Discussion 5: Research Design III

THE METHODOLOGICAL ADEQUACY OF LONGITUDINAL RESEARCH ON CRIME*

MICHAEL GOTTFREDSON TRAVIS HIRSCHI

University of Arizona

This paper argues that the increasing dominance in contemporary crim­ inology of the longitudinal or cohort study is not justified on methodologi­ cal grounds, that this research design has taken criminological theory in unproductive directions, has produced illusory substantive findings, and has promoted policy conclusions of doubtful utility. In addition, it is noted that longitudinal research is very expensive and therefore has high opportunity costs, costs that have not been properly evaluated. The positive thesis is that many of the apparent benefits of longitudinal research can be obtained by carefully designed and reasonably conceptualized cross-sec­ tional studies, at substantially reduced cost.

As a by-product of research on the relationship between age and crime (Hirschi and Gottfredson, 1983), we came to the conclusion that the concept of a "career criminal" was inconsistent with the evidence (Gottfredson and Hirschi, 1986) and that longitudinal research designs were not necessary for the study of crime and criminality. The conclusion of age invariance in crime proved to be controversial (Greenberg, 1985; Farrington, 1986a), as did the conclusions about the value of the criminal careers concept. If controversy implies disagreement, the least controversial conclusion of this research was that longitudinal research is not required for the study of crime. Almost no one agrees with this conclusion; on the contrary, nearly everyone agrees, it seems, that longitudinal research is essential for the proper study of crime causation.

Indeed, groups of the nation's leading scholars have recently called for even greater emphasis on longitudinal designs in criminology. (These groups include the National Academy of Sciences panels on deterrence and incapaci­ tation (Blumstein, Cohen, and Nagin, 1978) and on criminal careers (Blum­ stein, Cohen, Roth, and Visher, 1986), and a MacArthur Foundation panel on criminological knowledge (Farrington, Ohlin, and Wilson, 1986).) Obvi­ ously, if more longitudinal research is required for the proper study of crime causation, our conclusion about the value of this design is wrong. Since the

*We wish to thank David Riley, Doug Wholey, and David Farrington for comments on an early draft of this paper. Work on portions of this manuscript was supported by National Science Foundation grant SES8500244.

CRIMINOLOGY VOLUME 25 NUMBER 3 1987 581

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conclusion about longitudinal designs derived from substantive and theoreti­ cal considerations, the question of the methodological adequacy of longitudi­ nal designs may be seen as a question of theory and substance. But this position is not new. On the contrary, the adequacy of a research design is always judged by its relevance to questions of substance, theory, or policy (and not vice versa). Therefore, the preference for longitudinal designs must also stem from theoretical or policy preferences. Since methods cannot be divorced from substance and theory, they cannot be evaluated in isolation from issues of substance and theory. The purpose of this paper is to subject arguments favoring longitudinal designs in criminology to substantive, theo­ retical, and methodological analysis.

Early Longitudinal Research. Systematic empirical research on crime in this country is perhaps best traced to the pioneering work of Glueck and Glueck (1930, 1940). The Gluecks' early work (for example, 500 Criminal Careers, 1930) was primarily longitudinal, following large numbers of offend­ ers over long periods of time. A major problem with such research was loca­ tion of a reasonable comparison group. The Gluecks initially relied on statistics from the general population for this purpose, 1 but they eventually turned to comparisons of matched samples of offenders and nonoffenders (on such things as age, IQ, and neighborhood) in a standard cross-sectional design. Their major cross-sectional study was published in 1950 as Unrav­ eling Juvenile Delinquency. The Gluecks continued to follow over many years the 500 delinquents and 500 nondelinquents first identified for Unrav­ eling, and published the results in 1968 under the title Delinquents and Nondelinquents in Perspective.

The Gluecks' major work is Unraveling Juvenile Delinquency. Although citations are only one measure of influence of scholarly works, Wolfgang, Figlio, and Thornberry ( 1978) report that as of 1972 Unraveling was the most heavily cited book in criminology. Since publication of the longitudinal work (Delinquents and Nondelinquents in Perspective), the cross-sectional study has been cited 403 times (through 1984) and the longitudinal study 89 times, less

1. In comparison with the general population, the delinquents studied by the Gluecks in the 1920s were more likely to have dropped out of school, to have come from unhealthy home situations, to have bad companions, to come from densely populated areas, to be educationally retarded, to have started work at an early age, to have moved frequently from place to place at an early age, and to have engaged in sex, gambling, and drugs (Glueck and Glueck, 1930: 306-309). Despite the myriad criticisms of the Gluecks' work, their findings have proven to be amazingly consistent with subsequent research.

At the time the Gluecks were collecting data for Unraveling Juvenile Delinquency, the Cambridge-Somerville Youth Study got under way. This important study (Powers and Witmer, 1951; McCord and McCord, 1959) is essentially a long-term follow-up of the effects of a counseling program on potential delinquents. It is mentioned here as further evidence of the long history of longitudinal research in criminology, a history not always acknowledged by recent calls for increased emphasis on this design.

