Qunatative Cross National Research Methods (Esping Andersen G. - Przeworsky a., 2000)

7/30/2019 Qunatative Cross National Research Methods (Esping Andersen G. - Przeworsky a., 2000)

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Section 2.3 no. 64

QUANTITATIVE CROSS-NATIONAL RESEARCH METHODS

Gosta Esping-Andersen

CPISUniversitat Pompeu Fabra

and

Adam Przeworski

Department of Political Science

New York University

Trade-offs in Quantitative Comparisons

Quantitative nation comparisons pose inevitable trade-offs. One is that much of the

contextual reality of individual nations is sacrificed for the sake of broader

generalization. We fail to capture the uniqueness that defines a nations culture,

historical heritage, and endemic logic. The interpretation of a variable may, indeed, only

be possible when its is studied contextually (Ragin, 1987; and Lieberson, 1991).

Boolean analysis, as Ragin argues, helps overcome this dilemma. It has advantages,

such as its ability to build conjunctural models with very few cases, and its ability to

analyze non-events. But it needs to be guided by strong theory and substantial

knowledge, its applicability is limited to relatively few cases, and it may be too biased

in favor of non-additive, conjunctural models. For an empirical application, see Ragin(1994). See also Section 2.3, no. 72.

A second trade-off has to do with the often limited number of observations available,

especially in studies of advanced (OECD) democracies where the N rarely exceeds 25.

In broader World comparisons, however, the N approaches 200. Many attempt to

supplement few nations with over-time data, as in the case of pooled cross sectional

and time series analyses. As ever longer data series for individual countries become

available, the small N problem will gradually diminish. A 20 year time series for 20

countries yields 400 observations; a 20 year time series for 200 nations yields 4000.

The most serious small N problem, then, occurs where for theoretical or other reasons,the natural universe is limited. Small samples do not necessarily pose problems of

statistical inference. Strong theory may not require many observations. They do,

however, limit what statistical tools can be brought to bear. Fearon (1991 ) argues that

the smaller the N, the greater the need to make counterfactuals explicit in other words,

to tighten the theoretical formulation about the precise conditions that will (or will not)

produce an outcome. Vague theory implies uncertainty about the number of contending

explanations (which can grow very large) and about their mutual relationship within a

causal order. The consequence is possible multi-collinearity and, more generally, large

error terms all of which can only be managed by having more observations. Hence, it

is likely that estimations will yield non-robust results. The less ambiguous the theory,

the less the need for large Ns. Small Ns are therefore an especially acute problem in

disciplines without a firm theoretical architecture, like Sociology or Political Science.


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Western (1998a) and Western and Jackman (1994) argue that Bayesian estimation, by

allowing for greater uncertainty, produces more robust results when Ns are few, theory

vague, and explanations are many. For a critique, see Firebaugh (1995); for an

empirical application, contrasting conventional regression with Bayesian estimation, see

Western (1996).

Small Ns can even hold advantages, because a limited nation-sample implies that the

researcher can far more easily gain maximum advantage from diagnostic scrutiny of the

residual plots. A set of systematic outliers, for example, can be easily identified in terms

of their nationhood, and any good comparativist should be able to pin down what

variable(s) drives their deviance from the fitted regression line. Diagnostics on small

samples can approach the advantages of in-depth case studies.

There are, nonetheless, problems inherent in quantitative national comparisons that are

both more generic and potentially more serious than the small N problem. The

remainder of our presentation will focus on qualitative and limited dependent variables,

on selection bias, on lack of independence between observations, and on the problem of

endogeneity of variables.

Qualitative and Limited Dependent Variables

Many dependent variables in cross-national research are either qualitative (assuming

discrete values) or limited (they assume continues values within some range). The

choice whether to measure a variable in a qualitative or continuous way is often

controversial. Bollen and Jackman (1989: 612), for example, argue that difficulties in

classiying some political regimes speak in favor of using continuous scales becauseDichotomizing democracy blurs distinctions between borderline cases. In contrast,

Przeworski et.al. (in press) prefer to treat regimes dichotomously or mulitnomially.

