that different countries should perhaps not be considered and analysed as independent data points, given their common cultural origin (e.g. the UK and Australia). Phylogenetic methods are probably the only clear-cut solution to the issue, even though Gorodnichenko and Roland (Reference Gorodnichenko and Roland2017) conduct a series of robustness tests that also speak to this issue. Specifically, the authors show that their baseline results are confirmed also when restricting attention to countries with historically high shares of indigenous populations. This pattern suggests that the individualism–economic development relationship is not solely driven by European migration patterns that could have brought individualistic values to the US, Australia and other parts of the world. The instrumental variable estimation results also hold within continents, suggesting that the individualism–wealth relationship is not only driven by some macro geo-cultural area.

Geography, history and their interactions. Finding valid instruments is often more of an art than a science, requiring substantial subject-matter expertise and creativity. Indeed, a good instrument is often a variable ‘that you would never think to include in a model of the outcome variable, and in fact you may be surprised to find that it ever had anything to do with assigning treatment’ (Huntington-Klein, Reference Huntington-Klein2021, chapter 19). It is, thus, impossible to formulate some specific guidelines on where to find instruments, yet some ideas related to instrumental variables and culture (and cultural persistence, specifically) can be found in several articles that we briefly touch upon.

For instance, some authors have relied on instruments based on geo-climatic variables to study how traditional subsistence systems have led to the emergence of norms related to individualism and collectivism, as well as obedience, leadership, and gender roles (e.g. Alesina et al., Reference Alesina, Giuliano and Nunn2013; Buggle, Reference Buggle2020; Lonati, Reference Lonati2020; Talhelm et al., Reference Talhelm, Zhang, Oishi, Shimin, Duan, Lan and Kitayama2014). The intuition here is that specific environmental conditions predict whether entire societies develop a specific subsistence system. These systems, in turn, are linked to the emergence of specific cultural traits, which tend to be then transmitted over time (e.g. herding favouring autonomy and agriculture favouring interdependence; see Nisbett et al., Reference Nisbett, Peng, Choi and Norenzayan2001; Uskul et al., Reference Uskul, Kitayama and Nisbett2008). Other authors have used geographic instruments to study the persistent effect of traumatic historical events. For instance, Nunn and Wantchekon (Reference Nunn and Wantchekon2011) study the negative effects of the slave trade in Africa on current norms of trust by instrumenting the historical slave export data by distance from the coast of different locations in the continent (i.e. the more distant from the coast a location is, the lower the chance it experienced the slave trade; see also Pierce & Snyder, Reference Pierce and Snyder2017; Teso, Reference Teso2019).

Note that these examples cannot pinpoint a clear-cut cultural story thanks to instrumental variables alone, as the long-term effects of subsistence systems (as instrumented by geo-climatic conditions) or of the slave trade (as instrumented by distance from the coast) could also be sustained by non-cultural causes, like institutions, economic systems and demography. Yet instrumental variable estimation can provide some suggestive evidence related to culture and cultural transmission. In turn, we hope that these examples can offer some clever ideas on how researchers can find plausibly valid instruments.

3.1.4. More advanced considerations

Instrumental variable estimation allows the identification of the causal effect of culture even if the culture–outcome relationship of interest is confounded. This result is remarkable but comes at a hefty price: to relax the unconfoundedness assumption, researchers need to invoke three new assumptions, some of which are untestable and by no means weaker than unconfoundedness. This does not seem like a good bargain, so why would researchers ever want to use instruments?

First, we invite our readers to see instrumental variable estimation not as a substitute – but rather as a complement – to strategies based on unconfoundedness and positivity. As these two approaches rely on different assumptions, finding converging evidence for a causal effect of culture with both of them might indicate a particularly credible result. Second, while independence and exclusion are ultimately untestable, some statistical tests (Wooldridge, Reference Wooldridge2002, chapter 15), sensitivity analyses (Conley et al., Reference Conley, Hansen and Rossi2012) and ad-hoc falsification tests (see e.g. Nunn & Wantchekon, Reference Nunn and Wantchekon2011) can be used to bolster the credibility of an instrument. Third, even when the exclusion assumption is not satisfied, the effect of the instrument on the outcome can still have a causal meaning – the so-called ‘intention to treat’ effect. For instance, even if the instrument affects the outcome directly (Figure 3d), the intention to treat is unbiased, effectively representing the effect of being encouraged to take the treatment rather than the effect of treatment intake per se. Note, however, that the intention to treat still relies on the (conditional) independence of the instrument. That is, if the instrument is not as good as random (as in Figure 3c and f), the intention to treat will not be causally interpretable.

