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Ethnography
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DOI: 10.1177/1466138108099586
2009 10: 5Ethnography
Mario Luis Small
field-based research
`How many cases do I need?' : On science and the logic of case selection in
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‘How many cases do I need?’
On science and the logic of case selection in
field-based research
■ Mario Luis Small
University of Chicago, USA
A B S T R A C T ■ Today, ethnographers and qualitative researchers in
fields such as urban poverty, immigration, and social inequality face an
environment in which their work will be read, cited, and assessed by
demographers, quantitative sociologists, and even economists. They also
face a demand for case studies of poor, minority, or immigrant groups and
neighborhoods that not only generate theory but also somehow speak to
empirical conditions in other cases (not observed). Many have responded
by incorporating elements of quantitative methods into their designs, such
as selecting respondents ‘at random’ for small, in-depth interview projects
or identifying ‘representative’ neighborhoods for ethnographic case
studies, aiming to increase generalizability. This article assesses these
strategies and argues that they fall short of their objectives. Recognizing
the importance of the predicament underlying the strategies – to
determine how case studies can speak empirically to other cases – it
presents two alternatives to current practices, and calls for greater clarity
in the logic of design when producing ethnographic research in a multimethod
intellectual environment.
K E Y W O R D S ■ ethnographic methods, generalizability,
representativeness, validity, case study, sequential interviewing, extended
case method, science
graphy
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A R T I C L E
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Probably the most memorable of the lectures of Nobel-prize winning physicist
Richard Feynman was his 1974 commencement address at Caltech,
where he described what he calls ‘cargo cult science’. Feynman, worried
about the preponderance of what he believes are pseudo-sciences, compares
these practices to the cargo cults of the South Pacific:
In the South Seas there is a Cargo Cult of people. During the war they saw
airplanes land with lots of good materials, and they want the same thing to
happen now. So they’ve arranged to make things like runways, to put fires
along the sides of the runways, to make a wooden hut for a man to sit in . . .
[the controller] – and they wait for the airplanes to land. They’re doing everything
right. The form is perfect. It looks exactly the way it looked before.
But it doesn’t work. No airplanes land. So I call these things Cargo Cult
Science, because they follow all the apparent precepts and forms of scientific
investigation, but they’re missing something essential, because the planes
don’t land. (Feynman, 1999: 208–9)
Feynman’s lecture was devoted largely to practices such as ESP, but the hints
about social science were difficult to miss. (In fact, he criticized a psychologist’s
advice to his student not to replicate the studies of others.) Pseudoscientists
were expert imitators but terrible practitioners, adopting the form
of science but nothing else. In this respect, his analogy might have been
stronger had he noted that some New Guinean cargo cultists had fashioned
their own airplanes out of logs, sticks, and leaves, remarkably accurate
replicas that, lacking engines and a foundation in aerodynamics, would
never fly (Harris, 1974; Worsley, 1968).
While Feynman probably underestimated the successes of social science,
his observations are worth noting by at least one major segment of contemporary
ethnographers, for whom the temptations of imitation have never
been stronger. The problem of imitation is not new to social scientists, who
from the start have argued heatedly (and repeatedly) over the merits of
emulating the natural sciences in pursuit of social scientific methods
(Dilthey, 1988; Lieberson and Lynn, 2002; Saiedi, 1993). But today, an
important subset of ethnographic researchers – and of qualitative
researchers more generally – faces its own version of that dilemma: whether
to emulate basic principles in quantitative social sciences in establishing
standards of evidence for qualitative work. Some background is necessary.1
The predicament of ethnographic work in multi-method contexts
The predicament arises from what might seem to be an unqualified accomplishment,
the simmering of the counterproductive debates, which reached
a boiling point during the 1980s, over the relative merits of quantitative
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versus qualitative research. Today’s calmer waters have been especially
regenerative for the fields of urban poverty, social inequality, and immigration,
where both quantitative and qualitative works flourish, and where
experts in one methodological tradition frequently cite those in others. In
fact, several major studies in these fields have employed, with varying
degrees of integration, both quantitative and qualitative data, the latter
being at times interview-based and at times ethnographic. Examples are
Portes and Rumbaut’s recent studies of the children of US immigrants
(Portes and Rumbaut, 2001; Rumbaut and Portes, 2001), Wilson and his
colleagues’ studies of urban conditions in Chicago (Wilson, 1996; Wilson
et al., 1987), and England and Edin and their colleagues’ studies of urban
single mothers in the US (see England and Edin, 2007). These fields stand
in contrast to others where, for epistemological, political, or historical
reasons, most practitioners work within a single method or set of methods,
as in symbolic interactionism or the interpretive work on culture.
But the more cooperative spirit in urban poverty, social inequality, and
immigration has only spread so far. Despite the more methodologically open
environment, research in these fields remains dominated by quantitative
sociologists, demographers, and even economists (Wacquant, 1997; see also
Burawoy, 2005). While important ethnographies in these fields continue to
be published and highly cited (e.g. Duneier, 1999; Levitt, 2001; Pattillo,
1999; see Newman and Massengill, 2006), most articles in these fields
published in the top generalist journals, such as American Journal of
Sociology, the American Sociological Review, and Social Forces, remain
quantitative in nature.2 The preponderance of statistical research stems in
part from the steady and continuous supply of easily accessible quantitative
data, such as the decennial US Census, the Current Population Survey,
the Panel Study of Income Dynamics, and the National Longitudinal Survey
of Youth, all of which contain many variables related to poverty, immigration,
urban conditions, neighborhoods, and socio-economic status. In
addition, urban poverty, social inequality, and immigration (along with
criminology, education, and public health) remain among the most highly
funded fields in US social science, and the largest funders in these fields –
nonprofit organizations and government agencies such as the Russell Sage
Foundation, the Ford Foundation, the National Science Foundation, the US
Department of Housing and Urban Development, and the National Institutes
of Health – have exhibited a greater inclination to fund quantitative
projects. The edited volumes generated by these funding streams bear
evidence to this claim. Consider a few highly cited collections: Goering and
Feins’ (2003) recent volume on the effects of neighborhood poverty, funded
by HUD; Neckerman’s (2004) volume on social inequality, funded by
Russell Sage; and O’Connor et al.’s (2001) study of urban inequality in
multiple cities, funded by both Russell Sage and the Ford Foundation. Each
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of these volumes, while demonstrating deference to ethnographic research,
overwhelmingly reports quantitative findings.3
These circumstances have produced at least two consequences. First, in
contrast to other fields where ethnographers work, ethnographic studies in
urban poverty, inequality, and immigration are often evaluated – even
on methodological grounds – by quantitative researchers. Thus, while
ethnographers doing work on, for example, narrative and culture can confidently
expect their work to be reviewed primarily, if not exclusively, by
other qualitative researchers, those in the aforementioned fields must count
among the potential reviewers of their work, demographers, quantitative
sociologists, and even economists – scholars who are experts on the subject
matter without necessarily being experts on the method. Inevitably, the
reviews will cover issues not traditionally addressed in closed ethnographic
intellectual communities. For example, my Villa Victoria, an ethnographic
study of a predominantly Puerto Rican housing complex in Boston, was
reviewed in Contemporary Sociology by a demographer, who, in a generally
balanced article, covered both theoretical and methodological issues.
Yet the methodological discussion did not center on the extent to which I
attained an empathetic understanding of my informants, on the level of
reflexivity in the work, or on the extent to which the history of the neighborhood
informed the analysis; instead, it focused on one of demography’s
central concerns, whether the neighborhood was representative:
While the conditional approach is an asset from a theoretical stand point, it
is a limitation from a methodological perspective. The generalizability of the
findings is a concern. Since theories are based on generalizations, focusing
on exceptions as advocated by the conditional approach makes us question
the applicability of these findings to other neighborhoods. (Morales, 2006:
284)
Consider another example. Fordham and Ogbu’s (1986) highly cited study
of ‘acting white’ among black students in a Washington, DC middle school
has been rediscovered over the last 10 years by sociologists and economists
interested in culture and urban inequality, a rediscovery oriented toward
methodological and empirical issues. But this attention centered on none of
the core issues identified in Burawoy’s (2003) recent review of types of
ethnographic ‘revisits’, such as reconstructing the theory after returning to
the school or assessing the structural forces at play in US cities during the
late 1980s. Instead, the new critiques focused on whether the few dozen
students interviewed by Fordham and Ogbu were statistically representative
of black students in US society (Ainsworth-Darnell and Downey, 1998;
Cook and Ludwig, 1997). Consider a third example, from the literature
on transnationalism, where ethnographies, such as Levitt’s (2001) study
among Domincan migrants to the US, have confirmed the prevalence of
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transnational practices among immigrants in all continents. In an important
recent study evaluating these works, quantitative researchers critiqued
the latter on methodological terms – but not by focusing on the authors’
ability to conduct multi-site ethnography, or on the challenges of establishing
rapport quickly and effectively in different countries. Instead, the
critiques focused on the questions that worry demographers, even employing
explicitly the language of variable selection:
This emerging literature on immigrant transnationalism is characterized by
an empirical base consisting exclusively of case studies. Qualitative case
studies consistently sample on the dependent variable, that is, they document
in detail the characteristics of immigrants involved in transnational activities
but say little about those who are not. (Portes et al., 2002: 279; italics
added)
We may set aside for the moment whether any of these critiques is valid in
order to highlight the larger predicament: ethnographers in these fields can
expect to be assessed on their methods by quantitative researchers.