Yet, whether the dependent variable is qualitative or limited, the consequences are the

same, namely, the need to use non-linear models. Whether we give political regimes the

values of 0-1 (as do Przeworski et.al, op.cit) or 1-100 (as does Bollen, 1980), it remains

that the value on the dependent variable cannot exceed its maximum when the

independent variable(s) tend to infinity, and it cannot fall below its minimum when

these variables tend to infinity. Linear models, at best, can provide an approximation

within some range of the independent variables.

The standard model when the dependent variable is multinomial is

Pr (Y=j X=x) = F(x),

where j= 0,1,,J-1 and F is the cummulative distribution function. Since such models

are treated by any standard textbook (such as Greene, 1997), we need not present them

here. Such models can be applied to panel data unless the number of repeated

observations is large.


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Event history analysis is one particular class of non-linear models applied in cross-

national research. 1 In such models the dependent variable is an event, such as a

revolution, regime transition, or a policy adoption. The general model is

Pr [Y(t+dt)=j] = f[y(t), x(t) ], dt 0

Most often, such models can be conveniently estimated as

log S (t) = log [1-F(t)],

where S (t) is the survival function, or the probability that an event lasts beyond time t,

and F (t) is the cdf. 2 See Section 2.3, no. 53.

For dichotomous dependent variables, logit and probit give very similar results. For

multinomial variables, it is often assumed that the errors are independent across the

values of the dependent variable, which leads to a logit specification. But this implies a

strong assumption, namely the irrelevance of independent alternatives, that rarely holds

in practice (Schmertmann, 1994). Multinomial probit, in turn, requires computing

multiple integrals, which was until recently computationally expensive. Alternatives

would be semi- and non-parametric methods.

The distributions which are commonly used in estimating survival models include the

exponential, Weibul, logistic, and Poisson distributions. The difficulty here is that it is

very difficult to statistically distinguish between such distributions (with the exception

of the Weibull and exponential). The Poisson distribution should be favored when the

events are rare.

Methods for studying qualitative dependent variables are now standard textbook fare,

but what warrants emphasis is that the traditional distinction between qualitative and

quantitative research is becoming increasingly obsolete. Phenomena such as social

revolutions may be rare, but this just means they occur with a low probability. They

can, nevertheless, be studied systematically using maximum likelihood methods.

The Problem of Selection Bias

In comparative research we are often interested in the effect of some systemic feature,

institution, or policy on some outcome. Examples include the effect of labor marketinstitutions on unemployment, the effect of political regimes on economic growth, or

the effect of electoral rules on the number of political parties.

In such cases, the question is how some feature of X affects some outcomes Y in the

presence of conditions Z, or PR (Y | X,Z), where the hypothesis is that y = f(x). Thegeneric problem is how to isolate the effects of X and Z on Y.

If sampling is exogenous (i.e. the probability of observing any y is independent of z),

the pr (Y=y |z) = pr (y), and standard statistical methods can be used. But if pr (Y= y |z)

1 For an example, see Usui (1994)2 Again, we refer to standard textbooks for details.


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is different under different conditions Z, sampling is endogenous and the assumptions of

the standard statistical model are violated. For a detailed treament, see Section 2.3, no.

87.

To exemplify the problem: suppose we want to know the impact of political regimes on

economic growth. We observe Chile in 1985 (Z), which was a dictatorship (X), inwhich case per capita income declined at the rate of Y= -2.26. To assess the effect of

political regimes, we need to know what would have been the rate of growth (Y) in

Chile had it been a democracy. This cannot be answered with the available observations

because Chile in 1985 was indeed a dictatorship. The comparativist in such a case

would proceed quasi-experimentally, and look for a case that matches Chile in all

aspects except authoritarianism. In this way one would compare an authoritarian with a

democratic Chile.

But what if Chiles status as a dictatorship in 1985 was due to some factors that also

affected its economic performance? This could be because growth itself influences the

survival of regimes; a countrys level of development may be associated both with

regime selection and growth; some unobservable factors (say enlightened leadership

or, perhaps, measurement error) may be common to both variables. Whatever the

underlying selection mechanism, the basic consequence is that there will be cases

without a match, and this implies that our inferences will be biased.