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than one fourth as often (Social Science Citation Index, 1966-1984). Given the tremendous overlap in measurement, conceptualization, and analysis, the disproportionate influence of the cross-sectional study, Unraveling, over the longitudinal study, Delinquents and Nondelinquents, does not seem to favor the idea that, all else equal, longitudinal research is more important or valua­ ble for criminology. (After all, to use a criterion much favored by longitudi­ nal researchers, in this comparison the Gluecks serve as their own control.) Despite the claims of those favoring longitudinal designs (Farrington et al., 1986), other comparisons of longitudinal and cross-sectional research lead to the same conclusion: the assertion that longitudinal research, study for study, has had greater impact than cross-sectional research is inconsistent with the evidence.

What, then, accounts for the widespread view that longitudinal designs in criminology should be preferred to cross-sectional designs? We see two answers to this question. The first involves alleged methodological superior­ ity, according to which longitudinal research solves causal questions beyond the reach of cross-sectional designs. The second involves alleged substantive superiority, according to which the facts of crime and criminality require lon­ gitudinal designs for their explication. The adequacy of each answer will be considered in turn.

DESIGN FEATURES OF LONGITUDINAL RESEARCH

The ideal design in scientific research is the true experiment, where subjects are randomly assigned to treatment conditions and the effects of the various treatments are then compared (see Campbell and Stanley, 1963: 3, who refer to experimentation as "the basic language of proof, as the only decision court for disagreement between rival theories ... "). This design, with sufficient replication, uniquely satisfies the three criteria of causation: (1) association between cause and effect; (2) temporal precedence of cause over effect; 3) non­ spuriousness (Hirschi and Selvin, 1967; Cook and Campbell, 1979). All other designs are inferior, but some are better than others. For example, Cook and Campbell (1979) persuasively argue that next to the true experiment in scien­ tific adequacy is the quasi-experiment, a design involving some of the active intervention of the true experiment without its control over extraneous condi­ tions. (This design satisfies the first two criteria of causality and sometimes, if one is lucky, the third as well.) Further down the list of scientific adequacy, one finds passive observational designs, where the investigator takes what nature gives and attempts to infer the elements of causation through correla­ tional or similar statistical methods. Passive designs are able to establish cor­ relations between variables, but they have difficulty distinguishing cause from effect, and they can only weakly approximate the experiment by statistically controlling for other variables that may be producing the correlations of

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interest. These difficulties cannot be overcome by advances in multivariate statistics, since such statistics remain ambiguous substitutes for manipulation and randomization (Cook and Campbell, 1979: 9).

Of course, experimentation, even quasi-experimentation, is not often possi­ ble with phenomena such as crime, and researchers are forced to do the best they can with the less than ideal designs available to them. (It should be noted that designs ideal in theory are themselves often less than ideal in prac­ tice. Thus, many true experiments are simply uninformative, and others are more trouble and expense than they are worth.) Nonexperimental designs also differ among themselves with respect to the extent to which they satisfy the criteria of causation, with respect to other valid scientific criteria such as external validity of their results and their compatibility with the phenomenon at issue, and with respect to such nonscientific but important criteria as cost in time and money. Obviously, selection of an appropriate research design involves consideration of a good many things, a simple fact that makes a priori design preference by funding agencies or panels of academicians (Mor­ ris, 1986; Farrington et al., 1986; Blumstein et al., 1986) hard to justify. Such considerations apply as well to critics of the longitudinal design. There can be no a priori objection to longitudinal research. The question is whether longitudinal research is appropriate to the study of crime and criminality, whether its methodological strengths compensate for its methodological defi­ ciencies, and whether its efficiencies outweigh its costs.

The longitudinal design involves repeated measures of the same subjects, where the frequency and duration of the "follow-up" is a function of the phe­ nomenon in question. In longitudinal studies of crime, the researcher some­ times collects data every year (for example, Elliott, Huizinga, and Ageton, 1985), sometimes every two years (West and Farrington, 1977), but usually at longer intervals (McCord and McCord, 1959; Glueck and Glueck, 1968; Wolfgang, Figlio, and Sellin, 1972). The longitudinal design does not entail any particular method or frequency of data collection, sampling strategy, method of analysis, or project duration. However, some argue that the tim­ ing of data collection is a crucial distinction among longitudinal studies, with the "prospective" study (where subjects are identified before the events of interest occur) usually seen as preferable to the "retrospective" study (where subjects are identified after the events of interest have taken place). (The pro­ spective study does have advantages. For example, the measurement of independent variables cannot be affected by knowledge of the values of the dependent variable. However, the prospective study has disadvantages as well: it costs more (in time, money, and sample size) and is considerably more risky (in terms of theory, data analysis, sample adequacy, and the like). Some (Farrington, 1979) regard the frequency of data collection as a crucial design issue, with frequent data collection being superior to infrequent collec­ tion for purposes of making causal inferences. Unfortunately, more data are

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not necessarily better than less data, especially if they are essentially the same data. Practice or testing effects are often substantial in survey research, and the stability of characteristics is often insufficiently known to justify a priori claims to superiority of "more frequent" data collection. (After all, some stability in behavior is required to justify the "developmental" or longitudinal study in the first place.)