Second, ethnographic studies in urban poverty, social inequality, and
immigration operate in an environment at once thirsty for in-depth case
studies that describe conditions in poor, minority, immigrant, or otherwise
non-mainstream groups, neighborhoods and communities, and either skeptical
or uncertain about the relationship between these ‘small-n’ studies and
the larger population of groups, neighborhoods, and communities that the
case studies are expected to represent (Lieberson, 1991). Consider a
contrast. When Geertz (1973) wrote on the cockfights in a small Balinese
village, many expected his theoretical model (of how games can embody
societal power relations) to be applicable to other sites, but few expected
the empirical findings to be so applicable – that is, for cockfights to look
similar or to follow the same rules in other villages throughout or outside
of Indonesia. The latter would be wholly beside the point.4 But ethnographers
in the aforementioned fields work in a professional, intellectual, and
policy environment that demands empirical findings applicable to other
cases. When ethnographers today describe conditions in, for example, one
poor black neighborhood in St Louis, MO, many of their readers in the
urban poverty literature expect to be learning about the conditions in poor
black neighborhoods in general – in Boston, Los Angeles, New York, and
perhaps even London and Rio de Janeiro – not merely that neighborhood
in St Louis. In fact, ethnographies of single neighborhoods are often cited
to argue that conditions in ‘the ghetto’, ‘the underclass’, ‘the immigrant
enclave’, or other similar categories exhibit some set of empirical characteristics,
such as desolation, graffiti, street disorder, gang presence, street
entrepreneurship, etc. (on the perils of this practice, see Small, 2007, forthcoming
b). Similar expectations surround the interpretation of in-depth
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interview studies with small numbers of respondents. When interpreting a
study of, for example, 40 immigrant low-income women in San Diego, CA,
researchers expect to learn something empirical about the conditions of
low-income immigrants in other cities and regions, not merely about those
40 women. In sum, in fields such as urban poverty and immigration in the
US, ethnographic case studies are often explicitly expected to represent
larger entities. Nevertheless – and this is key – the precise relationship
between such cases and the larger populations they are expected to
represent remains unclear.
It is in this context that imitation, as described earlier, arises. The core
predicament that many ethnographers face is deceptively straightforward:
how to produce ethnographic work that keeps at bay the critiques expected
from quantitative researchers while also addressing the thirst for in-depth
studies that somehow or other ‘speak’ to empirical conditions in other cases
(not observed). How to select studies such that these types of inferences are
valid?
As I discuss below, for all too many in recent years, the answer has been
to emulate the practices of quantitative researchers, especially the foundation
in classical or frequentist statistics – that is, to match, as closely as
either possible or practical, standard survey practices designed to ensure
representativeness, and thus generalizability (e.g. Klinenberg, 2002). The
result has been a form of imitation grounded in language, or, more precisely,
the adoption of words with only a superficial (and at times incorrect) application
of their meaning. Today, many researchers in these fields encourage
their students doing ethnographic work to ensure that their small samples
are ‘unbiased’ or that their single-case studies are ‘representative’ or ‘not
selected on the dependent variable’. As we shall see, the most formal
expression of this perspective is represented in King et al. (1994), but
informal versions of this approach abound. The basic critique of this article
is that these practices constitute little more than applying words without
adopting their meaning, constructing sticks-and-leaves airplanes that will
never fly.
The problems faced by ethnographers working in interdisciplinary fields
today are both substantively and publicly important, creating a need for
programmatic clarity about these questions. That clarity, however, has been
missing, and, in fact, many of the most commonly employed fieldwork
manuals hardly address the topic (Hammersley and Atkinson, 1995;
Lofland and Lofland, 1995).5 Methods of scientific inquiry are languages
to the extent that they constitute systems of thought, with terms and ways
of framing problems that are specific to their systems. I will argue that
solutions should involve developing alternative languages and clarifying
their separate objectives, rather than imitating the language of classical
statistics for problems to which it is not suited. What I have described is a
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large and complex problem that I cannot hope to cover entirely in one
article. Instead, I will examine one issue, that of ‘generalizability’, one of
the most central concerns that quantitative researchers raise about ethnographic
research in the aforementioned fields. To make the problem clear,
I will discuss two common scenarios, one from in-depth interview work
and one from participant observation, under which ethnographers
concerned about science attempt to make their work ‘generalizable’. After
critiquing these forms of thinking about generalizability, I discuss two major
alternatives.6
First scenario: the ‘representative’ small-n interview-based study
One of the most common practices in qualitative sociology today is to
conduct in-depth, open-ended interviews. Sometimes, these are fielded on
hundreds of respondents (Lamont, 1992; Newman, 1999); more typically,
they involve a small number of interviewees (30 or 40). It is in this latter
case that the problems are more salient, since the questions of generalizability
are more obvious and the answers to these less clear. Consider the
following scenario.
The most common question
Jane, for her second-year paper, would like to study the attitudes toward
immigration of working-class African Americans. To capture the depth and
nuance of these attitudes, she wishes to conduct lengthy open-ended interviews,
and she is planning to interview 35 respondents. Having taken
courses in basic statistics and research design, Jane worries that, by doing
‘qualitative work’, she is not conducting truly scientific research. She sits
before her adviser, and asks one of the most common questions posed by
beginning students doing in-depth interview work in these fields: ‘How do
I ensure my findings will be generalizable?’
Her adviser recommends finding a city with a large working-class African
American population, obtaining a telephone directory, and randomly
sampling people from it. He knows to expect, at best, a 50 percent response
rate, so he recommends contacting 100 people selected at random. Jane
follows the plan, and miraculously all phone numbers are valid and
everyone answers the phone. Of the 100 respondents, 60 hang up on her,
40 agree to an interview, and 35 follow through with it. (Experienced interviewers
know these figures to be highly optimistic.) The city is so segregated
that all of them happen to be African American. She conducts 35
high-quality two-hour interviews that delve deeply into attitudes about
immigration, uncovering subtle relationships among attitudes, experience
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with discrimination, gender, and Southern origins, and she happily
completes her paper. Since (she believes) her method mirrors that of
Lamont’s (1992) well-regarded Money, Morals, & Manners, she is confident
in the ‘generalizability’ of her findings about the black working class.7
Jane’s predicament is standard; her solution, rather common (e.g.
Hermanowicz, 1998; Walzer, 1997; to a lesser extent, Aries and Seider,
2005). There is, however, an important problem: under no statistical definition
of ‘generalizability’ could the responses of those 35 individuals be
considered to reflect reliably the conditions of the African American
working class. From the perspective of statistical generalizability, Jane’s
research suffers from two problems.
First, the sample has an inbuilt and unaccounted for bias.8 Jane only
interviewed the 35 percent of respondents who were polite enough to talk
to her, friendly enough to make an appointment based on a stranger’s cold
call, and extroverted enough to share their feelings with this stranger for
two hours. These people may have systematically different attitudes about
others, including immigrants, than non-respondents. Since she knows
nothing about those who did not respond (they hung up), she has no way
of adjusting the inferences she obtained from the 35 respondents. In
addition, since she knows nothing about working-class blacks in other
cities, she still does not know if, had she attained 100 percent response
rates, the respondents in her city would be typical or atypical of the black
working class.