The problem raised by non-random selection is how to make inferences from what we

observe to what we do not. It is a problem of identification (Manski, 1995). For what do

we know when we observe Chile as a dictatorship in 1985? We observe the fact that,

given conditions Z, the Chilean regime (X) is a dictatorship. We also know its rate of

economic growth, given that it is a dictatorship under conditions Z. We do not observe,however, its rate of growth as a democracy under conditions Z. The issue is one of

counterfactual observations: the rate of growth that an observation with Z = zi ,

observed under dictatorship, would have had under democracy. We do not know what

this value is and, hence, we face under-identification.

What we need to know are two distributions, P(Y=y | x=j, Z) and P(Y=y | x=k, Z), andtheir expected values, where we now think of the possible values of X more generally as

j,k = 0,1,2,,N. The first is the distribution of Y in the entire population if all cases

were observed as dictatorships; the second is the distribution of Y in the entire

population if all cases were observed as democracies. Clearly, if we want to know the

impact on y of being in states x, we need to determine the difference between these twodistributions, conditional on z.

It may seem strange to refer to the population as including unobserved cases. But in

order to compare the effects of states x on the performance of an individual case

characterizedby a zi , we must allow the case to be potentially observable under the full

range of X. 3 We observed this case as X = j, but must also imagine the possibility that

it would have been X j. We must think in terms of a super-population consisting ofa continuum of potential cases. The actual sample is then regarded as having been

drawn by nature from this super-population (Pudney, 1989: 45).

3 Note that in our example X assumes only two values. But, generically, this is not necessary.


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If the actual population is an exogenous sample of the potential one, any multivariate

combination (xi, zi) can be drawn with a positive probability. Such exogenous sampling

allows us to isolate the effect of x on y given z, that is, to control for z the effects of x

on y. If the sample is exogenous, we can match pairs (x i = j, zi) and (xi = k, zi). But if

sampling is endogenous, there will be some cases without a match: some of the x i s

will not have support. Where we have non-random selection, quasi-experimentalcomparisons fail regardless of the number of observations.

The methods to correct for selection bias consist of constructing counterfactuals, that is,

of filling the unobserved supports of the distribution Y for all X. Following Heckman

(1979), when sampling is not random, the regressions y = f(x,z) suffer from omitted

variable bias. When such regressions are estimated on the basis of the observed sample,

the variable that is omitted is the expected value of the error in the equation that

specifies how the observations are selected into the sample:

Pr (x=j) = F(Z) + u.

If E (uj | x=j) 0, then

E (uj| x) = juE (u | x),

where ju is a regression coefficient of uj on u.

Finally, E (u | x=j) = j, where the j s are the inverse Mill ratios, or the hazard rates.

Since we know that Yj is observed when x=j, we can write the expected values in the

observed sample as

E (yj | x=j, z) = zj + juj .

Note that if this equation is estimated on the basis of the observed sample, the variable

j is omitted from the specification.

We can now see why controlling for the variables that enter both into selection and

outcome equations may indeed worsen the selection bias (Achen, 1986). Following

Heckman (1988), we distinguish first between selection on observables and on

unobservables. Selection on observables occurs when the expected covariance E (uju

|

z) 0, but once the observed variables Z are controlled for it vanishes, so that E (uju |z) = 0. Selection is on unobservables when E (uju) 0 and E (uju | z) 0, which meansthat controlling for the factors observed by the investigator does not remove the

covariance between the errors in the outcome and the selection equations. Now note

that the regression coefficient ju = cov (uju)/var (uj). If selection is on unobservables,controlling for some variable x in the outcome equation may reduce the error variance uj

without equally reducing the covariance uju. Hence, the coefficient on the omitted

variable will be larger and the bias will be exacerbated.

In short, the expected values of the observed cases will be biased because they covary

with the variable which determines which cases are observed. If selection is exclusively


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on observables, this bias can be corrected by traditional controlling techniques. But if it

is on unobservables, such controls only worsen the bias.