Some regard sampling distinctions to be critical in evaluating these designs. When all subjects share a common experience (for example, are born in a single hospital or in a single year), longitudinal studies are called "cohort" studies. When the sample includes people from more than one cohort (for example, people born in two different years), longitudinal studies are called multicohort studies. When such a study completes a second wave of data collection, it becomes a multiwave, multicohort study. The multiwave, mul­ ticohort study is designed to allow separation of the effects of age, period, and cohort. It is designed to determine whether it matters that the subjects were born in a particular year (or hospital), that they are a particular age, and that the study was conducted at a particular period of time. Obviously, the mul­ tiwave, multicohort study is typically thought to be better than the single­ wave, single-cohort study and, of course, better than the cross-sectional study, which, in terms thus far introduced, turns out to be a retrospective, single-wave, multicohort study with minimum frequency of data collection.

One of the alleged strengths of the prospective longitudinal study is that it entails lack of knowledge of "outcome" variables. In other words, the longi­ tudinal researcher does not know which subjects are going to be delinquents and which are going to be nondelinquents. When confronted with this prob­ lem, standard sampling strategy would be to stratify the population on vari­ ables known to be closely associated with the dependent variable and to oversample subjects likely to be delinquent (a strategy that assumes stability in the correlates of crime or in the tendency to commit criminal acts). Longi­ tudinal researchers in crime and delinquency tend not to adopt this common procedure (Elliott et al., 1985; Wolfgang et al., 1972; Tracy, Wolfgang, and Figlio, 1985)). Some see the frequency of data collection as critical, restricting the longitudinal study to those cases where there is more than one "follow­ up" or more than one contact involving information about the subjects. Others allow the term to be applied to one-time studies that gather informa­ tion about more than one point in time in the subject's life. All of these distinctions must be treated as measurement, sampling, or theoretical issues rather than design issues, since none of them bears on the adequacy of the longitudinal design as a basis for causal inference. Moreover, these research choices have direct counterparts in all other designs, whether experimental, quasiexperimental, or, as in the case of the longitudinal study, preexperi­ mental or passive observational.

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CAUSAL ORDER

In the criminological literature, it is frequently asserted that the longitudi­ nal design is superior to the cross-sectional design when one is interested in the problem of causal order. Elliott and Voss (1974: 7-8) assert that

Because of the difficulty involved in establishing the temporal order of variables, causal inferences are difficult to derive from cross-sectional data. Data gathered at one point in time generally preclude insight into developmental sequences or processes that lead to delinquent behavior or dropout. . . . [T]he availability of data gathered at different points in time permits assessment of the direction and amount of change in these scores during the course of the study and enables us to derive causal inferences.

Farrington (1986a: 212) asserts: "Another advantage of a longitudinal study is its superiority over cross-sectional research in establishing cause and effect, by showing that changes in one factor are followed by changes in another." Petersilia (1980: 337) claims that longitudinal research is "superior to cross­ sectional if one is primarily interested in drawing causal inferences." Blum­ stein et al. ( 1986: 199) provide a list of substantive areas in which the longitu­ dinal design is "required":

Many issues about criminal careers cannot be adequately addressed in cross-sectional research: the influence of various life events on an indi­ vidual's criminal career; the effects of interventions on career develop­ ment; and distinguishing between developmental sequences and heterogeneity across individuals in explaining apparent career evolution. Answering these and related questions requires a prospective longitudi­ nal study of individuals of different ages.2

Such statements illustrate the extent of the belief that longitudinal designs solve the problem of causal order (although they suggest that faith in the design extends beyond the causal order question). They do not, however, provide evidence or even illustration of the actual ability of the design to produce such solutions. Nor, for that matter, do these proponents of longitu­ dinal research show that causal order is an especially difficult problem for criminology. ls causal order especially problematic in crime and delinquency

2. Blumstein et al. (1986) urge the longitudinal design, apparently for the same rea­ sons it has been urged for about 100 years. According to Wolfgang et al. (1972: 5), Kohner asserted in 1893 that "correct statistics of offenders can be developed by a study of the total life history of individuals." Without discussing the merits of the theoretical issues raised by the Blumstein et al. characterization of the problem as being the "inherently longitudinal and dynamic characteristics of the criminal career," it is apparent that causal order is only one of the several claims for methodological superiority being attributed to the longitudinal design.

LONGITUDINAL RESEARCH 587

research? However defined, criminal acts and delinquencies are not tempo­ rally ambiguous. Typically, their occurrence can be pinpointed to the minute or hour. When was the liquor store robbed? When did the assault or bur­ glary or homicide or arson take place? These are not inherently difficult or ambiguous questions. Some crimes or delinquencies are of course more diffi­ cult to locate precisely in time. When did the child begin to use cigarettes or drugs? When did the child become incorrigible? But even these more ambig­ uous offenses can be located in time with sufficient precision to allow unam­ biguous conclusions about temporal sequence, at least with respect to most nontrivial causal variables.