Second, regardless of how it was selected, the sample is too small to make
confident predictions about complex relationships in the population of
working-class blacks at large. Among my graduate students working on indepth
interview study designs, perhaps the single most common question I
hear is, ‘How many people do I need to interview (for my findings to be
generalizable)?’ The answer depends on the distribution of the variables of
interest, whether the students want to describe distributions (e.g. proportion
Democrat) or present causal relationships (e.g. whether Republicans will
have stronger anti-immigrant attitudes than Democrats), and how many
variables are involved, among other factors (King et al. (1994) provide a
formula, based on standard statistical assumptions). The short answer,
however, is that rarely will students have enough well-selected in-depth
interview respondents that their findings about subtle causal relationships
involving multiple variables will be statistically generalizable to a large
national population. For that, one needs a survey.
Suppose Jane only wanted to discover how many working-class blacks
are pro-immigration reform (one ‘yes or no’ question); and that she wanted
to be confident at a 95 percent level that the average in her sample matched
the average in the population at large within +/– five percentage points;
and that the population of working-class blacks in the US was 2,000,000
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people (for large populations, the exact size does not matter very much).9
In this case, she would need 385 respondents.10 If Jane narrowed her focus,
and only wanted to be confident about the 1000 working-class blacks in
one city, she would need 278.
In fact, nothing Jane could do with her three dozen people would ensure
that they matched, with high certainty, the characteristics of the US
working-class black population. Some interview-based researchers prefer to
ignore these two problems and refer to studies such as Jane’s as ‘representative’
because they were based on a ‘random’ sample. In doing so, they are
simply adopting words without adopting their meaning, referring to
wooden tubes as airplanes. If Jane sought a representative study, she should
have conducted a survey (and assumed all of its limitations, such as having
to construct a formal questionnaire and reducing its length to maintain high
response rates).
Better than nothing?
The natural question is whether, having acknowledged these difficulties,
Jane is still not better served by selecting her respondents ‘at random’ (in
quotation marks because her final sample is not statistically random due to
the large proportion of people who did not respond) than to have adopted
some other non-random selection strategy. Not always. Consider two
standard alternatives in light of these questions.
One is sampling for range, a longstanding technique which might yield
better and more reliable data depending on her interests (Weiss, 1994). By
this technique, the analyst identifies sub-categories of the group under
study and ensures to interview a given number of people in that category.
For example, suppose Jane suspected that gay and lesbian respondents
might be more sympathetic to immigrants, and decided this was one of
the core issues she wanted to understand. Even a truly random sample
would have yielded, at best, three or four gay or lesbian respondents out
of 35, of which one or two, at best, would reveal this to her. This would
leave her no room to examine her question. In these circumstances, Jane
would be better served designing her study to include a large, pre-determined
number of gay and lesbian respondents, even if this required finding
them through non-random means, such as contacting formal organizations
and requesting references. For many questions of interest to interviewbased
researchers in the social sciences, sampling for range is more
effective. Of course, from the language of statistics, Jane will continue
having problems with bias and representativeness. However, from a more
appropriate language, she will now be able to identify (at least some of)
the mechanisms through which sexual orientation and attitudes about
immigration are related.
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Another alternative is snow-ball sampling, the well-known practice of
asking interviewees to recommend other interviewees (Weiss, 1994). Snowballing
almost always increases the number of respondents, because people
become more receptive to a researcher when the latter has been vouched
for by a friend as trustworthy. (This trustworthiness might also translate
into greater openness, producing deeper interviews, but I have not seen
anyone demonstrate this proposition.) For example, if Jane had contacted
100 people, each based on a personal referral, she might have interviewed
75 (it is impossible to know), but certainly many more than the number
obtained by cold-calling.
One consequence of snowballing is that the final interviewees are more
likely to know one another than would be the case had they been selected
at random. Thus, they are more likely to constitute a social network. For
this reason, many argue, again following the precepts of classical statistics,
that snowball samples in a small study such as Jane’s would be ‘more biased’
than the ‘random’ sample she employed. (This type of critique is often
applied to interview-based studies of social networks.)
I believe this view is mistaken on two grounds. First, suppose we assessed
both methods by the standards of classical statistics. In one case, there are
75 out of 100 people interviewed through personal referrals; in the other,
there are 35 who agreed to participate out of 100 selected at random. By
the standards of classical statistics, both samples would have a bias
problem, the first due to in-network selection and the second due to nonresponse.
What proponents of the random selection approach to small-n
in-depth interviewing rarely mention is that many people who are coldcalled
will not agree to long, in-depth interviews on personal topics with a
stranger. This often buried detail – how many people refused, hung up, or
were not home? – is critical. I am not surprised that many such studies do
not report it.
Second, we should not assess either method by the standards of classical
statistics. That is to say, in a deeper and more important sense, ‘bias’ is the
wrong term. What an in-depth interviewer with three dozen respondents
faces is not a ‘bias’ problem but a set of cases with particular characteristics
that, rather than being ‘controlled away’, should be understood,
developed, and incorporated into her understanding of the cases at hand
(more on this below). By inaccurately labeling ‘representative’ the strategy
that Jane employed, we erroneously assume that the others are ‘biased’. Not
only would Jane’s ostensibly representative sample be biased by quantitative
standards – neither bias nor representativeness is an appropriate
standard for the kind of research Jane wanted to conduct.
To be clear, there are only two solutions to Jane’s predicament: she
should not conduct the study or she should change the language through
which she interprets it. The half-way solution, of ‘trying to make it
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representative’, does not work. Many are reluctant to agree to the first
because it seems to imply that all interview-based studies should involve
large samples (such as Newman, 1999). While such large studies are
valuable, there is a place for a small interview study to make meaningful
contributions to knowledge, provided the language and assumptions
through which it is interpreted differ. In fact, as I suggest later, we might
benefit from not calling Jane’s interviewees a ‘sample of n = 35’, but,
instead, a ‘set of 35 cases’.
Second scenario: the study of an ‘average’ neighborhood
There is a similar problem in participant observation research aimed at
dealing with large-n questions. Today, major generalizations in both the
public and in the academic sphere are made about conditions in urban
areas, such as black and Latino inner-city neighborhoods in the US, favelas
in Brazil, or banlieues in Paris. Ethnographers are expected and asked to
penetrate the neighborhoods and report to the public on conditions in such
neighborhoods, not only to test the generalizations but also to produce their
own, to explain, for example, whether neighborhood conditions exacerbate
the effects of heat waves or natural disasters. The question remains – how
to select a case and design a study to render such statements empirically
valid? Again, a common answer, implicit or explicit, is to search for
representative cases. A hypothetical scenario should be instructive.
Selecting the average
Bill, a graduate student in sociology, wishes to study how neighborhood
poverty affects out-of-wedlock births, by conducting an in-depth ethnographic
study of a single high-poverty neighborhood. His main concern is
to uncover the set of mechanisms underlying this process. However, like
Jane, he wants to ensure his findings are ‘generalizable’ to poor neighborhoods.
Dissatisfied with the absence of a clear answer in his standard
graduate methods course, he turns to the highly citied King et al. (1994)
model. The authors address a similar problem directly, and Bill finds solace
in their solution:
For example, we could first select our community very carefully in order to
make sure that it is especially representative of the rest of the country . . .
We might ask a few residents or look at newspaper reports to see whether
it was an average community or whether some nonsystematic factor had
caused the observation to be atypical . . . This would be the most difficult
part of the case-study estimator, and we would need to be very careful that
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bias does not creep in. Once we are reasonably confident that bias is minimized,
we could focus on increasing efficiency. To do this, we might spend
many weeks in the community conducting numerous separate studies . . .
(King et al., 1994: 67–8)11
Bill turns to the census, finds a neighborhood that is 40 percent poor, 60
percent black, with 80 percent of the households female headed and (he
discovers at the site) most streets littered and covered in graffiti, all of which
seem to accord with his definition of a ‘representative’ poor neighborhood
(or, to paraphrase King et al., an average poor community). To comply with
IRB regulations, Bill gives his neighborhood a pseudonym, ‘The Streets’,
and reports that it is located in a ‘large Midwestern city’.12 Bill conducts
his study, and finds that residents in this neighborhood are distrustful of
each other. This distrust, he finds, makes women unwilling to marry the
fathers of their children. Since his neighborhood was representative, Bill
surmises, he is confident that neighborhood poverty increases out-ofwedlock
births in poor neighborhoods at large through the mechanism of
reduced trust, among mothers, toward potential fathers.