Correcting for selection bias is not uncontroversial. It has been found that corrections

for selection are not robust, but are highly sensitive to relatively minor changes in

assumptions about distributions (Goldberger, 1983). Others have found that someestimation methods fail to correct for this bias and may even exacerbate it (Stolzenberg

and Relles, 1990). As Heckman (1988: 7) argues, the quandary we face is that different

methods of correcting for selection bias are robust if there is nobias to begin with; if

there is, there is no guarantee that the methods are robust.

The logic of the problem is similar whether we study large or small Ns (Fearon, 1991).

When de Toqueville concluded that revolutions do not bring about social change, the

reason might be that they occur only in countries where it is difficult to change society.

Even when N=1, the issue of selection bias does not disappear: The French revolution

in 1789 may have been caused by the same conditions that made social change so

difficult. It is possible that a revolution in a country where social relations are easier to

change would have provoked change. But then a revolution would not have been

necessary.

Comparativists who conduct case studies cannot benefit from statistical distributions to

generate the counterfactuals. Yet, as in all cases of comparison the problem remains and

it should, therefore, be standard practice to ask counterfactual questions of ones case or

cases.

The Problem of Independence

Statistical inference must assume that the observations on a variable are independent

one of the other. Is country A s performance truly independent of what happens in

country B? Is what happens at t+1 independent of events in t? Usually not, and this

implies the need for corrective procedures. In most cases, however, rigorous correction

will entail that the de facto N (nations or years) diminishes; in some instances,

statistical dependency cannot be resolved at all.

Cross-sectional analysis almost invariably assumes that nations and their properties (say

budgets or institutions) are independent one of the other. This should not be assumed.

We know that the Scandinavian countries have a similar and shared history, deliberatelylearning from each other through centuries, thus creating similar institutions and path

dependencies. The same goes for Austria and Germany, for Belgium and the

Netherlands and, arguably, for all the Anglosaxon nations. The issue is captured in

Castles (1993) families of nations. World samples have a similar problem: Japans

long hegemony in East Asia will have influenced Korean society; Confucianism has had

a pervasive influence throughout the region. Similar stories are easily told for Latin

America and Africa. If the World is a set of nation clusters, the real N is not 20-odd

OECD countries or 150-odd World nations.

When nations form families, but are treated as if they were all unique and independent,

we are likely to get biased coefficients and, very probably, unequal error variance

(heteroskadisticity). Sweden alone will drive the regression line in just about any


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welfare state analysis, and when also Denmark and Norway are treated as discrete

observations, the bias is multiplied in so far as all three in reality form part of the same

political economy (Scandinavia). Diffusion effects that operate between members of a

nation-cluster can also result in heteroskadistic disturbance in the cross-section. Such

can be corrected by, for example, adding a variable that captures the common

underlying property that drives the disturbance (say, a dummy for being Scandinavia)but, again, this correction absorbs precious degrees of freedom in a small N study and,

substantively, amounts to reducing the three nations to one observation. One attempt to

estimate comparative models in which it is presumed that nations cluster can be found

in Esping-Andersen (1999).

Lack of independence in a time-series is normally taken for granted, since this years

budget or election outcome is almost inevitably related to last years budget or the

previous election. The standard assumption is a first-order (AR1) serial correlation. In

comparative research virtually all time-series applications are pooled with cross-

sections. But, where Ns are very small, one may as well simply compare across

individual time-series estimations, as do Abraham and Hausman (1994), or Esping-

Andersen and Sonnberger (1991). Time-series are meant to capture historical process.

Yet as Isaac and Griffin (1989) argue, they easily end up being a-historical.