So, even if the researcher's interest is in sequences of criminal events (in order to more accurately describe the life history of the career criminal), it should be easy to say where an event occurred in a sequence of events.

It would appear, then, that the causal order problem must be attributable to difficulties in establishing the order of crime and its potential causes. Since crime is, in these terms, relatively nonproblematic, one is led to infer that the potential causes of crime are especially problematic in terms of when they occur.

What causes of crime are seen by longitudinal researchers as problematic in these terms? One can infer from their discussions four categories of variables for which temporal order is problematic to longitudinal researchers: (1) age, period, and cohort; (2) standard causal variables thought to be implicated in crime and delinquency causation; (3) treatment and criminal justice interven­ tions; and (4) the effects of ordinary life events.

AGE, PERIOD, AND COHORT

In standard cross-sectional research, the observation that age is correlated with crime is subject to alternative interpretations. Differences apparently due to age (for example, higher rates among the young) may in fact be due to recent changes in economic or social factors important in crime causation. Suggestions that apparent age effects may be period or cohort effects are a major justification for longitudinal research for those urging a greater empha­ sis on this design (Farrington, 1986a; Blumstein and Cohen, 1979; Blumstein et al., 1986; Greenberg, 1985). If a single cohort (persons born within a lim­ ited period of time) is followed from birth to death, age differences cannot be due to between-cohort differences. Unfortunately, they may be due to period effects-that is, it may be that high-rate ages reflect nothing more than high rates of crime in the society when the cohort was at a particular age. Obvi­ ously, the cohort design must be complicated to allow resolution of this prob­ lem (or the researcher must look at data not collected as part of the cohort design), but the reader will note that none of this bears on the question of causal order, the question with which we are now dealing. However complex

588 GOTTFREDSON AND HIRSCHI

age, period, and cohort questions may become in terms of determining which of these three variables may be responsible for observed differences, there seems to be little controversy about whether they precede or follow crime. Since crime cannot cause age, period, or cohort, a longitudinal study is not required to answer the causal order question.

The much-touted ability of the complex longitudinal study to separate age, period, and cohort effects could not be of less theoretical or practical conse­ quence. In fact, a good case could be made for the view that concern for this distinction has distracted attention from more interesting crime data and has caused the field to misinterpret long available data on the issue. For example, longitudinal researchers frequently wonder whether the apparent age distri­ bution of crime could be a "cohort" or a "period" effect rather than an age effect (Cohen and Land, 1987; Farrington, l 986a; Blumstein and Cohen, 1979; Greenberg, 1985) when an empirical answer to this question may be had by examining the age distribution of crime for differing periods and cohorts (Hirschi and Gottfredson, 1983; Gottfredson and Hirschi, 1986). For that matter, the longitudinal study appears to be a grossly inefficient method of discovering period effects. The post-World War II crime wave was well documented by ordinary cross-sectional data long before it was reported by longitudinal researchers (Tracy et al., 1985). Concern for cohort effects is even more puzzling. Suppose it is found that a given cohort has a higher crime rate than an adjacent cohort, when age and period effects have been removed. What is to be made of this difference-that is, what life circum­ stances distinguish one cohort from the other? The answer, alas, is that the number of possible explanatory variables is for all practical purposes unlim­ ited. It could be the size or composition of the cohorts, it could also be that they were of different ages when one of many natural catastrophes occurred. (A further irony of interest in "cohort effects" is that they can be identified only long after their occurrence. They are therefore immune to manipulation and devoid of policy significance.)

STANDARD CAUSAL VARIABLES

The recent report of the National Academy of Sciences Panel on Research on Criminal Careers (Blumstein et al., 1986), summarizes the crime research literature using its own "criminal career paradigm." Since this report strongly supports longitudinal research, its list of causal variables should be representative of those considered important by longitudinal researchers and can help structure a consideration of the causal literature. What are these variables?

Sex. The Blumstein et al. panel reports that "the most consistent pattern with respect to gender is the extent to which male criminal participation in serious crimes at any age greatly exceeds that of females, regardless of source of data, crime type, level of involvement, or measure of participation" (1986:

LONGITUDINAL RESEARCH 589

40; see also Hirschi and Gottfredson, 1983; compare Farrington, 1986a). If sex differences are sufficiently robust that they survive all these conditions, including age, longitudinal research is not required to discover them. If the sex difference is the same at every age, as argued by Blumstein et al. (see also Hirschi and Gottfredson, 1983), examination of this difference at any age will be sufficient to determine its magnitude, and sex differences in crime cannot be used to justify longitudinal research, however crime might be measured or defined.

Race. Blumstein et al. of course do not suggest that the race-crime correla­ tion is problematic with respect to causal order. What, then, might be the value of a longitudinal design with respect to a race-crime connection? It is possible that race is more important at some ages than at others. In fact, the Wolfgang et al. cohort study (1972) suggested that blacks "start earlier" than whites. Reanalysis of the Wolfgang et al. data (Hirschi and Gottfredson, 1983) suggested that "age of onset" differences between blacks and whites were in fact merely rate differences in crime, differences that could be easily determined by cross-sectional research at any age. In other words, a cohort study was not required to discover them. This conceptual issue is not recog­ nized by Blumstein et al., who rely on other research to suggest that the race­ crime relation depends on age. This research is the Elliott et al. National Survey of Youth, a multiple cohort longitudinal study. According to Blum­ stein et al., the National Survey of Youth shows that race ratios differ by age. In the example cited, the black-to-white robbery ratio falls from 2.25: 1 when the cohort members were 11-17 years of age to 1.5: 1 when the cohort mem­ bers were 15-21 years of age, four years later.