3.2.1. Identification assumptions

In general terms, regression discontinuity design leverages variation generated by a cutoff that sharply separates two groups, one treated and one untreated (see the pioneering work of Thistlethwaite & Campbell, Reference Thistlethwaite and Campbell1960). Regression discontinuity design applications usually rely on discontinuities in time (e.g. before vs. after an unexpected terroristic attack; see Bastardoz et al., Reference Bastardoz, Jacquart and Antonakis2022), thresholds set by law or public authorities (e.g. Medicare eligibility at age 65, see Card et al., Reference Card, Dobkin and Maestas2008), or vote shares necessary to obtain a majority (e.g. Flammer, Reference Flammer2015; Lee, Reference Lee2008). When studying culture as a cause, however, the appeal of the regression discontinuity design becomes clearest in spatial terms, wherein a specific geographical border might assign different units to different cultural groups while holding constant most other conditions, thus representing a natural experiment that approximates a physical randomisation of culture.

More formally, a spatial regression discontinuity design is a design where all units have a score (often labelled ‘running’ or ‘forcing’ variable) representing their distance from a border. This border is known ex-ante to separate two cultural groups, thus the process of assigning units to either group is completely known. If this score is above the cutoff, a unit is assigned to one cultural group. If the score is below the cutoff, the unit is assigned to another cultural group. Thus, the jump exhibited by the observed outcomes of the two groups exactly at the cutoff can be used to estimate the difference in the groups’ potential outcomes (Cattaneo et al., Reference Cattaneo, Idrobo and Titiunik2023; Imbens & Lemieux, Reference Imbens and Lemieux2008). Graphically, this local average treatment effect is represented by the local jump in the two solid curves of Figure 4.

Figure 4.

Regression discontinuity: a representation (see Cattaneo et al., Reference Cattaneo, Idrobo and Titiunik2023). Note: The solid curves represent observed outcomes; the dotted curves represent unobserved outcomes.

In a spatial regression discontinuity design, the key identification assumption is that cultural affiliation to a group (i.e. the treatment) is the only factor that varies discontinuously at the cutoff (see Technical box 4). This assumption is conceptually similar to unconfoundedness because it requires all units’ characteristics (both observed and unobserved) other than culture to be similar in the vicinity of the cutoff. This so-called ‘continuity assumption’ (Hahn et al., Reference Hahn, Todd and Van der Klaauw2001) can be visualised in Figure 4, wherein the same-coloured curves do not jump discontinuously at the cutoff. Another way to think about continuity is in the graph of Figure 5 (Huntington-Klein, Reference Huntington-Klein2021): regression discontinuity design does not assume that the score is as good as random, but rather that being on the left or the right side of the cultural border is (see also Cunningham, Reference Cunningham2021; Steiner et al., Reference Steiner, Kim, Hall and Su2017).

Figure 5.

Regression discontinuity: an alternative representation (see Huntington-Klein, Reference Huntington-Klein2021).