Pooling cross-sectional with time series data (panel regressions) has become very

widespread, especially in studies of the limited group of advanced (OECD) societies. In

many cases, the panel design is chiefly cross-sectional (more nations than years), as

exemplified by Alvarez et.al. (1991), and Iversen and Wren (1998); others are

temporally dominated (as in the case of Hicks, 1994a; or Hicks and Swank, 1992; for a

discussion, see Stimson, 1985). Panel models are especially problematic because they

can contain simultaneous diachronic and spatial interdependence and, worse, the twomay interact. The standard method for correcting contemporaneous error correlation

(GLS) applies only where the ts well exceed nations (which is rare). The consequence

is that t-statistics are overestimated, errors underestimated, and the results may therefore

not be robust (Hicks, 1994b; Beck and Katz ,1995) . The Beck and Katz (1995)

procedure, can correct for temporal and cross-sectional dependency one at a time, but if

the two interact, no solution exists. See also Beck et.al (1998) for an application to

maximum likelihood estimation.

Panel models can be based on two types of theoretical justification. One is that events

or shocks occur over time that affect the cross-sectional variance. There is, for

example, a huge recent literature on the impact of labor market rigidities onunemployment: regulations vary across nations but also across time because of de-

regulatory legislation (see for example Nickell, 1997). De-regulation in a country

should produce a break in its time series, and the auto-correlation element will be split

into the years preceding and following the break. The second justification, not often

exploited, is to interpret autocorrelation as an expression of institutional or policy path

dependency. In this instant, the rho must be treated as a variable. The problem, of

course, is that the rho is likely to combine theoretically relevant information as well as

unknown residual autocorrelation. The researcher can accordingly not avoid including a

variable that explicitly measures path dependency.

If we insist on faithful adherance to the real World, panel regressions will require so

much correction against dependency that the hard-won additional degrees of freedom


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that come with a time-series are easily eaten up. And how many can truthfully claim

that time and country dependencies do not interact? Indeed, most sensible

comparativists would assume they do: if nations form part of families it should also be

the case that the timing of their shocks, events, or policies is interdependent. Such

intractable problems are certainly much more severe in small-N comparisons, and this is

reflected in the prevailing lack of robustness that is endemic in the OECD arealiterature. In Beck and Katz (1995) re-estimations of the Hicks and Swank (1992)

study, to give an example, several key variables turned out insignificant. A marginal

difference in measurement, the inclusion or exclusion of one country, the addition or

subtraction of a year here or there, or the substitution of one variable for another, can

change the entire model.

One alternative is to construct multi-level models which explicitly take into account the

possibility that nations may cluster (for an overview, see Goldstein, 1987).

Nieuwbeerta and Ultee (1999) have, for example, estimated a three level (nation, time,

and individual) model of the impact of class on party choice within the context of

nations social mobility structure. A second alternative, in particular when the

dependent variable is categorical, is to exploit the advantages of event history analysis.

But, here the time series needs to be quite long considering that theoretically interesting

events, such as revolutions, democratization, or even welfare reforms, are far between.

In the event history context, analytical priority is usually given to temporal change,

which brings it much closer to traditional time series analysis. But rather than having to

manipulate autocorrelation, time sequencing (states and events) is actively modelled

and thus gains analytic status. For an application to nation comparisons, see Strang

(1994), Usui (1994) and, especially Western (1998b), which also can stand as an

exemplar of how to minimize the interdependency problem. See also Section 2.3, no.

53.

There are two particular cases where the lack of independence among observations

simply prohibits adequate estimation. The first, noted above, occurs when time and

nation dependencies interact. The second is when globalization penetrates all nations

and when many nations (such as the European Union) become subsumed under

identical constraints. In this instance, existing cross-national correlations will strenthen

and we may, indeed be moving towards an N=1. Of course, global shocks or European

Union membership do not necessarily produce similar effects on the dependent variable

across nations or time. If nations institutional filters differ, so will most likely the

impact of a global shock on, say, national unemployment rates. Here we would specify

interaction effects, but that would be impossible in a pure cross-section, and extremelydifficult in a time series, unless we already know how the lag structure will differ

according to institutional variation.

4. The Endogeneity Problem

All probabilistic statistics require conditional independence, namely that the values of

the predictor variables are assigned independently of the dependent variable. The basic

problem of endogeneity occurs when the explanans (X) may be influenced by the

explanandum (Y) or both may be jointly influenced by an unmeasured third. The

endogeneity problem is one aspect of the broader question of selection bias discussed


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earlier. General overviews of the endogeneity problem can be found in Manski (1995)

and King, Keohane and Verba (1994). See also Section 2.3., no. 88.

