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HBS Case Selections

case study on selection

Innovation at Moog Inc.

  • Brian J. Hall
  • Ashley V. Whillans
  • Davis Heniford
  • Dominika Randle
  • Caroline Witten

Innovation at Google Ads: The Sales Acceleration and Innovation Labs (SAIL) (A)

  • Linda A. Hill
  • Emily Tedards

Juan Valdez: Innovation in Caffeination

  • Michael I. Norton
  • Jeremy Dann

UGG Steps into the Metaverse

  • Shunyuan Zhang
  • Sharon Joseph
  • Sunil Gupta
  • Julia Kelley

Metaverse Wars

  • David B. Yoffie
  • Matt Higgins

Roblox: Virtual Commerce in the Metaverse

  • Ayelet Israeli
  • Nicole Tempest Keller

Timnit Gebru: "SILENCED No More" on AI Bias and The Harms of Large Language Models

  • Tsedal Neeley
  • Stefani Ruper

Hugging Face: Serving AI on a Platform

  • Shane Greenstein
  • Kerry Herman
  • Sarah Gulick

SmartOne: Building an AI Data Business

  • Karim R. Lakhani
  • Pippa Tubman Armerding
  • Gamze Yucaoglu
  • Fares Khrais

Honeywell and the Great Recession (A)

  • Sandra J. Sucher
  • Susan Winterberg

Target: Responding to the Recession

  • Ranjay Gulati
  • Catherine Ross
  • Richard S. Ruback
  • Royce Yudkoff

Hometown Foods: Changing Price Amid Inflation

  • Julian De Freitas
  • Jeremy Yang
  • Das Narayandas

Elon Musk's Big Bets

  • Eric Baldwin

Elon Musk: Balancing Purpose and Risk

  • Shikhar Ghosh
  • Sarah Mehta

Tesla's CEO Compensation Plan

  • Krishna G. Palepu
  • John R. Wells
  • Gabriel Ellsworth

China Rapid Finance: The Collapse of China's P2P Lending Industry

  • William C. Kirby
  • Bonnie Yining Cao
  • John P. McHugh

Forbidden City: Launching a Craft Beer in China

  • Christopher A. Bartlett
  • Carole Carlson

Booking.com

  • Stefan Thomke
  • Daniela Beyersdorfer

Innovation at Uber: The Launch of Express POOL

  • Chiara Farronato
  • Alan MacCormack

Racial Discrimination on Airbnb (A)

  • Michael Luca
  • Scott Stern
  • Hyunjin Kim

GitLab and the Future of All-Remote Work (A)

  • Prithwiraj Choudhury
  • Emma Salomon

TCS: From Physical Offices to Borderless Work

Creating a virtual internship at goldman sachs.

  • Iavor Bojinov

Unilever's Response to the Future of Work

  • William R. Kerr
  • Emilie Billaud
  • Mette Fuglsang Hjortshoej

AT&T, Retraining, and the Workforce of Tomorrow

  • Joseph B. Fuller
  • Carl Kreitzberg

Leading Change in Talent at L'Oreal

  • Lakshmi Ramarajan
  • Vincent Dessain
  • Emer Moloney
  • William W. George
  • Andrew N. McLean

Eve Hall: The African American Investment Fund in Milwaukee

  • Steven S. Rogers
  • Alterrell Mills

United Housing - Otis Gates

  • Mercer Cook

The Home Depot: Leadership in Crisis Management

  • Herman B. Leonard
  • Marc J. Epstein
  • Melissa Tritter

The Great East Japan Earthquake (B): Fast Retailing Group's Response

  • Hirotaka Takeuchi
  • Kenichi Nonomura
  • Dena Neuenschwander
  • Meghan Ricci
  • Kate Schoch
  • Sergey Vartanov

Insurer of Last Resort?: The Federal Financial Response to September 11

  • David A. Moss
  • Sarah Brennan

Under Armour

  • Rory McDonald
  • Clayton M. Christensen
  • Daniel West
  • Jonathan E. Palmer
  • Tonia Junker

Hunley, Inc.: Casting for Growth

  • John A. Quelch
  • James T. Kindley

Bitfury: Blockchain for Government

  • Mitchell B. Weiss
  • Elena Corsi

Deutsche Bank: Pursuing Blockchain Opportunities (A)

  • Lynda M. Applegate
  • Christoph Muller-Bloch

Maersk: Betting on Blockchain

  • Scott Johnson

Yum! Brands

  • Jordan Siegel
  • Christopher Poliquin

Bharti Airtel in Africa

  • Tanya Bijlani

Li & Fung 2012

  • F. Warren McFarlan
  • Michael Shih-ta Chen
  • Keith Chi-ho Wong

Sony and the JK Wedding Dance

  • John Deighton
  • Leora Kornfeld

United Breaks Guitars

David dao on united airlines.

  • Benjamin Edelman
  • Jenny Sanford

Marketing Reading: Digital Marketing

  • Joseph Davin

Social Strategy at Nike

  • Mikolaj Jan Piskorski
  • Ryan Johnson

The Tate's Digital Transformation

Social strategy at american express, mellon financial and the bank of new york.

  • Carliss Y. Baldwin
  • Ryan D. Taliaferro

The Walt Disney Company and Pixar, Inc.: To Acquire or Not to Acquire?

  • Juan Alcacer
  • David J. Collis

Dow's Bid for Rohm and Haas

  • Benjamin C. Esty

Finance Reading: The Mergers and Acquisitions Process

  • John Coates

Apple: Privacy vs. Safety? (A)

  • Henry W. McGee
  • Nien-he Hsieh
  • Sarah McAra

Sidewalk Labs: Privacy in a City Built from the Internet Up

  • Leslie K. John

Data Breach at Equifax

  • Suraj Srinivasan
  • Quinn Pitcher
  • Jonah S. Goldberg

Apple's Core

  • Noam Wasserman

Design Thinking and Innovation at Apple

  • Barbara Feinberg

Apple Inc. in 2012

  • Penelope Rossano

Iz-Lynn Chan at Far East Organization (Abridged)

  • Anthony J. Mayo
  • Dana M. Teppert

Barbara Norris: Leading Change in the General Surgery Unit

  • Boris Groysberg
  • Nitin Nohria
  • Deborah Bell

Adobe Systems: Working Towards a "Suite" Release (A)

  • David A. Thomas
  • Lauren Barley
  • Jan W. Rivkin

Starbucks Coffee Company: Transformation and Renewal

  • Nancy F. Koehn
  • Kelly McNamara
  • Nora N. Khan
  • Elizabeth Legris

JCPenney: Back in Business

  • K. Shelette Stewart
  • Christine Snively

Home Nursing of North Carolina

Castronics, llc, gemini investors, angie's list: ratings pioneer turns 20.

  • Robert J. Dolan

Basecamp: Pricing

  • Frank V. Cespedes
  • Robb Fitzsimmons

J.C. Penney's "Fair and Square" Pricing Strategy

J.c. penney's 'fair and square' strategy (c): back to the future.

  • Jose B. Alvarez

Osaro: Picking the best path

  • James Palano
  • Bastiane Huang

HubSpot and Motion AI: Chatbot-Enabled CRM

  • Thomas Steenburgh

GROW: Using Artificial Intelligence to Screen Human Intelligence

  • Ethan S. Bernstein
  • Paul D. McKinnon
  • Paul Yarabe

case study on selection

Arup: Building the Water Cube

  • Robert G. Eccles
  • Amy C. Edmondson
  • Dilyana Karadzhova

(Re)Building a Global Team: Tariq Khan at Tek

Managing a global team: greg james at sun microsystems, inc. (a).

  • Thomas J. DeLong

Organizational Behavior Reading: Leading Global Teams

Ron ventura at mitchell memorial hospital.

  • Heide Abelli

Anthony Starks at InSiL Therapeutics (A)

  • Gary P. Pisano
  • Vicki L. Sato

Wolfgang Keller at Konigsbrau-TAK (A)

  • John J. Gabarro

The 2010 Chilean Mining Rescue (A)

  • Faaiza Rashid

IDEO: Human-Centered Service Design

  • Ryan W. Buell
  • Andrew Otazo
  • Benjamin Jones
  • Alexis Brownell

case study on selection

David Neeleman: Flight Path of a Servant Leader (A)

  • Matthew D. Breitfelder

Coach Hurley at St. Anthony High School

  • Scott A. Snook
  • Bradley C. Lawrence

Shapiro Global

  • Michael Brookshire
  • Monica Haugen
  • Michelle Kravetz
  • Sarah Sommer

Kathryn McNeil (A)

  • Joseph L. Badaracco Jr.
  • Jerry Useem

Carol Fishman Cohen: Professional Career Reentry (A)

  • Myra M. Hart
  • Robin J. Ely
  • Susan Wojewoda

Alex Montana at ESH Manufacturing Co.

  • Michael Kernish

Michelle Levene (A)

  • Tiziana Casciaro
  • Victoria W. Winston

John and Andrea Rice: Entrepreneurship and Life

  • Howard H. Stevenson
  • Janet Kraus
  • Shirley M. Spence

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The Oxford Handbook of Political Methodology

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28 Case Selection for Case‐Study Analysis: Qualitative and Quantitative Techniques

John Gerring is Professor of Political Science, Boston University.

  • Published: 02 September 2009
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This article presents some guidance by cataloging nine different techniques for case selection: typical, diverse, extreme, deviant, influential, crucial, pathway, most similar, and most different. It also indicates that if the researcher is starting from a quantitative database, then methods for finding influential outliers can be used. In particular, the article clarifies the general principles that might guide the process of case selection in case-study research. Cases are more or less representative of some broader phenomenon and, on that score, may be considered better or worse subjects for intensive analysis. The article then draws attention to two ambiguities in case-selection strategies in case-study research. The first concerns the admixture of several case-selection strategies. The second concerns the changing status of a case as a study proceeds. Some case studies follow only one strategy of case selection.

Case ‐study analysis focuses on one or several cases that are expected to provide insight into a larger population. This presents the researcher with a formidable problem of case selection: Which cases should she or he choose?

In large‐sample research, the task of case selection is usually handled by some version of randomization. However, in case‐study research the sample is small (by definition) and this makes random sampling problematic, for any given sample may be wildly unrepresentative. Moreover, there is no guarantee that a few cases, chosen randomly, will provide leverage into the research question of interest.

In order to isolate a sample of cases that both reproduces the relevant causal features of a larger universe (representativeness) and provides variation along the dimensions of theoretical interest (causal leverage), case selection for very small samples must employ purposive (nonrandom) selection procedures. Nine such methods are discussed in this chapter, each of which may be identified with a distinct case‐study “type:” typical, diverse, extreme, deviant, influential, crucial, pathway, most‐similar , and most‐different . Table 28.1 summarizes each type, including its general definition, a technique for locating it within a population of potential cases, its uses, and its probable representativeness.

While each of these techniques is normally practiced on one or several cases (the diverse, most‐similar, and most‐different methods require at least two), all may employ additional cases—with the proviso that, at some point, they will no longer offer an opportunity for in‐depth analysis and will thus no longer be “case studies” in the usual sense ( Gerring 2007 , ch. 2 ). It will also be seen that small‐ N case‐selection procedures rest, at least implicitly, upon an analysis of a larger population of potential cases (as does randomization). The case(s) identified for intensive study is chosen from a population and the reasons for this choice hinge upon the way in which it is situated within that population. This is the origin of the terminology—typical, diverse, extreme, et al. It follows that case‐selection procedures in case‐study research may build upon prior cross‐case analysis and that they depend, at the very least, upon certain assumptions about the broader population.

In certain circumstances, the case‐selection procedure may be structured by a quantitative analysis of the larger population. Here, several caveats must be satisfied. First, the inference must pertain to more than a few dozen cases; otherwise, statistical analysis is problematic. Second, relevant data must be available for that population, or a significant sample of that population, on key variables, and the researcher must feel reasonably confident in the accuracy and conceptual validity of these variables. Third, all the standard assumptions of statistical research (e.g. identification, specification, robustness) must be carefully considered, and wherever possible, tested. I shall not dilate further on these familiar issues except to warn the researcher against the unreflective use of statistical techniques. 1 When these requirements are not met, the researcher must employ a qualitative approach to case selection.

The point of this chapter is to elucidate general principles that might guide the process of case selection in case‐study research, building upon earlier work by Harry Eckstein, Arend Lijphart, and others. Sometimes, these principles can be applied in a quantitative framework and sometimes they are limited to a qualitative framework. In either case, the logic of case selection remains quite similar, whether practiced in small‐ N or large‐ N contexts.

Before we begin, a bit of notation is necessary. In this chapter “ N ” refers to cases, not observations. Here, I am concerned primarily with causal inference, rather than inferences that are descriptive or predictive in nature. Thus, all hypotheses involve at least one independent variable ( X ) and one dependent variable ( Y ). For convenience, I shall label the causal factor of special theoretical interest X   1 , and the control variable, or vector of controls (if there are any), X   2 . If the writer is concerned to explain a puzzling outcome, but has no preconceptions about its causes, then the research will be described as Y‐centered . If a researcher is concerned to investigate the effects of a particular cause, with no preconceptions about what these effects might be, the research will be described as X‐centered . If a researcher is concerned to investigate a particular causal relationship, the research will be described as X   1 / Y‐centered , for it connects a particular cause with a particular outcome. 2   X ‐ or Y ‐centered research is exploratory; its purpose is to generate new hypotheses. X   1 / Y‐centered research, by contrast, is confirmatory/disconfirmatory; its purpose is to test an existing hypothesis.

1 Typical Case

In order for a focused case study to provide insight into a broader phenomenon it must be representative of a broader set of cases. It is in this context that one may speak of a typical‐case approach to case selection. The typical case exemplifies what is considered to be a typical set of values, given some general understanding of a phenomenon. By construction, the typical case is also a representative case.

Some typical cases serve an exploratory role. Here, the author chooses a case based upon a set of descriptive characteristics and then probes for causal relationships. Robert and Helen Lynd (1929/1956) selected a single city “to be as representative as possible of contemporary American life.” Specifically, they were looking for a city with

1) a temperate climate; 2) a sufficiently rapid rate of growth to ensure the presence of a plentiful assortment of the growing pains accompanying contemporary social change; 3) an industrial culture with modern, high‐speed machine production; 4) the absence of dominance of the city's industry by a single plant (i.e., not a one‐industry town); 5) a substantial local artistic life to balance its industrial activity …; and 6) the absence of any outstanding peculiarities or acute local problems which would mark the city off from the midchannel sort of American community. ( Lynd and Lynd 1929/1956 , quoted in Yin 2004 , 29–30)

After examining a number of options the Lynds decided that Muncie, Indiana, was more representative than, or at least as representative as, other midsized cities in America, thus qualifying as a typical case.

This is an inductive approach to case selection. Note that typicality may be understood according to the mean, median, or mode on a particular dimension; there may be multiple dimensions (as in the foregoing example); and each may be differently weighted (some dimensions may be more important than others). Where the selection criteria are multidimensional and a large sample of potential cases is in play, some form of factor analysis may be useful in identifying the most‐typical case(s).

However, the more common employment of the typical‐case method involves a causal model of some phenomenon of theoretical interest. Here, the researcher has identified a particular outcome ( Y ), and perhaps a specific X   1 / Y hypothesis, which she wishes to investigate. In order to do so, she looks for a typical example of that causal relationship. Intuitively, one imagines that a case selected according to the mean values of all parameters must be a typical case relative to some causal relationship. However, this is by no means assured.

Suppose that the Lynds were primarily interested in explaining feelings of trust/distrust among members of different social classes (one of the implicit research goals of the Middletown study). This outcome is likely to be affected by many factors, only some of which are included in their six selection criteria. So choosing cases with respect to a causal hypothesis involves, first of all, identifying the relevant parameters. It involves, secondly, the selection of a case that has a “typical” value relative to the overall causal model; it is well explained. Cases with untypical scores on a particular dimension (e.g. very high or very low) may still be typical examples of a causal relationship. Indeed, they may be more typical than cases whose values lie close to the mean. Thus, a descriptive understanding of typicality is quite different from a causal understanding of typicality. Since it is the latter version that is more common, I shall adopt this understanding of typicality in the remainder of the discussion.

From a qualitative perspective, causal typicality involves the selection of a case that conforms to expectations about some general causal relationship. It performs as expected. In a quantitative setting, this notion is measured by the size of a case's residual in a large‐ N cross‐case model. Typical cases lie on or near the regression line; their residuals are small. Insofar as the model is correctly specified, the size of a case's residual (i.e. the number of standard deviations that separate the actual value from the fitted value) provides a helpful clue to how representative that case is likely to be. “Outliers” are unlikely to be representative of the target population.

Of course, just because a case has a low residual does not necessarily mean that it is a representative case (with respect to the causal relationship of interest). Indeed, the issue of case representativeness is an issue that can never be definitively settled. When one refers to a “typical case” one is saying, in effect, that the probability of a case's representativeness is high, relative to other cases. This test of typicality is misleading if the statistical model is mis‐specified. And it provides little insurance against errors that are purely stochastic. A case may lie directly on the regression line but still be, in some important respect, atypical. For example, it might have an odd combination of values; the interaction of variables might be different from other cases; or additional causal mechanisms might be at work. For this reason, it is important to supplement a statistical analysis of cases with evidence drawn from the case in question (the case study itself) and with our deductive knowledge of the world. One should never judge a case solely by its residual. Yet, all other things being equal, a case with a low residual is less likely to be unusual than a case with a high residual, and to this extent the method of case selection outlined here may be a helpful guide to case‐study researchers faced with a large number of potential cases.

By way of conclusion, it should be noted that because the typical case embodies a typical value on some set of causally relevant dimensions, the variance of interest to the researcher must lie within that case. Specifically, the typical case of some phenomenon may be helpful in exploring causal mechanisms and in solving identification problems (e.g. endogeneity between X   1 and Y , an omitted variable that may account for X   1   and Y , or some other spurious causal association). Depending upon the results of the case study, the author may confirm an existing hypothesis, disconfirm that hypothesis, or reframe it in a way that is consistent with the findings of the case study. These are the uses of the typical‐case study.

2 Diverse Cases

A second case‐selection strategy has as its primary objective the achievement of maximum variance along relevant dimensions. I refer to this as a diverse‐case method. For obvious reasons, this method requires the selection of a set of cases—at minimum, two—which are intended to represent the full range of values characterizing X   1 , Y , or some particular X   1 / Y relationship. 3

Where the individual variable of interest is categorical (on/off, red/black/blue, Jewish/Protestant/Catholic), the identification of diversity is readily apparent. The investigator simply chooses one case from each category. For a continuous variable, the choices are not so obvious. However, the researcher usually chooses both extreme values (high and low), and perhaps the mean or median as well. The researcher may also look for break‐points in the distribution that seem to correspond to categorical differences among cases. Or she may follow a theoretical hunch about which threshold values count, i.e. which are likely to produce different values on Y .

Another sort of diverse case takes account of the values of multiple variables (i.e. a vector), rather than a single variable. If these variables are categorical, the identification of causal types rests upon the intersection of each category. Two dichotomous variables produce a matrix with four cells. Three trichotomous variables produce a matrix of eight cells. And so forth. If all variables are deemed relevant to the analysis, the selection of diverse cases mandates the selection of one case drawn from within each cell. Let us say that an outcome is thought to be affected by sex, race (black/white), and marital status. Here, a diverse‐case strategy of case selection would identify one case within each of these intersecting cells—a total of eight cases. Things become slightly more complicated when one or more of the factors is continuous, rather than categorical. Here, the diversity of case values do not fall neatly into cells. Rather, these cells must be created by fiat—e.g. high, medium, low.

It will be seen that where multiple variables are under consideration, the logic of diverse‐case analysis rests upon the logic of typological theorizing—where different combinations of variables are assumed to have effects on an outcome that vary across types ( Elman 2005 ; George and Bennett 2005 , 235; Lazarsfeld and Barton 1951 ). George and Smoke, for example, wish to explore different types of deterrence failure—by “fait accompli,” by “limited probe,” and by “controlled pressure.” Consequently, they wish to find cases that exemplify each type of causal mechanism. 4

Diversity may thus refer to a range of variation on X or Y , or to a particular combination of causal factors (with or without a consideration of the outcome). In each instance, the goal of case selection is to capture the full range of variation along the dimension(s) of interest.

Since diversity can mean many things, its employment in a large‐ N setting is necessarily dependent upon how this key term is defined. If it is understood to pertain only to a single variable ( X   1 or Y ), then the task is fairly simple. A categorical variable mandates the choice of at least one case from each category—two if dichotomous, three if trichotomous, and so forth. A continuous variable suggests the choice of at least one “high” and “low” value, and perhaps one drawn from the mean or median. But other choices might also be justified, according to one's hunch about the underlying causal relationship or according to natural thresholds found in the data, which may be grouped into discrete categories. Single‐variable traits are usually easy to discover in a large‐ N setting through descriptive statistics or through visual inspection of the data.

Where diversity refers to particular combinations of variables, the relevant cross‐ case technique is some version of stratified random sampling (in a probabilistic setting) or Qualitative Comparative Analysis (in a deterministic setting) ( Ragin 2000 ). If the researcher suspects that a causal relationship is affected not only by combinations of factors but also by their sequencing , then the technique of analysis must incorporate temporal elements ( Abbott 2001 ; Abbott and Forrest 1986 ; Abbott and Tsay 2000 ). Thus, the method of identifying causal types rests upon whatever method of identifying causal relationships is employed in the large‐ N sample.

Note that the identification of distinct case types is intended to identify groups of cases that are internally homogeneous (in all respects that might affect the causal relationship of interest). Thus, the choice of cases within each group should not be problematic, and may be accomplished through random sampling or purposive case selection. However, if there is suspected diversity within each category, then measures should be taken to assure that the chosen cases are typical of each category. A case study should not focus on an atypical member of a subgroup.

Indeed, considerations of diversity and typicality often go together. Thus, in a study of globalization and social welfare systems, Duane Swank (2002) first identifies three distinctive groups of welfare states: “universalistic” (social democratic), “corporatist conservative,” and “liberal.” Next, he looks within each group to find the most‐typical cases. He decides that the Nordic countries are more typical of the universalistic model than the Netherlands since the latter has “some characteristics of the occupationally based program structure and a political context of Christian Democratic‐led governments typical of the corporatist conservative nations” ( Swank 2002 , 11; see also Esping‐Andersen 1990 ). Thus, the Nordic countries are chosen as representative cases within the universalistic case type, and are accompanied in the case‐study portion of his analysis by other cases chosen to represent the other welfare state types (corporatist conservative and liberal).

Evidently, when a sample encompasses a full range of variation on relevant parameters one is likely to enhance the representativeness of that sample (relative to some population). This is a distinct advantage. Of course, the inclusion of a full range of variation may distort the actual distribution of cases across this spectrum. If there are more “high” cases than “low” cases in a population and the researcher chooses only one high case and one low case, the resulting sample of two is not perfectly representative. Even so, the diverse‐case method probably has stronger claims to representativeness than any other small‐ N sample (including the standalone typical case). The selection of diverse cases has the additional advantage of introducing variation on the key variables of interest. A set of diverse cases is, by definition, a set of cases that encompasses a range of high and low values on relevant dimensions. There is, therefore, much to recommend this method of case selection. I suspect that these advantages are commonly understood and are applied on an intuitive level by case‐study researchers. However, the lack of a recognizable name—and an explicit methodological defense—has made it difficult for case‐study researchers to utilize this method of case selection, and to do so in an explicit and self‐conscious fashion. Neologism has its uses.

3 Extreme Case

The extreme‐case method selects a case because of its extreme value on an independent ( X   1 ) or dependent ( Y ) variable of interest. Thus, studies of domestic violence may choose to focus on extreme instances of abuse ( Browne 1987 ). Studies of altruism may focus on those rare individuals who risked their lives to help others (e.g. Holocaust resisters) ( Monroe 1996 ). Studies of ethnic politics may focus on the most heterogeneous societies (e.g. Papua New Guinea) in order to better understand the role of ethnicity in a democratic setting ( Reilly 2000–1 ). Studies of industrial policy often focus on the most successful countries (i.e. the NICS) ( Deyo 1987 ). And so forth. 5

Often an extreme case corresponds to a case that is considered to be prototypical or paradigmatic of some phenomena of interest. This is because concepts are often defined by their extremes, i.e. their ideal types. Italian Fascism defines the concept of Fascism, in part, because it offered the most extreme example of that phenomenon. However, the methodological value of this case, and others like it, derives from its extremity (along some dimension of interest), not its theoretical status or its status in the literature on a subject.

The notion of “extreme” may now be defined more precisely. An extreme value is an observation that lies far away from the mean of a given distribution. This may be measured (if there are sufficient observations) by a case's “Z score”—the number of standard deviations between a case and the mean value for that sample. Extreme cases have high Z scores, and for this reason may serve as useful subjects for intensive analysis.