Continuity is not a weak assumption and is ultimately untestable. When studying culture as cause, continuity would intuitively be met if all units were effectively randomised to live on either side of the border. Yet individuals are probably able – and willing – to sort on their preferred side of the border (see e.g. Aepli et al., Reference Aepli, Kuhn and Schweri2021). Yet isn't this a major violation of spatial regression discontinuity design assumptions? Quite probably it is. However, the regression discontinuity intuition can be still useful, even without a formal spatial regression discontinuity design and without its formal properties (Keele & Titiunik, Reference Keele and Titiunik2016). Specifically, limiting the analysis to adjacent units might not allow completely clean causal estimates, but it will usually mitigate major confounding issues by design – a so-called ‘conditional local geographic ignorability’ design (e.g. Aepli et al., Reference Aepli, Kuhn and Schweri2021; Eugster et al., Reference Eugster, Lalive, Steinhauer and Zweimüller2017; Keele & Titiunik, Reference Keele and Titiunik2016). This strategy can be thought of as a form of design-based approach (Card, Reference Card2022; Keele, Reference Keele2015) that mixes the spatial regression discontinuity design intuition with the selection on observables one.

3.2.2. Estimation: Basic notions

Parametric estimation is the most intuitive way to understand the logic of spatial regression discontinuity design and related approaches. In a nutshell, regression discontinuity design requires either fitting two regression lines – one on the left and one on the right of the cutoff – or one regression line with an interaction term of the form

(13)$$Y_i = \alpha + \tau D_i + \beta _1Z_i + \beta _2D_iZ_i + e_i$$

where Y_i is the outcome of interest, Z_i is the distance from the border, D_i is an indicator of the cultural group membership and e_i is an unobserved disturbance (i.e. all unmodelled factors affecting Y_i). The main parameter of interest is τ (i.e. the effect of being in one or the other cultural group), while β ₁ measures if the distance from the border associates with the outcome on one side of the border, and the parameter β ₂ allows for a different effect of distance from the border on the other side of the border. Of course, more complex versions of this model are also possible (e.g. powers of Z_i, see, e.g. Angrist & Pischke, Reference Angrist and Pischke2014).

As the identifying assumption of spatial regression discontinuity design (as well as the logic of the conditional local geographic ignorability design) can be valid only in the vicinity of the threshold, this regression should only be run on observations that lie in the vicinity of the cultural border and not over the entire domain of the score. To show the robustness of their results, researchers usually run the regression in Equation (13) using various windows of data, test the robustness of their regression specification using polynomials for D_i (but see Gelman & Imbens, Reference Gelman and Imbens2019) and/or use a specific non-parametric technique that puts more weight on observations closer to the cutoff (i.e. kernel regression). Concerning statistical inference, calculations of standard errors in spatial regression discontinuity design are a rather delicate matter; we thus re-direct readers interested in this topic to Cattaneo and Titiunik (Reference Cattaneo and Titiunik2022) or Cattaneo et al. (Reference Cattaneo, Idrobo and Titiunik2020).

Technical box 4:

Regression discontinuity design

Let Z_i be the running variable. Units are assigned either to the cultural group D_i = 1 if Z_i ≥ c or to D_i = 0 otherwise, where c denotes the cutoff point/border. In this scenario, unconfoundedness holds trivially, because D_i is a deterministic function of the running variable Z_i. However, positivity never holds, because P [D_i = 1|Z_i = z] is either 0 or 1 (Imbens & Lemieux, Reference Imbens and Lemieux2008). Identification, thus, relies on a different assumption, known as continuity (Hahn et al., Reference Hahn, Todd and Van der Klaauw2001):

(14)$$E[ Y_i( 1 ) \vert Z_i = c\left]{\,{\rm and}\; E} \right[Y_i( 0 ) \vert Z_i = c] \,{\rm are\ continuous\ in}\; z\,{\rm at}\;c$$

Formally, the continuity assumption allows us to define the estimand of interest as,

(15)$$E[ Y_i( 1 ) -Y_i( 0 ) \vert Z_i = c]$$

which is identified by

(16)$$\mathop {{\rm lim}}\limits_{z\downarrow c} \, E[ Y_i\vert Z_i = z] -\mathop {{\rm lim}}\limits_{z\uparrow c} \, E[ Y_i\vert Z_i = z]$$

where ↓ (resp. ↑) means that z is approaching c from above (resp. from below). Equations (15) and (16) describe a local causal effect in that they focus on the difference between the potential outcomes precisely at the cutoff c. Thus, much like the parameter identified by instrumental variable estimation, regression discontinuity design identifies a local average treatment effect.