In this instance, the National Youth Survey might be better used to illus­ trate the weakness rather than the strength of the longitudinal design. Put­ ting aside the disconcerting overlap in the age ranges compared, the cited differences do not appear to be statistically significant at conventionally accepted levels. The large standard errors of these age-race-crime specific estimates stem from the sample limitations imposed by the National Youth Survey's longitudinal design. In fact, this survey is unable simultaneously to disaggregate by sex in making race comparisons. Since race-sex interactions are routinely reported by cross-sectional research (Hindelang, Hirschi, and Weis, 1981; Hindelang, 1981 ), there would be reason to question the study's findings even were they to survive tests of statistical conclusion validity. (Incidentally, the Elliott et al. survey reports as much variability in crime­ specific sex ratios over age as it reports in crime-specific race ratios over age (Blumstein et al., 1986, Table A-4, p. 242), suggesting that the panel did not apply consistent standards in its review of the literature.) In any event, there is as of now little evidence to support the view that longitudinal research would shed light on the race-crime relation over and above that shed by less costly designs.

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Age. The Blumstein et al. panel argues that to resolve important age and crime issues "data are needed for a common sample on crime-specific age distributions of initiation and current participation according to both official records and self reports" (1986: 42). They then conclude, however, that dem­ ographic patterns "are of little use in explaining participation or in providing a basis of policy intended to prevent initiation of criminal careers" (1986: 42). Why the research community needs useless data is not clear. Certainly such need should not be used to justify longitudinal research. In any event, many believe that the age-crime relation is of crucial significance for criminological theory and crime control policy (Gottfredson and Hirschi, 1986; Hirschi and Gottfredson, 1983, 1986; Greenberg, 1977, 1985; Shavit and Rattner, 1986; Cohen and Land, 1987), and there can be no doubt that understanding of this relation is central to the issue of the alleged "need" for longitudinal research. As a result, the significance of the relation between age and crime goes far beyond the causal order question (which is again nonproblematic). In the authors' view, the evidence supports the notion that the age-crime relation is for all practical and theoretical purposes invariant. In the view of those pro­ moting longitudinal research, the evidence supports the notion that the age­ crime relation is sufficiently variable to justify expensive longitudinal research aimed at understanding how the causes of crime vary from one age to another. Making explicit what has been implicit in this controversy: propo­ nents of longitudinal designs argue that potential age-causal variable interac­ tions are of great theoretical and policy significance. We argue that such interactions are trivial compared to the theoretical and policy implications of a large and direct influence of age on crime. Current attempts to document age-causal variable interactions have done little more than shift attention from a major factor in crime causation to minor and inexplicable fluctuations in particular data sets.

Our original conclusion that the age-crime relation is invariant was based on inspection of available data, much of it of course cross-sectional. Conclu­ sions about age effects from cross-sectional data are traditionally treated as suspect, and investigation of the age effect often surfaces as a major justifica­ tion for longitudinal research. The record, both within criminology and else­ where, does not support these suspicions: "All too often, students of aging now fail to recognize that cross-sectional data, properly analyzed and supple­ mented with information from other sources can often provide more nearly conclusive evidence about the effects of aging than can any other one kind of data. Furthermore, the recognition of the hazards of inferring age effects from cross-sectional data was all too often accompanied by an unwarranted enthusiasm for longitudinal data" (Glenn, 1981: 362).

Family Variables. The Blumstein et al. panel considers such family vari­ ables as parenting, parental criminality, family disruption, and family size and structure. It concludes that these factors have "a strong and consistent

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effect on participation [in delinquent acts]" (1986: 43). It also concludes that "longitudinal studies that relate measures of parenting and family structure when a child is in elementary school to later official records or self-reports of that child's participation in serious or adult criminal behavior are particularly well suited to assess the impact of parenting on criminal involvement" ( 1986: 43, citing Farrington, 1983, and West and Farrington, 1977).

There can be no doubt that the family plays a major role in delinquency causation (Glueck and Glueck, 1950; Hirschi, 1969, 1983). What do the panel's longitudinal studies add to previously available information on the nature of the impact of family variables on crime? With respect to parenting, the panel suggests that "consistent, strict discipline; close supervision; and strong parent-child relationships including communication, affection, and interest in the child's activities" are associated with low rates of criminal par­ ticipation (1986: 43). These factors, it should be noted, are precisely those identified by Glueck and Glueck in the 1940s by cross-sectional research (Glueck and Glueck, 1950). These factors have been replicated by much sub­ sequent cross-sectional research (see, for example, Patterson, 1980), and are not dependent on longitudinal designs for their acceptance. In fact, longitu­ dinal studies are perhaps best seen as having confirmed the results of cross­ sectional designs, and as having shown that the methodological criticisms of cross-sectional family research were not justified. The relation between parental criminality and the criminality of the child poses no serious causal order issue. And the possible ways this relation might be produced are so numerous that no research design can reasonably claim to be particularly useful in studying it.