For a continuous variable, the distance from the mean may be in either direction (positive or negative). For a dichotomous variable (present/absent), extremeness may be interpreted as unusual . If most cases are positive along a given dimension, then a negative case constitutes an extreme case. If most cases are negative, then a positive case constitutes an extreme case. It should be clear that researchers are not simply concerned with cases where something “happened,” but also with cases where something did not. It is the rareness of the value that makes a case valuable, in this context, not its positive or negative value. 6 Thus, if one is studying state capacity, a case of state failure is probably more informative than a case of state endurance simply because the former is more unusual. Similarly, if one is interested in incest taboos a culture where the incest taboo is absent or weak is probably more useful than a culture where it is present or strong. Fascism is more important than nonfascism. And so forth. There is a good reason, therefore, why case studies of revolution tend to focus on “revolutionary” cases. Theda Skocpol (1979) had much more to learn from France than from Austro‐Hungary since France was more unusual than Austro‐Hungary within the population of nation states that Skocpol was concerned to explain. The reason is quite simple: There are fewer revolutionary cases than nonrevolutionary cases; thus, the variation that we explore as a clue to causal relationships is encapsulated in these cases, against a background of nonrevolutionary cases.

Note that the extreme‐case method of case selection appears to violate the social science folk wisdom warning us not to “select on the dependent variable.” 7 Selecting cases on the dependent variable is indeed problematic if a number of cases are chosen, all of which lie on one end of a variable's spectrum (they are all positive or negative), and if the researcher then subjects this sample to cross‐case analysis as if it were representative of a population. 8 Results for this sort of analysis would almost assuredly be biased. Moreover, there will be little variation to explain since the values of each case are explicitly constrained.

However, this is not the proper employment of the extreme‐case method. (It is more appropriately labeled an extreme‐ sample method.) The extreme‐case method actually refers back to a larger sample of cases that lie in the background of the analysis and provide a full range of variation as well as a more representative picture of the population. It is a self‐conscious attempt to maximize variance on the dimension of interest, not to minimize it. If this population of cases is well understood— either through the author's own cross‐case analysis, through the work of others, or through common sense—then a researcher may justify the selection of a single case exemplifying an extreme value for within‐case analysis. If not, the researcher may be well advised to follow a diverse‐case method, as discussed above.

By way of conclusion, let us return to the problem of representativeness. It will be seen that an extreme case may be typical or deviant. There is simply no way to tell because the researcher has not yet specified an X   1 / Y causal proposition. Once such a causal proposition has been specified one may then ask whether the case in question is similar to some population of cases in all respects that might affect the X   1 / Y relationship of interest (i.e. unit homogeneous). It is at this point that it becomes possible to say, within the context of a cross‐case statistical model, whether a case lies near to, or far from, the regression line. However, this sort of analysis means that the researcher is no longer pursuing an extreme‐case method. The extreme‐case method is purely exploratory—a way of probing possible causes of Y , or possible effects of X , in an open‐ended fashion. If the researcher has some notion of what additional factors might affect the outcome of interest, or of what relationship the causal factor of interest might have with Y , then she ought to pursue one of the other methods explored in this chapter. This also implies that an extreme‐case method may transform into a different kind of approach as a study evolves; that is, as a more specific hypothesis comes to light. Useful extreme cases at the outset of a study may prove less useful at a later stage of analysis.

4 Deviant Case

The deviant‐case method selects that case(s) which, by reference to some general understanding of a topic (either a specific theory or common sense), demonstrates a surprising value. It is thus the contrary of the typical case. Barbara Geddes (2003) notes the importance of deviant cases in medical science, where researchers are habitually focused on that which is “pathological” (according to standard theory and practice). The New England Journal of Medicine , one of the premier journals of the field, carries a regular feature entitled Case Records of the Massachusetts General Hospital. These articles bear titles like the following: “An 80‐Year‐Old Woman with Sudden Unilateral Blindness” or “A 76‐Year‐Old Man with Fever, Dyspnea, Pulmonary Infiltrates, Pleural Effusions, and Confusion.” 9 Another interesting example drawn from the field of medicine concerns the extensive study now devoted to a small number of persons who seem resistant to the AIDS virus ( Buchbinder and Vittinghoff 1999 ; Haynes, Pantaleo, and Fauci 1996 ). Why are they resistant? What is different about these people? What can we learn about AIDS in other patients by observing people who have built‐in resistance to this disease?

Likewise, in psychology and sociology case studies may be comprised of deviant (in the social sense) persons or groups. In economics, case studies may consist of countries or businesses that overperform (e.g. Botswana; Microsoft) or underperform (e.g. Britain through most of the twentieth century; Sears in recent decades) relative to some set of expectations. In political science, case studies may focus on countries where the welfare state is more developed (e.g. Sweden) or less developed (e.g. the United States) than one would expect, given a set of general expectations about welfare state development. The deviant case is closely linked to the investigation of theoretical anomalies. Indeed, to say deviant is to imply “anomalous.” 10

Note that while extreme cases are judged relative to the mean of a single distribution (the distribution of values along a single variable), deviant cases are judged relative to some general model of causal relations. The deviant‐case method selects cases which, by reference to some (presumably) general relationship, demonstrate a surprising value. They are “deviant” in that they are poorly explained by the multivariate model. The important point is that deviant‐ness can only be assessed relative to the general (quantitative or qualitative) model. This means that the relative deviant‐ness of a case is likely to change whenever the general model is altered. For example, the United States is a deviant welfare state when this outcome is gauged relative to societal wealth. But it is less deviant—and perhaps not deviant at all—when certain additional (political and societal) factors are included in the model, as discussed in the epilogue. Deviance is model dependent. Thus, when discussing the concept of the deviant case it is helpful to ask the following question: Relative to what general model (or set of background factors) is Case A deviant?

Conceptually, we have said that the deviant case is the logical contrary of the typical case. This translates into a directly contrasting statistical measurement. While the typical case is one with a low residual (in some general model of causal relations), a deviant case is one with a high residual. This means, following our previous discussion, that the deviant case is likely to be an un representative case, and in this respect appears to violate the supposition that case‐study samples should seek to reproduce features of a larger population.

However, it must be borne in mind that the primary purpose of a deviant‐case analysis is to probe for new—but as yet unspecified—explanations. (If the purpose is to disprove an extant theory I shall refer to the study as crucial‐case, as discussed below.) The researcher hopes that causal processes identified within the deviant case will illustrate some causal factor that is applicable to other (more or less deviant) cases. This means that a deviant‐case study usually culminates in a general proposition, one that may be applied to other cases in the population. Once this general proposition has been introduced into the overall model, the expectation is that the chosen case will no longer be an outlier. Indeed, the hope is that it will now be typical , as judged by its small residual in the adjusted model. (The exception would be a circumstance in which a case's outcome is deemed to be “accidental,” and therefore inexplicable by any general model.)

This feature of the deviant‐case study should help to resolve questions about its representativeness. Even if it is not possible to measure the new causal factor (and thus to introduce it into a large‐ N cross‐case model), it may still be plausible to assert (based on general knowledge of the phenomenon) that the chosen case is representative of a broader population.

5 Influential Case

Sometimes, the choice of a case is motivated solely by the need to verify the assumptions behind a general model of causal relations. Here, the analyst attempts to provide a rationale for disregarding a problematic case or a set of problematic cases. That is to say, she attempts to show why apparent deviations from the norm are not really deviant, or do not challenge the core of the theory, once the circumstances of the special case or cases are fully understood. A cross‐case analysis may, after all, be marred by several classes of problems including measurement error, specification error, errors in establishing proper boundaries for the inference (the scope of the argument), and stochastic error (fluctuations in the phenomenon under study that are treated as random, given available theoretical resources). If poorly fitting cases can be explained away by reference to these kinds of problems, then the theory of interest is that much stronger. This sort of deviant‐case analysis answers the question, “What about Case A (or cases of type A)? How does that, seemingly disconfirming, case fit the model?”

Because its underlying purpose is different from the usual deviant‐case study, I offer a new term for this method. The influential case is a case that casts doubt upon a theory, and for that reason warrants close inspection. This investigation may reveal, after all, that the theory is validated—perhaps in some slightly altered form. In this guise, the influential case is the “case that proves the rule.” In other instances, the influential‐case analysis may contribute to disconfirming, or reconceptualizing, a theory. The key point is that the value of the case is judged relative to some extant cross‐case model.

A simple version of influential‐case analysis involves the confirmation of a key case's score on some critical dimension. This is essentially a question of measurement. Sometimes cases are poorly explained simply because they are poorly understood. A close examination of a particular context may reveal that an apparently falsifying case has been miscoded. If so, the initial challenge presented by that case to some general theory has been obviated.

However, the more usual employment of the influential‐case method culminates in a substantive reinterpretation of the case—perhaps even of the general model. It is not just a question of measurement. Consider Thomas Ertman's (1997) study of state building in Western Europe, as summarized by Gerardo Munck. This study argues

that the interaction of a) the type of local government during the first period of statebuilding, with b) the timing of increases in geopolitical competition, strongly influences the kind of regime and state that emerge. [Ertman] tests this hypothesis against the historical experience of Europe and finds that most countries fit his predictions. Denmark, however, is a major exception. In Denmark, sustained geopolitical competition began relatively late and local government at the beginning of the statebuilding period was generally participatory, which should have led the country to develop “patrimonial constitutionalism.” But in fact, it developed “bureaucratic absolutism.” Ertman carefully explores the process through which Denmark came to have a bureaucratic absolutist state and finds that Denmark had the early marks of a patrimonial constitutionalist state. However, the country was pushed off this developmental path by the influence of German knights, who entered Denmark and brought with them German institutions of local government. Ertman then traces the causal process through which these imported institutions pushed Denmark to develop bureaucratic absolutism, concluding that this development was caused by a factor well outside his explanatory framework. ( Munck 2004 , 118)

Ertman's overall framework is confirmed insofar as he has been able to show, by an in‐depth discussion of Denmark, that the causal processes stipulated by the general theory hold even in this apparently disconfirming case. Denmark is still deviant, but it is so because of “contingent historical circumstances” that are exogenous to the theory ( Ertman 1997 , 316).

Evidently, the influential‐case analysis is similar to the deviant‐case analysis. Both focus on outliers. However, as we shall see, they focus on different kinds of outliers. Moreover, the animating goals of these two research designs are quite different. The influential‐case study begins with the aim of confirming a general model, while the deviant‐case study has the aim of generating a new hypothesis that modifies an existing general model. The confusion stems from the fact that the same case study may fulfill both objectives—qualifying a general model and, at the same time, confirming its core hypothesis.

Thus, in their study of Roberto Michels's “iron law of oligarchy,” Lipset, Trow, and Coleman (1956) choose to focus on an organization—the International Typographical Union—that appears to violate the central presupposition. The ITU, as noted by one of the authors, has “a long‐term two‐party system with free elections and frequent turnover in office” and is thus anything but oligarchic ( Lipset 1959 , 70). As such, it calls into question Michels's grand generalization about organizational behavior. The authors explain this curious result by the extraordinarily high level of education among the members of this union. Michels's law is shown to be true for most organizations, but not all. It is true, with qualifications. Note that the respecification of the original model (in effect, Lipset, Trow, and Coleman introduce a new control variable or boundary condition) involves the exploration of a new hypothesis. In this instance, therefore, the use of an influential case to confirm an existing theory is quite similar to the use of a deviant case to explore a new theory.

In a quantitative idiom, influential cases are those that, if counterfactually assigned a different value on the dependent variable, would most substantially change the resulting estimates. They may or may not be outliers (high‐residual cases). Two quantitative measures of influence are commonly applied in regression diagnostics ( Belsey, Kuh, and Welsch 2004 ). The first, often referred to as the leverage of a case, derives from what is called the hat matrix . Based solely on each case's scores on the independent variables, the hat matrix tells us how much a change in (or a measurement error on) the dependent variable for that case would affect the overall regression line. The second is Cook's distance , a measure of the extent to which the estimates of all the parameters would change if a given case were omitted from the analysis. Cases with a large leverage or Cook's distance contribute quite a lot to the inferences drawn from a cross‐case analysis. In this sense, such cases are vital for maintaining analytic conclusions. Discovering a significant measurement error on the dependent variable or an important omitted variable for such a case may dramatically revise estimates of the overall relationships. Hence, it may be quite sensible to select influential cases for in‐depth study.

Note that the use of an influential‐case strategy of case selection is limited to instances in which a researcher has reason to be concerned that her results are being driven by one or a few cases. This is most likely to be true in small to moderate‐sized samples. Where N is very large—greater than 1,000, let us say—it is extremely unlikely that a small set of cases (much less an individual case) will play an “influential” role. Of course, there may be influential sets of cases, e.g. countries within a particular continent or cultural region, or persons of Irish extraction. Sets of influential observations are often problematic in a time‐series cross‐section data‐set where each unit (e.g. country) contains multiple observations (through time), and hence may have a strong influence on aggregate results. Still, the general rule is: the larger the sample, the less important individual cases are likely to be and, hence, the less likely a researcher is to use an influential‐case approach to case selection.

6 Crucial Case

Of all the extant methods of case selection perhaps the most storied—and certainly the most controversial—is the crucial‐case method, introduced to the social science world several decades ago by Harry Eckstein. In his seminal essay, Eckstein (1975 , 118) describes the crucial case as one “that must closely fit a theory if one is to have confidence in the theory's validity, or, conversely, must not fit equally well any rule contrary to that proposed.” A case is crucial in a somewhat weaker—but much more common—sense when it is most, or least, likely to fulfill a theoretical prediction. A “most‐likely” case is one that, on all dimensions except the dimension of theoretical interest, is predicted to achieve a certain outcome, and yet does not. It is therefore used to disconfirm a theory. A “least‐likely” case is one that, on all dimensions except the dimension of theoretical interest, is predicted not to achieve a certain outcome, and yet does so. It is therefore used to confirm a theory. In all formulations, the crucial‐case offers a most‐difficult test for an argument, and hence provides what is perhaps the strongest sort of evidence possible in a nonexperimental, single‐case setting.

Since the publication of Eckstein's influential essay, the crucial‐case approach has been claimed in a multitude of studies across several social science disciplines and has come to be recognized as a staple of the case‐study method. 11 Yet the idea of any single case playing a crucial (or “critical”) role is not widely accepted among most methodologists (e.g. Sekhon 2004 ). (Even its progenitor seems to have had doubts.)

Let us begin with the confirmatory (a.k.a. least‐likely) crucial case. The implicit logic of this research design may be summarized as follows. Given a set of facts, we are asked to contemplate the probability that a given theory is true. While the facts matter, to be sure, the effectiveness of this sort of research also rests upon the formal properties of the theory in question. Specifically, the degree to which a theory is amenable to confirmation is contingent upon how many predictions can be derived from the theory and on how “risky” each individual prediction is. In Popper's (1963 , 36) words, “Confirmations should count only if they are the result of risky predictions ; that is to say, if, unenlightened by the theory in question, we should have expected an event which was incompatible with the theory—and event which would have refuted the theory. Every ‘good’ scientific theory is a prohibition; it forbids certain things to happen. The more a theory forbids, the better it is” (see also Popper 1934/1968 ). A risky prediction is therefore one that is highly precise and determinate, and therefore unlikely to be achieved by the product of other causal factors (external to the theory of interest) or through stochastic processes. A theory produces many such predictions if it is fully elaborated, issuing predictions not only on the central outcome of interest but also on specific causal mechanisms, and if it is broad in purview. (The notion of riskiness may also be conceptualized within the Popperian lexicon as degrees of falsifiability .)

These points can also be articulated in Bayesian terms. Colin Howson and Peter Urbach explain: “The degree to which h [a hypothesis] is confirmed by e [a set of evidence] depends … on the extent to which P(eČh) exceeds P (e) , that is, on how much more probable e is relative to the hypothesis and background assumptions than it is relative just to background assumptions.” Again, “confirmation is correlated with how much more probable the evidence is if the hypothesis is true than if it is false” ( Howson and Urlbach 1989 , 86). Thus, the stranger the prediction offered by a theory—relative to what we would normally expect—the greater the degree of confirmation that will be afforded by the evidence. As an intuitive example, Howson and Urbach (1989 , 86) offer the following:

If a soothsayer predicts that you will meet a dark stranger sometime and you do in fact, your faith in his powers of precognition would not be much enhanced: you would probably continue to think his predictions were just the result of guesswork. However, if the prediction also gave the correct number of hairs on the head of that stranger, your previous scepticism would no doubt be severely shaken.

While these Popperian/Bayesian notions 12 are relevant to all empirical research designs, they are especially relevant to case‐study research designs, for in these settings a single case (or, at most, a small number of cases) is required to bear a heavy burden of proof. It should be no surprise, therefore, that Popper's idea of “riskiness” was to be appropriated by case‐study researchers like Harry Eckstein to validate the enterprise of single‐case analysis. (Although Eckstein does not cite Popper the intellectual lineage is clear.) Riskiness, here, is analogous to what is usually referred to as a “most‐ difficult” research design, which in a case‐study research design would be understood as a “least‐likely” case. Note also that the distinction between a “must‐fit” case and a least‐likely case—that, in the event, actually does fit the terms of a theory—is a matter of degree. Cases are more or less crucial for confirming theories. The point is that, in some circumstances, a paucity of empirical evidence may be compensated by the riskiness of the theory.

The crucial‐case research design is, perforce, a highly deductive enterprise; much depends on the quality of the theory under investigation. It follows that the theories most amenable to crucial‐case analysis are those which are lawlike in their precision, degree of elaboration, consistency, and scope. The more a theory attains the status of a causal law, the easier it will be to confirm, or to disconfirm, with a single case. Indeed, risky predictions are common in natural science fields such as physics, which in turn served as the template for the deductive‐nomological (“covering‐law”) model of science that influenced Eckstein and others in the postwar decades (e.g. Hempel 1942 ).

A frequently cited example is the first important empirical demonstration of the theory of relativity, which took the form of a single‐event prediction on the occasion of the May 29, 1919, solar eclipse ( Eckstein 1975 ; Popper 1963 ). Stephen Van Evera (1997 , 66–7) describes the impact of this prediction on the validation of Einstein's theory.

Einstein's theory predicted that gravity would bend the path of light toward a gravity source by a specific amount. Hence it predicted that during a solar eclipse stars near the sun would appear displaced—stars actually behind the sun would appear next to it, and stars lying next to the sun would appear farther from it—and it predicted the amount of apparent displacement. No other theory made these predictions. The passage of this one single‐case‐study test brought the theory wide acceptance because the tested predictions were unique—there was no plausible competing explanation for the predicted result—hence the passed test was very strong.

The strength of this test is the extraordinary fit between the theory and a set of facts found in a single case, and the corresponding lack of fit between all other theories and this set of facts. Einstein offered an explanation of a particular set of anomalous findings that no other existing theory could make sense of. Of course, one must assume that there was no—or limited—measurement error. And one must assume that the phenomenon of interest is largely invariant; light does not bend differently at different times and places (except in ways that can be understood through the theory of relativity). And one must assume, finally, that the theory itself makes sense on other grounds (other than the case of special interest); it is a plausible general theory. If one is willing to accept these a priori assumptions, then the 1919 “case study” provides a very strong confirmation of the theory. It is difficult to imagine a stronger proof of the theory from within an observational (nonexperimental) setting.

In social science settings, by contrast, one does not commonly find single‐case studies offering knockout evidence for a theory. This is, in my view, largely a product of the looseness (the underspecification) of most social science theories. George and Bennett point out that while the thesis of the democratic peace is as close to a “law” as social science has yet seen, it cannot be confirmed (or refuted) by looking at specific causal mechanisms because the causal pathways mandated by the theory are multiple and diverse. Under the circumstances, no single‐case test can offer strong confirmation of the theory ( George and Bennett 2005 , 209).

However, if one adopts a softer version of the crucial‐case method—the least‐likely (most difficult) case—then possibilities abound. Indeed, I suspect that, implicitly , most case‐study work that makes a positive argument focusing on a single case (without a corresponding cross‐case analysis) relies largely on the logic of the least‐ likely case. Rarely is this logic made explicit, except perhaps in a passing phrase or two. Yet the deductive logic of the “risky” prediction is central to the case‐study enterprise. Whether a case study is convincing or not often rests on the reader's evaluation of how strong the evidence for an argument might be, and this in turn—wherever cross‐ case evidence is limited and no manipulated treatment can be devised—rests upon an estimation of the degree of “fit” between a theory and the evidence at hand, as discussed.

Lily Tsai's (2007) investigation of governance at the village level in China employs several in‐depth case studies of villages which are chosen (in part) because of their least‐likely status relative to the theory of interest. Tsai's hypothesis is that villages with greater social solidarity (based on preexisting religious or familial networks) will develop a higher level of social trust and mutual obligation and, as a result, will experience better governance. Crucial cases, therefore, are villages that evidence a high level of social solidarity but which, along other dimensions, would be judged least likely to develop good governance, e.g. they are poor, isolated, and lack democratic institutions or accountability mechanisms from above. “Li Settlement,” in Fujian province, is such a case. The fact that this impoverished village nonetheless boasts an impressive set of infrastructural accomplishments such as paved roads with drainage ditches (a rarity in rural China) suggests that something rather unusual is going on here. Because her case is carefully chosen to eliminate rival explanations, Tsai's conclusions about the special role of social solidarity are difficult to gainsay. How else is one to explain this otherwise anomalous result? This is the strength of the least‐likely case, where all other plausible causal factors for an outcome have been minimized. 13

Jack Levy (2002 , 144) refers to this, evocatively, as a “Sinatra inference:” if it can make it here, it can make it anywhere (see also Khong 1992 , 49; Sagan 1995 , 49; Shafer 1988 , 14–6). Thus, if social solidarity has the hypothesized effect in Li Settlement it should have the same effect in more propitious settings (e.g. where there is greater economic surplus). The same implicit logic informs many case‐study analyses where the intent of the study is to confirm a hypothesis on the basis of a single case.

Another sort of crucial case is employed for the purpose of dis confirming a causal hypothesis. A central Popperian insight is that it is easier to disconfirm an inference than to confirm that same inference. (Indeed, Popper doubted that any inference could be fully confirmed, and for this reason preferred the term “corroborate.”) This is particularly true of case‐study research designs, where evidence is limited to one or several cases. The key proviso is that the theory under investigation must take a consistent (a.k.a. invariant, deterministic) form, even if its predictions are not terrifically precise, well elaborated, or broad.

As it happens, there are a fair number of invariant propositions floating around the social science disciplines (Goertz and Levy forthcoming; Goertz and Starr 2003 ). It used to be argued, for example, that political stability would occur only in countries that are relatively homogeneous, or where existing heterogeneities are mitigated by cross‐cutting cleavages ( Almond 1956 ; Bentley 1908/1967 ; Lipset 1960/1963 ; Truman 1951 ). Arend Lijphart's (1968) study of the Netherlands, a peaceful country with reinforcing social cleavages, is commonly viewed as refuting this theory on the basis of a single in‐depth case analysis. 14

Granted, it may be questioned whether presumed invariant theories are really invariant; perhaps they are better understood as probabilistic. Perhaps, that is, the theory of cross‐cutting cleavages is still true, probabilistically, despite the apparent Dutch exception. Or perhaps the theory is still true, deterministically, within a subset of cases that does not include the Netherlands. (This sort of claim seems unlikely in this particular instance, but it is quite plausible in many others.) Or perhaps the theory is in need of reframing; it is true, deterministically, but applies only to cross‐ cutting ethnic/racial cleavages, not to cleavages that are primarily religious. One can quibble over what it means to “disconfirm” a theory. The point is that the crucial case has, in all these circumstances, provided important updating of a theoretical prior.

Heretofore, I have treated causal factors as dichotomous. Countries have either reinforcing or cross‐cutting cleavages and they have regimes that are either peaceful or conflictual. Evidently, these sorts of parameters are often matters of degree. In this reading of the theory, cases are more or less crucial. Accordingly, the most useful—i.e. most crucial—case for Lijphart's purpose is one that has the most segregated social groups and the most peaceful and democratic track record. In these respects, the Netherlands was a very good choice. Indeed, the degree of disconfirmation offered by this case study is probably greater than the degree of disconfirmation that might have been provided by other cases such as India or Papua New Guinea—countries where social peace has not always been secure. The point is that where variables are continuous rather than dichotomous it is possible to evaluate potential cases in terms of their degree of crucialness .

Note that the crucial‐case method of case‐selection, whether employed in a confirmatory or disconfirmatory mode, cannot be employed in a large‐ N context. This is because an explicit cross‐case model would render the crucial‐case study redundant. Once one identifies the relevant parameters and the scores of all cases on those parameters, one has in effect constructed a cross‐case model that confirms or disconfirms the theory in question. The case study is thenceforth irrelevant, at least as a means of decisive confirmation or disconfirmation. 15 It remains highly relevant as a means of exploring causal mechanisms, of course. Yet, because this objective is quite different from that which is usually associated with the term, I enlist a new term for this technique.