For completeness, note that a different school of thought suggests seeing regression discontinuity design as a local experiment, thus implying a more demanding assumption of as-if randomisation in a small window around the cutoff. We do not cover these differences in this paper, re-directing interested readers to De la Cuesta and Imai (Reference De la Cuesta and Imai2016) and Cattaneo and Titiunik (Reference Cattaneo and Titiunik2022).

Finally, note the difference between a standard regression discontinuity design and both its geographic (or spatial) version and the conditional local geographic ignorability design. In a geographic regression discontinuity design, the location of each unit i is determined by two coordinates (e.g. latitude and longitude), which define a set of cutoff points along a border. In a conditional local geographic ignorability design, the continuity assumption is not directly invoked, but the vicinity to the cutoff is used as a way to approximate (conditional) unconfnoundedness by design, in that it is more reasonable to assume the independence of the potential outcomes for units closer to the cutoff rather than for units distant from it.

3.2.3. Where to find cultural discontinuities?

Different cultural groups are often divided more or less sharply by administrative borders (e.g. country or state borders). Using these cutoffs for a spatial regression discontinuity design might seem tempting, but care is required. The problem is that groups separated by these borders are not only culturally different but also experience different laws, economic conditions, histories, etc. This leads to confusion: is this geographical contrast identifying the effect of culture, some institutional difference, or other differences? For this reason, we believe that the most convincing types of cultural discontinuities are often found within the same administrative unit. We discuss some such examples below.

The Röstigraben in Switzerland. A cultural cutoff that is sometimes discussed in the economics literature is the linguistic border in Switzerland (e.g. Cottier, Reference Cottier2018; Eugster et al., Reference Eugster, Lalive, Steinhauer and Zweimüller2011; Gentili et al., Reference Gentili, Masiero and Mazzonna2017). Switzerland is a small European country divided into several autonomous administrative regions, so-called ‘cantons’. Most cantons belong to one of the country's two main linguistic/cultural groups: Romance (i.e. French and Italian, living for instance in Lausanne or Lugano) or German (e.g. Zurich). Despite their small size and geographical proximity, these cantons sometimes exhibit strikingly different attitudes and values reflected in important aggregated outcomes, such as voting patterns and labour-market conditions. A natural question is whether culture causes these differences. However, directly comparing Romance- and German-speaking cantons is not a particularly convincing empirical strategy. The problem is that, while cantons share major infrastructures, several federal laws and generally prosperous economic conditions, they also vary importantly in geographic and demographic factors, gross domestic product per capita, local constitutions, policing and judiciary systems. So, how to identify the causal effect of culture in this case?

Luckily, a handful of cantons are divided down the middle by a centuries-old cultural border, the so-called Röstigraben. The Rösti is a potato-based dish typical of the German-speaking cantons, and a literal translation of der Röstigraben would be something like ‘the hash brown ditch’. This linguistic/cultural border represents a distinctive empirical opportunity. Living in the same administrative unit, individuals share similar ecological, demographic, economic and institutional environments, yet they are embedded in two different linguistic/cultural groups. Intuitively, the similarity between these culturally different individuals will be maximal around the Röstigraben.

Eugster et al. (Reference Eugster, Lalive, Steinhauer and Zweimüller2017) leverage exactly this intuition, pursuing a conditional local geographic ignorability design to study the cultural causes of unemployment duration in these two groups. After having lost a job, Romance speakers tend to stay unemployed for longer than German speakers, hinting at systematically different attitudes towards work. To isolate the role of these socially transmitted norms and beliefs, the authors compare job seekers only in the vicinity of the Röstigraben, restricting their attention to individuals living up to 50 km away (in terms of road distance) from the cultural border. Their results highlight a sizeable and robust effect of the linguistic border, consistent with an effect of culture net of environmental confounds.