The endogeneity issue has been intensely debated within the economic growth literature

in terms of the causal relationship between technology and growth. But it applies

equally to many fields. For example, comparativists often argue that left power explainswelfare state development. But are we certain that left power, itself, is not a function of

strong welfare states? Or, equally likely, are both large welfare states andleft power

just two faces of the same coin, different manifestations of one underlying, yet un-

defined, phenomenon? Would Sweden have had the same welfare state even without its

legendary social democratic tradition? Perhaps, if Swedens cultural past

overdetermines its unique kind of social democracy and social policy. If this kind of

endogeneity exists, the true X for Sweden is not left power but a full list of all that is

Sweden. The vector of the Xs becomes a list of all that is nationally unique.

The endogeneity problem becomes easily intractable in quantitative cross-national

research because we observe variables ( Ys andXs) that represent part of the reality of

the nations we sample. Our variables are in effect a partial reflection of the society

under study, and the meaning of a variable score for one nation may not be metrically

equivalent to that of another a weighted left cabinet score of 35 for Denmark and 40

for Sweden probably misrepresents the Danish-Swedish difference if, that is, the two

social democracies are two different beasts.

A related, and equally problematic, issue arises in the interpretation of coefficient

estimations. In the simple cross-sectional regression, the coeffient for left power,

economic development or for coordinated bargaining can only be interpreted in one

way: as a constant, across-the-board effect irrespective of national context. If Denmarkhad 5 points more left power, its welfare state should match the Swedish (all else held

constant). In fixed-effects panel regressions, the Xs are assumed to have an identical

impact on Y, irrespective of country. Can we really accept such assumptions? Probably

not.

The reason that we cannot is that it is difficult to assume that variables, say a bargaining

institution or party power balance, will produce homogenous, monotonically identical,

effects across nations for the simple reason that they are embedded in a more complex

reality (called nation) which has also given rise to its version of the dependent variable.

In this case, the bias remains equally problematic whether we study few or many Ns; it

will not disappear if we add more nations.

Quantitative national comparisons rarely, if ever, address such endogeneity problems.

Studies of labor market or economic performance routinely presume that labor market

regulations or bargaining centralization are truly exogenous variables, whose effects on

employment is conditionally identical whether it is Germany, Norway or the United

States (well-known examples are Calmfors and Driffill, 1988; Hicks and Kenworthy,

1999). The same goes for welfare state comparisons with their belief that demography

and left power are fully exogenous and conditionally unitary (for example, Wilensky,

1975; Pampel and Williamson, 1989).

There exist several, not necessarily efficient, ways of correcting for the endogeneity

bias. If we have some incling that the bias comes from variable ommission, the obvious


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correction entails the inclusion of additional controls. An example of this kind was

Jackmans (1986) argument that Norways North Sea Oil was over-determining the

results in the Lange and Garrett (1985) study. Small N studies with strong endogeneity

have little capacity to extend the number of potentially neccessary controls. A second

approach is to limit endogeneity in X by re-conceptualizing and, most likely, narrowing

Y. The welfare state literature provides a proto-typical example: aggregate socialexpenditure was increasingly replaced by measures of specific welfare state traits.

Controls, no matter how many, will however not resolve the problem under conditions

of strong sampling bias. As discussed above, the best solution in such a situation is to

concentrate more on the theoretical elaboration of causal relations between variables. If

we can assume that our estimations are biased because Y affects the values on X, or

because both are jointly attributable to a third underlying force, thinking in

counterfactual terms (would Swedens welfare state be the same without Swedens

social democracy) will force the researcher to identify more precisely the direct or

derived causal connections (Lieberson, 1987; Fearon, 1991). If bias can be assumed to

come from the assumption of monotonically homogeneous effects of the X across all

nations, the researchers attention should concentrate on identifying more precisely the

conditional mechanisms that are involved in the causal passage from an X to a Y (why

and how will a 5 point rise in left power make the Danish welfare state converge with

the Swedish?).

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