7 Pathway Case

One of the most important functions of case‐study research is the elucidation of causal mechanisms. But which sort of case is most useful for this purpose? Although all case studies presumably shed light on causal mechanisms, not all cases are equally transparent. In situations where a causal hypothesis is clear and has already been confirmed by cross‐case analysis, researchers are well advised to focus on a case where the causal effect of X   1 on Y can be isolated from other potentially confounding factors ( X   2 ). I shall call this a pathway case to indicate its uniquely penetrating insight into causal mechanisms. In contrast to the crucial case, this sort of method is practicable only in circumstances where cross‐case covariational patterns are well studied and where the mechanism linking X   1 and Y remains dim. Because the pathway case builds on prior cross‐case analysis, the problem of case selection must be situated within that sample. There is no standalone pathway case.

The logic of the pathway case is clearest in situations of causal sufficiency—where a causal factor of interest, X   1 , is sufficient by itself (though perhaps not necessary) to account for Y 's value (0 or 1). The other causes of Y , about which we need make no assumptions, are designated as a vector, X   2 .

Note that wherever various causal factors are substitutable for one another, each factor is conceptualized (individually) as sufficient ( Braumoeller 2003 ). Thus, situations of causal equifinality presume causal sufficiency on the part of each factor or set of conjoint factors. An example is provided by the literature on democratization, which stipulates three main avenues of regime change: leadership‐initiated reform, a controlled opening to opposition, or the collapse of an authoritarian regime ( Colomer 1991 ). The case‐study format constrains us to analyze one at a time, so let us limit our scope to the first one—leadership‐initiated reform. So considered, a causal‐pathway case would be one with the following features: (a) democratization, (b) leadership‐initiated reform, (c) no controlled opening to the opposition, (d) no collapse of the previous authoritarian regime, and (e) no other extraneous factors that might affect the process of democratization. In a case of this type, the causal mechanisms by which leadership‐initiated reform may lead to democratization will be easiest to study. Note that it is not necessary to assume that leadership‐initiated reform always leads to democratization; it may or may not be a deterministic cause. But it is necessary to assume that leadership‐initiated reform can sometimes lead to democratization on its own (given certain background features).

Now let us move from these examples to a general‐purpose model. For heuristic purposes, let us presume that all variables in that model are dichotomous (coded as 0 or 1) and that the model is complete (all causes of Y are included). All causal relationships will be coded so as to be positive: X   1 and Y covary as do X   2 and Y . This allows us to visualize a range of possible combinations at a glance.

Recall that the pathway case is always focused, by definition, on a single causal factor, denoted X   1 . (The researcher's focus may shift to other causal factors, but may only focus on one causal factor at a time.) In this scenario, and regardless of how many additional causes of Y there might be (denoted X   2 , a vector of controls), there are only eight relevant case types, as illustrated in Table 28.2 . Identifying these case types is a relatively simple matter, and can be accomplished in a small‐ N sample by the construction of a truth‐table (modeled after Table 28.2 ) or in a large‐ N sample by the use of cross‐tabs.

Notes : X   1 = the variable of theoretical interest. X   2 = a vector of controls (a score of 0 indicates that all control variables have a score of 0, while a score of 1 indicates that all control variables have a score of 1). Y = the outcome of interest. A–H = case types (the N for each case type is indeterminate). G, H = possible pathway cases. Sample size = indeterminate.

Assumptions : (a) all variables can be coded dichotomously (a binary coding of the concept is valid); (b) all independent variables are positively correlated with Y in the general case; ( c ) X   1 is (at least sometimes) a sufficient cause of Y .

Note that the total number of combinations of values depends on the number of control variables, which we have represented with a single vector, X   2 . If this vector consists of a single variable then there are only eight case types. If this vector consists of two variables ( X   2a , X   2b ) then the total number of possible combinations increases from eight (2 3 ) to sixteen (2 4 ). And so forth. However, none of these combinations is relevant for present purposes except those where X   2a and X   2b have the same value (0 or 1). “Mixed” cases are not causal pathway cases, for reasons that should become clear.

The pathway case, following the logic of the crucial case, is one where the causal factor of interest, X   1 , correctly predicts Y while all other possible causes of Y (represented by the vector, X   2 ) make “wrong” predictions. If X   1 is—at least in some circumstances—a sufficient cause of Y , then it is these sorts of cases that should be most useful for tracing causal mechanisms. There are only two such cases in Ta b l e 28.2—G and H. In all other cases, the mechanism running from X   1 to Y would be difficult to discern either because X   1 and Y are not correlated in the usual way (constituting an unusual case, in the terms of our hypothesis) or because other confounding factors ( X   2 ) intrude. In case A, for example, the positive value on Y could be a product of X   1 or X   2 . An in‐depth examination of this case is not likely to be very revealing.

Keep in mind that because the researcher already knows from her cross‐case examination what the general causal relationships are, she knows (prior to the case‐ study investigation) what constitutes a correct or incorrect prediction. In the crucial‐ case method, by contrast, these expectations are deductive rather than empirical. This is what differentiates the two methods. And this is why the causal pathway case is useful principally for elucidating causal mechanisms rather than verifying or falsifying general propositions (which are already more or less apparent from the cross‐case evidence). Of course, we must leave open the possibility that the investigation of causal mechanisms would invalidate a general claim, if that claim is utterly contingent upon a specific set of causal mechanisms and the case study shows that no such mechanisms are present. However, this is rather unlikely in most social science settings. Usually, the result of such a finding will be a reformulation of the causal processes by which X   1 causes Y —or, alternatively, a realization that the case under investigation is aberrant (atypical of the general population of cases).

Sometimes, the research question is framed as a unidirectional cause: one is interested in why 0 becomes 1 (or vice versa) but not in why 1 becomes 0. In our previous example, we asked why democracies fail, not why countries become democratic or authoritarian. So framed, there can be only one type of causal‐pathway case. (Whether regime failure is coded as 0 or 1 is a matter of taste.) Where researchers are interested in bidirectional causality—a movement from 0 to 1 as well as from 1 to 0—there are two possible causal‐pathway cases, G and H. In practice, however, one of these case types is almost always more useful than the other. Thus, it seems reasonable to employ the term “pathway case” in the singular. In order to determine which of these two case types will be more useful for intensive analysis the researcher should look to see whether each case type exhibits desirable features such as: (a) a rare (unusual) value on X   1 or Y (designated “extreme” in our previous discussion), (b) observable temporal variation in X   1 , ( c ) an X   1 / Y relationship that is easier to study (it has more visible features; it is more transparent), or (d) a lower residual (thus indicating a more typical case, within the terms of the general model). Usually, the choice between G and H is intuitively obvious.

Now, let us consider a scenario in which all (or most) variables of concern to the model are continuous, rather than dichotomous. Here, the job of case selection is considerably more complex, for causal “sufficiency” (in the usual sense) cannot be invoked. It is no longer plausible to assume that a given cause can be entirely partitioned, i.e. rival factors eliminated. However, the search for a pathway case may still be viable. What we are looking for in this scenario is a case that satisfies two criteria: (1) it is not an outlier (or at least not an extreme outlier) in the general model and (2) its score on the outcome ( Y ) is strongly influenced by the theoretical variable of interest ( X   1 ), taking all other factors into account ( X   2 ). In this sort of case it should be easiest to “see” the causal mechanisms that lie between X   1 and Y .

Achieving the second desiderata requires a bit of manipulation. In order to determine which (nonoutlier) cases are most strongly affected by X   1 , given all the other parameters in the model, one must compare the size of the residuals for each case in a reduced form model, Y = Constant + X   2 + Res reduced , with the size of the residuals for each case in a full model, Y = Constant + X   2 + X   1 + Res full . The pathway case is that case, or set of cases, which shows the greatest difference between the residual for the reduced‐form model and the full model (ΔResidual). Thus,

Note that the residual for a case must be smaller in the full model than in the reduced‐ form model; otherwise, the addition of the variable of interest ( X   1 ) pulls the case away from the regression line. We want to find a case where the addition of X   1 pushes the case towards the regression line, i.e. it helps to “explain” that case.

As an example, let us suppose that we are interested in exploring the effect of mineral wealth on the prospects for democracy in a society. According to a good deal of work on this subject, countries with a bounty of natural resources—particularly oil—are less likely to democratize (or once having undergone a democratic transition, are more likely to revert to authoritarian rule) ( Barro 1999 ; Humphreys 2005 ; Ross 2001 ). The cross‐country evidence is robust. Yet as is often the case, the causal mechanisms remain rather obscure. In order to better understand this phenomenon it may be worthwhile to exploit the findings of cross‐country regression models in order to identify a country whose regime type (i.e. its democracy “score” on some general index) is strongly affected by its natural‐research wealth, all other things held constant. An analysis of this sort identifies two countries— the United Arab Emirates and Kuwait—with high Δ Residual values and modest residuals in the full model (signifying that these cases are not outliers). Researchers seeking to explore the effect of oil wealth on regime type might do well to focus on these two cases since their patterns of democracy cannot be well explained by other factors—e.g. economic development, religion, European influence, or ethnic fractionalization. The presence of oil wealth in these countries would appear to have a strong independent effect on the prospects for democratization in these cases, an effect that is well modeled by general theory and by the available cross‐case evidence.

To reiterate, the logic of causal “elimination” is much more compelling where variables are dichotomous and where causal sufficiency can be assumed ( X   1 is sufficient by itself, at least in some circumstances, to cause Y ). Where variables are continuous, the strategy of the pathway case is more dubious, for potentially confounding causal factors ( X   2 ) cannot be neatly partitioned. Even so, we have indicated why the selection of a pathway case may be a logical approach to case‐study analysis in many circumstances.

The exceptions may be briefly noted. Sometimes, where all variables in a model are dichotomous, there are no pathway cases, i.e. no cases of type G or H (in Table 28.2 ). This is known as the “empty cell” problem, or a problem of severe causal multicollinearity. The universe of observational data does not always oblige us with cases that allow us to independently test a given hypothesis. Where variables are continuous, the analogous problem is that of a causal variable of interest ( X   1 ) that has only minimal effects on the outcome of interest. That is, its role in the general model is quite minor. In these situations, the only cases that are strongly affected by X   1 —if there are any at all—may be extreme outliers, and these sorts of cases are not properly regarded as providing confirmatory evidence for a proposition, for reasons that are abundantly clear by now.

Finally, it should be clarified that the identification of a causal pathway case does not obviate the utility of exploring other cases. One might, for example, want to compare both sorts of potential pathway cases—G and H—with each other. Many other combinations suggest themselves. However, this sort of multi‐case investigation moves beyond the logic of the causal‐pathway case.

8 Most‐similar Cases

The most‐similar method employs a minimum of two cases. 16 In its purest form, the chosen pair of cases is similar in all respects except the variable(s) of interest. If the study is exploratory (i.e. hypothesis generating), the researcher looks for cases that differ on the outcome of theoretical interest but are similar on various factors that might have contributed to that outcome, as illustrated in Table 28.3 (A) . This is a common form of case selection at the initial stage of research. Often, fruitful analysis begins with an apparent anomaly: two cases are apparently quite similar, and yet demonstrate surprisingly different outcomes. The hope is that intensive study of these cases will reveal one—or at most several—factors that differ across these cases. These differing factors ( X   1 ) are looked upon as putative causes. At this stage, the research may be described by the second diagram in Table 28.3 (B) . Sometimes, a researcher begins with a strong hypothesis, in which case her research design is confirmatory (hypothesis testing) from the get‐go. That is, she strives to identify cases that exhibit different outcomes, different scores on the factor of interest, and similar scores on all other possible causal factors, as illustrated in the second (hypothesis‐testing) diagram in Table 28.3 (B) .

The point is that the purpose of a most‐similar research design, and hence its basic setup, often changes as a researcher moves from an exploratory to a confirmatory mode of analysis. However, regardless of where one begins, the results, when published, look like a hypothesis‐testing research design. Question marks have been removed: (A) becomes (B) in Table 28.3 .

As an example, let us consider Leon Epstein's classic study of party cohesion, which focuses on two “most‐similar” countries, the United States and Canada. Canada has highly disciplined parties whose members vote together on the floor of the House of Commons while the United States has weak, undisciplined parties, whose members often defect on floor votes in Congress. In explaining these divergent outcomes, persistent over many years, Epstein first discusses possible causal factors that are held more or less constant across the two cases. Both the United States and Canada inherited English political cultures, both have large territories and heterogeneous populations, both are federal, and both have fairly loose party structures with strong regional bases and a weak center. These are the “control” variables. Where they differ is in one constitutional feature: Canada is parliamentary while the United States is presidential. And it is this institutional difference that Epstein identifies as the crucial (differentiating) cause. (For further examples of the most‐similar method see Brenner 1976 ; Hamilton 1977 ; Lipset 1968 ; Miguel 2004 ; Moulder 1977 ; Posner 2004 .)

X   1 = the variable of theoretical interest. X   2 = a vector of controls. Y = the outcome of interest.

Several caveats apply to any most‐similar analysis (in addition to the usual set of assumptions applying to all case‐study analysis). First, each causal factor is understood as having an independent and additive effect on the outcome; there are no “interaction” effects. Second, one must code cases dichotomously (high/low, present/absent). This is straightforward if the underlying variables are also dichotomous (e.g. federal/unitary). However, it is often the case that variables of concern in the model are continuous (e.g. party cohesion). In this setting, the researcher must “dichotomize” the scoring of cases so as to simplify the two‐case analysis. (Some flexibility is admissible on the vector of controls ( X   2 ) that are “held constant” across the cases. Nonidentity is tolerable if the deviation runs counter to the predicted hypothesis. For example, Epstein describes both the United States and Canada as having strong regional bases of power, a factor that is probably more significant in recent Canadian history than in recent American history. However, because regional bases of power should lead to weaker parties, rather than stronger parties, this element of nonidentity does not challenge Epstein's conclusions. Indeed, it sets up a most‐difficult research scenario, as discussed above.)

In one respect the requirements for case control are not so stringent. Specifically, it is not usually necessary to measure control variables (at least not with a high degree of precision) in order to control for them. If two countries can be assumed to have similar cultural heritages one needn't worry about constructing variables to measure that heritage. One can simply assert that, whatever they are, they are more or less constant across the two cases. This is similar to the technique employed in a randomized experiment, where the researcher typically does not attempt to measure all the factors that might affect the causal relationship of interest. She assumes, rather, that these unknown factors have been neutralized across the treatment and control groups by randomization or by the choice of a sample that is internally homogeneous.

The most useful statistical tool for identifying cases for in‐depth analysis in a most‐ similar setting is probably some variety of matching strategy—e.g. exact matching, approximate matching, or propensity‐score matching. 17 The product of this procedure is a set of matched cases that can be compared in whatever way the researcher deems appropriate. These are the “most‐similar” cases. Rosenbaum and Silber (2001 , 223) summarize:

Unlike model‐based adjustments, where [individuals] vanish and are replaced by the coefficients of a model, in matching, ostensibly comparable patterns are compared directly, one by one. Modern matching methods involve statistical modeling and combinatorial algorithms, but the end result is a collection of pairs or sets of people who look comparable, at least on average. In matching, people retain their integrity as people, so they can be examined and their stories can be told individually.

Matching, conclude the authors, “facilitates, rather than inhibits, thick description” ( Rosenbaum and Silber 2001 , 223).

In principle, the same matching techniques that have been used successfully in observational studies of medical treatments might also be adapted to the study of nation states, political parties, cities, or indeed any traditional paired cases in the social sciences. Indeed, the current popularity of matching among statisticians—relative, that is, to garden‐variety regression models—rests upon what qualitative researchers would recognize as a “case‐based” approach to causal analysis. If Rosenbaum and Silber are correct, it may be perfectly reasonable to appropriate this large‐ N method of analysis for case‐study purposes.

As with other methods of case selection, the most‐similar method is prone to problems of nonrepresentativeness. If employed in a qualitative fashion (without a systematic cross‐case selection strategy), potential biases in the chosen case must be addressed in a speculative way. If the researcher employs a matching technique of case selection within a large‐ N sample, the problem of potential bias can be addressed by assuring the choice of cases that are not extreme outliers, as judged by their residuals in the full model. Most‐similar cases should also be “typical” cases, though some scope for deviance around the regression line may be acceptable for purposes of finding a good fit among cases.

X   1 = the variable of theoretical interest. X   2a–d = a vector of controls. Y = the outcome of interest.

9 Most‐different Cases

A final case‐selection method is the reverse image of the previous method. Here, variation on independent variables is prized, while variation on the outcome is eschewed. Rather than looking for cases that are most‐similar, one looks for cases that are most‐ different . Specifically, the researcher tries to identify cases where just one independent variable ( X   1 ), as well as the dependent variable ( Y ), covary, while all other plausible factors ( X   2a–d ) show different values. 18

The simplest form of this two‐case comparison is illustrated in Table 28.4 . Cases A and B are deemed “most different,” though they are similar in two essential respects— the causal variable of interest and the outcome.

As an example, I follow Marc Howard's (2003) recent work, which explores the enduring impact of Communism on civil society. 19 Cross‐national surveys show a strong correlation between former Communist regimes and low social capital, controlling for a variety of possible confounders. It is a strong result. Howard wonders why this relationship is so strong and why it persists, and perhaps even strengthens, in countries that are no longer socialist or authoritarian. In order to answer this question, he focuses on two most‐different cases, Russia and East Germany. These two countries were quite different—in all ways other than their Communist experience— prior to the Soviet era, during the Soviet era (since East Germany received substantial subsidies from West Germany), and in the post‐Soviet era, as East Germany was absorbed into West Germany. Yet, they both score near the bottom of various cross‐ national indices intended to measure the prevalence of civic engagement in the current era. Thus, Howard's (2003 , 6–9) case selection procedure meets the requirements of the most‐different research design: Variance is found on all (or most) dimensions aside from the key factor of interest (Communism) and the outcome (civic engagement).

What leverage is brought to the analysis from this approach? Howard's case studies combine evidence drawn from mass surveys and from in‐depth interviews of small, stratified samples of Russians and East Germans. (This is a good illustration, incidentally, of how quantitative and qualitative evidence can be fruitfully combined in the intensive study of several cases.) The product of this analysis is the identification of three causal pathways that, Howard (2003 , 122) claims, help to explain the laggard status of civil society in post‐Communist polities: “the mistrust of communist organizations, the persistence of friendship networks, and the disappointment with post‐communism.” Simply put, Howard (2003 , 145) concludes, “a great number of citizens in Russia and Eastern Germany feel a strong and lingering sense of distrust of any kind of public organization, a general satisfaction with their own personal networks (accompanied by a sense of deteriorating relations within society overall), and disappointment in the developments of post‐communism.”

The strength of this most‐different case analysis is that the results obtained in East Germany and Russia should also apply in other post‐Communist polities (e.g. Lithuania, Poland, Bulgaria, Albania). By choosing a heterogeneous sample, Howard solves the problem of representativeness in his restricted sample. However, this sample is demonstrably not representative across the population of the inference, which is intended to cover all countries of the world.

More problematic is the lack of variation on key causal factors of interest— Communism and its putative causal pathways. For this reason, it is difficult to reach conclusions about the causal status of these factors on the basis of the most‐different analysis alone. It is possible, that is, that the three causal pathways identified by Howard also operate within polities that never experienced Communist rule.

Nor does it seem possible to conclusively eliminate rival hypotheses on the basis of this most‐different analysis. Indeed, this is not Howard's intention. He wishes merely to show that whatever influence on civil society might be attributed to economic, cultural, and other factors does not exhaust this subject.

My considered judgment is that the most‐different research design provides minimal leverage into the problem of why Communist systems appear to suppress civic engagement, years after their disappearance. Fortunately, this is not the only research design employed by Howard in his admirable study. Indeed, the author employs two other small‐ N cross‐case methods, as well as a large‐ N cross‐country statistical analysis. These methods do most of the analytic work. East Germany may be regarded as a causal pathway case (see above). It has all the attributes normally assumed to foster civic engagement (e.g. a growing economy, multiparty competition, civil liberties, a free press, close association with Western European culture and politics), but nonetheless shows little or no improvement on this dimension during the post‐ transition era ( Howard 2003 , 8). It is plausible to attribute this lack of change to its Communist past, as Howard does, in which case East Germany should be a fruitful case for the investigation of causal mechanisms. The contrast between East and West Germany provides a most‐similar analysis since the two polities share virtually everything except a Communist past. This variation is also deftly exploited by Howard.

I do not wish to dismiss the most‐different research method entirely. Surely, Howard's findings are stronger with the intensive analysis of Russia than they would be without. Yet his book would not stand securely on the empirical foundation provided by most‐different analysis alone. If one strips away the pathway‐case (East Germany) and the most‐similar analysis (East/West Germany) there is little left upon which to base an analysis of causal relations (aside from the large‐ N cross‐national analysis). Indeed, most scholars who employ the most‐different method do so in conjunction with other methods. 20 It is rarely, if ever, a standalone method. 21

Generalizing from this discussion of Marc Howard's work, I offer the following summary remarks on the most‐different method of case analysis. (I leave aside issues faced by all case‐study analyses, issues that are explored in Gerring 2007 .)

Let us begin with a methodological obstacle that is faced by both Millean styles of analysis—the necessity of dichotomizing every variable in the analysis. Recall that, as with most‐similar analysis, differences across cases must generally be sizeable enough to be interpretable in an essentially dichotomous fashion (e.g. high/low, present/absent) and similarities must be close enough to be understood as essentially identical (e.g. high/high, present/present). Otherwise the results of a Millean style analysis are not interpretable. The problem of “degrees” is deadly if the variables under consideration are, by nature, continuous (e.g. GDP). This is a particular concern in Howard's analysis, where East Germany scores somewhat higher than Russia in civic engagement; they are both low, but Russia is quite a bit lower. Howard assumes that this divergence is minimal enough to be understood as a difference of degrees rather than of kinds, a judgment that might be questioned. In these respects, most‐different analysis is no more secure—but also no less—than most‐similar analysis.

In one respect, most‐different analysis is superior to most‐similar analysis. If the coding assumptions are sound, the most‐different research design may be quite useful for eliminating necessary causes . Causal factors that do not appear across the chosen cases—e.g. X   2a–d in Table 28.4 —are evidently unnecessary for the production of Y . However, it does not follow that the most‐different method is the best method for eliminating necessary causes. Note that the defining feature of this method is the shared element across cases— X   1 in Table 28.4 . This feature does not help one to eliminate necessary causes. Indeed, if one were focused solely on eliminating necessary causes one would presumably seek out cases that register the same outcomes and have maximum diversity on other attributes. In Table 28.4 , this would be a set of cases that satisfy conditions X   2a–d , but not X   1 . Thus, even the presumed strength of the most‐different analysis is not so strong.

Usually, case‐study analysis is focused on the identification (or clarification) of causal relations, not the elimination of possible causes. In this setting, the most‐ different technique is useful, but only if assumptions of causal uniqueness hold. By “causal uniqueness,” I mean a situation in which a given outcome is the product of only one cause: Y cannot occur except in the presence of X . X is necessary, and in some situations (given certain background conditions) sufficient, to cause Y . 22

Consider the following hypothetical example. Suppose that a new disease, about which little is known, has appeared in Country A. There are hundreds of infected persons across dozens of affected communities in that country. In Country B, located at the other end of the world, several new cases of the disease surface in a single community. In this setting, we can imagine two sorts of Millean analyses. The first examines two similar communities within Country A, one of which has developed the disease and the other of which has not. This is the most‐similar style of case comparison, and focuses accordingly on the identification of a difference between the two cases that might account for variation across the sample. A second approach focuses on communities where the disease has appeared across the two countries and searches for any similarities that might account for these similar outcomes. This is the most‐different research design.

Both are plausible approaches to this particular problem, and we can imagine epidemiologists employing them simultaneously. However, the most‐different design demands stronger assumptions about the underlying factors at work. It supposes that the disease arises from the same cause in any setting. This is often a reasonable operating assumption when one is dealing with natural phenomena, though there are certainly many exceptions. Death, for example, has many causes. For this reason, it would not occur to us to look for most‐different cases of high mortality around the world. In order for the most‐different research design to effectively identify a causal factor at work in a given outcome, the researcher must assume that X   1 —the factor held constant across the diverse cases—is the only possible cause of Y (see Table 28.4 ). This assumption rarely holds in social‐scientific settings. Most outcomes of interest to anthropologists, economists, political scientists, and sociologists have multiple causes. There are many ways to win an election, to build a welfare state, to get into a war, to overthrow a government, or—returning to Marc Howard's work—to build a strong civil society. And it is for this reason that most‐different analysis is rarely applied in social science work and, where applied, is rarely convincing.