Is this result causally interpretable? The Röstigraben contrast would be shaky if individuals living on either side of the cultural border were systematically different in some non-cultural factors. For instance, if German speakers were more educated than the Romance ones, they could more easily obtain jobs because of non-cultural factors. Similarly, if German speakers were to live in a richer economy, they might have more job offers owing, again, to non-cultural factors. Such scenarios are not implausible, as the descriptive evidence of Eugster et al. (Reference Eugster, Lalive, Steinhauer and Zweimüller2017) suggests that some individual and municipality characteristics are unbalanced in the two cultural groups, even when limiting the attention only to observations in the vicinity of the Röstigraben. To reduce such concerns, Eugster et al. (Reference Eugster, Lalive, Steinhauer and Zweimüller2017) include several covariates measuring potentially problematic individual characteristics (e.g. individual qualifications) and municipalities’ characteristics (e.g. demographic structure, median wage), as well as other potential confounds (e.g. year of interview, city of residence dummies). As a result, this study might not decisively conclude that cultural traits related to job attitudes are the only factor that drives the different behaviours of German- and Romance-speaking Swiss, but it can at least show that the explanatory power of alternative non-cultural explanations (e.g. economic conditions) seems too small to be the sole reason for the observed discontinuity between the two groups.

Finally, from a cultural transmission viewpoint, three points are noteworthy. First, the already mentioned issue of cultural non-independence (Mace et al., Reference Mace, Pagel, Bowen, Gupta, Otterbein, Ridley and Voland1994) is almost certainly present in this setting. However, we believe that it is unlikely to drive the results reported by Eugster et al. (Reference Eugster, Lalive, Steinhauer and Zweimüller2017). The non-independence argument suggests that Romance- and German-speaking Swiss should be culturally similar, as they probably share extensive cultural ancestry. Yet the fact that one finds a difference rather than a similarity between these groups suggests that culture plays a role here despite the cultural non-independence. Second, Eugster et al. (Reference Eugster, Lalive, Steinhauer and Zweimüller2017) cannot pinpoint the exact cultural trait responsible for the difference. Rather, by holding the environment constant, the article infers that differences in unemployment between the Romance and German groups must reflect a cultural trait related to attitudes to work. To this extent, spatial regression discontinuity design and similar approaches are especially appropriate if researchers aim at identifying a broad constellation of cultural traits responsible for a given effect, but might be insufficient if researchers are interested in a very specific cultural trait. Last, spatial regression discontinuity design and similar approaches usually do not allow differentiation between vertical and horizontal (or oblique) cultural transmission. As culture changes sharply at the border for all individuals embedded in a group, researchers cannot identify the effect of, say, coming from a German-speaking family (i.e. vertical transmission) net of the effect of living among German-speakers (i.e. horizontal and oblique transmission).

Discontinuities based on historical borders. Finding credible cultural discontinuities is no easy task and requires subject-matter expertise, as well as data availability. Aside from relying on within-country linguistic or ethnic borders similar to the Röstigraben (see Moscona et al., Reference Moscona, Nunn and Robinson2020), researchers might find it useful to look for borders that existed in the past, like historical administrative boundaries (Becker et al., Reference Becker, Boeckh, Hainz and Woessmann2016; Lowes et al., Reference Lowes, Nunn, Robinson and Weigel2017; Testa, Reference Testa2021). These historical borders separated areas that experienced different institutions, economic conditions and cultural traits in the past, but are now part of the same country or district and, thus, share a similar socio-economic environment. As such, finding evidence of behavioural differences in groups separated by historical administrative borders suggests that historical cultural differences might have persisted till this date.

3.2.4. More advanced considerations

Using geo-cultural cutoffs as an identification strategy is an intuitively compelling and conceptually straightforward way to make causal claims about culture. However, special care is needed when using geographical borders as discontinuities. These difficulties are potentially serious, so we briefly cover them here, re-directing our readers to Keele and Titiunik (Reference Keele and Titiunik2015, Reference Keele and Titiunik2016) and Keele et al. (Reference Keele, Titiunik and Zubizarreta2015) for more details.