Either explicit or implicit versions of Bill’s approach to selecting study
sites – that is, studying neighborhoods that seem to be typical ghettos,
enclaves, or housing projects in order to improve one’s confidence in the
generalizability of empirical statements to other neighborhoods – abound.13
The problem with this approach is that, no matter how Bill selected his
single neighborhood, it will never be representative of poor neighborhoods.
Bill suffers from two problems. The first is exacerbated by his conception
of an ‘average’ neighborhood. Since Bill lacked the means to determine –
beyond the limited neighborhood characteristics recorded in the US Census
– that his neighborhood was in fact statistically average, he settled on a
neighborhood that appeared typical, one exhibiting a preponderance of
graffiti, for example, since this accorded with his picture of the conditions
in an ‘average’ poor neighborhood. This selection was no doubt influenced
by film and television images of poor neighborhoods, images produced for
commercial reasons which may or may not bear any resemblance to statistically
average neighborhoods. The second problem is Bill’s confusion of
‘representative’ with ‘average’. The neighborhood’s conditions may happen
to match the traits that, from the census, one knows to be at the mean on
observed demographic characteristics. But, as Frankfort-Nachmias and
Nachmias (2000: 167) write, ‘a sample is considered representative if the
analyses made using the sampling units produce results similar to those that
would be obtained had the entire population been analyzed’. No ‘sample’
of a single neighborhood can meet this criterion. In fact, there is no way to
determine whether the same results would have been obtained by studying
the population of neighborhoods at large. Bill has painted himself into the
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figurative corner in which he has assumed a warrant to make generalizations
based on a one-n study (Lieberson, 1991; on warrants, see Katz,
1997).
To be clear on the hopelessness of Bill’s situation given his objectives,
consider one potential solution, obtaining copious and very detailed information
on the neighborhood, the generally sensible recommendation by
King et al. (1994). Some believe that Bill could make up for the ‘lack of
variation’ in his single study by generating variation from within, and make
up for the overall ‘lack of statistical power’ by digging deeper into his single
case. Bill, for example, could examine in depth his neighborhood’s history
and institutions, and produce a rich, detailed, multi-layered study of its
conditions. Obtaining more data on a case is always a laudable practice,
but from the perspective of statistical generalizability, this ‘solution’ offers
no advantage. Suppose that instead of neighborhoods we were studying
individuals, and selected one person with the characteristics of the average
American: a married 36-year-old female with a high school education who
earned $36,911 last year.14 We interviewed this female for many hours
about her opinions on the admission of Turkey into the European Union.
How confident would we be that her thoughts accurately reflected those of
the average American? A scientist would have no confidence, and interviewing
her for 20 or 200 additional hours would not change this fact.15
The same logic is applicable in Bill’s case. As his readers, we may want
to believe that he tapped into the true (essential?) nature of ‘the American
ghetto’ because the neighborhood either matched census-collected traits of
the average poor neighborhood or it generally accorded with pre-existing
notions of conditions in such neighborhoods, a sentiment reinforced by the
neighborhood’s pseudonym (‘The Streets’) and anonymous location. In fact,
this is precisely how researchers in urban sociology, immigration, and social
inequality frequently interpret and cite neighborhood ethnographies (see
Small, 2007, 2008b). But reason would compel us to think otherwise: Bill
has earned a warrant to speak empirically about the average ‘ghetto’ that
is no greater than a study of the single 36-year-old female would have
earned to speak empirically about the average American. In the language
of statistics, these are both samples of one.
Better than the alternatives?
One could question, again, whether Bill’s strategy is not superior to any
alternative. An alternative is to search for unique cases (Small, 2004; van
Velsen, 1978 [1967]). Suppose that Bill had chosen a neighborhood with a
40 percent poverty rate but little garbage or graffiti and a unique architectural
design due to the influence of a mayor interested in promoting
architecture in the city. It is tempting to assume that inferences based on
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this neighborhood would be less statistically generalizable than those based
on ‘The Streets’, since the latter was more ‘typical’ (in fact, this assumption
informed Morales, 2006). But, based on a sample of one, they are neither
more nor less so. As before, one could ask if there is any harm in pursuing
the statistics-inspired ‘random’ or ‘average’ strategy. Sometimes there is.
Suppose the mayor in the second case also had instituted a radical and
unique policy whereby mothers received significantly higher rent subsidies
plus $1000 per child for a college fund if they married before the birth of
their second child. This rare case would suddenly present Bill an exceptional
opportunity to examine the relationship among high poverty, policy,
and out-of-wedlock births in ways that cases that happen to be at the mean
might not. In case studies, rare situations are often precisely what the
researcher wants (Small, 2004; Yin, 2002; also Schudson, 1992). (More on
this below.)
Alternatives
Jane and Bill’s designs, and related approaches to render field studies more
generalizable, simply fail in their objectives. I see only three solutions to
this predicament: 1) to ignore the problem; 2) to qualify the work by
explaining that it is provisional or ‘hypothesis generating’; and 3) to
conceive and design the work from a different perspective and language of
inquiry.
While ignoring the problem may seem to be inappropriate, it remains
a suitable option under some circumstances, given the different goals that
underlie different theoretical perspectives. As in the case of Geertz’s (1973)
cockfight study, the theoretical perspective informing a case study may
render irrelevant whether the study provides empirical information on
conditions in other cases. For example, ethnomethodologists aim to study
practical life as it is experienced, and they assume that social reality is
both inter-subjective and radically situational, such that the meaning of
actions and events can only be explained within the particular set of
circumstances in which they occurred (Garfinkel, 1967). This assumption
(that meanings are indexed to particular situations) implies that whether
other sites – for example, other neighborhoods – would exhibit the same
empirical characteristics is not merely beside the point, but it would
erroneously presume that the analyst can simply extract the characteristics
of a neighborhood from the context in which actors experienced them
and expect them to have the same consequences elsewhere. Similarly,
narrative theories fundamentally assume that identity derives from
personal experiences and the narratives actors tell themselves about them.
And while conditions shared with others, such as the experience of race
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discrimination, can affect an actor’s narrative of self, her ultimate narrative
identity depends on her accumulation of experiences, which is hers alone
(Somers, 1994). In this light, asking whether the experiences of one actor
reveal something empirical about others would be conceptually senseless,
and beside the point.16
But while these and other perspectives can afford to (in fact, by design
often must) ignore the problem without consequences, not all perspectives
can. The intellectual, professional, and public environment described at the
start of this article undermines efforts to simply ignore the problem in the
context of urban poverty, immigration, and social inequality scholarship.
The field requires ethnographic and in-depth interview-based case studies,
and it requires some answer about the empirical relationship between such
case studies and other sites not observed.
The second solution, conceiving of the work as hypothesis generating, is
also suitable. However, as I show below, hypotheses may be either logical
or senseless, and different strategies will yield substantially better hypotheses
than those a project such as Bill’s might generate. Simply adding a
qualifier or disclaimer without articulating the difference between good and
bad hypotheses is merely a reactive solution to an external threat, not an
epistemological position grounded in a sound perspective.
In the rest of the article, I make a case for the third option that provides
a way of not only generating better hypotheses but also producing
compelling empirical statements. While several of the ideas I propose have
been discussed in other contexts, they have not been examined in light of
the contemporary predicament presented at the start of this article. For this
reason, the ideas require refinement, development, and in one case major
elaboration; their implications for what scholars such as Jane and Bill
should do must be articulated. I will discuss systematically two alternatives,
an extension of the extended case method and what I term sequential
interviewing.
First alternative: extending the extended case method
Probably the most prominent recent solution to the problem of generalization
in case studies has been the extended case method, by which researchers
analyze a particular social situation in relation to the broader social forces
shaping it. In American sociology, the extended case method is most often
associated with Burawoy (Burawoy, 1998; Burawoy et al., 1991); elsewhere,
it is associated with Gluckman and the Manchester School
(Gluckman, 1961; also Evens and Handelman, 2006). Even though
Burawoy learned the method from van Velsen, one of Gluckman’s students
(Burawoy et al., 1991), there are still, in fact, several extended case
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methods, or several conceptions of the core of the procedure. For example,
Mitchell (1983) and van Velsen (1978 [1967]) describe the core of the
method in somewhat different terms, with the latter placing greater
emphasis on the identification of unique cases; and Burawoy’s latest (1998)
formulation differs in important details from his initial statement in 1991,
which itself was an ‘extension’ of van Velsen’s (Burawoy et al., 1991: 326).