If this seems a tad severe, there is a more charitable way of approaching the most‐different method. Arguably, this is not a pure “method” at all but merely a supplement, a way of incorporating diversity in the sub‐sample of cases that provide the unusual outcome of interest. If the unusual outcome is revolutions, one might wish to encompass a wide variety of revolutions in one's analysis. If the unusual outcome is post‐Communist civil society, it seems appropriate to include a diverse set of post‐Communist polities in one's sample of case studies, as Marc Howard does. From this perspective, the most‐different method (so‐called) might be better labeled a diverse‐case method, as explored above.

10 Conclusions

In order to be a case of something broader than itself, the chosen case must be representative (in some respects) of a larger population. Otherwise—if it is purely idiosyncratic (“unique”)—it is uninformative about anything lying outside the borders of the case itself. A study based on a nonrepresentative sample has no (or very little) external validity. To be sure, no phenomenon is purely idiosyncratic; the notion of a unique case is a matter that would be difficult to define. One is concerned, as always, with matters of degree. Cases are more or less representative of some broader phenomenon and, on that score, may be considered better or worse subjects for intensive analysis. (The one exception, as noted, is the influential case.)

Of all the problems besetting case‐study analysis, perhaps the most persistent— and the most persistently bemoaned—is the problem of sample bias ( Achen and Snidal 1989 ; Collier and Mahoney 1996 ; Geddes 1990 ; King, Keohane, and Verba 1994 ; Rohlfing 2004 ; Sekhon 2004 ). Lisa Martin (1992 , 5) finds that the overemphasis of international relations scholars on a few well‐known cases of economic sanctions— most of which failed to elicit any change in the sanctioned country—“has distorted analysts view of the dynamics and characteristics of economic sanctions.” Barbara Geddes (1990) charges that many analyses of industrial policy have focused exclusively on the most successful cases—primarily the East Asian NICs—leading to biased inferences. Anna Breman and Carolyn Shelton (2001) show that case‐study work on the question of structural adjustment is systematically biased insofar as researchers tend to focus on disaster cases—those where structural adjustment is associated with very poor health and human development outcomes. These cases, often located in sub‐Saharan Africa, are by no means representative of the entire population. Consequently, scholarship on the question of structural adjustment is highly skewed in a particular ideological direction (against neoliberalism) (see also Gerring, Thacker, and Moreno 2005) .

These examples might be multiplied many times. Indeed, for many topics the most‐studied cases are acknowledged to be less than representative. It is worth reflecting upon the fact that our knowledge of the world is heavily colored by a few “big” (populous, rich, powerful) countries, and that a good portion of the disciplines of economics, political science, and sociology are built upon scholars' familiarity with the economics, political science, and sociology of one country, the United States. 23 Case‐study work is particularly prone to problems of investigator bias since so much rides on the researcher's selection of one (or a few) cases. Even if the investigator is unbiased, her sample may still be biased simply by virtue of “random” error (which may be understood as measurement error, error in the data‐generation process, or as an underlying causal feature of the universe).

There are only two situations in which a case‐study researcher need not be concerned with the representativeness of her chosen case. The first is the influential case research design, where a case is chosen because of its possible influence on a cross‐case model, and hence is not expected to be representative of a larger sample. The second is the deviant‐case method, where the chosen case is employed to confirm a broader cross‐case argument to which the case stands as an apparent exception. Yet even here the chosen case is expected to be representative of a broader set of cases—those, in particular, that are poorly explained by the extant model.

In all other circumstances, cases must be representative of the population of interest in whatever ways might be relevant to the proposition in question. Note that where a researcher is attempting to disconfirm a deterministic proposition the question of representativeness is perhaps more appropriately understood as a question of classification: Is the chosen case appropriately classified as a member of the designated population? If so, then it is fodder for a disconfirming case study.

If the researcher is attempting to confirm a deterministic proposition, or to make probabilistic arguments about a causal relationship, then the problem of representativeness is of the more usual sort: Is case A unit‐homogeneous relative to other cases in the population? This is not an easy matter to test. However, in a large‐ N context the residual for that case (in whatever model the researcher has greatest confidence in) is a reasonable place to start. Of course, this test is only as good as the model at hand. Any incorrect specifications or incorrect modeling procedures will likely bias the results and give an incorrect assessment of each case's “typicality.” In addition, there is the possibility of stochastic error, errors that cannot be modeled in a general framework. Given the explanatory weight that individual cases are asked to bear in a case‐study analysis, it is wise to consider more than just the residual test of representativeness. Deductive logic and an in‐depth knowledge of the case in question are often more reliable tools than the results of a cross‐case model.

In any case, there is no dispensing with the question. Case studies (with the two exceptions already noted) rest upon an assumed synecdoche: The case should stand for a population. If this is not true, or if there is reason to doubt this assumption, then the utility of the case study is brought severely into question.

Fortunately, there is some safety in numbers. Insofar as case‐study evidence is combined with cross‐case evidence the issue of sample bias is mitigated. Indeed, the suspicion of case‐study work that one finds in the social sciences today is, in my view, a product of a too‐literal interpretation of the case‐study method. A case study tout court is thought to mean a case study tout seul . Insofar as case studies and cross‐case studies can be enlisted within the same investigation (either in the same study or by reference to other studies in the same subfield), problems of representativeness are less worrisome. This is the virtue of cross‐level work, a.k.a. “triangulation.”

11 Ambiguities

Before concluding, I wish to draw attention to two ambiguities in case‐selection strategies in case‐study research. The first concerns the admixture of several case‐ selection strategies. The second concerns the changing status of a case as a study proceeds.

Some case studies follow only one strategy of case selection. They are typical , diverse , extreme , deviant , influential , crucial , pathway , most‐similar , or most‐different research designs, as discussed. However, many case studies mix and match among these case‐selection strategies. Indeed, insofar as all case studies seek representative samples, they are always in search of “typical” cases. Thus, it is common for writers to declare that their case is, for example, both extreme and typical; it has an extreme value on X   1 or Y but is not, in other respects, idiosyncratic. There is not much that one can say about these combinations of strategies except that, where the cases allow for a variety of empirical strategies, there is no reason not to pursue them. And where the same cases can serve several functions at once (without further effort on the researcher's part), there is little cost to a multi‐pronged approach to case analysis.

The second issue that deserves emphasis is the changing status of a case during the course of a researcher's investigation—which may last for years, if not decades. The problem is acute wherever a researcher begins in an exploratory mode and proceeds to hypothesis‐testing (that is, she develops a specific X   1 / Y proposition) or where the operative hypothesis or key control variable changes (a new causal factor is discovered or another outcome becomes the focus of analysis). Things change. And it is the mark of a good researcher to keep her mind open to new evidence and new insights. Too often, methodological discussions give the misleading impression that hypotheses are clear and remain fixed over the course of a study's development. Nothing could be further from the truth. The unofficial transcripts of academia— accessible in informal settings, where researchers let their guards down (particularly if inebriated)—are filled with stories about dead‐ends, unexpected findings, and drastically revised theory chapters. It would be interesting, in this vein, to compare published work with dissertation prospectuses and fellowship applications. I doubt if the correlation between these two stages of research is particularly strong.

Research, after all, is about discovery, not simply the verification or falsification of static hypotheses. That said, it is also true that research on a particular topic should move from hypothesis generating to hypothesis‐testing. This marks the progress of a field, and of a scholar's own work. As a rule, research that begins with an open‐ended ( X ‐ or Y ‐centered) analysis should conclude with a determinate X   1 / Y hypothesis.

The problem is that research strategies that are ideal for exploration are not always ideal for confirmation. The extreme‐case method is inherently exploratory since there is no clear causal hypothesis; the researcher is concerned merely to explore variation on a single dimension ( X or Y ). Other methods can be employed in either an open‐ ended (exploratory) or a hypothesis‐testing (confirmatory/disconfirmatory) mode. The difficulty is that once the researcher has arrived at a determinate hypothesis the originally chosen research design may no longer appear to be so well designed.

This is unfortunate, but inevitable. One cannot construct the perfect research design until (a) one has a specific hypothesis and (b) one is reasonably certain about what one is going to find “out there” in the empirical world. This is particularly true of observational research designs, but it also applies to many experimental research designs: Usually, there is a “good” (informative) finding, and a finding that is less insightful. In short, the perfect case‐study research design is usually apparent only ex post facto .

There are three ways to handle this. One can explain, straightforwardly, that the initial research was undertaken in an exploratory fashion, and therefore not constructed to test the specific hypothesis that is—now—the primary argument. Alternatively, one can try to redesign the study after the new (or revised) hypothesis has been formulated. This may require additional field research or perhaps the integration of additional cases or variables that can be obtained through secondary sources or through consultation of experts. A final approach is to simply jettison, or de‐emphasize, the portion of research that no longer addresses the (revised) key hypothesis. A three‐case study may become a two‐case study, and so forth. Lost time and effort are the costs of this downsizing.

In the event, practical considerations will probably determine which of these three strategies, or combinations of strategies, is to be followed. (They are not mutually exclusive.) The point to remember is that revision of one's cross‐case research design is normal and perhaps to be expected. Not all twists and turns on the meandering trail of truth can be anticipated.

12 Are There Other Methods of Case Selection?

At the outset of this chapter I summarized the task of case selection as a matter of achieving two objectives: representativeness (typicality) and variation (causal leverage). Evidently, there are other objectives as well. For example, one wishes to identify cases that are independent of each other. If chosen cases are affected by each other (sometimes known as Galton's problem or a problem of diffusion), this problem must be corrected before analysis can take place. I have neglected this issue because it is usually apparent to the researcher and, in any case, there are no simple techniques that might be utilized to correct for such biases. (For further discussion of this and other factors impinging upon case selection see Gerring 2001 , 178–81.)

I have also disregarded pragmatic/logistical issues that might affect case selection. Evidently, case selection is often influenced by a researcher's familiarity with the language of a country, a personal entrée into that locale, special access to important data, or funding that covers one archive rather than another. Pragmatic considerations are often—and quite rightly—decisive in the case‐selection process.

A final consideration concerns the theoretical prominence of a particular case within the literature on a subject. Researchers are sometimes obliged to study cases that have received extensive attention in previous studies. These are sometimes referred to as “paradigmatic” cases or “exemplars” ( Flyvbjerg 2004 , 427).

However, neither pragmatic/logistical utility nor theoretical prominence qualifies as a methodological factor in case selection. That is, these features of a case have no bearing on the validity of the findings stemming from a study. As such, it is appropriate to grant these issues a peripheral status in this chapter.

One final caveat must be issued. While it is traditional to distinguish among the tasks of case selection and case analysis, a close look at these processes shows them to be indistinct and overlapping. One cannot choose a case without considering the sort of analysis that it might be subjected to, and vice versa. Thus, the reader should consider choosing cases by employing the nine techniques laid out in this chapter along with any considerations that might be introduced by virtue of a case's quasi‐experimental qualities, a topic taken up elsewhere ( Gerring 2007 , ch. 6 ).

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Gujarati (2003) ; Kennedy (2003) . Interestingly, the potential of cross‐case statistics in helping to choose cases for in‐depth analysis is recognized in some of the earliest discussions of the case‐study method (e.g. Queen 1928 , 226).

This expands on Mill (1843/1872 , 253), who wrote of scientific enquiry as twofold: “either inquiries into the cause of a given effect or into the effects or properties of a given cause.”

This method has not received much attention on the part of qualitative methodologists; hence, the absence of a generally recognized name. It bears some resemblance to J. S. Mill's Joint Method of Agreement and Difference ( Mill 1843/1872 ), which is to say a mixture of most‐similar and most‐different analysis, as discussed below. Patton (2002 , 234) employs the concept of “maximum variation (heterogeneity) sampling.”

More precisely, George and Smoke (1974 , 534, 522–36, ch. 18 ; see also discussion in Collier and Mahoney 1996 , 78) set out to investigate causal pathways and discovered, through the course of their investigation of many cases, these three causal types. Yet, for our purposes what is important is that the final sample includes at least one representative of each “type.”

For further examples see Collier and Mahoney (1996) ; Geddes (1990) ; Tendler (1997) .

Traditionally, methodologists have conceptualized cases as having “positive” or “negative” values (e.g. Emigh 1997 ; Mahoney and Goertz 2004 ; Ragin 2000 , 60; 2004 , 126).

Geddes (1990) ; King, Keohane, and Verba (1994) . See also discussion in Brady and Collier (2004) ; Collier and Mahoney (1996) ; Rogowski (1995) .

The exception would be a circumstance in which the researcher intends to disprove a deterministic argument ( Dion 1998 ).

Geddes (2003 , 131). For other examples of casework from the annals of medicine see “Clinical reports” in the Lancet , “Case studies” in Canadian Medical Association Journal , and various issues of the Journal of Obstetrics and Gynecology , often devoted to clinical cases (discussed in Jenicek 2001 , 7). For examples from the subfield of comparative politics see Kazancigil (1994) .

For a discussion of the important role of anomalies in the development of scientific theorizing see Elman (2003) ; Lakatos (1978) . For examples of deviant‐case research designs in the social sciences see Amenta (1991) ; Coppedge (2004) ; Eckstein (1975) ; Emigh (1997) ; Kendall and Wolf (1949/1955) .

For examples of the crucial‐case method see Bennett, Lepgold, and Unger (1994) ; Desch (2002) ; Goodin and Smitsman (2000) ; Kemp (1986) ; Reilly and Phillpot (2003) . For general discussion see George and Bennett (2005) ; Levy (2002) ; Stinchcombe (1968 , 24–8).

A third position, which purports to be neither Popperian or Bayesian, has been articulated by Mayo (1996 , ch. 6 ). From this perspective, the same idea is articulated as a matter of “severe tests.”

It should be noted that Tsai's conclusions do not rest solely on this crucial case. Indeed, she employs a broad range of methodological tools, encompassing case‐study and cross‐case methods.

See also the discussion in Eckstein (1975) and Lijphart (1969) . For additional examples of case studies disconfirming general propositions of a deterministic nature see Allen (1965); Lipset, Trow, and Coleman (1956) ; Njolstad (1990) ; Reilly (2000–1) ; and discussion in Dion (1998) ; Rogowski (1995) .

Granted, insofar as case‐study analysis provides a window into causal mechanisms, and causal mechanisms are integral to a given theory, a single case may be enlisted to confirm or disconfirm a proposition. However, if the case study upholds a posited pattern of X/Y covariation, and finds fault only with the stipulated causal mechanism, it would be more accurate to say that the study forces the reformulation of a given theory, rather than its confirmation or disconfirmation. See further discussion in the following section.

Sometimes, the most‐similar method is known as the “method of difference,” after its inventor ( Mill 1843/1872 ). For later treatments see Cohen and Nagel (1934) ; Eggan (1954) ; Gerring (2001 , ch. 9 ); Lijphart (1971 ; 1975) ; Meckstroth (1975) ; Przeworski and Teune (1970) ; Skocpol and Somers (1980) .

For good introductions see Ho et al. (2004) ; Morgan and Harding (2005) ; Rosenbaum (2004) ; Rosenbaum and Silber (2001) . For a discussion of matching procedures in Stata see Abadie et al. (2001) .

The most‐different method is also sometimes referred to as the “method of agreement,” following its inventor, J. S. Mill (1843/1872) . See also De Felice (1986) ; Gerring (2001 , 212–14); Lijphart (1971 ; 1975) ; Meckstroth (1975) ; Przeworski and Teune (1970) ; Skocpol and Somers (1980) . For examples of this method see Collier and Collier (1991/2002) ; Converse and Dupeux (1962) ; Karl (1997) ; Moore (1966) ; Skocpol (1979) ; Yashar (2005 , 23). However, most of these studies are described as combining most‐similar and most‐different methods.

In the following discussion I treat the terms social capital, civil society, and civic engagement interchangeably.

E.g. Collier and Collier (1991/2002) ; Karl (1997) ; Moore (1966) ; Skocpol (1979) ; Yashar (2005 , 23). Karl (1997) , which affects to be a most‐different system analysis (20), is a particularly clear example of this. Her study, focused ostensibly on petro‐states (states with large oil reserves), makes two sorts of inferences. The first concerns the (usually) obstructive role of oil in political and economic development. The second sort of inference concerns variation within the population of petro‐states, showing that some countries (e.g. Norway, Indonesia) manage to avoid the pathologies brought on elsewhere by oil resources. When attempting to explain the constraining role of oil on petro‐states, Karl usually relies on contrasts between petro‐states and nonpetro‐states (e.g. ch. 10 ). Only when attempting to explain differences among petro‐states does she restrict her sample to petro‐states. In my opinion, very little use is made of the most‐different research design.

This was recognized, at least implicitly, by Mill (1843/1872 , 258–9). Skepticism has been echoed by methodologists in the intervening years (e.g. Cohen and Nagel 1934 , 251–6; Gerring 2001 ; Skocpol and Somers 1980 ). Indeed, explicit defenses of the most‐different method are rare (but see De Felice 1986 ).

Another way of stating this is to say that X is a “nontrivial necessary condition” of Y .

Wahlke (1979 , 13) writes of the failings of the “behavioralist” mode of political science analysis: “It rarely aims at generalization; research efforts have been confined essentially to case studies of single political systems, most of them dealing …with the American system.”

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Case selection and causal inferences in qualitative comparative research

Thomas plümper.

1 Department of Socioeconomics, Vienna University of Economics and Business, Vienna, Austria

Vera E. Troeger

2 Department of Economics, University of Warwick, Coventry, United Kingdom

Eric Neumayer

3 Department of Geography and Environment, London School of Economics and Political Science, London, United Kingdom

Associated Data

Replication files for the Monte Carlo simulations can be accessed here: Troeger, Vera Eva; Plümper, Thomas; Neumayer, Eric, 2017, "Replication Data for: Case selection and causal inferences in qualitative comparative research", doi: 10.7910/DVN/3H5EDP , Harvard Dataverse, V1.

Traditionally, social scientists perceived causality as regularity. As a consequence, qualitative comparative case study research was regarded as unsuitable for drawing causal inferences since a few cases cannot establish regularity. The dominant perception of causality has changed, however. Nowadays, social scientists define and identify causality through the counterfactual effect of a treatment. This brings causal inference in qualitative comparative research back on the agenda since comparative case studies can identify counterfactual treatment effects. We argue that the validity of causal inferences from the comparative study of cases depends on the employed case-selection algorithm. We employ Monte Carlo techniques to demonstrate that different case-selection rules strongly differ in their ex ante reliability for making valid causal inferences and identify the most and the least reliable case selection rules.

Introduction

We demonstrate that the validity of causal inferences based on the qualitative comparison of cases depends on the data-generating process and on the choice of case-selection algorithm. While the first factor is beyond the influence of scientists, researchers can freely choose the algorithm that determines the selection of cases. Of course, methodologists have long since been aware of the importance of case-selection for qualitative comparative research [ 1 , 2 , 3 ]. One can trace back systematic theoretical and methodological reasoning on case-selection to at least John Stuart Mill [ 4 ]. After all this time, one might expect that the optimal case-selection algorithms are known. Yet, this is only partially the case. We offer one of the first rigorous analyses of the relative performance of both simple and more complex case-selection rules under conditions of relevance to real world comparative research [ 5 ].

Specifically, we vary the size of the total set of cases from which specific cases are selected, we vary the degrees to which the causal factor of interest is correlated with confounding factors, and we vary the “signal-to-noise ratio”, that is, the (relative) strength of the effect of the causal factor of interest. Using a Monte Carlo design we compare the relative performance of 11 case-selection algorithms, partly following suggestions of qualitative methodologists and partly derived from common practice in comparative case analyses. The very best case-selection algorithm results in an estimated average effect that is almost a hundred times closer to the true effect than the worst algorithm. We also evaluate the conditions conducive to higher validity of causal inferences from qualitative comparative research. We find that the best selection algorithms exhibit relatively high ex ante reliability for making valid inferences if: a) the explanatory variable of interest exerts a strong influence on the dependent variable relative to random noise and confounding factors, b) the variable of interest is not too strongly correlated with confounding variables, and c) the dependent variable is not dichotomous. More importantly, while the best algorithms are still fairly reliable even in the presence of strong stochastic influences on the dependent variable and other complications, the worst algorithms are highly unreliable even if the conditions are met under which qualitative comparative research works best.

Our research contributes to both qualitative and quantitative methodological debates. Quantitative researchers assume that it is impossible to derive valid causal inferences from qualitative comparative research methods. However, we argue that this assumption is outdated because the concept of causality as regularity [ 6 , 4 , 7 ] has been superseded by the concept of causality as counterfactual effect [ 8 , 9 , 10 ]. In fact, the counterfactual concept of causation requires only a single case for causal inference if only it were possible to observe the counterfactual [ 11 , 12 , 13 ]. In the absence of directly observable counterfactual outcomes, the closest methodological equivalents according to the ‘identification school’ are randomization of treatment [ 14 ] and stratification of treatment and control group [ 15 ] through case-selection. It is this latter research strategy of rule- or model-based case-selection that demands a re-evaluation of qualitative comparative designs.

The logic of causal inference typically invoked by quantitative methodologists therefore also applies to qualitative comparative methods: if two or more cases are identical in all relevant dimensions but vary in the treatment, causal inference is internally valid. In addition, our research demonstrates that if these two cases are sampled so that the difference in the treatment is maximized the precision of the computed causal effect is large. We understand of course that these optimal conditions often do not exist and that selected cases vary in more dimensions than the treatment effect. Analyzing how different case-selection rules perform as a function of different conditions in which they must operate is exactly the purpose of our contribution.

As for the debate amongst qualitative methodologists, our results first and foremost speak to qualitative comparative researchers who, in the tradition of John Stuart Mill, draw inferences from the comparison of two sufficiently similar cases that vary in respect to the variable of interest (the ‘treatment’). Yet, the research design logic supported by our results also applies to scholars who compare a single case at two or more different points in time with a ‘treatment’ occurring in between the first and the last observation of the selected single case. These research designs are comparative in nature, and thus our findings that inferences are most likely to be valid if researchers maximize the variance of the variable of interest and minimize the variance of the confounding factors for selecting the case or cases they analyze over time also holds for a comparison of two different observations in time of a single case.

Yet, our research also contrasts with some of the acquired wisdom of qualitative methodologists. We agree that qualitative research, including the in-depth study of one or more cases and the comparative study of cases, can serve many other purposes and are, arguably, better suited for inductive purposes such as theory and concept development [ 16 , 17 ]. Qualitative research often seeks to generate ideas about the data-generating process so that little knowledge of the data-generating process can be assumed to exist prior to the case selection. Clearly, the logic of case selection for deductive causal inference research differs from the logic of case selection for inductive research. We therefore do not believe that our results can or indeed should be extended to inductive research. Importantly, however, many empirical qualitative researchers do make causal inferences and generalize their findings from the analyzed cases to a broader population. Our analysis enables those qualitative researchers who do wish to make causal inferences based on the comparative analysis of cases to understand how case-selection rules differ with respect to their ex ante reliability for detecting the direction and strength of a causal effect. Crucially, given limited knowledge about the data-generating process, we show that the relatively best-performing algorithms remain best-performing no matter what the underlying data-generating process (of those we have analyzed).

Qualitative researchers might struggle with a second aspect of our research design. Qualitative comparative researchers hardly ever estimate the strength of an effect and thus an analysis of effect strengths must seem irrelevant for them (but see [ 18 ]). Yet, we do not compute the effect strength from a comparison of two cases to tempt qualitative researchers to quantify effect strengths. We merely compute the effect strength and compare it to the assumed true effect size to have an indicator against which we can judge the ex ante reliability of selection algorithms. Computing the effect size is a tool, not the goal. Even if qualitative comparative researchers only intend to make inferences on the direction of a causal effect, they should agree that the expected deviation of an implied effect strength estimate from the truth–called root mean squared error by the quantitative tribe–is a good indicator for the relative ex ante reliability of case-selection algorithms: The larger this deviation, the more likely that even the inferred direction of an effect is wrong.

The paper is organized as follows: the next section shows that the now dominant modern concept of causality as counterfactual analysis implies that one can make causal inferences based on qualitative comparative analysis. One cannot make such inferences with certainty, however, and the validity of inferences will crucially depend on how cases are selected. We review what methodologists have advised on the selection of cases in qualitative comparative research in section 3. This informs our choice of selection algorithms that we subject to Monte Carlo analysis, though we also add some original algorithms to test whether and, if so, how much better they can perform. Section 4 describes these algorithms, the Monte Carlo design and how we evaluate the relative performance of the case-selection algorithms. Section 5 presents results from the Monte Carlo simulations.

Causal inference and qualitative comparative research

Causality as regularity dominated the philosophy of science at least from Hume to Popper. Hume [ 5 ] argued that scientists cannot have knowledge of causality beyond observed regularities in associations of events. He therefore suggests inferring causality through a systematic comparison of situations in which the presumed causal factor is present or absent, or varies in strength. The concept of causality as regularity became the central element of Hempel and Oppenheim’s [ 19 ] deductive-nomological model of scientific explanation. Hempel was also the first to develop the concept further to include statistical inference [ 20 ]. In Popper’s conception of a non-degenerative research program [ 7 ], a single falsification effectively leads to the rejection of the tested hypothesis or, worse, the theory from which the hypothesis derives. The “regularity” perspective culminates in the definition of science as “unbroken, natural regularity” [ 21 ].