The first issue relates to the very definition of ‘distance from a border’, which we discussed in our paper as an absolute scalar measure, but should be thought of as a multidimensional one (i.e. longitude and latitude) if one wants to strictly apply a spatial regression discontinuity design. The second issue relates to measurement error in the distance from border measure (i.e. it is often hard to locate precisely a unit) and to the possibility of observations clustering around the cutoff (i.e. most units might live in a specific location, like a city or a village). The third issue concerns the fact that geo-cultural borders are rarely – if ever – deterministic cutoffs. Rather, they can be often thought of as ‘nudges’ that increase the probability of an individual belonging to a given cultural group. If that is the case, the so-called ‘fuzzy regression discontinuity design’ can be more appropriate (i.e. a technique wherein the cutoff does not determine cultural affiliation directly, but increases the probability of belonging to a cultural group).

The last, and probably most important, difficulty revolves around the key assumption of spatial regression discontinuity design and related strategies, which requires units around the cultural border to be ‘virtual clones’, similar to a randomised experiment. This assumption is ultimately untestable and can be a heroic one to make. Subject-matter expertise is, thus, required to make this call. Still, there are several empirical ways to probe its plausibility. For instance, researchers can compare the distribution of observable covariates for units on either side of the border, hoping to see a balanced distribution around the cutoff (see e.g. Abadie & Cattaneo, Reference Abadie and Cattaneo2018). A similar falsification test revolves around showing in a plot if suspicious covariates jump around the threshold. If some jumps are detected, or if some imbalances are found in the vicinity of the border, this signals that the continuity assumption might be violated and that individuals might actively manipulate their exact location around the cutoff (cf. Imbens & Lemieux, Reference Imbens and Lemieux2008). Researchers can also test whether placebo cutoffs (which should assign units to no specific treatment) actually have no effect, thus bolstering the idea that treatment is determined only by the distance from the threshold chosen (for more details, see Cattaneo & Titiunik, Reference Cattaneo and Titiunik2022; Cattaneo et al., Reference Cattaneo, Idrobo and Titiunik2020).

3.3.1. Identification assumptions

The epidemiological approach intuition echoes a design sometimes used by epidemiologists (hence the name), who try to separate the genetic and environmental contributions of some medical conditions by contrasting immigrants to natives. When applied to culture, the logic is similar, although researchers focus on the cultural (rather than genetic) contribution net of the environment where individuals live. Thus, the notional experiment the epidemiological approach tries to approximate is one in which individuals from culturally diverse groups were to be moved randomly to a single common environment, so as to observe their behaviours in the same environment. If immigrants’ behaviours remain identical to the ones they exhibit in their native environment, then the culture is a plausible cause of behaviours. If, on the contrary, immigrants from different cultural groups behave identically in the new environment, then the environment is the plausible cause of behaviours.

Here lie both the strengths and the weaknesses of the epidemiological approach. Compared to a strategy based on purely observational data and statistical adjustment, the epidemiological approach can minimise environmental confounding by design. Yet violations of unconfoundedness do not only arise from environmental factors but can emerge because of other omitted common causes (e.g. characteristics of the individuals) or because of selection problems. Both issues stem from the fact that cultural evolutionary researchers clearly cannot run a ‘common garden’ or ‘transplant’ experiment with individuals (cf. Atran et al., Reference Atran, Medin, Ross, Lynch, Vapnarsky, Ek and Baran2002). Rather, they merely observe the behaviours of individuals who have decided, at least partly, whether they want to move out from their original environment and where they prefer to go. Given this inherently observational nature, any use of the epidemiological approach should be very well thought through and researchers should examine if and why they feel confounding is not a major issue in the context at hand.

3.3.2. Estimation: Basic notions

Estimation of epidemiological approach-type strategies follows essentially the same principles of any strategy based on unconfoundedness and positivity. Specifically, the epidemiological approach is usually estimated via a regression of the form:

(17)$$Y_{ior} = \alpha + \beta D_o + \delta X_i + \epsilon _{ior}$$

where Y_ior is an outcome of interest for an individual i having an environment of origin o and an environment of residence r (where o ≠ r), D_o is a cultural trait of interest present in the environment of origin, X_i are some covariates used to meet the unconfoundedness assumption and ɛ_ior is the disturbance (i.e. all unmodelled factors affecting Y_ior). β is the parameter measuring if culture affects individuals’ choices in the novel environment of residence.