Blumstein et al. summarize the traditional speculations about the meaning of the family disruption- delinquency relation, leaving the impression that the various longitudinal studies of delinquency have fared no better than cross­ sectional research in unraveling this association. The discussion in fact sug­ gests that the question is whether family disruption causes criminal participa­ tion or merely reflects the true causes of criminal participation, such as marital conflict. Since crime and family dissolution are easy to locate in time, this causal configuration could be disentangled without resort to expensive longitudinal research.

According to the Gluecks (1950), the larger the number of children in the family, the greater the likelihood that each of them will be delinquent. The Blumstein et al. panel (1986) agrees. It seems unlikely that a reasonable lon­ gitudinal study could shed additional light on this factor. Following families from "onset" to "desistence" with additional time for the last child to com­ plete a criminal career would take more time than its findings are likely to be worth-even if it is assumed that the study would not have to be repeated immediately to determine whether its findings were replicable.

Early Antisocial Behavior. The continuity of the criminal career has been a

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major focus of longitudinal research. As a consequence, longitudinal research should now be able to tell us whether longitudinal research is required. If there is continuity over the life course in criminal activity (or its absence), it is unnecessary to follow people over time. If there is little or no continuity in criminal activity over the life course, it is again unnecessary to follow people over time. So, the longitudinal design assumes patterned change or development over the life course-patterned change or develop­ ment in criminal activity. What do the results of longitudinal research say about this assumption? Given the good amount of longitudinal research con­ ducted in recent years, one should be able to find many estimates of the stabil­ ity of delinquency.

Using Bachman's data (Bachman, Kahn, Mednick, Davidson, and John­ ston, 1967), Matsueda (1986) reports stability coefficients for delinquency of .75, .81, and 0.59 for four waves of data collected on boys from ages 15 to 18.3 Farrington (1973) reports data reflecting a correlation uncorrected for attenu­ ation of .62 (gamma) between self-reported delinquency at ages 14-15 and self-reported delinquency at ages 16-17 in his London cohort (Hindelang et al., 1981: 79). As Hindelang et al. note, such stability is about all that could be expected from a behavioral inventory, even if the underlying personality characteristic or propensity did not change.

And, in fact, when an underlying personality characteristic is invoked, the evidence for stability becomes even more impressive. From a review of 24 longitudinal studies of aggression among males, Olweus concludes that "for an interval of five years, the estimated disattenuated stability correlation is 0.69 and for an interval of ten years is .60" (1979: 866). Shannon (1978) reported a correlation of .52 between number of police contacts before 18 and number of police contacts after 18 (by the time the subjects reached 32). Elli­ ott et al. (1985) report correlations of .58 and .71 between prior delinquency and delinquency between years in their National Youth Survey.4 Indeed, the Blumstein et al. panel summarizes the evidence on persistence in crime, con­ cluding that "while the precise fraction persisting into adult criminal careers

3. Matsueda concludes that "delinquent behavior is determined largely by previous delinquent behavior" immediately after concluding that cross-sectional research designs are unjustified and potentially misleading (1986: 21). Matsueda's position may be traced to the view that the causal structure of a phenomenon may be equated with a particular research design. Thus, he begins by assuming that crime is an inherently dynamic phenomenon and goes from there to the view that the "correct causal structure" for crime is found in a "longitudinal cross-lagged autoregressive model" ( 1986: 21 ).

4. Several features of the correlations in the Elliott data are of interest. First, the . 71 correlation between prior delinquency and subsequent delinquency makes this single varia­ ble as good a predictor of delinquency as the entire "integrated" theory constructed by Elliott and his colleagues to explain delinquency in the first place. Second, since the test of the "model" adopted by Elliott et al. entails control for prior delinquency, the dependent variable becomes delinquency net of prior delinquency--or, in statistical terms, residual

LONGITUDINAL RESEARCH 593

varies by jurisdiction, by domain of crime, and by the criterion used for char­ acterizing the adult record (for example, arrests or convictions), there is strong evidence that the existence of a juvenile delinquency career foreshad­ ows adult criminal careers" (1986: 88).

Thus, according to the Blumstein et al. panel (and virtually all reviews of developmental research-for example, Loeber and Dishion, 1983; McCord, 1979; West and Farrington, 1973; Hirschi and Gottfredson, 1986), differences in antisocial behavior remain reasonably stable from the time they are first identified. In the language of the longitudinal researcher, early antisocial behavior predicts antisocial behavior in adulthood. Given good long-term predictability, short-term predictability should be excellent. This presents something of a problem for those advocating longitudinal research: how to make short-term change the principal focus of study when little change is in fact occurring. s

Longitudinal researchers use two devices to deal with this problem. One is to suggest that the continuity thus far observed has not been established over the entire life span. This suggests that future longitudinal research should concentrate on the period before ages eight to ten and on the period after about age 50. Longitudinal researchers have had a hard time generating interest in these periods, however, and for obvious reasons: longitudinal research assumes that institutional experiences generate differences in crime propensity. Not much happens to infants or young children that is relevant to theories stressing adolescent gangs, marriage, or the effects of the criminal justice system. Equally obvious, crime by the elderly is so rare that efforts to make something of it are hard to justify.