For our purposes, two of these formulations matter most, Burawoy’s and
Mitchell’s.
The Berkeley school
Michael Burawoy made his first major statement on the method in a work
coauthored with several of his Berkeley graduate students, who conducted
empirical analyses applying the extended case method (Burawoy et al.,
1991). For them, the method is one of two ways to relate conditions in a
given case (organization, neighborhood, social event) to the society at large
in which it is embedded. In the interpretive method, Burawoy argues, the
case reveals the essential nature of society at large, the way in Geertz’s work
the cockfight embodied the social organization of Balinese society (Geertz,
1973). In the extended case method, the case is understood by investigating
the larger forces shaping conditions in the case – Geertz’s cockfight
would be understood as a ‘ritual of resistance to colonial and then Javanese
domination’, and the economic and political forces shaping it would be the
subject of analysis (Burawoy et al., 1991: 278; Burawoy, 1998). Burawoy’s
distinction seems to suggest that ‘extending’ is what the analyst does to
understand the case: the analyst investigates society at large to determine
its impacts on the case at hand.
But what is the basis of generalization in Burawoy’s conception? By my
reading, Burawoy is inconsistent on this point. On the one hand, he seems
to suggest that the method is not inductive, in contrast, for example, to
grounded theory. In fact, he defines the core of the method as one ‘which
examines how the social situation is shaped by external forces’ (Burawoy
et al., 1991: 6), which suggests that the ultimate purpose is to understand
the social situation. As he explains when contrasting the method to
grounded theory, while the latter develops ‘micro foundations of a macrosociology’,
the extended case method develops the ‘macro foundations of a
microsociology’ (Burawoy et al., 1991: 280; Burawoy, 1998), which seems
to imply that the purpose is to understand the case, not to generalize from
it.17 On the other hand, Burawoy does provide at least part of an answer.
Rather than ‘statistical significance’, he argues, the extended case method
searches for ‘societal significance. The importance of the single case lies in
what it tells us about society as a whole rather than about the population
of similar cases’ (Burawoy et al., 1991: 281).
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This appears to be an appropriate solution, until one wonders how it
would work in practice – that is, what the ethnographer would do
differently. One clue comes from understanding how the method would
select cases, a practice that follows directly from van Velsen (1978 [1967]).
Through the method, deviant or unique cases are especially interesting,
because they provide for ways of developing or extending theories. This
represents a potentially appropriate alternative to Bill’s predicament.
But this line of thinking would suggest that the ultimate purpose is
refining or reconstructing a theory (see Burawoy, 1998, 2003; Burawoy et
al., 1991), rather than identifying an empirical fact about society, for which
some understanding of the relationship between the case and other cases is
important. For example, a theory might propose that small nonprofit
organizations must be connected to stable funders to survive more than five
years from birth in highly competitive environments. The extended case
researcher might then find a small nonprofit that was not so connected but
nevertheless survived 10 years, and ask why. Clearly, an interesting development
of the theory might emerge from such a study. Less clear is what kind
of empirical knowledge of society would emerge from it, unless one adopts
an a priori model of society as a whole, which Burawoy and his students
do from a perspective of ‘domination and resistance’ and ‘globalization’
(Burawoy et al., 1991, 2000). Once the neo-Marxist or globalization
perspective (or a pre-determined alternative) is abandoned, the ethnographer
is still at a loss as to the type of empirical knowledge gained.18 Either
it is knowledge about how one case works, or it is knowledge about how
other cases work. If it is the latter, then some logical justification, some basis
for feeling confident that another nonprofit with no connection to stable
funders would exhibit similar patterns, is still missing.
In this sense, I suggest that Burawoy’s (1998; Burawoy et al., 1991)
extended case method is only a partial solution to Bill’s particular predicament.
It provides a potentially effective way of improving theories, by
proposing (as many others have) the use of unique or deviant cases to
improve on existing theories. It does not quite propose a model for
distinguishing a good from a bad hypothesis, since this is not the way it
orients its research. And it does not provide an explicit criterion to make
empirical assessments relevant to other cases.19
Manchester revisited
An earlier proponent of the extended case method, Clyde Mitchell, provides
a clearer answer to our particular set of questions. Mitchell’s conception of
the method elaborates on Gluckman’s but differs from Burawoy’s. In a 1983
essay, Mitchell, following Gluckman, distinguishes ‘apt illustrations’ from
‘extended case studies’ in that the latter require ‘further elaboration of the
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basic study of case material’ because they ‘[deal] with a sequence of events
sometimes over quite a long period, where the same actors are involved in
a series of situations’ (Mitchell, 1983: 193). Whereas Burawoy believes the
key to the method is explaining local conditions in light of external forces,
Mitchell believes the key to the method is its ability to uncover process:
The particular significance of the extended case study is that since it traces
the events in which the same set of main actors in the case study are involved
over a relatively long period, the processual aspect is given particular
emphasis. The extended case study enables the analyst to trace how events
chain on to one another and how therefore events are necessarily linked to
one another through time. (1983: 194)
This focus is generally consistent with the idea that fieldwork should
devote itself to uncovering mechanisms and tracing processes (Lamont and
White, forthcoming). However, Mitchell does much more.
Mitchell takes up specifically the question Bill asked, in slightly different
language: ‘How do you know that the case you have chosen is typical?’
(1983: 188). Mitchell’s answer is consistent with mine: he argues ‘that this
question betrays a confusion between the procedures appropriate in making
inferences from statistical data and those appropriate to the study of an
idiosyncratic combination of elements or events which constitute a “case”’
(Mitchell, 1983: 188). Mitchell believes that statistical representativeness is
an irrelevant criterion, which implies that trying to find representative cases
is a mistake. Thus, he argues, ‘extrapolation is in fact based on the validity
of the analysis rather than the representativeness of the events’ (1983: 190).
The natural question is how to determine that an analysis is ‘valid’. To
answer, Mitchell contrasts ‘statistical inference’ from what he variously calls
‘logical’, ‘causal’, or (more impishly) ‘scientific inference’.20 The former is
‘the process by which the analyst draws conclusions about the existence of
two or more characteristics in some wider population from some sample
of that population . . .’; the latter, ‘the process by which the analyst draws
conclusions about the essential linkage between two or more characteristics
in terms of some explanatory schema’ (1983: 199–200). Most quantitative
research, he argues, employs both types of inference; case study methods
can only employ the latter: ‘inference from case studies . . . cannot be statistical
and . . . extrapolability from any one case study to like situations in
general is based only on logical inference’ (1983: 200).
With a little elaboration, Mitchell’s distinction between statistical and
logical inference provides an effective way to distinguish good from bad
hypotheses. Hypotheses based on case studies such as Bill’s, Mitchell might
argue, should never be statistical, only logical. Thus, it would be erroneous
for Bill to hypothesize that because he observed a preponderance of, say,
public cocaine consumption in his neighborhood then the average poor
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neighborhood will exhibit a preponderance of cocaine use in public. In this
hypothesis, logic played no role; it is a descriptive inference based on one
case, a mechanical connection between characteristics in two settings that
would only have worked if the laws of probability could justify it. By this
way of thinking, if Bill had observed a preponderance of cross-dressing, he
would have been forced to hypothesize that the average poor neighborhood
experiences a preponderance of cross-dressing. In fact, whether Bill’s
hypothesis ‘sounds’ right or not, the inference is both statistically unjustified
and illogical – or more precisely logically unjustified, since there is no
logical reason to believe it. This makes it an ineffective hypothesis.
But suppose Bill had observed that whenever a crime erupted in the neighborhood,
some people retreated into their homes while others felt compelled
to get organized. He also observed that those in the latter group had stronger
connections to the neighborhood. Their parents had been raised there and
their extended family lived nearby. Their mothers, fathers, and uncles had,
years earlier, collaborated with other neighbors in the creation of the local
community center and the foundation of a recreation area. Bill might have
uncovered a causal relationship between attachment and participation. He
might then hypothesize that the reaction to crime will depend on the
strength of local attachment, such that those strongly attached (through
various mechanisms) are likely to participate while those weakly attached
are likely to retreat. This is not a descriptive hypothesis; it is a logical (or
what Mitchell might call ‘causal’) one. While it still requires testing it is,
nonetheless, logically justified, which makes it an effective hypothesis.