3.3.3. Where to find different cultural groups in the same environment?

Immigrants and immigrants’ descendants. A popular way to implement the epidemiological approach is with immigrants’ data (for an intuitive graphical representation, see Figure 6). However, many researchers do not focus only on first generations (i.e. individuals who live in a given country or region, yet are born in a different one), but rather study second generations, that is, native-born children of immigrants. There are several reasons for this choice. For starters, second-generation immigrants are likely to have fewer direct connections with their country of origin compared to first generations, thus making the culture of origin–environment of residence separation more clear-cut. Moreover, it is often unrealistic to assume that first-generation immigrants are as-if randomised to a destination country. Rather, it seems plausible that these immigrants might actively choose their country of residence based on geographical or cultural proximity with their country of origin, economic development in the country of destination, and other factors (Fernández, Reference Fernández2011). Such concerns are less obviously relevant for second generations, who do not directly decide where to live or whether or not to carry the culture of origin of their parents.

Figure 6.

Epidemiological approach using immigrants’ data: a representation (see Luttmer & Singhal, Reference Luttmer and Singhal2011). Note: Each circle represents the average observations of immigrants coming from a given country. The dimensions of circles represent a different number of migrants observed.

Immigrants data in an epidemiological approach-type framework have been used in economics to study predictors and outcomes as diverse as family ties (Alesina & Giuliano, Reference Alesina and Giuliano2010), preference for redistribution (Luttmer & Singhal, Reference Luttmer and Singhal2011), kinship structures (Enke, Reference Enke2019), traditionalism (Giuliano & Nunn, Reference Giuliano and Nunn2021), attitudes related to gender roles (Alesina et al., Reference Alesina, Giuliano and Nunn2013) and group conformity (Buggle, Reference Buggle2020). Cultural evolutionary scholars have also sometimes employed variants of the epidemiological approach to study psychological processes (Mesoudi et al., Reference Mesoudi, Magid and Hussain2016) and attitudes towards female genital cutting (Vogt et al., Reference Vogt, Efferson and Fehr2017). In a particularly impactful piece that we now discuss more in detail, Fernández and Fogli (Reference Fernández and Fogli2009) use census data to study whether the fertility rate and worked hours of 30–40 US-born married women having foreign-born parents are explained by the fertility rate and female labour force participation in their parents’ countries of origin. The authors find robust relationships between these variables, suggesting that culture causes these patterns.

Three potential issues could in principle hamper the causal interpretability of Fernández and Fogli's (Reference Fernández and Fogli2009) results. First, immigrants from different cultural groups might be systematically different for reasons other than culture (e.g. demographic characteristics, education levels). To deal with this concern, Fernández and Fogli include several individual-level covariates that might represent potential common causes, like women's education level, parental education and age. Note that these covariates might also be ‘bad controls’, to the extent that they might be caused by the culture of origin (cf. Cinelli et al., Reference Cinelli, Forney and Pearl2022). Thus, including them might be akin to adjusting for a mediator (something we should usually avoid doing, see e.g. Major-Smith, Reference Major-Smith2023). At worst, adjusting for these covariates might even lead to collider bias owing to conditioning on common effects. It is thus reassuring to see that Fernández and Fogli's (Reference Fernández and Fogli2009) results emerge both when adjusting or not adjusting for these variables.

Second, the environments where immigrants currently live might still be not so comparable. For instance, even if two immigrants live in the same country of residence, they might still be exposed to completely different contexts (e.g. large city vs. rural area). To address this potential concern, Fernández and Fogli (Reference Fernández and Fogli2009) adjust in a regression framework for metropolitan standard areas’ fixed effects where the sampled women live, effectively comparing women in the same area. Relatedly, immigrants might re-create some of the institutional conditions typical of their home country in their new country of residence. This might be especially the case if migrants’ location choices are predicted by previous settlement patterns, causing immigrants to reside in geographical clusters (e.g. Little Italy, Chinatown). Indeed, Fernández and Fogli (Reference Fernández and Fogli2009) find that the effect of fertility in the father's country of origin is stronger if a woman comes from a cultural group that tends to cluster in a given area, suggesting that either a horizontal cultural transmission or an institutional pressure is at play. Note, however, that ethnic density is not solely responsible for the results.