This “strict regularity” concept of causality had ambiguous implications for comparative social science qualitative researchers’ ability to make causal inferences. On the one hand, the analysis of a small number of cases cannot establish regularity. On the other hand, if, conversely, a single deviant case suffices to refute a causal claim or even a theory, as Popper believes, then strength in numbers does not exist [ 22 , 23 , 17 ]. The “strict regularity” perspective is dead, however, because a) not all regularities are causal (“correlation is not causation”) and b) causality can be probabilistic rather than deterministic and can thus exist without strict regularity.

Probabilistic causal mechanisms paved the way for an interpretation of regularity as statistical regularity. Yet, not even the brilliant idea of statistical inference saved the regularity concept of causality. If correlation is not causality, then high correlation does not imply causality either and low correlation and statistical insignificance may indicate low-probability causality and a lack of sufficient variation rather than the absence of causality. Eventually, this insight eliminated the support for the causality as regularity view.

Over the last three decades, the concept of causality as regularity was replaced by the counterfactual concept of causality, also called the potential outcomes framework. Its understanding of causality is tautological: causality exists if a cause exerts a causal effect on the outcome, and a cause exerts a causal effect on the outcome when the relation is causal. This tautology seems to be the main reason why scholars advancing the counterfactual perspective [ 9 , 10 , 24 , 25 ] focus on causal inference and the identification of causal effects rather than on causality itself [ 24 ].

According to the counterfactual concept of causality, causality is perfectly identified if one observes the outcome given treatment and the outcome given no treatment at the same time for the same person(s). Naturally, this is impossible. Hence, a counterfactual analysis starts with a ‘missing data’ problem and then immediately turns to ‘second-best’ options for inferring causality. If one cannot observe the potential or counterfactual outcome for any one single case, then one needs to resort to comparing the outcomes of different cases. This raises the challenge that either one must make sure that the cases compared are equal or sufficiently similar in all dimensions that matter or that one can render the influence of all potential confounders irrelevant. Otherwise, no causal effect has been ‘identified’.

The approach generally preferred by identification scholars–what they call the “gold standard”–aspires to render potential confounders irrelevant by randomizing treatment across a large number of cases in a controlled experiment (but see [ 25 , 26 ]). Though practically all actual experiments fall way short of the ideal of experimental designs, the randomization of treatments in a sample where N approaches infinity guarantees that the treatment will be uncorrelated with both observable and, crucially, unobservable confounders. Because of this lack of correlation with any potential confounder, any observable difference in outcomes between the two groups must be due to the treatment. If one assumes causal homogeneity among cases and assumes away that potential confounders might condition the effect of treatment, then ideal experiments will not only have identified a cause-effect relationship but will also allow the calculation of the unbiased effect size.

Clearly, from the experimentalist viewpoint, qualitative small-N comparative research is useless for causal inferences. In fact, so is everything else. Its diehard proponents explicitly argue that experiments are a necessary condition for causal inference. For example, Light, Singer, and Willett [ 27 ] claim that “to establish a causal link, you must conduct an experiment (…). Only experimental inquiries allow you to determine whether a treatment causes an outcome to change.” This claim wrongly assumes that identification is a necessary condition for causal inference, whereas in fact perfect identification is only a necessary condition for making causal inferences that are valid with certainty. The idea that one can only make causal inferences if scientists are certain about having identified a cause-effect relationship via experiments is absurd, however. If the claim was correct, scientists would not be able to infer that more education causes higher lifetime income, or that smoking causes lung cancer. For that matter, social scientists would not be able to explore much of interest. The quest for causal inference in the social sciences is not about certainty; it is about how to deal with uncertainty and how much uncertainty about the validity of inferences can be tolerated.

More importantly, making certainty a prerequisite for causal inference runs into a logical problem for the social sciences because experiments that social scientists are able to conduct do not generate inferences that are valid with certainty. Even ignoring causal heterogeneity and potential conditionalities [ 28 ], the confounding-factors problem can only be solved asymptotically, that is, by increasing the sample size to infinity. With a finite number of participants, randomization of treatment does not suffice to render treatment uncorrelated to unobserved confounders like mood, experience, knowledge, or intelligence, and often to even observed confounders like age, sex, income, or education. As a remedy, many experimenters control for observable differences in addition to randomizing treatment. Since it is impossible to control for all factors that influence human behavior, not least because some of them may be unobserved, the problem of confounders can be reduced but not eliminated by experiments. Yet, if experiments only increase the probability that causal inferences are correct, then the strict dichotomy between experiments and all other research methods that Light, Singer, and Willett make is unjustified.

The second approach to solving the “missing data” problem in the counterfactual concept of causality argues that causal effects are identified if cases can be selected so as to guarantee that all the relevant properties of the treatment group exactly match the properties of the control group [ 29 , 30 , 31 ]. Identification via selection or matching on the properties of the treatment and control groups requires perfect knowledge of all the factors that influence outcomes and also that one can match cases on these properties. As with experiments, falling short of this ideal will mean that a causal effect has not been identified with certainty, but does not render causal inference impossible. For experimentalists, matching is far inferior to experiments because they doubt one can know all the relevant properties (one can know the so-called data-generating process) and even if one could know these properties, one cannot measure all of these properties, some of which are unobservable, and thus one cannot match on them.

This second approach substitutes impossible counterfactual analyses with a possible analysis of cases that have been carefully selected to be homogeneous with respect to confounding variables. This strategy is obviously encouraging for causal inference based on case comparison. Nothing in this matching approach suggests that the validity of causal inferences depends on the number of cases. If cases are homogeneous, causal inferences based on small-N qualitative comparative methods become possible, and the validity of these causal inferences depends on the employed selection rule.

Qualitative comparative researchers have always made arguments that closely resemble matching [ 5 ]: if two cases are identical in all relevant dimensions but vary in the dimension of interest (the treatment), then it is possible to directly infer causality and to compute a causal effect size. This possibility does not imply that causal inference from qualitative comparative research is optimal or easy, however. Of course, there is the issue of knowing all relevant dimensions and finding at least two cases which are identical in all these dimensions. There are other difficulties, too: First, if causal processes are stochastic, as they are bound to be, then a single small-N comparative analysis, which cannot control for noise and random errors, will not reveal the truth but some random deviation from the truth. Matching cases in a quantitative analysis with large N therefore can be superior—though the greater difficulty of adequately matching a larger number of cases means that any positive effect on the validity of causal inferences from efficiency gains may be defeated by the negative effect due to problems in matching. Second, perfect homogeneity among cases on all confounding factors can only be achieved if researchers know the true data-generating process, which is unlikely to be the case even if qualitative researchers argue that their in-depth study of cases allow them to know much more about this process than quantitative researchers do [ 32 , 33 ]. In the absence of knowledge of the true data-generating process, qualitative comparative researchers should make sure that selected cases do not differ in respect to known strong confounding factors. The potential for bias grows with the strength of the potentially confounding factor (for which no controls have been included), and the size of the correlation between the variable of interest and the confounder.

Case-selection and qualitative comparisons

Methodological advice on the selection of cases in qualitative research stands in a long tradition. John Stuart Mill in his A System of Logic , first published in 1843, proposed five methods meant to enable researchers to make causal inferences: the method of agreement, the method of difference, the double method of agreement and difference, the method of residues, and the method of concomitant variation [ 4 ]. Methodologists have questioned and criticized the usefulness and general applicability of Mill’s methods [ 34 , 35 ]. However, without doubt Mill’s proposals had a major and lasting impact on the development of the two most prominent modern methods, namely the “most similar” and “most different” comparative case-study designs [ 1 , 36 , 37 ].

Yet, as Seawright and Gerring [ 3 ] point out, these and other methods of case-selection are “poorly understood and often misapplied”. Qualitative researchers mean very different things when they invoke the same terms “most similar” or “most different” and usually the description of their research design is not precise enough to allow readers to assess exactly how cases have been chosen. Seawright and Gerring have therefore provided a formal definition and classification of these and other techniques of case-selection. They [ 3 ] suggest that “in its purest form” the “most similar” design chooses cases which appear to be identical on all controls ( z ) but different in the variable of interest ( x ). Lijphart [ 1 ] suggested what might be regarded a variant of this method that asks researchers to maximize “the ratio between the variance of the operative variables and the variance of the control variables”.

Naturally, the “most similar” technique is not easily applied because researchers find it difficult to match cases such that they are identical on all control variables. As Seawright and Gerring [ 3 ] concede: “Unfortunately, in most observational studies, the matching procedure described previously–known as exact matching–is impossible.” This impossibility has three sources: first, researchers usually do not know the true model and thus cannot match on all control variables. Second, even if known to affect the dependent variable, many variables remain unobserved. And third, even if all necessary pieces of information are available, two cases that are identical in all excluded variables may not exist.

Qualitative comparative researchers prefer the “most similar” technique, despite ambiguity in its definition and practical operationalization, to its main rival, the “most different” design. Seawright and Gerring [ 3 ] believe that this dominance of “most similar” over “most different” design is well justified. Defining the “most different” technique as choosing two cases that are identical in the outcome y and in the main variable of interest x but different in all control variables z , they argue that this technique does not generate much leverage. They criticize three points: first, the chosen cases never represent the entire population (if x can in fact vary in the population). Second, the lack of variation in x renders it impossible to identify causal effects. And third, elimination of rival hypotheses is impossible. As Gerring [ 38 ] formulates poignantly: “There is little point in pursuing cross-unit analysis if the units in question do not exhibit variation on the dimensions of theoretical interest and/or the researcher cannot manage to hold other, potentially confounding, factors constant.”

For comparative case studies, Seawright and Gerring also identify a third selection technique, which they label the “diverse” technique. It selects cases so as to “represent the full range of values characterizing X, Y, or some particular X/Y relationship” [ 3 ]. This definition is somewhat ambiguous and vague (“some particular relationship”), but one of the selection algorithms used below in our MC simulations captures the essence of this technique by simultaneously maximizing variation in y and x .

Perhaps surprisingly, King, Keohane and Verba’s [ 39 ] seminal contribution to qualitative research methodology discusses case-selection only from the perspective of unit homogeneity–broadly understood as constant effect assumption–and selection bias–defined as non-random selection of cases that are not statistically representative of the population. Selecting cases in a way that does not avoid selection bias negatively affects the generalizability of inferences. Random sampling from the population of cases would clearly avoid selection bias. Thus, given the prominence of selection bias in King et al.’s discussion of case-selection, the absence of random sampling in comparative research may appear surprising. But it is not. Random selection of cases leads to inferences which are correct on average when the number of conducted case studies approaches infinity, but the sampling deviation is extremely large. As a consequence, the reliability of single studies of randomly sampled cases remains low. The advice King and his co-authors give on case-selection, then, lends additional credibility to commonly chosen practices by qualitative comparative researchers, namely to avoid truncation of the dependent variable, to avoid selection on the dependent variable, while at the same time selecting according to the categories of the “key causal explanatory variable”. King et al. [ 39 ] also repeatedly claim that increasing the number of observations makes causal inferences more reliable. Qualitative methodologists have argued that this view, while correct in principle, does not do justice to qualitative research [ 40 , 41 , 42 ]. More importantly, they also suggest that the extent to which the logic of quantitative research can be superimposed on qualitative research designs has limits.

While there is a growing consensus on the importance of case-selection for comparative research, as yet very little overall agreement has emerged concerning the use of central terminology and the relative advantages of different case-selection rules. Scholars largely agree that random sampling is unsuitable for qualitative comparative research (but see [ 5 ]), but disagreement on sampling on the dependent variable, and the appropriate use of information from observable confounding factors persists. Our Monte Carlo analysis will shed light on this issue by exploring which selection algorithms are best suited under a variety of assumptions about the data-generating process.

A Monte Carlo analysis of case-selection algorithms

In statistics, Monte Carlo experiments are employed to compare the performance of estimators. The term Monte Carlo experiments describes a broad set of techniques that randomly draw values from a probability distribution to add error to a predefined equation that serves as data-generating process. Since the truth is known, it is straightforward to compare the estimated or computed effects to the true effects. An estimator performs the better the smaller the average distance between the estimated effect and the truth. This average distance is usually called the root mean squared error.

Our Monte Carlo experiments follow this common practice in statistics and merely replace the estimators by a case-selection rule or algorithm. We compare selection rules commonly used in applied qualitative comparative research, as well as various simple permutations and extensions. Without loss of generality, we assume a data-generating process in which the dependent variable y is a linear function of a variable of interest x , a control variable z and an error term ε . Since we can interpret z as a vector of k control variables, we can generalize findings to analyses with multiple controls.

Case-selection algorithms

Ignoring for the time being standard advice against sampling on the dependent variable, researchers might wish to maximize variation of y , maximize variation of x , minimize variation of z or some combination thereof. Employing addition and subtraction, the two most basic functions to aggregate information on more than one variable, leads to seven permutations of information from which to choose; together with random sampling this results in eight simple case-selection algorithms–see Table 1 . The mathematical description of the selection algorithms, as shown in the last column of the table, relies on the set-up of the Monte Carlo analyses (described in the next section). In general, for each variable we generate Euclidean distance matrices, which are N×N matrices representing the difference or distance in a set of cases i and j forming the case-dyad ij . Starting from these distance matrices, we select two cases that follow a specific selection rule. For example, max(x) only considers the explanatory variable of interest, thereby ignoring the distance matrices for the dependent variable y and the control variable z . With max(x) , we select the two cases that represent the cell of the distance matrix with the largest distance value. We refrain from analyzing case-selection algorithms for qualitative research with more than two cases. Note, however, that all major results we show here carry over to selecting more than two cases based on a single algorithm. However, we do not yet know whether all our results carry over to analyses of more than two cases when researchers select cases based on different algorithms–a topic we will revisit in future research.

Algorithm 1 does not use information (other than that a case belongs to the population), and samples cases randomly. We include this algorithm for completeness and because qualitative methodologists argue that random sampling–the gold standard for sampling in quantitative research–does not work well in small-N comparative research.

We incorporate the second algorithm–pure sampling on the dependent variable without regard to variation of either x or z –for the same completeness reason. Echoing Geddes [ 43 ], many scholars have argued that sampling on the dependent variable biases the results [ 39 , 44 , 45 ]. Geddes demonstrates that “selecting on the dependent variable” lies at the core of invalid results generated from qualitative comparative research in fields as diverse as economic development, social revolution, and inflation.

But does Geddes’s compelling critique of sampling on the dependent variable imply that applied researchers should entirely ignore information on the dependent variable when they also use information on the variable of interest or the confounding factors? Algorithms 5, 6, and 8 help us to explore this question. These rules include selection on the dependent variable in addition to selection on x and/or z . Theoretically, these algorithms should perform better than the algorithm 2, but we are more interested in analyzing how these biased algorithms perform in comparison to their counterparts, namely algorithms 3, 4, and 7, which, respectively, maximize variation of x , minimize variation of z , and simultaneously maximize variation of x and minimize variation of z , just as algorithms 5, 6 and 8 do, but this time without regard to variation of y .

Theoretically, one would expect algorithm 7 to outperform algorithms 3 and 4. Qualitative methodlogists such as Gerring and Seawright and Gerring [ 17 , 3 ] expect this outcome and we concur. Using more information must be preferable to using less information when it comes to sampling. This does not imply, however, that algorithm 7 necessarily offers the optimal selection rule for qualitative comparative research. Since information from at least two different variables has to be aggregated, researchers have at their disposal multiple possible algorithms that all aggregate information in different ways. For example, in addition to the simple unweighted sum (or difference) that we assume in Table 1 , one can aggregate by multiplying or dividing the distances, and one can also weight the individual components.

Lijphart [ 1 ] has suggested an alternative function for aggregation, namely maximizing the ratio of the variance in x and z : max[dist(x)/dist(z)] . We include Lijphart’s suggestion as our algorithm 9 even though it suffers from a simple problem which reduces its usefulness: when the variance of the control variable z is smaller than 1.0, the variance of what Lijphart calls the operative variable x becomes increasingly unimportant for case-selection (unless of course the variation of the control variables is very similar across different pairs of cases). We solve this problem by also including in the competition an augmented version of Lijphart’s suggestion. This algorithm 10 adds one to the denominator of the algorithm proposed by Lijphart: max[dist(x)/(1+dist(z))] . Observe that adding one to the denominator prevents the algorithm from converging to min[dist(z)] when dist(z) becomes small. Finally, we add a variance-weighted version of algorithm 7 as our final algorithm 11 to check whether weighting improves on the simple algorithms. Table 2 summarizes the additional analyzed algorithms that aggregate information using more complicated functions.

Note that thus far we have given the selection algorithms formal and technical labels, avoiding terminology of case-selection rules commonly used in the literature. Nevertheless, there are connections between some of the above algorithms and the terminology commonly used in the literature. For example, algorithms 2, 3 and 5 are variants of selection rules described by Seawright and Gerring [ 3 ] as “diverse” case-selection rules. Algorithms 2, 5, 6, and 8 all use information on variation of the dependent variable and are thus variants of selection on the dependent variable. More importantly, algorithms 4 and 7 as well as algorithms 9 to 11 seem to be variants of the most similar design. However, we do not call any of these algorithms “selection on the dependent variable” or “most similar”. The reason is that, as discussed above, there is a lack of consensus on terminology and different scholars prefer different labels and often mean different things when they invoke rules such as “sampling on the dependent variable” or “most similar”.

The Monte Carlo design

The use of Monte Carlo techniques may appear to be strange to qualitative researchers. However, Monte Carlo simulations are perfectly suited for the purpose of exploring the ex ante reliability of case-selection algorithms. As we have explained above, Monte Carlo simulations provide insights into the expected accuracy of inferences given certain pre-defined properties of the data-generating process. While they are commonly used to compare estimators, one can equally use them to compare the performance of different sampling rules.

Monte Carlo simulations allow us to systematically change the data-generating process, and to explore the comparative advantages of different selection algorithms depending on the assumptions we make about the data-generating process. Possible systematic changes include variation in the assumed level of correlation between explanatory variables, the relative importance of uncertainty, the level of measurement error, and so on. Unsystematic changes are modelled by repeated random draws of the error term.

Specifically, we define various data-generating processes from which we draw a number of random samples, and then select two cases from each sample according to a specific algorithm, as defined above. As a consequence of the unaccounted error process, the computed effects from the various Monte Carlo simulations will deviate somewhat from the truth. Yet, since we confront all selection algorithms to the same set of data-generating processes, including the same error processes, performance differences must result from the algorithms themselves. These differences occur because different algorithms will select different pairs of cases i and j , and, as a consequence, the computed effect and the distance of this effect from the true effect differ. Our analysis explores to what extent a comparison of two cases allows researchers to estimate the effect that one explanatory variable, called x , exerts on a dependent variable, called y . We assume that this dependent variable y is a function of x , a single control variable z , which is observed, and some error term ε : y i = βx i + γz i + ε i , where β, γ represent coefficients and ε is an iid error process. Obviously, as var( ε ) approaches zero, the data-generating process becomes increasingly deterministic. We follow the convention of quantitative methodology and assume that the error term is randomly drawn from a standard normal distribution. Note, however, that since we are not interested in asymptotic properties of case-selection algorithms, we could as well draw the error term from different distributions. This would have no consequence other than adding systematic bias to all algorithms alike. The process resembles what Gerring and McDermott [ 46 ] call a “spatial comparison” (a comparison across n observations), but our conclusions equally apply to “longitudinal” (a comparison across t periods) and “dynamic comparisons” (a comparison across n · t observations). We conducted simulations with both a continuous and a binary dependent variable. We report results for the continuous variable in detail in the next section and briefly summarize the results for the binary dependent variable with full results reported in the appendices.

There are different ways to think about the error term. First, usually scientists implicitly assume that the world is not perfectly determined and they allow for multiple equilibria which depend on random constellations or the free will of actors. In this respect, the error term accounts for the existence of behavioral randomness. Second, virtually all social scientists acknowledge the existence of systematic and unsystematic measurement error. The error term can be perceived as accounting for information that is partly uncertain. And third, the error term can be interpreted as model uncertainty–that is, as unobserved omitted variables also exerting an influence on the dependent variable. Only if randomness and free will, measurement error, and model uncertainty did not exist, would the inclusion of an error term make no sense.

We always draw x and z from a normal distribution, but, of course, alternative assumptions are possible. Given the low number of observations, it comes without loss in generality that we draw ε from a normal distribution with mean zero and standard deviation of 1.5; and, unless otherwise stated, all true coefficients take the value of 1.0; the standard deviation of variables is 1.0; correlations are 0.0; and the number of observations N, representing the size of the sample from which researchers can select cases, equals 100.

Evaluating the results from the Monte Carlo simulations

We compare the reliability of inference on effect strength. Specifically, the effect size of x on y from a comparative case study with two cases equals

where subscripts [ i , j ] represent the two selected cases. We take the root mean squared error (RMSE) as our measure for the reliability of causal inference as it reacts to both bias and inefficiency. The RMSE is defined as

This criterion not only incorporates bias (the average deviation of the computed effect from the true effect), but also accounts for inefficiency, which is a measure of the sampling variation of the computed effect that reflects the influence of random noise on the computed effect. Qualitative researchers cannot appropriately control for the influence of noise on estimates. The best they can do to account for randomness is to choose a case-selection algorithm that responds less than others to noise. Naturally, these are case-selection algorithms that make best use of information. In quantitative research, the property characterizing the best use of information is called efficiency , and we see no reason to deviate from this terminology.

Results from the Monte Carlo analysis of case-selection algorithms

We conduct three sets of MC simulations, in which we vary the parameters of the data-generating process, and evaluate the effect of this variation on the precision with which the algorithms approach the true coefficients together with the efficiency of the estimation. In each type of analysis we draw 1,000 samples from the underlying data-generating process. In the first set of simulations, we change the number of observations from which the two cases are chosen ( i = 1,…N), thereby varying the size of the sample, i.e., the total number of cases from which researchers can select two cases. In the second set of simulations, we vary the correlation between x and z –that is, the correlation between the variable of interest and the confounding factor. In the final set of simulations, we vary the variance of x and thus the effect size or explanatory power of x relative to the effect size of the confounding factor z .

Analyzing the impact of varying the number of analyzed cases on the validity of inferences in qualitative comparative research may seem strange at first glance. After all, qualitative researchers usually study a fairly limited number of cases. In fact, in our Monte Carlo analyses we generate effects by looking at a single pair of cases selected by each of the case-selection algorithms. So why should the number of cases from which we select the two cases matter? The reason is that if qualitative researchers can choose from a larger number of cases about which they have theoretically relevant information, they will be able to select a better pair of cases given the chosen algorithm. The more information researchers have before they select cases, the more reliable their inferences should thus become. In other words, N does not represent the number of cases analyzed, but the number of the total set of cases from which the analyzed cases are chosen.

By varying the correlation between x and the control variable z we can analyze the impact of confounding factors on the performance of the case-selection algorithms. With increasing correlation, inferences should become less reliable. Thereby, we look at the effect of potential model misspecification on the validity of inference in qualitative comparative research. While quantitative researchers can eliminate the potential for bias from correlated control variables by including these on the right-hand-side of the regression model, qualitative researchers have to use appropriate case-selection rules to reduce the potential for bias.

Finally, in varying the standard deviation of x we analyze the impact of varying the strength of the effect of the variable of interest on the dependent variable. The larger this relative effect size of the variable of interest, the more reliable causal inferences should become. The smaller the effect of the variable of interest x on y in comparison to the effect on y of the control or confounding variables z , the harder it is to identify the effect correctly, and the less valid the inferences become–especially when the researcher does not know the true specification of the model.

Table 3 reports the Monte Carlo results obtained when we only vary the size of the sample from which we draw the two cases we compare. In this set of simulations, we do not allow for systematic correlation between the variable of interest x and the confounding factor z . The deviations of computed effects from the true effect occur because of “normal” sampling error, and how efficiently the algorithm deals with the available information.

Note: corr(x,z) = 0, SD(x) = 1

The table displays the root mean squared error. Smaller numbers indicate higher reliability.

Observe, first, that of the basic case-selection algorithms, max(x)min(z) performs up to 100 times better with respect to the average deviation from the true effect (the root mean squared error) than the poorest-performing competitors, namely random , which draws two cases randomly from the sample, and max(y) , which purely selects on the dependent variable. The drawback from selecting on the dependent variable declines if researchers additionally take into account variation of x and/or variation of z , but these algorithms 5, 6, and 8 are typically inferior to their counterparts 3, 4, and 7, which ignore variation of the dependent variable. Accordingly, selection on the dependent variable not only leads to unreliable inferences that are likely to be wrong, it also makes other selection algorithms less reliable. Hence, researchers should not pay attention to variation in the dependent variable y when they select cases. By selecting cases on the variable of interest x while at the same time controlling for the influence of confounding factors, researchers are likely to choose cases which vary in their outcome if x indeed exerts an effect on y .