If this solution to the problem of little short-term change is problematic, the second has a good deal of appeal: despite consistency over the life course, this consistency is not perfect. To quote Blumstein et al.: "There is little knowledge of the factors that reliably identify antisocial preadolescents who do not progress to offending patterns involving serious crime. Furthermore, there is evidence that suggests it is even more difficult to predict eventual serious criminal behavior among persons who first become offenders in young adulthood" (1986: 47).

variation in delinquency. The theory, designed to explain a "sustained pattern of delin­ quency" is tested by examining the effects of the theory's causal variables on "unexpected delinquency."

5. This might be called the "iron bar problem." It would be nice to see what hap­ pens to an iron bar over time (for example, with respect of oxidization, and so on), but the rate of change is so slow that those interested in rust are likely to turn to other designs. A similar problem is encountered in research on atoms whose decay rate is one in a billion per year. One could follow a single atom for a few billion years, or devise an alternative method by which the rate might be estimated. To date, these alternative methods appear to have been reasonably precise. Likewise, the "iron bar problem" does not seem to be high on the list of intellectual priorities among physical scientists.

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The idea of concentrating research attention on cases not yet explained is old and obvious. If explanatory effectiveness is to be improved, one must concentrate on cases whose behavior has not yet been explained. For exam­ ple, if having a low IQ and being poorly supervised by one's parents predicts delinquency, the puzzling case is the well-supervised delinquent with a high IQ. This problem surfaced early in delinquency research, appearing under several guises. It is the problem of the "good boy in a high delinquency area," the "middle-class delinquent," the "late corner to crime," and of the "school drop-out who makes good." Pursuing this problem, Glueck and Glueck systematically followed 500 delinquents into adulthood in an attempt to explain the delinquency of those boys classified as being at "low-risk" of delinquency (based on supervision by mother, discipline by mother, and fam­ ily cohesiveness). The Gluecks' extensive analysis of their longitudinal data (an analysis not cited by the NAS Panel calling for longitudinal research directed at this precise question) failed to uncover variables predictive of delinquency among the sample of delinquents. In other words, subsequent delinquency cannot be predicted among groups homogeneous on current delinquency, an observation previously reported in just these terms (Hirschi and Gottfredson, 1983) and repeatedly confirmed by attempts to predict sub­ sequent crime among offenders. For example, the lengthy history of parole prediction demonstrates that the principal factor that reliably distinguishes subsequent offenders from nonoffenders is the extent of their prior records of offending (see, for example, Gottfredson and Gottfredson, 1987). The signifi­ cance of the results of these longitudinal studies for the idea that change in level of crime can be explained by longitudinal research that follows offenders over time has apparently not been appreciated by those calling for more research focusing directly on the same question.

Our assertion that only crime can now predict crime is apparently contra­ dicted by the results of longitudinal research that claims to predict delin­ quency when prior delinquency is held constant. Elliott et al. report that "the only variables having a direct effect on [subsequent delinquency or drug use] are involvement with delinquent peers and prior delinquency or drug use" (1985: 117). Does this finding contradict previous longitudinal research?

The answer is to be found in the fact that Elliott et al. do not use the longitudinal feature of their longitudinal design in testing the theory that jus­ tified the design in the first place. Instead, they decide that with respect to the relation between delinquency of peers and changes in delinquency, "the use of the concurrent measures is not necessarily inappropriate, however, because certain relationships may be expected to operate at more or less the same time" (1985: 107). As a result, the Elliott et al. study becomes in effect a cross-sectional analysis with a control for prior delinquency and its findings

LONGITUDINAL RESEARCH 595

do not contradict prior longitudinal analysis.6 (It can be argued that many of the problems identified here are unique to

the particular study in question, and therefore say little or nothing about the virtues of the longitudinal method. Such arguments ignore the fact that the studies in question were designed in large part to reveal the virtues of the method. That they fail to do so cannot be dismissed as irrelevant to their justification.)