Last, immigrants might be a non-random sample of the inhabitants of their country of origin (Borjas et al., Reference Borjas, Bronars and Trejo1992). For instance, immigrants might be more or less skilled, rich or educated than their non-migrated compatriots. This issue certainly hampers the generalisability of the findings, in that Fernández and Fogli (Reference Fernández and Fogli2009) are not studying the effect of culture in the general population, but rather in a specific sub-group composed only of immigrants. Yet this issue might also threaten causal identification if the studied cultural trait affects the decision to migrate (and, thus, the probability of being observed by the researchers), leading to potential issues related to conditioning on a common effect.

From a cultural evolutionary viewpoint, two additional points are worth mentioning. First, an epidemiological approach strategy like the one used by Fernández and Fogli (Reference Fernández and Fogli2009) is bound to find evidence that culture does not matter. As the cultural trait of interest is assumed to be transmitted only from parents (i.e. vertical cultural transmission), finding no effect of culture of origin does not mean that culture does not matter, but rather that vertically transmitted culture does not play a major role. Conversely, finding evidence that culture of origin matters does not mean that horizontal and oblique transmission channels are not at play. Second, using an epidemiological approach strategy based on immigrants coming from different countries of origin/residence implicitly assumes that different countries are separate units of analysis. This might lead to some conceptual issues (i.e. country and culture are not synonyms), as well as to the already-mentioned issues related to common cultural ancestry (Mace et al., Reference Mace, Pagel, Bowen, Gupta, Otterbein, Ridley and Voland1994). Note, however, that the epidemiological approach offers some ways to circumvent this issue, by explicitly considering the geographical, historical and cultural distance between a migrant's country of origin and the country of destination.

Epidemiological approach beyond immigrants’ data. Employing immigrant data is a particularly intuitive way to apply the epidemiological approach. Yet it is not the only one. Some applications are particularly creative. For instance, Fisman and Miguel (Reference Fisman and Miguel2007) study whether culture causes corruption by examining variations in United Nations diplomats’ parking violations. The identification strategy is as follows. United Nations diplomats belong to different cultural groups, yet they all work in the same environment (i.e. Manhattan) and, crucially, benefit from diplomatic immunity. This means that any difference in their misbehaviour – which the authors clearly document – cannot be due to environmental differences or fear of punishment (i.e. institutions, cf. Powers et al., Reference Powers, Van Schaik and Lehmann2016), but could be caused by culture.

A more recent application of an epidemiological approach-type strategy is Frake and Harmon (Reference Frake and Harmon2023). In their paper, the authors study the emergence and further transmission of a culture of misconduct at the Chicago Police Department. Specifically, the paper studies whether young police recruits – who must undergo a long and intense academy training – engage in more misconducts (e.g. illegal searches, falsification of evidence) if they are exposed during their training to misconduct-prone peers and if, once promoted to managers, they transmit their misconduct culture to their subordinates. To eliminate several issues related to selection and omitted common causes, the authors leverage the fact that young recruits are randomly assigned (i.e. a lottery) to a training cohort and, thus, to a culture of misconduct to begin with. Their results highlight both a horizontal transmission of misconduct and an inter-generational one.

3.3.4. More advanced considerations

The design features of the epidemiological approach make it a relatively credible identification strategy in the context of studying culture as cause. However, it is important to reiterate that the epidemiological approach still faces all the potential limitations typical of strategies relying on unconfoundedness and positivity. Solving these issues by mixing the epidemiological approach logic with quasi-experiments is in principle possible (e.g. exogenous shocks in migrants’ locations owing to country of origin or country of destination factors), but such exogenous sources of variation are certainly hard to find (cf. Frake & Harmon, Reference Frake and Harmon2023). We, thus, invite cultural evolutionary scholars to use the epidemiological approach while minding its potential weaknesses.