The former hypothesis took the form ‘All entities of type A will exhibit
characteristic Z’, which was ineffective because there was no logical reason
to believe it. The latter hypothesis takes the form ‘When X occurs, whether
Y will follow depends on W’, which is logically justified given the processes
observed. They are both hypotheses, to be sure, and both would require
further testing. But only the latter is a good hypothesis (see Small, 2004).
One set of answers
Mitchell has brought us closer to solving Bill’s predicament, by clarifying
the role of logic in distinguishing appropriate from inappropriate hypotheses
based on single-case studies.21 Even if Bill only followed this principle
his approach to his research would increase in sophistication. Notice that,
for this model, whether Bill selected an ostensibly typical or an apparently
atypical case would be immaterial, since the hypothesis would be based on
a) logical inference and b) the internal conditions of the case.
While Mitchell provides a way to derive effective hypotheses, he still does
not clarify what kind of empirical statement Bill might make. In this respect,
Bill is limited but not powerless, since he can, with justification, offer one
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category of empirical statement – ontological statements, those regarding
the discovery of something previously unknown to exist. That is, a wellexecuted
single-case study can justifiably state that a particular process,
phenomenon, mechanism, tendency, type, relationship, dynamic, or practice
exists (Glaser and Strauss, 1967; Lofland and Lofland, 1995). This, in fact,
remains one of the advantages of ethnographic work, the possibility of truly
emergent knowledge.
Second alternative: sequential interviewing
When it comes to making empirical statements, Jane possesses an advantage
over Bill. While we have already provided several ideas about how Jane
might approach her research differently, there is a more radical solution to
Jane’s predicament. This solution involves rethinking not merely her objectives
but also her understanding of each of her interviews. As I will show,
this will yield not only better hypotheses but also a more grounded
foundation to make empirical statements relevant to the cases not observed.
The foundation is to adopt Yin’s (2002) distinction between case study
logic and sampling logic (see Ragin and Becker, 1992). Yin’s work is on
case studies, and I am extrapolating from his work. I will argue that case
study logic can be effectively applied to in-depth interview-based studies,
such that the latter may be conceived as not small-sample studies but
multiple-case studies. I do not believe all interview-based studies should be
conducted in this fashion, but, for some objectives, it will likely produce
the most effective answers.22
Sampling and case study logic approaches are different and fully independent
ways of approaching data – they constitute wholly different
languages. Sampling logic refers to the principles of selection associated
with standard survey research. In a sampling model, the number of units
(e.g. individuals) to be studied is predetermined; the sample is meant to be
representative; all units should have equal (or known) probability of selection;
and all units must be subject to exactly the same questionnaire. If
conducted properly, the characteristics of the sample are expected to reflect,
within a margin of error, those of the population as a whole. The objective
is statistical representativeness. For example, a researcher designing a survey
of political attitudes in the US would determine how many respondents she
needs, develop a sampling frame, create a short questionnaire that every
respondent is given, and ensure that her sample is statistically representative.
The objective would be to make sure that the distribution of responses
in her sample matched that in the population.
Case study logic, in Yin’s terms, proceeds sequentially, such that each
case provides an increasingly accurate understanding of the question at
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hand. In a case model, the number of units (cases) is unknown until the
study is completed; the collection of units is, by design, not representative;
each unit has its own probability of selection; and different units are subject
to different questionnaires. The first unit or case yields a set of findings and
a set of questions that inform the next case. If the study is conducted
properly, the very last case examined will provide very little new or surprising
information. The objective is saturation. An important component of
case study design is that each subsequent case attempts to replicate the prior
ones. Through ‘literal replication’ a similar case is found to determine
whether the same mechanisms are in play; through ‘theoretical replication’
a case different according to the theory is found to determine whether the
expected difference is found. Sampling logic is superior when asking
descriptive questions about a population; case study logic is probably more
effective when asking how or why questions about processes unknown
before the start of the study.
To elaborate and demonstrate the fruitfulness of case-study logic,
consider an example based not on interviews but on experiments. Alfonse
conducts an experiment in which one group of black and white students at
Cal Tech is told they will receive an IQ test and another is told nothing.
Both complete the test, and blacks in the first group do much worse than
whites, while those in the second do as well as whites in their group. Alfonse
concludes that the fear of fulfilling a stereotype about low IQs among blacks
is at play. This inference is based on this one case.23
However, Alfonse realizes that black and white students at Cal Tech
might differ from those elsewhere, and that how college students take tests
might differ from how other people take them. That is, he realizes that he
did not have what statisticians would refer to as a representative sample of
the population. In addition, he realizes that his theory is not, strictly
speaking, about black people, but about the impact of fears of fulfilling
stereotypes on performance. For this reason, he then conducts literal and
theoretical replications. With a colleague at Duke, Alfonse repeats the
experiment among Duke undergraduates (literal replication); back at Cal
Tech, he repeats it, but using women and men instead of blacks and whites,
since he knows that there are stereotypes about women’s inability to
perform well on math tests (theoretical replication). If the theory is right,
Alfonse infers, it should work for anyone, not just blacks and whites.
Some tests confirm his findings; others do not. Then he tries it among
Asians and whites, and among issues other than IQ, and on more campuses,
and with high school students and senior citizens, and on and on. With
each experiment, he refines and re-evaluates his understanding of the
process. Slowly, as the number of experiments (i.e. cases) increases, his
confidence that his theory is right begins to grow. Eventually, every new
experiment contributes very little new knowledge, such that the 89th
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experiment, with immigrant Asians and Russians in a low-income high
school, shows exactly what he expected, even though he expected much
more subtle relationships than he could have envisioned during the first
experiment. At this point, he has attained saturation.
Alfonse has just conducted (after many years) a type of multiple-case
study. Notice that at no point did Alfonse conduct a random sample of any
kind. On the contrary, the characteristics of respondents in every subsequent
experiment were chosen deliberately, based on his increasingly refined
and continuously re-evaluated understanding of the underlying phenomenon.
Furthermore, he cannot make accurate descriptive statements about
the distribution of characteristics in the population as a whole. Alfonse
would not report that, for example, 80 percent of blacks are susceptible to
stereotype threat, or that, since 75 percent of the experiments confirmed his
theory, his theory is right 75 percent of the time (this would be wrong on
many, many counts). Instead, he has identified, and confirmed beyond
reasonable empirical doubt, an important mechanism affecting test
performance. I suggest that this approach may be used to think about indepth
interview research.24
Reconsider Jane’s predicament. Jane was applying, or attempting to
apply, sampling logic, and by that logic she had a weak sample. By a case
logic, she would have had a weak selection of cases as well, because
inferential logic played little role in her selection of each subsequent interviewee.
However, depending on her question, she might have attained
saturation even if, in the end, the number of individuals interviewed was
relatively small.
The key is to conceive of every individual the way Alfonse conceived of
every single experiment, as a single case. Jane, without knowing how many
respondents she will eventually interview, interviews one. After a two-hour
interview, the person, say, recalls and recounts experiencing discrimination
from Latino immigrants when she was a child, thus developing antiimmigrant
sentiments and favoring Draconian immigration reform. From
the interview, Jane has begun to form a new understanding of her initial
issue, the attitudes of African Americans about immigration. She theorizes
that native-born blacks who have experienced discrimination from Latino
immigrants will favor immigration reform due to their personal experience.
She then searches for blacks who report discrimination from Latinos (literal
replication), as well as those who have not experienced it (theoretical replication)
and those who experienced discrimination from Russian immigrants
(theoretical replication). Importantly, she alters each new interview to
include increasingly refined questions about different aspects of discrimination,
since every interview is refining and forcing her to re-evaluate her
understanding of the phenomenon. She repeats the process multiple times.