Maximizing variation of x while at the same time minimizing variation of z appears optimal. Algorithm 7 uses subtraction as a basic function for aggregating information from more than one variable. Would using a more complicated function dramatically improve the performance of case-selection? The results reported in Table 3 show that, at least for this set of simulations, this is not the case. Algorithm 7 performs roughly 10 percent better than the augmented version of Lijphart’s proposal ( augmented lijphart ), and while algorithm 11, the variance-weighted version of algorithm 7, is very slightly superior, not much separates the performance of the two.

Another interesting finding from Table 3 is that only four algorithms become systematically more reliable when the population size from which we draw two cases increases. These four algorithms are: max(x) , max(x)min(z) and its weighted variant, weighted max(x)min(z) , as well as augmented lijphart . Algorithms need to have a certain quality to generate, in expectation, improvements in the validity of causal inferences when the population size becomes larger. Random selection, for example, only improves on average if the increase in population size leads to relatively more “onliers” than “outliers”. This may be the case, but there is no guarantee. When researchers use relatively reliable case-selection algorithms, however, an increase in the size of the sample, on which information is available, improves causal inferences unless one adds extreme outliers to the sample. Inferences become more reliable if cases are selected from a larger sample of cases for which researchers have sufficient information. We are not making any normative claim about enlarging the population size, because the improvements of enlarging the population from which cases are selected has to be discounted by the deteriorations caused by an increase in case heterogeneity caused by an enlarged sample.

The results from Table 3 support King, Keohane and Verba’s [ 39 ] arguments against both random selection and sampling on the dependent variable. At first sight, our results seem to differ from Herron and Quinn’s [ 5 ] finding that “simple random sampling outperforms most methods of case selection” even when the number of analyzed cases “is as small as 5 or 7”. However, our results are consistent with Herron and Quinn’s finding that random sampling is not reliable when the number of cases is two. In fact, the number of cases required to make random sampling a viable strategy depends on the heterogeneity of cases and the signal-to-noise ratio of the causal effect of interest: the more homogeneous and stronger the effect researchers are interested in, the better the performance of random selection of cases and the lower the number of cases for sufficiently reliable inferences.

In Table 4 , we report the results of Monte Carlo simulations from varying the correlation between the variable of interest x and the confounding factor z .

Note: SD(x) = 1.0, N = 100, SD(z) = 1.0, Varying Correlation (x,z). The table displays the root mean squared error. Smaller numbers indicate higher reliability.

Note that all substantive results from Table 3 remain valid if we allow for correlation between the variable of interest and the confounding factor. In particular, algorithm 11, which weights the individual components of the best-performing simple case-selection algorithm 7, performs only very slightly better; while the performance gap between simple algorithm max(x)min(z) , based on subtraction, and the augmented Lijphart algorithm ( augmented lijphart ), which uses the ratio as aggregation function, increases only marginally. Table 4 also demonstrates that correlation between the variable of interest and confounding factors renders causal inferences from qualitative comparative research less reliable. Over all simulations and algorithms, the RMSE increases by at least 100 percent when the correlation between x and z increases from 0.0 to either -0.9 or +0.9.

Finally, we examine how algorithms respond to variation in the strength of the effect of the variable of interest. In this final set of simulations for which results are reported in Table 5 we vary the standard deviation of the explanatory factor x ; a small standard deviation indicates a small effect of x on y relative to the effect exerted from z on y . The results show that the performance of all case-selection algorithms suffers from a low “signal-to-noise” ratio. As one would expect, the smaller the effect of the variable of interest x on y relative to the effect of z on y , the less reliable the causal inferences from comparative case study research becomes. Yet, we find that the algorithms which performed best in the previous two sets of simulations also turn out to be least vulnerable to a small effect of the variable of interest. Accordingly, while inferences do become more unreliable when the effect of the variable of interest becomes small relative to the total variation of the dependent variable, comparative case studies are not simply confined to analyzing the main determinant of the phenomenon of interest if one of the top performing case-selection algorithms are used. As in the previous sets of simulations, we find that little is gained by employing more complicated functions for aggregating information from more than one variable as, for example, the ratio ( augmented lijphart ) or weighting by the variance of x and z ( weighted max(x)min(z) ). Sticking to the most basic aggregation function has little cost, if any.

Note: corr(x,z) = 0.0, N = 100, SD(z) = 1.0, Varying SD(x)

We now briefly report results from additional Monte Carlo simulations which we show in full in the appendix to the paper ( S1 File ). First, weighting x and z by their respective sample range becomes more important when the data-generating process includes correlation between x and z and the effect of x on y is relatively small (see Table A in S1 File ). In this case, weighting both the variation of x and z before using the max(x)min(z) selection rule for identifying two cases slightly increases the reliability of causal inferences.

Second, we also conducted the full range of Monte Carlo simulations with a dichotomous dependent variable (see Tables B- E in S1 File ). We find that the algorithms that perform best with a continuous dependent variable also dominate with respect to reliability when we analyze dichotomous dependent variables. Yet, causal inferences from qualitative comparative case study research become far less reliable when the dependent variable is dichotomous for all selection algorithms compared to the case of a continuous dependent variable. The root mean squared error roughly doubles for the better-performing algorithms. As a consequence, causal inferences with a binary dependent variable and an additional complication (either a non-trivial correlation between x and z or a relatively small effect of x on y ) are not reliable. Accordingly, qualitative researchers should not throw away variation by dichotomizing their dependent variable. Where the dependent variable is dichotomous, qualitative comparative research is confined to what most qualitative researchers actually do in these situations: trying to identify strong and deterministic relationships or necessary conditions [ 47 , 48 ]. In both cases, the strong deterministic effect of x on y compensates for the low level of information in the data.

Case-selection rules employed in qualitative research resemble ‘matching’ algorithms developed by identification scholars in quantitative research and thus can be employed to derive causal inferences. They also share their most important shortcoming: the extent to which causal inferences from selected samples are valid is partly determined by the extent of knowledge of the data-generating process. The more is known about the “true model”, the better researchers can select cases to maximize the ex ante reliability of their causal inferences.

Our major contribution has been to guide qualitative comparative researchers on what are the selection rules with the highest ex ante reliability for the purpose of making causal inferences under a range of conditions regarding the underlying data-generating process. The validity of causal inferences from qualitative comparative research will necessarily always be uncertain but following our guidance will allow qualitative comparative researchers to maximize the imperfect validity of their inferences.

Qualitative comparative researchers can take away six important concrete lessons from our Monte Carlo simulations: First, ceteris paribus, selecting cases from a larger set of potential cases gives more reliable results. Qualitative researchers often deal with extremely small samples. Sometimes nothing can be done to increase sample size, but where there are no binding constraints it can well be worth the effort expanding the sample from which cases can be selected. Second, for all the better-performing selection algorithms, it holds that ignoring information on the dependent variable for the purpose of selecting cases makes inferences much more reliable. Tempting though it may seem, qualitative comparative researchers should not select on the dependent variable at all. Third, selecting cases based on both the variable of interest and confounding factors improves the ex ante reliability of causal inferences in comparison to selection algorithms that consider just the variable of interest or just confounding factors–even if this means that one no longer chooses the cases that match most closely on confounding factors. These algorithms are relatively best-performing, no matter what the underlying data-generating process (of those we have analyzed). This is a crucial lesson because qualitative comparative researchers might not have much knowledge about the kind of data-generating process they are dealing with. Fourth, correlation between the variable of interest and confounding factors renders the selection algorithms less reliable. The same holds if the analyzed effect is weak. This reinforces existing views that qualitative case comparison is most suitable for studying strong and deterministic causal relationships [ 47 , 48 ]. Fifth, the reliability of case-selection rules depends on the variation in the dependent variable scholars can analyze. Accordingly, unless there are very strong over-riding theoretical or conceptual reasons, throwing away information by dichotomizing the dependent variable is a bad idea. A continuous dependent variable allows for more valid inferences; a dichotomous dependent variable should only be used if there is no alternative. Sixth, employing basic functions for aggregating information from more than one variable (such as maximizing the difference between variation of x and variation of z ) does not reduce by much the ex ante reliability of case-selection compared to more complicated aggregation functions (such as maximizing the ratio or the variance-weighted difference). The only exceptions occur if x and z are highly correlated and the effect of x on y is relatively small compared to the effect of z on y . As a general rule, one does not lose much by opting for the most basic aggregation function.

In conclusion, our Monte Carlo study is broadly consistent with the views of qualitative methodologists. After all, the best- or nearly best-performing algorithms in our analysis of alternative selection algorithms appear to be variants of the most similar design, which in turn draws on Przeworski and Teune’s [ 35 ] and Lijphart’s [ 49 ] suggestions for case-selection. However, we are the first to provide systematic evidence that upholds existing recommendations in the presence of stochastic error processes. In addition, we demonstrated that simple functions for linking variation of the explanatory variable with variation of the confounding variables perform relatively well in general. There is little reason to resort to more advanced functions unless the explanatory variable has a weak effect and is strongly correlated with the confounding variables. One important area for further analysis comes from settings in which comparative qualitative researchers assess claims about two or more causal factors interacting with each other.

Supporting information

Funding statement.

The authors received no funding for this work.

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  • What Is a Case Study? | Definition, Examples & Methods

What Is a Case Study? | Definition, Examples & Methods

Published on May 8, 2019 by Shona McCombes . Revised on November 20, 2023.

A case study is a detailed study of a specific subject, such as a person, group, place, event, organization, or phenomenon. Case studies are commonly used in social, educational, clinical, and business research.

A case study research design usually involves qualitative methods , but quantitative methods are sometimes also used. Case studies are good for describing , comparing, evaluating and understanding different aspects of a research problem .

Table of contents

When to do a case study, step 1: select a case, step 2: build a theoretical framework, step 3: collect your data, step 4: describe and analyze the case, other interesting articles.

A case study is an appropriate research design when you want to gain concrete, contextual, in-depth knowledge about a specific real-world subject. It allows you to explore the key characteristics, meanings, and implications of the case.

Case studies are often a good choice in a thesis or dissertation . They keep your project focused and manageable when you don’t have the time or resources to do large-scale research.

You might use just one complex case study where you explore a single subject in depth, or conduct multiple case studies to compare and illuminate different aspects of your research problem.

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Once you have developed your problem statement and research questions , you should be ready to choose the specific case that you want to focus on. A good case study should have the potential to:

  • Provide new or unexpected insights into the subject
  • Challenge or complicate existing assumptions and theories
  • Propose practical courses of action to resolve a problem
  • Open up new directions for future research

TipIf your research is more practical in nature and aims to simultaneously investigate an issue as you solve it, consider conducting action research instead.

Unlike quantitative or experimental research , a strong case study does not require a random or representative sample. In fact, case studies often deliberately focus on unusual, neglected, or outlying cases which may shed new light on the research problem.

Example of an outlying case studyIn the 1960s the town of Roseto, Pennsylvania was discovered to have extremely low rates of heart disease compared to the US average. It became an important case study for understanding previously neglected causes of heart disease.

However, you can also choose a more common or representative case to exemplify a particular category, experience or phenomenon.

Example of a representative case studyIn the 1920s, two sociologists used Muncie, Indiana as a case study of a typical American city that supposedly exemplified the changing culture of the US at the time.

While case studies focus more on concrete details than general theories, they should usually have some connection with theory in the field. This way the case study is not just an isolated description, but is integrated into existing knowledge about the topic. It might aim to:

  • Exemplify a theory by showing how it explains the case under investigation
  • Expand on a theory by uncovering new concepts and ideas that need to be incorporated
  • Challenge a theory by exploring an outlier case that doesn’t fit with established assumptions

To ensure that your analysis of the case has a solid academic grounding, you should conduct a literature review of sources related to the topic and develop a theoretical framework . This means identifying key concepts and theories to guide your analysis and interpretation.

There are many different research methods you can use to collect data on your subject. Case studies tend to focus on qualitative data using methods such as interviews , observations , and analysis of primary and secondary sources (e.g., newspaper articles, photographs, official records). Sometimes a case study will also collect quantitative data.

Example of a mixed methods case studyFor a case study of a wind farm development in a rural area, you could collect quantitative data on employment rates and business revenue, collect qualitative data on local people’s perceptions and experiences, and analyze local and national media coverage of the development.

The aim is to gain as thorough an understanding as possible of the case and its context.

In writing up the case study, you need to bring together all the relevant aspects to give as complete a picture as possible of the subject.

How you report your findings depends on the type of research you are doing. Some case studies are structured like a standard scientific paper or thesis , with separate sections or chapters for the methods , results and discussion .

Others are written in a more narrative style, aiming to explore the case from various angles and analyze its meanings and implications (for example, by using textual analysis or discourse analysis ).

In all cases, though, make sure to give contextual details about the case, connect it back to the literature and theory, and discuss how it fits into wider patterns or debates.

If you want to know more about statistics , methodology , or research bias , make sure to check out some of our other articles with explanations and examples.

  • Normal distribution
  • Degrees of freedom
  • Null hypothesis
  • Discourse analysis
  • Control groups
  • Mixed methods research
  • Non-probability sampling
  • Quantitative research
  • Ecological validity

Research bias

  • Rosenthal effect
  • Implicit bias
  • Cognitive bias
  • Selection bias
  • Negativity bias
  • Status quo bias

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“Ye Shall Know Them by Their Fruits” pp 259–267 Cite as

Case Selection Criteria, Methods, and Data Treatment

  • Jason García Portilla   ORCID: orcid.org/0000-0003-3374-8659 2  
  • Open Access
  • First Online: 12 December 2021

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Part of the Contributions to Economics book series (CE)

This chapter examines the criteria for selecting the cases analysed in this study. It explains the application of critical discourse analysis (CDA) as its principal empirical method. It discusses CDA methods and data treatment as well as the empirical analysis of CDA results. Finally, it compares and summarises the case selection criteria.

Four countries were compared: Switzerland, Uruguay, Cuba, and Colombia. These cases are also linked to the correlated variables in the quantitative model and to the sufficient conditions in the QCA. Cases were selected based on the “extreme case method”.

Each of the selected countries serves as a proxy of a larger group of countries (Latin American Strong Catholic, Secular, Communism, Protestant or mixed Old World.).

Critical discourse analysis (CDA) and religion constitute the qualitative method (micro-component). Sixty semi-structured interviews were conducted and analysed using memos and open coding.

  • Critical discourse analysis (CDA) and religion
  • Qualitative method
  • Roman Catholicism
  • Protestantism
  • Case studies
  • Switzerland

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Nested cases (at the opposite ends of a negative-to-positive scale) were selected from the quantitative database (Appendices 1–4 and Supplementary Materials) for more in-depth empirical (i.e. within-case) analysis. Four countries were compared: Switzerland, Uruguay, Cuba, and Colombia. These cases are also linked to the correlated variables in the quantitative model and to the sufficient conditions in the QCA.

Cases were selected based on the “extreme case method”. This consists of a selection of cases exemplifying extreme or unusual values of one of the variables of analysis. This approach is appropriate for exploratory research (Gerring & Seawright, 2008 ). The QCA cases (Sect. 16.3.3 ) already mentioned some of the variables that characterise these countries as extreme. Section 17.5 further illustrates and compares some of the variables considered. The cases also analyse within-country variations by region (whenever possible) (i.e. more Catholic versus more Protestant areas in Switzerland, Uruguay, Colombia). Such analysis may also be a source of inferential leverage. This approach combines within-case and cross-case causal inferences to elucidate the causal mechanisms giving rise to empirical regularities (Goertz, 2017 ). To offer the broadest possible comparability, multiple case studies were conducted rather than a single in-depth case study.

1 Extreme Positive Case (Worldwide): Switzerland

Switzerland has the highest competitiveness score in the world (World Economic Forum, 2016 ), one of the lowest homicide rates (0.6 (UNODC, 2013 )), and one of the lowest corruption indices in the world (85 (Transparency International, 2016 )). The country also enjoys widely acclaimed political, economic, and social stability. Its population and cantonal (i.e. federated) system exhibit a mixed distribution of Roman Catholics and Protestants, making it an ideal case to analyse and compare the historical influences of these denominations. Furthermore, the author developed this research in Switzerland, which facilitated accessing and gathering primary and secondary information.

2 Extreme Positive Case (Latin America): Uruguay

Uruguay has the highest social progress score in Latin America (Porter et al., 2015 ). Besides Chile, it is also one of the most transparent countries in Latin America (Transparency International, 2016 ) and one of the continent’s most secular countries (Pew Research Center, 2014 ). These facts make Uruguay a worthwhile case for examining whether the factors that made Uruguay less religious have also made the country less corrupt and more equal. Consequently, this case provides vital information for understanding the interrelations between the variables under study.

3 Cuba: A sui generis Case (Communist Proxy)

Cuba is the only Communist country in the Americas. Communism and secularism are still in force in a country of contrasts: Cuba has one of the lowest homicide rates in the Americas (4.2 (UNODC, 2013 )) but also one of the continent’s lowest social progress indexes (Porter et al., 2015 ).

The Cuban government actively suppressed religion for decades. However, since the fall of the Soviet Union, the government has increased religious liberty by opening up political space for religious belief and practice. This opening has resulted in a dramatic flourishing of religious life in recent years (Goldenziel, 2009 ). Further, Cuba might also serve as a proxy of former socialist countries that have tried to eradicate the influence of religion on the state through adopting Marxist ideology. Cuba currently faces corruption levels comparable to former Soviet countries (Transparency International, 2016 ).

4 Extreme Negative Case: Colombia

Colombia is a proxy country in Latin America. It is characterised by pervasive Roman Catholicism (i.e. with a valid Concordat, and one of the highest proportion of adults raised as Roman Catholics worldwide (Pew Research Center, 2014 )). Other dominant features include high levels of corruption (Transparency International, 2016 ), and one of the world’s lowest equality (World Bank, 2016 ) and safety rankings (World Economic Forum, 2017 ). Moreover, the author’s first-hand experience of working in government, civil society, and international agencies in his native country provided direct insight (along with his extensive network).

5 Summary of Case Selection Criteria

Each of the selected countries serves as a proxy of a larger group of countries (Latin American Strong Catholic, Secular, Communism, Protestant or mixed Old World.). Comparing Switzerland and Latin American countries illuminates how religion and prosperity indicators evolve differently within diverse political systems and against the background of different historical roots.

Nested (extreme) cases were chosen for more in-depth empirical, quantitative and QCA analysis (see Supplementary Materials). Table 17.1 summarises the four cases.

6 Methods and Data Treatment

The qualitative approach adopted here concentrated on which patterns in particular (Silverman, 2005 , p. 9) might trigger the observed effects, and hence complemented the analysis of empirical correlations and QCA. The aim was to gain a greater understanding of the research problem (Zikmund, 2003 , p. 111), hence complementing the statistical and QCA analyses of the previous chapters, even if this approach implies that matters are “subjective in nature” (Zikmund, 2003 , p. 132).

6.1 Qualitative Method: Critical Discourse Analysis (CDA) and Religion

Discourse analysis is central to this study, mainly because discourse, knowledge, and power are closely related (Burr, 2003 , p. 67; Carabine, 2001 , pp. 267–268). One especially fruitful type of discourse analysis was established by the French philosopher Michel Foucault. He suggested examining the interconnections between discourse, knowledge, and power based on his key concept of “genealogy”. This, as we will see, is related to institutions and prosperity.

Foucault ( 1972 ) developed an elaborate conceptual framework for discourse analysis and proposed a rigorous methodological system to underpin such analysis. However, he did not provide a “how to guide” to genealogy. Hence, methodologies and applications vary (Carabine, 2001 ).

Importantly, CDA cannot be applied mechanically (Hjelm, 2014 ). Nor does any universal CDA methodology exist (Fairclough, 2010 , p. 6). On the contrary, every analytical approach to discourse requires specific design (Hjelm, 2014 , p. 860). Oswick ( 2012 ) shares similar views and sees CDA as the only discursive method for considering ideology and power. CDA bridges cultural and linguistic studies in a critical approach. Thus, it enables researchers to adequately examine the role of religion in creating, transforming, reproducing, and sustaining inequalities (Hjelm, 2014 , pp. 855–58).

Equally importantly, CDA is ethically committed to exposing the processes through which discourses disseminate social structures that perpetuate hegemony (i.e. maintain and assert the interests of dominant groups or classes) (Fairclough and Wodak 1997 ; Wodak as cited in Heracleous, 2006 , p. 4) and suppress alternative constructions (Hjelm, 2014 , p. 860).

CDA is one of the most used methodologies for analysing language and texts in a wide range of fields, including management and organisation studies (The Editors, 2010 , p. 1192). However, studies employing CDA are scarce in the sociology of religion, and the valuable research potential of CDA has been underused as a result (Hjelm, 2014 ; Moberg, 2013 ). Therefore, Hjelm ( 2014 ) has strongly encouraged sociologists of religion to apply CDA, due to the obvious lack of critical approaches to religion that take inequality and hegemony seriously (p. 857).

6.2 Critical Discourse Analysis Protocol

Fairclough ( 1992 ), Fairclough ( 2010 ), and Gee ( 2011 ) have developed stringent guidelines for applying Critical Discourse Analysis (CDA). According to Fairclough ( 2010 ) selecting a CDA methodology involves developing a theoretical framework relevant to a specific research project than choosing from an existing repertoire of methods (Fairclough, 2010 , p. 225).

What makes CDA unique is its division of analysis into three, cross-fertilising aspects: (1) Textual analysis, (2) Analysis of discourse practice, and (3) Analysis of social practice (including the relationship to existing hegemonies) (Hjelm, 2014 , p. 861; Fairclough, 1992 , p. 73). These categories are of central interest for this study as they help produce a comprehensive understanding of the impact of religion on the three levels of analysis:

The first level of analysis (textual) involves closely studying a range of texts such as political constitutions or Christian documents including The Holy Bible. Especially the Scriptures are central to analysing Christianity, as the text has remained largely unaffected by time for centuries (i.e. King James or Martin Luther versions). In contrast, Christian traditions have changed over time and vary among denominations.

The second level (analysis of discourse practice) considers the paradigms and public discourse of Protestants, Roman Catholic Church-State leaders, and government and civil society stakeholders.

The third level (analysis of social practice) explores the coherence between formal and de facto discourses, including the “commonsensical” language of social practices. Typically, producing documents for their own sake neither relates to nor explains social practice. Nevertheless, it is possible to analyse their coherence and influence in institutions. Comparing lived reality beyond formal discourses allows identifying patterns of social acceptance related to corruption and prosperity.

6.3 Data Treatment

Sixty semi-structured interviews were conducted and analysed using memos and open coding. Protestant and Roman Catholic Church-State leaders, government, academics, and civil society stakeholders were interviewed in a snowball system between 2015 and 2017. Interviews were conducted in English, German, and French, in the German and French-speaking regions of Switzerland. Interviews in Latin America were conducted in Spanish and English (i.e. English speakers in the Colombian Caribbean). All interviews were translated into English before coding. For reasons of scope, not all the data or stakeholders interviewed appear in the main body of this book. Table 17.2 shows the total number of interviews conducted in each country.

Interviewees were mostly religious leaders or educated and informed stakeholders. Many stakeholders interviewed were also university professors or academic researchers. Protestants, Catholics, or non-religious interviewees were also asked about their different ideologies.

6.3.1 Protecting Interviewee Identity

Before interviewing, stakeholders agreed to release their data on condition of anonymity. Consequently, the discussion offered in this book and the corresponding public datasets only contain stakeholders’ general institutional affiliations for comparison/triangulation purposes (e.g. government officer, university expert-lawyer, Catholic priest, Protestant preacher). Other sensitive data possibly enabling identification were omitted.

6.3.2 Coding

Two qualitative researchers independently coded the data to align code application and code definitions (a total of three independent researchers). Moreover, the author took position in a separate memorandum (Appendix 5).

6.3.3 Triangulation

Triangulation is essential for crosschecking information through multiple procedures and sources. It produces either corroboration or convergence in the case of agreement or divergence in the case of disagreement.

The notion of identifiable Roman Catholic or Protestant traditions requires gathering theoretical and historical data as well as qualitative data from interviewees. Although interviewees shared their perceptions of religious traditions, these perceptions do not provide robust evidence of historical linkages or ramifications. Present-day interviewees can only share their impressions of what their country has inherited from its religious background.

Therefore, findings were triangulated using a triple strategy: (1) Diverse stakeholder perspectives were included in each code (e.g. interviews with a government officer, a Catholic priest, a Protestant pastor); (2) public documents or discourses; and (3) other materials (e.g. historical, theoretical, textbooks).

The next four chapters provide background information on the religion–prosperity–institution nexuses for each of the four cases. Each case study includes charts that compare the different stakeholder principles identified in terms of (1) Prosperity, (2) Corruption, or (3) Church-State relations. Each chart is followed by a three-level CDA analysis.

Case details vary depending on historical importance, the information relevant for comparison, and scope. More information is deliberately provided for Switzerland, since this is the only European country compared and contrasted with the three selected Latin American countries. Such detailed background information and three empirical analyses concern prosperity, corruption, and church-state relations. Consequently, the case of Switzerland also draws more detailed conclusions from its three empirical analyses. By comparison, each Latin American case contains briefer background information and merely one empirical analysis (Uruguay: prosperity; Cuba: corruption; Colombia: prosperity). The respective conclusions are synthesised in Chap. 22 .

Each case begins by characterising the background information and the main features of the prosperity–corruption–religion nexus. This is followed by empirical analysis.

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García Portilla, J. (2022). Case Selection Criteria, Methods, and Data Treatment. In: “Ye Shall Know Them by Their Fruits”. Contributions to Economics. Springer, Cham. https://doi.org/10.1007/978-3-030-78498-0_17

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Case Selection Module

Choosing cases.

Once we have a hypothesis to explore or test, and once we have settled on a general research design, then we need to choose specific cases to analyze. Case selection is important whether we are conducting a case study of a single civil war, an experiment involving a few dozen college students, or a statistical comparison of hundreds of elections. All social scientists should learn how to select cases with care.

Done well, case selection can enhance the external validity of our research, making us more confident that our results would hold true beyond our particular study. Case selection can also help the internal validity of our research, making us more confident that our conclusions hold true within the confines of our study. Done poorly, case selection can compromise our research or even render it useless.

The purpose of this module is to help you think systematically and intelligently about case selection.

View Module As PDF

1. population vs. sample.

The first question to ask is whether you plan to study the entire population of cases (often referred to as N) or a smaller sample (n) taken from that population.

Studying the entire population is appealing because it essentially guarantees the external validity of our research. We don’t need to make inferences about what happened or why; we have analyzed every relevant case. Over time, teams of scholars have developed datasets with information about every recorded vote in the history of Congress, and about every single interstate war over the last two centuries. Some research projects analyze entire populations like these.

Nevertheless, we usually lack the time, money, or skills needed to analyze the entire population of relevant cases. We might not even have a good way to identify the entire population; there is no master list, for example, of Kurdish rebels or newspaper stories about Senate elections. As a result of these various constraints, we typically pick a smaller sample. This is why polling firms interview 1500 people instead of 250 million. This is why undergraduates write their research papers about, say, democratization in India during the 20th century, and not about democratization in every country of the world over the last three centuries.

However, the choice between population and sample also depends on how we define the larger population. If we believe that “modern world wars” are conceptually distinct from “interstate wars” or “militarized conflicts,” then the population of modern world wars might consist of just two cases – World War I and World War II. Someone who wanted to study the origins of these world wars might actually have the resources needed to examine the entire population of cases. One can imagine other examples, such as “Communist nations in the 21st century” or “U.S. presidential elections decided by the Supreme Court” where the total population (N) is pretty small. In each of these examples, the author would have to justify the boundaries of their population. Are Communist nations in the 21st century really all that different from those that existed in the 20th century?

Suppose that someone wanted to study the relationship between motorcycle helmet laws and motorcycle fatalities in the American states. One could gather data for the most recent year available in all 50 states, which certainly sounds like the entire population of cases. If our aim is to generalize across a wider time period, though, then we would be dealing with a one-year sample. And if we are trying to generalize to some larger population of traffic laws, such as speed limits and seatbelts, and to a larger set of traffic fatalities, then our motorcycle helmet cases would also qualify as a sample.

Frankly, it seems unlikely that all you would want to accomplish in this example is to figure out what happened with one specific kind of law in one year. Doing so would really limit the larger significance of your work. Thus, the choice of sample versus population connects back to the larger aims of the study. When choosing cases we always need to ask ourselves, “What puzzle am I hoping to solve? To what scholarly literature or policy debate am I trying to contribute? What, then, is the population of relevant cases?”

2. Sampling: Random vs. Deliberate

The vast majority of the time, for practical or conceptual reasons, we are dealing with samples. At the most general level, we need to decide whether to choose a sample of cases randomly or deliberately. One might think that random selection would always be preferred because the sample would more likely resemble the entire population, thus giving our study added external validity. This intuition is correct – as long as the number of cases is pretty large. If the number is small, then one might randomly select an atypical sample, which would actually hurt external validity.

You can take a real course about probability and statistics to understand why, or you can accept the following example as a rough proof. Let’s imagine that a polling firm wanted to know what American adults think about a controversial issue like immigration. If the firm randomly selected just two people – let’s call them Border Wall Bob and No Amnesty Nancy – it might conclude that all Americans have strongly negative views toward immigrants. And those conclusions would be wrong. If that same firm chose 1000 or 1500 Americans at random, it would be much more likely to identify the full range of attitudes, as well as the correct distribution. (The sample would rarely look exactly like the population, but it would probably be close if the firm sampled correctly.) With so many cases, a few extreme values in any direction will not distort the entire sample.

Thus, if the research design is based on a statistical comparison of many cases, scholars will probably choose their cases randomly. (The large number of cases will have the added benefit of helping us to establish the internal validity of our research: we can become more confident in concluding whether our measures are correlated, and whether any apparent relationships could be spurious.) If the research design is a detailed case study, however, the cases will almost always be chosen deliberately.

With experimental designs, the cases could be chosen deliberately or randomly. A lab experiment will probably not rely on a random sample of individuals; researchers will usually have to take whoever is willing or required to participate in the experiment. A survey or field experiment, on the other hand, might select at random a large number of individuals, voting precincts, villages, development projects, or some other unit of analysis. Such random selection of cases will help the external validity of the study, while experimental controls and random assignment of cases will generate internal validity.

Whether we choose cases randomly or deliberately, we are concerned about generating a biased sample. Some types of bias originate with the researcher. Suppose you wanted to sample opinions from the entire college campus, but you only distributed surveys to three freshmen dorms. That sample would not reflect the full range of students on campus, and could bias the results if freshmen held different opinions from upperclassmen. Other types of sample bias are beyond the researchers’ control — sometimes just bad luck. We might distribute surveys to a variety of dorms on campus, yet the main people who filled them out and returned them might be freshmen. Therefore, after taking a sample, it often makes sense to compare it to whatever is known about the larger population.

3. Generating a Random Sample

To learn different ways of choosing cases randomly, you can consult standard research methods textbooks, which often do a good job of teaching this skill. See, for example, chapter 7 in Johnson and Reynolds, Political Science Research Methods 7th edition, or chapter 6 in Kellstedt and Whitten, The Fundamentals of Political Science Research 2nd edition. There you will encounter simple, systematic, stratified, and cluster random samples. You can also find helpful videos on-line, such as these two:

[Note: both of these videos discuss “convenience sampling,” which they don’t exactly endorse. Convenience samples and snowball samples are both nonprobability samples in which each element or group within the population does not have an equal chance of being selected. The external validity of such samples is thus highly suspect. Nonprobability samples are used occasionally in social scientific research, but not often.]

It is certainly possible to combine strategies as well. A survey research firm conducting an exit poll on Election Day could start with a simple random sample of congressional districts, then a systematic random sample of voting precincts within those districts, and finish with a stratified random sample of individuals who showed up to vote at those precincts. Someone analyzing trends in media coverage of terrorism might analyze only those years ending in 0, 2, 5, and 8, and then collect a simple random sample of stories for each year.

4. Picking Cases Deliberately

Standard methods textbooks are pretty useless if you intend to choose cases deliberately. That’s too bad, for it means that students planning to conduct case studies receive practically no guidance about a crucial step in the research process. One reason for this gap, I suspect, is that many social scientists view deliberate case selection with suspicion. A crafty researcher could pick one or two cases to prove, well, just about anything. What is supposed to be reputable social science could easily degenerate into intellectual sleight-of-hand or trickery. For a playful analogy, watch how master magician Ricky Jay manages to reveal just the right cards from a full deck:

While we might be delighted to watch someone manipulate cards so effortlessly, we could be outraged to discover a political scientist doing something similar when he or she picked cases to study. We would seriously doubt the study’s internal validity, external validity, or both. Carefully selecting a few vivid examples to “prove” a general point is common among policy advocates and strong partisans, but it is not good practice for social scientists.

To learn more about deliberate case selection, especially for case studies, I would recommend reading chapter 6 in Lipson, How to Write a BA Thesis; pages 77-88 of Van Evera, Guide to Methods for Students of Political Science; and, if you’re feeling ambitious, chapters 3 and 5 in Gerring, Case Study Research.

Because snappy YouTube videos about deliberate case selection are so rare, I will highlight some of their advice in the table below. One general strategy is to look for ways of maximizing the number of observations within each case; a related strategy is to find cases with analytically-useful variation (i.e., variation linked to the hypotheses we wish to explore or test). In both instances, we are trying to approximate the analytic leverage that comes with large-n statistical comparisons. But another strategy is simply to emphasize a distinctive strength of the case study design – identifying causal links and mechanisms through careful process tracing – and to choose a single case or a few cases that will enable the researcher to study a piece of the political world in real depth.

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Social Sci LibreTexts

2.3: Case Selection (Or, How to Use Cases in Your Comparative Analysis)

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  • Dino Bozonelos, Julia Wendt, Charlotte Lee, Jessica Scarffe, Masahiro Omae, Josh Franco, Byran Martin, & Stefan Veldhuis
  • Victor Valley College, Berkeley City College, Allan Hancock College, San Diego City College, Cuyamaca College, Houston Community College, and Long Beach City College via ASCCC Open Educational Resources Initiative (OERI)

Learning Objectives

By the end of this section, you will be able to:

  • Discuss the importance of case selection in case studies.
  • Consider the implications of poor case selection.

Introduction

Case selection is an important part of any research design. Deciding how many cases, and which cases, to include, will clearly help determine the outcome of our results. If we decide to select a high number of cases, we often say that we are conducting large-N research. Large-N research is when the number of observations or cases is large enough where we would need mathematical, usually statistical, techniques to discover and interpret any correlations or causations. In order for a large-N analysis to yield any relevant findings, a number of conventions need to be observed. First, the sample needs to be representative of the studied population. Thus, if we wanted to understand the long-term effects of COVID, we would need to know the approximate details of those who contracted the virus. Once we know the parameters of the population, we can then determine a sample that represents the larger population. For example, women make up 55% of all long-term COVID survivors. Thus, any sample we generate needs to be at least 55% women.

Second, some kind of randomization technique needs to be involved in large-N research. So not only must your sample be representative, it must also randomly select people within that sample. In other words, we must have a large selection of people that fit within the population criteria, and then randomly select from those pools. Randomization would help to reduce bias in the study. Also, when cases (people with long-term COVID) are randomly chosen they tend to ensure a fairer representation of the studied population. Third, your sample needs to be large enough, hence the large-N designation for any conclusions to have any external validity. Generally speaking, the larger the number of observations/cases in the sample, the more validity we can have in the study. There is no magic number, but if using the above example, our sample of long-term COVID patients should be at least over 750 people, with an aim of around 1,200 to 1,500 people.

When it comes to comparative politics, we rarely ever reach the numbers typically used in large-N research. There are about 200 fully recognized countries, with about a dozen partially recognized countries, and even fewer areas or regions of study, such as Europe or Latin America. Given this, what is the strategy when one case, or a few cases, are being studied? What happens if we are only wanting to know the COVID-19 response in the United States, and not the rest of the world? How do we randomize this to ensure our results are not biased or are representative? These and other questions are legitimate issues that many comparativist scholars face when completing research. Does randomization work with case studies? Gerring suggests that it does not, as “any given sample may be widely representative” (pg. 87). Thus, random sampling is not a reliable approach when it comes to case studies. And even if the randomized sample is representative, there is no guarantee that the gathered evidence would be reliable.

One can make the argument that case selection may not be as important in large-N studies as they are in small-N studies. In large-N research, potential errors and/or biases may be ameliorated, especially if the sample is large enough. This is not always what happens, errors and biases most certainly can exist in large-N research. However, incorrect or biased inferences are less of a worry when we have 1,500 cases versus 15 cases. In small-N research, case selection simply matters much more.

This is why Blatter and Haverland (2012) write that, “case studies are ‘case-centered’, whereas large-N studies are ‘variable-centered’". In large-N studies we are more concerned with the conceptualization and operationalization of variables. Thus, we want to focus on which data to include in the analysis of long-term COVID patients. If we wanted to survey them, we would want to make sure we construct questions in appropriate ways. For almost all survey-based large-N research, the question responses themselves become the coded variables used in the statistical analysis.

Case selection can be driven by a number of factors in comparative politics, with the first two approaches being the more traditional. First, it can derive from the interests of the researcher(s). For example, if the researcher lives in Germany, they may want to research the spread of COVID-19 within the country, possibly using a subnational approach where the researcher may compare infection rates among German states. Second, case selection may be driven by area studies. This is still based on the interests of the researcher as generally speaking scholars pick areas of studies due to their personal interests. For example, the same researcher may research COVID-19 infection rates among European Union member-states. Finally, the selection of cases selected may be driven by the type of case study that is utilized. In this approach, cases are selected as they allow researchers to compare their similarities or their differences. Or, a case might be selected that is typical of most cases, or in contrast, a case or cases that deviate from the norm. We discuss types of case studies and their impact on case selection below.

Types of Case Studies: Descriptive vs. Causal

There are a number of different ways to categorize case studies. One of the most recent ways is through John Gerring. He wrote two editions on case study research (2017) where he posits that the central question posed by the researcher will dictate the aim of the case study. Is the study meant to be descriptive? If so, what is the researcher looking to describe? How many cases (countries, incidents, events) are there? Or is the study meant to be causal, where the researcher is looking for a cause and effect? Given this, Gerring categorizes case studies into two types: descriptive and causal.

Descriptive case studies are “not organized around a central, overarching causal hypothesis or theory” (pg. 56). Most case studies are descriptive in nature, where the researchers simply seek to describe what they observe. They are useful for transmitting information regarding the studied political phenomenon. For a descriptive case study, a scholar might choose a case that is considered typical of the population. An example could involve researching the effects of the pandemic on medium-sized cities in the US. This city would have to exhibit the tendencies of medium-sized cities throughout the entire country. First, we would have to conceptualize what we mean by ‘a medium-size city’. Second, we would then have to establish the characteristics of medium-sized US cities, so that our case selection is appropriate. Alternatively, cases could be chosen for their diversity . In keeping with our example, maybe we want to look at the effects of the pandemic on a range of US cities, from small, rural towns, to medium-sized suburban cities to large-sized urban areas.

Causal case studies are “organized around a central hypothesis about how X affects Y” (pg. 63). In causal case studies, the context around a specific political phenomenon or phenomena is important as it allows for researchers to identify the aspects that set up the conditions, the mechanisms, for that outcome to occur. Scholars refer to this as the causal mechanism , which is defined by Falleti & Lynch (2009) as “portable concepts that explain how and why a hypothesized cause, in a given context, contributes to a particular outcome”. Remember, causality is when a change in one variable verifiably causes an effect or change in another variable. For causal case studies that employ causal mechanisms, Gerring divides them into exploratory case-selection, estimating case-selection, and diagnostic case-selection. The differences revolve around how the central hypothesis is utilized in the study.

Exploratory case studies are used to identify a potential causal hypothesis. Researchers will single out the independent variables that seem to affect the outcome, or dependent variable, the most. The goal is to build up to what the causal mechanism might be by providing the context. This is also referred to as hypothesis generating as opposed to hypothesis testing. Case selection can vary widely depending on the goal of the researcher. For example, if the scholar is looking to develop an ‘ideal-type’, they might seek out an extreme case. An ideal-type is defined as a “conception or a standard of something in its highest perfection” (New Webster Dictionary). Thus, if we want to understand the ideal-type capitalist system, we want to investigate a country that practices a pure or ‘extreme’ form of the economic system.

Estimating case studies start with a hypothesis already in place. The goal is to test the hypothesis through collected data/evidence. Researchers seek to estimate the ‘causal effect’. This involves determining if the relationship between the independent and dependent variables is positive, negative, or ultimately if no relationship exists at all. Finally, diagnostic case studies are important as they help to “confirm, disconfirm, or refine a hypothesis” (Gerring 2017). Case selection can also vary in diagnostic case studies. For example, scholars can choose an least-likely case, or a case where the hypothesis is confirmed even though the context would suggest otherwise. A good example would be looking at Indian democracy, which has existed for over 70 years. India has a high level of ethnolinguistic diversity, is relatively underdeveloped economically, and a low level of modernization through large swaths of the country. All of these factors strongly suggest that India should not have democratized, or should have failed to stay a democracy in the long-term, or have disintegrated as a country.

Most Similar/Most Different Systems Approach

The discussion in the previous subsection tends to focus on case selection when it comes to a single case. Single case studies are valuable as they provide an opportunity for in-depth research on a topic that requires it. However, in comparative politics, our approach is to compare. Given this, we are required to select more than one case. This presents a different set of challenges. First, how many cases do we pick? This is a tricky question we addressed earlier. Second, how do we apply the previously mentioned case selection techniques, descriptive vs. causal? Do we pick two extreme cases if we used an exploratory approach, or two least-likely cases if choosing a diagnostic case approach?

Thankfully, an English scholar by the name of John Stuart Mill provided some insight on how we should proceed. He developed several approaches to comparison with the explicit goal of isolating a cause within a complex environment. Two of these methods, the 'method of agreement' and the 'method of difference' have influenced comparative politics. In the 'method of agreement' two or more cases are compared for their commonalities. The scholar looks to isolate the characteristic, or variable, they have in common, which is then established as the cause for their similarities. In the 'method of difference' two or more cases are compared for their differences. The scholar looks to isolate the characteristic, or variable, they do not have in common, which is then identified as the cause for their differences. From these two methods, comparativists have developed two approaches.

Book cover of John Stuart Mill's A System of Logic, Ratiocinative and Inductive, 1843

What Is the Most Similar Systems Design (MSSD)?

This approach is derived from Mill’s ‘method of difference’. In a Most Similar Systems Design Design, the cases selected for comparison are similar to each other, but the outcomes differ in result. In this approach we are interested in keeping as many of the variables the same across the elected cases, which for comparative politics often involves countries. Remember, the independent variable is the factor that doesn’t depend on changes in other variables. It is potentially the ‘cause’ in the cause and effect model. The dependent variable is the variable that is affected by, or dependent on, the presence of the independent variable. It is the ‘effect’. In a most similar systems approach the variables of interest should remain the same.

A good example involves the lack of a national healthcare system in the US. Other countries, such as New Zealand, Australia, Ireland, UK and Canada, all have robust, publicly accessible national health systems. However, the US does not. These countries all have similar systems: English heritage and language use, liberal market economies, strong democratic institutions, and high levels of wealth and education. Yet, despite these similarities, the end results vary. The US does not look like its peer countries. In other words, why do we have similar systems producing different outcomes?

What Is the Most Different Systems Design (MDSD)?

This approach is derived from Mill’s ‘method of agreement’. In a Most Different System Design, the cases selected are different from each other, but result in the same outcome. In this approach, we are interested in selecting cases that are quite different from one another, yet arrive at the same outcome. Thus, the dependent variable is the same. Different independent variables exist between the cases, such as democratic v. authoritarian regime, liberal market economy v. non-liberal market economy. Or it could include other variables such as societal homogeneity (uniformity) vs. societal heterogeneity (diversity), where a country may find itself unified ethnically/religiously/racially, or fragmented along those same lines.

A good example involves the countries that are classified as economically liberal. The Heritage Foundation lists countries such as Singapore, Taiwan, Estonia, Australia, New Zealand, as well as Switzerland, Chile and Malaysia as either free or mostly free. These countries differ greatly from one another. Singapore and Malaysia are considered flawed or illiberal democracies (see chapter 5 for more discussion), whereas Estonia is still classified as a developing country. Australia and New Zealand are wealthy, Malaysia is not. Chile and Taiwan became economically free countries under the authoritarian military regimes, which is not the case for Switzerland. In other words, why do we have different systems producing the same outcome?

Planning Tank

4 Effective Tips to Choose the Right Case Study for Research

Has it ever occurred to you why case studies are more valued than the standalone research techniques (e.g. surveys)? It’s simple. Case studies function as an in-depth investigation of a specific person, group, time-period, event or anything that is the focus of your research. With case studies, readers can get a holistic review of the research work. However, it is important for you, as a researcher, to pick the right case study for particular research. Otherwise, you may end up producing inaccurate results which can cause a loss of credibility. In the academic field, you cannot afford that as a researcher. If a person is unable to find an apt case study or finding it too difficult they might take some help from faculty, peers, or friends.

Selecting Case Study

Here are some suggestions on how to make the right choice, in case you are having trouble choosing the case study for your research.

#1. Select a case that aligns with your topic of research

Choosing the right case study becomes a lot easier if you are clear about what you want with your research. Examine the area of study that you are choosing for your next research. Once you have the clarity of what you need with the research, you can look for case studies that complement the theme of the research.

In simpler words, your research should go hand in hand with the case study you choose. If you end up choosing a case study that hardly fits within the theme of the research, it is only going to break the flow of information.

Let’s say, you are working on a research topic within the area of the textile industry, but you choose a case study from literature. Even if the case study talks about the textile industry in the text, it isn’t going to make any sense to the readers. It is ideal if you can employ a case study within the textile industry. It will offer you raw data and responses from people who were/are a part of the industry, adding more value to your research.

Related: Defining Aim, Objective, Scope for conducting study | PlanningTank

#2. See if the case study has a universal applicability

Case studies often function as the sample for a group within a universe in which you are conducting the research. If you are choosing a case study that is not exactly applicable to the whole phenomena, your research is going to be unsuccessful. So, always choose a case study that has a universal appeal.

To determine which case study has the universal appeal, you may need to narrow down your choices for the case study and analyse them individually. It may be time-consuming, but it’s the most effective way to ensure the findings of the research are applicable to the whole occurring.

If you choose a particular textile company as a case study, make sure the findings are applicable for the other textile companies within the universe of the research. If the case study you have chosen operates like an exception, it is going to give incorrect results. Always confirm that the case study covers all the elements of the theory you are putting to test.

#3. Ensure the case study is relevant in today’s date

Relevance is one of the crucial factors that you need to keep in mind while choosing a case study. Just like the universal appeal, relevance is a basic element of a case study. Unless the case study is relevant to the readers and to the time of research, it is not going to be successful research.

It is recommended to choose a case study that is on the same page with the theme of the research. The research does not necessarily have to be based on current conditions. For example, you can explore the textile industries during the time of the industrial revolution. But then you need to choose a case study from that time-period only.

You also need to determine whether the findings of the research paper are going to make sense in today’s date, or add any value to the field of study. If the answer is no, you may need to reconsider the choice of case study as well as the research topic.

#4. Pick the right approach for case study selection

There are primarily two options for selecting case studies. Based on the requirements of the research, you can either choose a single case that functions as a sample, or select multiple cases that offer a broader overview. A single case is often chosen as the part of the holistic case study, while the multiple cases are chosen for the embedded case study.

In a holistic case study, you need to examine every aspect of the chosen subject. However, in an embedded case study, you should examine certain aspects of the chosen subjects and compare them to draw the inference.

The approach for case study selection depends solely on the requirements of the research you are conducting. Therefore, you need to study the research topic thoroughly and develop a better understanding of the requirements. Then only you can identify whether you need a single case study or multiple ones.

Related: Tips for Publishing in an Academic Journal

In conclusion ,

Case studies are undoubtedly time-consuming, but they are still considered the most effective tool by the researchers. Surveys, A/B testing, and other standalone research techniques may have some errors in the results. However, the right case study always delivers the most comprehensive results for research.

Author bio: Jedda Cain is a Philosophy professor at one of the renowned colleges in Australia. She has a PhD and has been serving in the field of academic for the past 10 years. She also offers assignment help to students on request.

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How to select cases?

Social scientists try to make statements about a theoretical set of units. Sometimes we are able to study all units we are interested in. This means we study a census. In most cases, however, only a subset of cases is studied. Case selection is a crucial part of empirical research, and largely determines the extent to which you can generalise from your findings to the larger target population. Case selection is also called sampling , although this word is most frequently used when larger numbers of cases are selected. The main types of sampling are probability sampling and non-probability sampling. The first is mostly associated with large n studies. The second is associated with both large and smaller n studies. If the researcher does not have the intention to make an inference to a larger target population, other selection procedures are available.

Target population and sampling frame

The target population is the set of units we make statements about; companies, persons, newspaper articles, products. In many cases the target population is not easily accessed. A sampling frame is a set of units we can draw samples from. For example, if the target population is local businesses, a suitable sampling frame might be the listings in the business section of the telephone book. Preferably the sampling frame includes nearly all of the population, although this is not always possible. The sample frame is then used to select cases from.