Her last interviews are longer than the first, and they include many more
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subtle variations on the way one experiences discrimination, including
many that had not occurred to her during the first interview. Eventually,
each new interview is telling her very little she had not already heard about
the relationship between discrimination and immigrant attitudes. She has
attained saturation.25
Jane’s new approach would violate nearly all of the tenets of (frequentist)
sampling logic. Her group of respondents is not representative; each
respondent received a slightly different questionnaire; there was no attempt
to minimize statistical bias. Consequently, Jane can make no accurate statement
about the distribution of attitudes. She would not report that, say, 25
percent of working-class blacks favor immigration reform, just as Alfonse
would not make statements about the distribution of his effect in the population
of African Americans. However, we would have the same confidence
in her empirical findings as we do in Alfonse’s statements that stereotype
threat reduces performance.26
As for the most common question, the answer is clear: she will know
how many interviewees she needs when her study is over – that is, when
she has attained saturation. This predicament is far less threatening than
may appear, since Jane retains the power to determine how to refine and
re-evaluate her theory. The more complex the process, the more interviewees
she will need, and it is not difficult to imagine that, with the identification
of a straightforward but unknown process or a complex but common
one, Jane might attain saturation with the 35th carefully selected case. For
a few years, my graduate students and I have been conducting a modified
version of this type of sequential analysis in interviews with urban mothers
whose children were enrolled in daycare centers in New York City. We were
studying many aspects of their social networks (including several for which
I was employing survey data), but one of the perplexing questions was how
they developed so many friendships with other mothers, especially in a place
where (I erroneously thought) all they did was drop off and retrieve their
children. After no more than a few dozen interviews – with rich and poor
mothers; with blacks, whites, and Latinas; in multiple boroughs; and with
even a few men – my research assistants and I had attained saturation on
the six or seven mechanisms through which mothers in New York City
centers made new ties (the PTA, the yearly fundraiser, the mandatory
meetings, etc.) (Small, forthcoming). I was relatively confident, and subsequent
interviews confirmed, that we would not identify new mechanisms
for friendship formation (or new opportunities for making friendships) that
we had not already seen. On this particular question, we had early on
attained saturation.27
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Conclusions
For ethnographers in many fields of study, the issues discussed in this article
do not arise. These ethnographers have no intellectual engagement with
quantitative researchers, no expectation that the latter will ever be reviewers,
no need to assess the work against a larger body of quantitative studies
asking similar or related questions. For many others, however, the issues
are critical. In urban sociology, the study of immigration, and social
inequality – as well as, to some extent, the sociology of organizations and
of education – ethnographers must contend, explicitly or implicitly, with
scholars trained in radically different traditions who claim expertise on the
same questions and may well assume a unity of method.
In this context, I have argued that no matter what they do within the
parameters of their original projects, Jane and Bill will never build airplanes
with the capacity to fly. The ‘representative’ single neighborhood does not
exist.28 Jane and Bill should not be building airplanes; they should be
building, say, boats, vessels that are equally important for transportation
and, during some circumstances, much more effective. And rather than
build boats that try to fly, they should build boats that sail effectively. I have
defended Mitchell’s elaboration of the extended case method and proposed
sequential interviewing – along with the (common) recommendations to
consider sampling for range, snowballing, and identifying unique cases – as
one set of tools, by no means the only ones, to build better vessels. Generally,
the approaches call for logical rather than statistical inference, for caserather
than sample-based logic, for saturation rather than representation as
the stated aims of research. The approaches produce more logically sensible
hypotheses and more transparent types of empirical statements. Regardless
of the method, ethnographers facing today’s cross-methods discourse and
critiques should pursue alternative epistemological assumptions better
suited to their unique questions, rather than retreat toward models designed
for statistical descriptive research. After all, to push the metaphor to its
limits, even the best built airplane will never do well at sea, and I do not
see any pilots losing sleep over it.
Notes
1 This article is a major elaboration of an earlier talk, ‘Lost in Translation’,
prepared for a 2005 National Science Foundation workshop on interdisciplinary
standards in qualitative research (Small, 2008a). I thank
members of the workshop, as well as Stanley Lieberson, Scott Lynch,
Sabrina Placeres, Loïc Wacquant, Yang Yang, the students in my logic of
inquiry courses at Princeton University and the University of Chicago, and
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the editors and anonymous reviewers of Ethnography for comments and
criticisms.
2 Social Problems and City and Community, among the mainstream journals
that publish papers in these fields, have exhibited stronger inclinations to
publish ethnographic work.
3 In fact, the National Science Foundation recently felt compelled to organize
two conferences, with accompanying reports, aimed at discussing what
constitutes ‘science’ in the context of ethnographic or interview-based
qualitative work (see Lamont and White, forthcoming; Ragin et al., 2004).
The purpose was clear, to help qualitative researchers negotiate a predominantly
quantitative discourse:
Workshop participants were asked to: 1) provide guidance both to reviewers
and investigators about the characteristics of strong qualitative research
proposals and the criteria for evaluating projects in NSF’s merit review
process, and 2) provide recommendations to address the broader issue of
how to strengthen qualitative methods in sociology and the social sciences
in general. The workshop was intended to contribute to advancing the
quality of qualitative research, and thus to advancing research capacity,
tools, and infrastructure in the social sciences. (Ragin et al., 2004: 5)
4 The more standard practice to assess the work against other cases would
resemble Sallaz’s (2008) recent study, which examines not cockfights but
casino card games in South Africa to assess the extent to which they also
embody social power relations and reflect larger structural transformations.
5 To be clear, these and other manuals certainly address questions of research
design, at length. However, they tend to say little explicitly about what
might be the most important questions for quantitative researchers. In fact,
the question of representativeness and statistical generalizability, probably
the most sensitive and ambiguous in the discourse between quantitative
and qualitative researchers, receives scant attention in the widely used
Hammersley and Atkinson (1995; see pages 42–5). It receives even less
coverage in Lofland and Lofland (1995).
6 Readers should note that they will not find in these pages an attack on
quantitative methods (which I often employ in my work). At issue is the
difference between an approach to science in which different questions are
asked within different epistemological frameworks and one in which all
social scientists attempt to answer all questions from one framework. It
should become obvious why this article defends epistemological pluralism.
7 I think Lamont’s study of 160 upper-middle-class men in France and the
United States is a methodologically sophisticated interview-based study.
However, I do not believe, as others have commented, that it is sophisticated
because ‘she had a representative sample’. The study’s response rate
was very low, between 42 percent and 58 percent, by liberal estimates
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(Lamont, 1992). (As Lamont [1992: 285] writes, the figures ‘do not include
potential respondents who did not provide the information necessary to
determine whether they qualified or not’ for the study. Thus, the figures
could overstate the response rate.) In addition, the samples are small, only
80 individuals in each country (40 in each site). The methodological sophistication
of the book comes from the sensitivity of the interview process;
Lamont’s ability to interpret the meaning of respondents’ statements within
their cultural contexts; her use of a comparative model to sharpen her
concepts; her judicious use of both semi-structured interviews, which allow
findings to emerge inductively, and a structured survey, which provides
comparative data across the cases; and her thoughtful selection of research
sites (Lamont, 1992, Appendix II).
8 For a discussion of these issues from researchers aimed at bridging the
qualitative/quantitative divide, see King et al. (1994, pp. 63ff).
9 A more accurate statement of her question is this: Jane would like to
know that, were she to sample the same population repeatedly, 95 out of
100 times the true number of working-class blacks who are proimmigration
reform would fall within +/– five percentage points of the
estimated value.
10 The formula is n = (Z2 ϫ p ϫ (1 – p)) / C2, where Z is the Z value (1.96
for a 95% confidence level); C is the confidence interval, expressed as a
decimal (in this case, .05); and p is the percentage of people who are
expected to be, in this case, pro-reform. We assume .5, the most conservative
assumption. (If 51% are pro- and 49% are anti-reform, the room for
error is high, so a large sample is needed; if 90% were pro-reform one
could get by on a much smaller sample of 139.) There are dozens of sample
size calculators on the Internet, where one can manipulate the assumptions.
For example, [www.raosoft.com/samplesize.html].
11 In this passage, the authors were discussing much broader issues, so this
selection does not do justice to their book. The purpose here is not to
produce a full-fledged critique of the authors’ book. Rather, it is to show
the pitfalls of this particular way of thinking about case study selection,
which the authors share with many others. One could argue that the
authors’ flaw in this instance stems from their attempt to use a case study
to find an ‘estimator’, in the quantitative sense. From that perspective, we
may quote Campbell and Stanley, who said of ‘the one-shot case study’
that ‘such studies have such a total absence of control as to be of almost
no scientific value’ (Campbell and Stanley, 1963: 6). I disagree strongly with
Campbell and Stanley’s implied assessment of the purpose of a case study;
however, I agree that, if the purpose were to make a statistically generalizable
statement of the effect of one variable on another, the authors would
be right, and their critique would apply to King et al.’s ‘case study
estimator’ (1994).
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12 On the research dilemmas brought about by IRBs and the problems of
confidentiality, see Shea (2000). Today, researchers have to make difficult
decisions about how to report their findings, since IRBs often require
ethnographers to guarantee the confidentiality of their respondents. All too
often, the solution requires thinking of neighborhoods in the abstract,
devoid of historical or political context, further reinforcing the tendency to
think of cases within sample-based logic.
13 In fact, one of the advantages of this section of King et al.’s (1994) book,
as seen through Bill’s application, is that it takes the logic of many such
studies – where the approach is implicit – to its natural conclusion. Some
ethnographers in these fields do, in fact, select their neighborhoods or cases
based on careful demographic assessments of whether the site is empirically
average (e.g. Klinenberg, 2002; McDermott, 2006). Others select, and
at times even stumble, onto their cases through more informal processes,
but with a similar understanding that the site being studied is somehow
typical (e.g. Pattillo, 1999; Venkatesh, 2000; Wacquant, 2007). (In fact,
this is one of the strongest proclivities inherited from the Chicago School
of sociology.) In both cases, the implication is that by studying the right
neighborhood, the ethnographer has earned a greater warrant to speak of
‘the ghetto’, ‘the American housing project’, ‘the immigrant enclave’, or
another equivalent type of case. Conversely (following that logic), had an
apparently atypical neighborhood been studied – such as a housing project
that managed to keep crime at bay – then the weight of the warrant would
be radically lowered. Of course, some ethnographers are more careful than
others in the care with which they subsequently make claims about other
neighborhoods, or neighborhoods in the general ‘type’, based on the study
of the ‘typical’ case. However, as we shall see, I argue that no single neighborhood,
whether apparently typical or radically atypical, produces such
a warrant; that there is little justification for studying apparently typical
neighborhoods within this context and several motivations to explicitly
study atypical ones; and that the language for discussing work in these
contexts should change radically.
14 The median age for males and females is 36; more individuals are married
than never married, widowed, or divorced; among persons 25 or older,
more are high school graduates or graduates with some college than not
high school graduates, college graduates, or persons with advanced degrees;
$36,911 is the median earnings for individuals for the year 2006. See
Section 1, Population, of the Statistical Abstract of the United States [http://
www.census.gov/prod/2007pubs/08statab/pop.pdf].
15 Early Chicago School criminologists adopted a version of this procedure
in their book-length studies of a single juvenile delinquent (Shaw, 1930,
1931). In a discussion included in one of the studies, Burgess convincingly
argues that an in-depth study of this nature is especially informative about
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the processes of becoming a full-time offender, but then unconvincingly
attempts to argue that the case is ‘representative’:
The case of Stanley appears also to be typical in a more real sense than can
be verified by any statistical calculation. It is typical (i.e., belonging to the
type) in the same way that every case is representative of its kind or species.
This case is a member of the criminal species . . . The individual person is
more intrinsically a specimen of any group of which he is a member than is
a plant or animal of its species . . . [T]he relation of the person to his group
is organic and hence representative upon a cultural rather than upon a
biological level. (Burgess, in Shaw, 1930, p. 186)
Burgess’s use of metaphors here does little to address the fact that a
completely different delinquent would have to be understood as equally
‘representative’, thus begging the initial question.
16 In his two articles proposing seven approaches from which to motivate
ethnographies, Katz (2001a, 2002) suggests several additional perspectives.
For example, when ethnographic data are praised as revealing either
hidden or overlooked aspects of social life, discovery becomes more
important than mere empirical applicability to other cases. (More on this
below.)
17 This interpretation is reinforced by his global ethnography, where he argues
that the larger functions that should play a role in understanding the case
are not merely societal but global (Burawoy et al., 2000).
18 Interestingly, one might trace this tendency – of the method to rest foundationally
on a theoretical proposition about society – to van Velsen (1978
[1967]). Van Velsen preferred the term ‘situational analysis’, because his
concern was that, when studying a case, one should present it as a situation
as a whole, with all of the local and external factors shaping the observed
phenomena. When identifying the assumptions of his model, van Velsen
(1978 [1967]: 146) writes: ‘One of the assumptions on which situational
analysis rests is that the norms of society do not constitute a constituent
and coherent whole. On the contrary, they are often vaguely formulated
and discrepant. . . . Situational analysis therefore lays stress on the study of
norms in conflict.’ In this respect, the method (situational analysis) presupposes
a theoretical subject matter (norms in conflict), the way Burawoy’s
extended case method presupposed, or seemed to, a theoretical subject
matter (domination and resistance).
19 Burawoy’s later work would not so much solve the problem as change the
question. In Burawoy (1998), Burawoy et al. (2000), and Burawoy (2003)
he pushes, respectively, for a reflexive mode of science that takes the obtrusiveness
of the researcher as a starting point; for an ethnographic program
that aims to understand the local case in light of global conditions; and for
an approach to revisiting sites in which not mere refutation but a revised
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understanding of the role of structure in affecting both present and past
conditions plays a role.
20 Many have made some version of this distinction: ‘statistical inference vs
logical inference’, ‘statistical generalizability vs analytical generalizability’
(Yin, 2002), and ‘enumerative induction vs analytical induction’. This last
distinction is Znaniecki’s (1934), whose predicament – defining case studies
in an age inclined to rely on quantitative research to examine social
problems – parallels our current one all too closely.
21 It is worth noting that many of the other, quite appropriate recommendations
– that ethnographers engage in ‘process tracing’ or ‘unpacking
mechanisms’ or ‘identifying conditions’ – are in essence more complex
versions of this basic insight (see e.g. Lamont and White, forthcoming).
22 Some of the ideas that follow are consistent with grounded theory. In fact,
the processes of literal and theoretical replication, described below, are
similar to Glaser and Strauss’s (1967: 59) description of ‘theoretical
sampling’. Readers will also notice that sequential interviewing has much
in common with Bayesian inference. See also Katz (2001b).
23 The inspiration for this example is the work of Claude Steele and colleagues
at Stanford University on ‘stereotype threat’ (see Aronson et al., 1999;
Steele, 1992; Steele and Aronson, 1995). The example by no means
attempts to represent the process through which Steele and his colleagues
actually performed their research.
24 To be clear, I do not believe Alfonse can now make determinist statements.
His understanding of the effect of stereotype threat would still fall within
the parameters of a probabilistic understanding of the social world
(Lieberson, 1991).
25 These descriptions of the research process are stylized, as all of them are forced
to be. In real life, Jane might have interviewed 10 people before any
semblance of a story had emerged. She then would have limited the scope of
her study and her questions, to prevent continuing to interview indefinitely.
26 Of course, if Jane had simply selected her 35 cases as she had before, she
would not be able to make statements about distributions either.
27 A reviewer asked how this approach would work in the large, team ethnographic
projects that have proliferated in recent years (e.g. Newman, 1999).
In theory, there should be no difference in the application of sequential
interviewing. However, the logistics of running such projects may render
the careful application of a sequential process difficult, which happens to
highlight one of their potential weaknesses. If one or two PIs supervise
without entering the field, or if the team is especially large, or if the project
takes place in multiple cities, it becomes difficult to coordinate early discoveries,
to devise literal or theoretical propositions to replicate, or to shift
direction collectively to answer newly pressing questions. Indeed, it is
possible that as the number of ethnographers increases the more the project
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will resemble a survey, rather than a study in which most of the discoveries
are emergent.
28 One of my first-year graduate students, convinced of the logic of these
arguments, nonetheless explained that ‘it feels better’ to pursue these
pseudo-representative samples, since, irrational as it may be, she had been
indoctrinated into worshiping the gods of statistical representativeness. To
this I have no reply, except perhaps to paraphrase Goya: when reason goes
to sleep, nothing but monsters comes to life.
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Znaniecki, F. (1934) The Method of Sociology. New York: Farrar &
Rinehart.
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■ MARIO LUIS SMALL is Associate Professor of Sociology and
the College at the University of Chicago. His research focuses on
urban poverty, neighborhoods, inequality and culture, and case
study methods. He is the author of Villa Victoria: The
Transformation of Social Capital in a Boston Barrio (2004), for
which he received the C. Wright Mills Prize, and of articles
published in journals such as the American Journal of Sociology,
Annual Review of Sociology, Social Forces, Theory and Society, and
Social Science Quarterly. His forthcoming book, Unanticipated
Gains: Origins of Network Inequality in Everyday Life, employs
qualitative and quantitative data on urban mothers to examine
how routine organizations affect the advantages that people can
secure from their networks. Address: 1126 E. 59th Street, Chicago,
IL 60637, USA. [home.uchicago.edu/~mariosmall, email:
mariosmall@uchicago.edu] ■
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