Probability sampling

There are various types of probability sampling. All procedures use some reference to the known probability an element from the sampling frame is actually selected for study. Different procedures can be used to get a representative sample of units. A distinction is made between single stage sampling (for example, simple probability sampling, systematic sampling, stratified sampling and cluster sampling) and multi-stage sampling (in which different procedures are used sequentially (for example, first selecting municipalities and the random samples within each municipality).

Non-probability sampling

The set of non-probability sampling procedures is huge. Examples are self selection, snowball sampling and quota sampling. With all these procedures the danger is that the selection might be biased: i.e. over- or under- representing units with certain attributes. These procedures should therefore be avoided if possible.

If only a small number of cases is selected using probability sampling, the risk too is that certain attributes are over- or under-represented. To avoid this, cases must be selected on the basis of prior knowledge of their attributes (intentional selection). If the researcher tries to test a causal hypothesis het must at least select cases to ensure variation on the main independent and dependent variables. You cannot infer anything about the causes of the success of companies, for example, if you limit your selection to successful companies. Note, however, that if the number of cases is small, your conclusions can easily be the consequence of mere chance.

Selection of one case or only a few cases

If the researcher wants to explore a topic, or further develop an existing and well-tested theory several other case selection options are available. If the aim is exploration cases in single case studies are selected on the basis of the information they are expected to provide. Single cases can be selected because the case:

  • is extreme (i.e. has an extremely low or high value on the central variable)
  • is critical (i.e. ‘If it is valid for this case, it is valid for all (or many) cases’ or the converse, ‘If it is not valid for this case, then it is not valid for any (or only few) cases.’)
  • is typical (i.e. an example of the phenomenon under investigation)
  • is deviant (i.e. has a combination of characteristics different from most other units)

Note that all case selection procedures mentioned here assume the existence of a (preferably tested) theory and some general knowledge of the central variables in the units of analysis on the basis of which single cases can be selected.

Basic readings

  • Babbie, Earl (2004). The Practice of Social Research (12 th edition) . Belmont: Wadsworth/Thomson. Chapter 7.
  • Shadish, William R., Thomas D. Cook and Donald T. Cambell (2002). Experimental and Quasi-Experimental Designs for Generalized Causal Inference. Boston: Houghton Mifflin. Chapter 3.
  • De Vaus, David (2001). Research Design in Social Research. London: Sage. Chapters 5, 8, 11, 14.

Additional readings

  • King, Gary, Robert O. Keohane and Sidney Verba (1994). Designing Social Inquiry: scientific inference in qualitative research. Princeton: Princeton University Press.
  • Yin, Robert K (1994). Case Study Research: Design and Methods (2 nd edition) . Thousand Oaks, California: Sage.
  • Swanborn, P. G (1996). Case-study’s: Wat, wanneer en hoe? Amsterdam: Boom.
  • Franzosi, Roberto P. (2004). Content Analysis , in: Melissa A. Hardy and Alan Bryman (eds). Handbook of Data Analysis. London, Sage
  • Berg, Bruce (2007) Qualitative Research Methods for the Social Sciences . Boston, Pearson.
  • Gerring, John (2001) Social Science Methodology: a criterial framework . Cambridge, Cambridge University Press. Chapter 8.

Organizing Your Social Sciences Research Assignments

  • Annotated Bibliography
  • Analyzing a Scholarly Journal Article
  • Group Presentations
  • Dealing with Nervousness
  • Using Visual Aids
  • Grading Someone Else's Paper
  • Types of Structured Group Activities
  • Group Project Survival Skills
  • Leading a Class Discussion
  • Multiple Book Review Essay
  • Reviewing Collected Works
  • Writing a Case Analysis Paper
  • Writing a Case Study
  • About Informed Consent
  • Writing Field Notes
  • Writing a Policy Memo
  • Writing a Reflective Paper
  • Writing a Research Proposal
  • Generative AI and Writing
  • Acknowledgments

A case study research paper examines a person, place, event, condition, phenomenon, or other type of subject of analysis in order to extrapolate  key themes and results that help predict future trends, illuminate previously hidden issues that can be applied to practice, and/or provide a means for understanding an important research problem with greater clarity. A case study research paper usually examines a single subject of analysis, but case study papers can also be designed as a comparative investigation that shows relationships between two or more subjects. The methods used to study a case can rest within a quantitative, qualitative, or mixed-method investigative paradigm.

Case Studies. Writing@CSU. Colorado State University; Mills, Albert J. , Gabrielle Durepos, and Eiden Wiebe, editors. Encyclopedia of Case Study Research . Thousand Oaks, CA: SAGE Publications, 2010 ; “What is a Case Study?” In Swanborn, Peter G. Case Study Research: What, Why and How? London: SAGE, 2010.

How to Approach Writing a Case Study Research Paper

General information about how to choose a topic to investigate can be found under the " Choosing a Research Problem " tab in the Organizing Your Social Sciences Research Paper writing guide. Review this page because it may help you identify a subject of analysis that can be investigated using a case study design.

However, identifying a case to investigate involves more than choosing the research problem . A case study encompasses a problem contextualized around the application of in-depth analysis, interpretation, and discussion, often resulting in specific recommendations for action or for improving existing conditions. As Seawright and Gerring note, practical considerations such as time and access to information can influence case selection, but these issues should not be the sole factors used in describing the methodological justification for identifying a particular case to study. Given this, selecting a case includes considering the following:

  • The case represents an unusual or atypical example of a research problem that requires more in-depth analysis? Cases often represent a topic that rests on the fringes of prior investigations because the case may provide new ways of understanding the research problem. For example, if the research problem is to identify strategies to improve policies that support girl's access to secondary education in predominantly Muslim nations, you could consider using Azerbaijan as a case study rather than selecting a more obvious nation in the Middle East. Doing so may reveal important new insights into recommending how governments in other predominantly Muslim nations can formulate policies that support improved access to education for girls.
  • The case provides important insight or illuminate a previously hidden problem? In-depth analysis of a case can be based on the hypothesis that the case study will reveal trends or issues that have not been exposed in prior research or will reveal new and important implications for practice. For example, anecdotal evidence may suggest drug use among homeless veterans is related to their patterns of travel throughout the day. Assuming prior studies have not looked at individual travel choices as a way to study access to illicit drug use, a case study that observes a homeless veteran could reveal how issues of personal mobility choices facilitate regular access to illicit drugs. Note that it is important to conduct a thorough literature review to ensure that your assumption about the need to reveal new insights or previously hidden problems is valid and evidence-based.
  • The case challenges and offers a counter-point to prevailing assumptions? Over time, research on any given topic can fall into a trap of developing assumptions based on outdated studies that are still applied to new or changing conditions or the idea that something should simply be accepted as "common sense," even though the issue has not been thoroughly tested in current practice. A case study analysis may offer an opportunity to gather evidence that challenges prevailing assumptions about a research problem and provide a new set of recommendations applied to practice that have not been tested previously. For example, perhaps there has been a long practice among scholars to apply a particular theory in explaining the relationship between two subjects of analysis. Your case could challenge this assumption by applying an innovative theoretical framework [perhaps borrowed from another discipline] to explore whether this approach offers new ways of understanding the research problem. Taking a contrarian stance is one of the most important ways that new knowledge and understanding develops from existing literature.
  • The case provides an opportunity to pursue action leading to the resolution of a problem? Another way to think about choosing a case to study is to consider how the results from investigating a particular case may result in findings that reveal ways in which to resolve an existing or emerging problem. For example, studying the case of an unforeseen incident, such as a fatal accident at a railroad crossing, can reveal hidden issues that could be applied to preventative measures that contribute to reducing the chance of accidents in the future. In this example, a case study investigating the accident could lead to a better understanding of where to strategically locate additional signals at other railroad crossings so as to better warn drivers of an approaching train, particularly when visibility is hindered by heavy rain, fog, or at night.
  • The case offers a new direction in future research? A case study can be used as a tool for an exploratory investigation that highlights the need for further research about the problem. A case can be used when there are few studies that help predict an outcome or that establish a clear understanding about how best to proceed in addressing a problem. For example, after conducting a thorough literature review [very important!], you discover that little research exists showing the ways in which women contribute to promoting water conservation in rural communities of east central Africa. A case study of how women contribute to saving water in a rural village of Uganda can lay the foundation for understanding the need for more thorough research that documents how women in their roles as cooks and family caregivers think about water as a valuable resource within their community. This example of a case study could also point to the need for scholars to build new theoretical frameworks around the topic [e.g., applying feminist theories of work and family to the issue of water conservation].

Eisenhardt, Kathleen M. “Building Theories from Case Study Research.” Academy of Management Review 14 (October 1989): 532-550; Emmel, Nick. Sampling and Choosing Cases in Qualitative Research: A Realist Approach . Thousand Oaks, CA: SAGE Publications, 2013; Gerring, John. “What Is a Case Study and What Is It Good for?” American Political Science Review 98 (May 2004): 341-354; Mills, Albert J. , Gabrielle Durepos, and Eiden Wiebe, editors. Encyclopedia of Case Study Research . Thousand Oaks, CA: SAGE Publications, 2010; Seawright, Jason and John Gerring. "Case Selection Techniques in Case Study Research." Political Research Quarterly 61 (June 2008): 294-308.

Structure and Writing Style

The purpose of a paper in the social sciences designed around a case study is to thoroughly investigate a subject of analysis in order to reveal a new understanding about the research problem and, in so doing, contributing new knowledge to what is already known from previous studies. In applied social sciences disciplines [e.g., education, social work, public administration, etc.], case studies may also be used to reveal best practices, highlight key programs, or investigate interesting aspects of professional work.

In general, the structure of a case study research paper is not all that different from a standard college-level research paper. However, there are subtle differences you should be aware of. Here are the key elements to organizing and writing a case study research paper.

I.  Introduction

As with any research paper, your introduction should serve as a roadmap for your readers to ascertain the scope and purpose of your study . The introduction to a case study research paper, however, should not only describe the research problem and its significance, but you should also succinctly describe why the case is being used and how it relates to addressing the problem. The two elements should be linked. With this in mind, a good introduction answers these four questions:

  • What is being studied? Describe the research problem and describe the subject of analysis [the case] you have chosen to address the problem. Explain how they are linked and what elements of the case will help to expand knowledge and understanding about the problem.
  • Why is this topic important to investigate? Describe the significance of the research problem and state why a case study design and the subject of analysis that the paper is designed around is appropriate in addressing the problem.
  • What did we know about this topic before I did this study? Provide background that helps lead the reader into the more in-depth literature review to follow. If applicable, summarize prior case study research applied to the research problem and why it fails to adequately address the problem. Describe why your case will be useful. If no prior case studies have been used to address the research problem, explain why you have selected this subject of analysis.
  • How will this study advance new knowledge or new ways of understanding? Explain why your case study will be suitable in helping to expand knowledge and understanding about the research problem.

Each of these questions should be addressed in no more than a few paragraphs. Exceptions to this can be when you are addressing a complex research problem or subject of analysis that requires more in-depth background information.

II.  Literature Review

The literature review for a case study research paper is generally structured the same as it is for any college-level research paper. The difference, however, is that the literature review is focused on providing background information and  enabling historical interpretation of the subject of analysis in relation to the research problem the case is intended to address . This includes synthesizing studies that help to:

  • Place relevant works in the context of their contribution to understanding the case study being investigated . This would involve summarizing studies that have used a similar subject of analysis to investigate the research problem. If there is literature using the same or a very similar case to study, you need to explain why duplicating past research is important [e.g., conditions have changed; prior studies were conducted long ago, etc.].
  • Describe the relationship each work has to the others under consideration that informs the reader why this case is applicable . Your literature review should include a description of any works that support using the case to investigate the research problem and the underlying research questions.
  • Identify new ways to interpret prior research using the case study . If applicable, review any research that has examined the research problem using a different research design. Explain how your use of a case study design may reveal new knowledge or a new perspective or that can redirect research in an important new direction.
  • Resolve conflicts amongst seemingly contradictory previous studies . This refers to synthesizing any literature that points to unresolved issues of concern about the research problem and describing how the subject of analysis that forms the case study can help resolve these existing contradictions.
  • Point the way in fulfilling a need for additional research . Your review should examine any literature that lays a foundation for understanding why your case study design and the subject of analysis around which you have designed your study may reveal a new way of approaching the research problem or offer a perspective that points to the need for additional research.
  • Expose any gaps that exist in the literature that the case study could help to fill . Summarize any literature that not only shows how your subject of analysis contributes to understanding the research problem, but how your case contributes to a new way of understanding the problem that prior research has failed to do.
  • Locate your own research within the context of existing literature [very important!] . Collectively, your literature review should always place your case study within the larger domain of prior research about the problem. The overarching purpose of reviewing pertinent literature in a case study paper is to demonstrate that you have thoroughly identified and synthesized prior studies in relation to explaining the relevance of the case in addressing the research problem.

III.  Method

In this section, you explain why you selected a particular case [i.e., subject of analysis] and the strategy you used to identify and ultimately decide that your case was appropriate in addressing the research problem. The way you describe the methods used varies depending on the type of subject of analysis that constitutes your case study.

If your subject of analysis is an incident or event . In the social and behavioral sciences, the event or incident that represents the case to be studied is usually bounded by time and place, with a clear beginning and end and with an identifiable location or position relative to its surroundings. The subject of analysis can be a rare or critical event or it can focus on a typical or regular event. The purpose of studying a rare event is to illuminate new ways of thinking about the broader research problem or to test a hypothesis. Critical incident case studies must describe the method by which you identified the event and explain the process by which you determined the validity of this case to inform broader perspectives about the research problem or to reveal new findings. However, the event does not have to be a rare or uniquely significant to support new thinking about the research problem or to challenge an existing hypothesis. For example, Walo, Bull, and Breen conducted a case study to identify and evaluate the direct and indirect economic benefits and costs of a local sports event in the City of Lismore, New South Wales, Australia. The purpose of their study was to provide new insights from measuring the impact of a typical local sports event that prior studies could not measure well because they focused on large "mega-events." Whether the event is rare or not, the methods section should include an explanation of the following characteristics of the event: a) when did it take place; b) what were the underlying circumstances leading to the event; and, c) what were the consequences of the event in relation to the research problem.

If your subject of analysis is a person. Explain why you selected this particular individual to be studied and describe what experiences they have had that provide an opportunity to advance new understandings about the research problem. Mention any background about this person which might help the reader understand the significance of their experiences that make them worthy of study. This includes describing the relationships this person has had with other people, institutions, and/or events that support using them as the subject for a case study research paper. It is particularly important to differentiate the person as the subject of analysis from others and to succinctly explain how the person relates to examining the research problem [e.g., why is one politician in a particular local election used to show an increase in voter turnout from any other candidate running in the election]. Note that these issues apply to a specific group of people used as a case study unit of analysis [e.g., a classroom of students].

If your subject of analysis is a place. In general, a case study that investigates a place suggests a subject of analysis that is unique or special in some way and that this uniqueness can be used to build new understanding or knowledge about the research problem. A case study of a place must not only describe its various attributes relevant to the research problem [e.g., physical, social, historical, cultural, economic, political], but you must state the method by which you determined that this place will illuminate new understandings about the research problem. It is also important to articulate why a particular place as the case for study is being used if similar places also exist [i.e., if you are studying patterns of homeless encampments of veterans in open spaces, explain why you are studying Echo Park in Los Angeles rather than Griffith Park?]. If applicable, describe what type of human activity involving this place makes it a good choice to study [e.g., prior research suggests Echo Park has more homeless veterans].

If your subject of analysis is a phenomenon. A phenomenon refers to a fact, occurrence, or circumstance that can be studied or observed but with the cause or explanation to be in question. In this sense, a phenomenon that forms your subject of analysis can encompass anything that can be observed or presumed to exist but is not fully understood. In the social and behavioral sciences, the case usually focuses on human interaction within a complex physical, social, economic, cultural, or political system. For example, the phenomenon could be the observation that many vehicles used by ISIS fighters are small trucks with English language advertisements on them. The research problem could be that ISIS fighters are difficult to combat because they are highly mobile. The research questions could be how and by what means are these vehicles used by ISIS being supplied to the militants and how might supply lines to these vehicles be cut off? How might knowing the suppliers of these trucks reveal larger networks of collaborators and financial support? A case study of a phenomenon most often encompasses an in-depth analysis of a cause and effect that is grounded in an interactive relationship between people and their environment in some way.

NOTE:   The choice of the case or set of cases to study cannot appear random. Evidence that supports the method by which you identified and chose your subject of analysis should clearly support investigation of the research problem and linked to key findings from your literature review. Be sure to cite any studies that helped you determine that the case you chose was appropriate for examining the problem.

IV.  Discussion

The main elements of your discussion section are generally the same as any research paper, but centered around interpreting and drawing conclusions about the key findings from your analysis of the case study. Note that a general social sciences research paper may contain a separate section to report findings. However, in a paper designed around a case study, it is common to combine a description of the results with the discussion about their implications. The objectives of your discussion section should include the following:

Reiterate the Research Problem/State the Major Findings Briefly reiterate the research problem you are investigating and explain why the subject of analysis around which you designed the case study were used. You should then describe the findings revealed from your study of the case using direct, declarative, and succinct proclamation of the study results. Highlight any findings that were unexpected or especially profound.

Explain the Meaning of the Findings and Why They are Important Systematically explain the meaning of your case study findings and why you believe they are important. Begin this part of the section by repeating what you consider to be your most important or surprising finding first, then systematically review each finding. Be sure to thoroughly extrapolate what your analysis of the case can tell the reader about situations or conditions beyond the actual case that was studied while, at the same time, being careful not to misconstrue or conflate a finding that undermines the external validity of your conclusions.

Relate the Findings to Similar Studies No study in the social sciences is so novel or possesses such a restricted focus that it has absolutely no relation to previously published research. The discussion section should relate your case study results to those found in other studies, particularly if questions raised from prior studies served as the motivation for choosing your subject of analysis. This is important because comparing and contrasting the findings of other studies helps support the overall importance of your results and it highlights how and in what ways your case study design and the subject of analysis differs from prior research about the topic.

Consider Alternative Explanations of the Findings Remember that the purpose of social science research is to discover and not to prove. When writing the discussion section, you should carefully consider all possible explanations revealed by the case study results, rather than just those that fit your hypothesis or prior assumptions and biases. Be alert to what the in-depth analysis of the case may reveal about the research problem, including offering a contrarian perspective to what scholars have stated in prior research if that is how the findings can be interpreted from your case.

Acknowledge the Study's Limitations You can state the study's limitations in the conclusion section of your paper but describing the limitations of your subject of analysis in the discussion section provides an opportunity to identify the limitations and explain why they are not significant. This part of the discussion section should also note any unanswered questions or issues your case study could not address. More detailed information about how to document any limitations to your research can be found here .

Suggest Areas for Further Research Although your case study may offer important insights about the research problem, there are likely additional questions related to the problem that remain unanswered or findings that unexpectedly revealed themselves as a result of your in-depth analysis of the case. Be sure that the recommendations for further research are linked to the research problem and that you explain why your recommendations are valid in other contexts and based on the original assumptions of your study.

V.  Conclusion

As with any research paper, you should summarize your conclusion in clear, simple language; emphasize how the findings from your case study differs from or supports prior research and why. Do not simply reiterate the discussion section. Provide a synthesis of key findings presented in the paper to show how these converge to address the research problem. If you haven't already done so in the discussion section, be sure to document the limitations of your case study and any need for further research.

The function of your paper's conclusion is to: 1) reiterate the main argument supported by the findings from your case study; 2) state clearly the context, background, and necessity of pursuing the research problem using a case study design in relation to an issue, controversy, or a gap found from reviewing the literature; and, 3) provide a place to persuasively and succinctly restate the significance of your research problem, given that the reader has now been presented with in-depth information about the topic.

Consider the following points to help ensure your conclusion is appropriate:

  • If the argument or purpose of your paper is complex, you may need to summarize these points for your reader.
  • If prior to your conclusion, you have not yet explained the significance of your findings or if you are proceeding inductively, use the conclusion of your paper to describe your main points and explain their significance.
  • Move from a detailed to a general level of consideration of the case study's findings that returns the topic to the context provided by the introduction or within a new context that emerges from your case study findings.

Note that, depending on the discipline you are writing in or the preferences of your professor, the concluding paragraph may contain your final reflections on the evidence presented as it applies to practice or on the essay's central research problem. However, the nature of being introspective about the subject of analysis you have investigated will depend on whether you are explicitly asked to express your observations in this way.

Problems to Avoid

Overgeneralization One of the goals of a case study is to lay a foundation for understanding broader trends and issues applied to similar circumstances. However, be careful when drawing conclusions from your case study. They must be evidence-based and grounded in the results of the study; otherwise, it is merely speculation. Looking at a prior example, it would be incorrect to state that a factor in improving girls access to education in Azerbaijan and the policy implications this may have for improving access in other Muslim nations is due to girls access to social media if there is no documentary evidence from your case study to indicate this. There may be anecdotal evidence that retention rates were better for girls who were engaged with social media, but this observation would only point to the need for further research and would not be a definitive finding if this was not a part of your original research agenda.

Failure to Document Limitations No case is going to reveal all that needs to be understood about a research problem. Therefore, just as you have to clearly state the limitations of a general research study , you must describe the specific limitations inherent in the subject of analysis. For example, the case of studying how women conceptualize the need for water conservation in a village in Uganda could have limited application in other cultural contexts or in areas where fresh water from rivers or lakes is plentiful and, therefore, conservation is understood more in terms of managing access rather than preserving access to a scarce resource.

Failure to Extrapolate All Possible Implications Just as you don't want to over-generalize from your case study findings, you also have to be thorough in the consideration of all possible outcomes or recommendations derived from your findings. If you do not, your reader may question the validity of your analysis, particularly if you failed to document an obvious outcome from your case study research. For example, in the case of studying the accident at the railroad crossing to evaluate where and what types of warning signals should be located, you failed to take into consideration speed limit signage as well as warning signals. When designing your case study, be sure you have thoroughly addressed all aspects of the problem and do not leave gaps in your analysis that leave the reader questioning the results.

Case Studies. Writing@CSU. Colorado State University; Gerring, John. Case Study Research: Principles and Practices . New York: Cambridge University Press, 2007; Merriam, Sharan B. Qualitative Research and Case Study Applications in Education . Rev. ed. San Francisco, CA: Jossey-Bass, 1998; Miller, Lisa L. “The Use of Case Studies in Law and Social Science Research.” Annual Review of Law and Social Science 14 (2018): TBD; Mills, Albert J., Gabrielle Durepos, and Eiden Wiebe, editors. Encyclopedia of Case Study Research . Thousand Oaks, CA: SAGE Publications, 2010; Putney, LeAnn Grogan. "Case Study." In Encyclopedia of Research Design , Neil J. Salkind, editor. (Thousand Oaks, CA: SAGE Publications, 2010), pp. 116-120; Simons, Helen. Case Study Research in Practice . London: SAGE Publications, 2009;  Kratochwill,  Thomas R. and Joel R. Levin, editors. Single-Case Research Design and Analysis: New Development for Psychology and Education .  Hilldsale, NJ: Lawrence Erlbaum Associates, 1992; Swanborn, Peter G. Case Study Research: What, Why and How? London : SAGE, 2010; Yin, Robert K. Case Study Research: Design and Methods . 6th edition. Los Angeles, CA, SAGE Publications, 2014; Walo, Maree, Adrian Bull, and Helen Breen. “Achieving Economic Benefits at Local Events: A Case Study of a Local Sports Event.” Festival Management and Event Tourism 4 (1996): 95-106.

Writing Tip

At Least Five Misconceptions about Case Study Research

Social science case studies are often perceived as limited in their ability to create new knowledge because they are not randomly selected and findings cannot be generalized to larger populations. Flyvbjerg examines five misunderstandings about case study research and systematically "corrects" each one. To quote, these are:

Misunderstanding 1 :  General, theoretical [context-independent] knowledge is more valuable than concrete, practical [context-dependent] knowledge. Misunderstanding 2 :  One cannot generalize on the basis of an individual case; therefore, the case study cannot contribute to scientific development. Misunderstanding 3 :  The case study is most useful for generating hypotheses; that is, in the first stage of a total research process, whereas other methods are more suitable for hypotheses testing and theory building. Misunderstanding 4 :  The case study contains a bias toward verification, that is, a tendency to confirm the researcher’s preconceived notions. Misunderstanding 5 :  It is often difficult to summarize and develop general propositions and theories on the basis of specific case studies [p. 221].

While writing your paper, think introspectively about how you addressed these misconceptions because to do so can help you strengthen the validity and reliability of your research by clarifying issues of case selection, the testing and challenging of existing assumptions, the interpretation of key findings, and the summation of case outcomes. Think of a case study research paper as a complete, in-depth narrative about the specific properties and key characteristics of your subject of analysis applied to the research problem.

Flyvbjerg, Bent. “Five Misunderstandings About Case-Study Research.” Qualitative Inquiry 12 (April 2006): 219-245.

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