Substance Abuse. The Blumstein et al. panel begins with the assumption that a relation between crime and substance abuse has been established. The panel in fact presents data showing a relation between self-reported delin­ quent acts and self-reported drug use from the Elliott study. The panel then notes that the association between drug use and crime does not answer the question about whether drug use leads people into crime. It concludes that "[a] longitudinal study of both criminal involvement and drug use is needed to sort out the causal relationship between substance abuse and criminal activity" ( 1986: 50-51 ).7

The panel's optimism about the benefits to be obtained from further longi­ tudinal research does not appear to be justified by prior longitudinal research. The question has already been addressed by longitudinal research. According to Elliott et al. data reproduced by the panel (Blumstein et al., 1986: 52), "the predominant pattern among drug users who are also delinquent was for initial drug use to follow delinquency or to occur simultaneously, rather than for drug use to precede delinquency" (1986: 51). Following the logic of Blum­ stein et al., drug use appears to protect against delinquency, since a majority of those who use drugs are not delinquent. For that matter, it is not clear from the table presented that the measures of delinquency and drug use are a result of longitudinal research. It appears that Elliott et al. determined tem­ poral order by merely asking respondents to recall when their delinquency and drug use occurred. Since this device is standard in cross-sectional research, it is also not clear (1) why the field needs expensive prospective longitudinal studies of the type proposed by the panel (and others, for exam­ ple, Farrington et al., 1986); and (2) what the Elliott et al. results might mean about the causal connection between drug use and crime. Taken at face value, for example, these results suggest that felony assault causes beer drink­ ing. The authors are not convinced that the field "needs to know" such facts or that longitudinal research is necessary to produce them.

6. To the extent that "involvement with delinquent peers" is merely one more mea­ sure of delinquency, the Elliott result would not contradict the authors' conclusion even if it were longitudinal.

7. The Elliott data cited by the NAS Panel are for two waves of the longitudinal study, the first and the fifth. Since the relation cited by the NAS panel does not depend on the wave being examined, questions are again raised about the informational value of the longitudinal design.

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The long-established relation between all forms of "delinquency" and all forms of drug use is amenable to an interpretation that does not require empirical examination of meaningless questions of temporal order. Outside the "criminal careers" perspective, it is ridiculous to ask whether robbery causes burglary or burglary causes robbery, because they are assumed to have a common etiology. Put another way, most criminal acts and delinquencies are assumed to be different manifestations of the same phenomenon. Empiri­ cal examination of their "sequencing" might be possible, but it would be without causal import. In the view of the authors (Hirschi and Gottfredson, 1986), drug use is delinquency and has therefore the same causes as delin­ quency. All existing evidence can be interpreted as consistent with this view.

Peer Group Influences. Perhaps the most problematic correlation in delin­ quency research is that between peer delinquency and delinquency. This cor­ relation is, in most studies, very strong, among the strongest in the field. The problem is that the meaning of the correlation is not clear. And this problem appears no nearer solution today than when the Gluecks considered it in 1950.

The Gluecks advanced the hypothesis that "birds of a feather flock together," suggesting that delinquency causes association with other delin­ quents. This hypothesis reverses the causal order from that asserted by differ­ ential association theory, according to which association with delinquents is a major or, in some versions, the sole cause of delinquency. Clearly, this would seem to be a case for longitudinal research: which comes first, delinquency or association with delinquents?

Longitudinal research replicates the standard cross-sectional finding of a correlation between the respondent's delinquency and the respondent's report of the delinquency of his friends (Elliott et al., 1985). The Blumstein et al. panel expresses awareness of this correlation, but seems to take the causal order issue as resolved, stating that "[s]everal longitudinal studies report that association with delinquent friends is clearly related to participation in seri­ ous criminal behavior at later ages" (1986: 53). Given this resolution (for the panel), the panel's attention turns to interpretation of the correlation: "Recent research ... is attempting to sort out the underlying causal relation­ ships, including the possible mediating effects of parental supervision and attachment, involvement in conventional activities, and exposure to conven­ tional attitudes" (1986: 53).

These statements illustrate problems inherent in calls for longitudinal research that longitudinal research itself cannot begin to resolve: quantitative research presupposes ideas that direct the collection, analysis, and interpreta­ tion of data. Absent such ideas, neither causal order nor spuriousness issues are likely to be resolved, whether the study is cross-sectional or longitudinal. For example, the "finding" that delinquent friends are present before "partic­ ipation in serious criminal behavior" is hardly evidence contrary to the birds

LONGITUDINAL RESEARCH 597

of a feather hypothesis since it would also be predicted by that hypothesis (which, after all, asserts that people acquire the propensity to delinquency, find delinquent friends, and then commit delinquent acts, including "serious criminal" acts). Unless this alternative hypothesis is acknowledged in the collection, analysis, and interpretation of data, the fact that a study is longitu­ dinal will mean nothing in terms of the likelihood that it will add to existing knowledge.

One longitudinal study purports to have considered these issues and to have collected evidence bearing on the temporal order issue. Elliott et al. (1985) present a test of an "integrated theory," the major feature of which is the idea that the sole cause of persistent delinquency is the delinquency of one's friends. The study uses a longitudinal design in a national probability self-report survey, with six waves of data already collected through 1983. Does this study shed new light on the delinquency/delinquency of friends question?

Which comes first, according to the National Youth Survey, delinquency of friends or delinquency? Interestingly, Elliott et al. argue that their longitudi­ nal design inhibits rather than facilitates unambiguous test of the causal order question, noting that their theory presupposes more rapid changes than their longitudinal design will accommodate. The actual test of the theory, then, as mentioned, is a composite cross-sectional-longitudinal design, where involvement with delinquent peers and self-reported delinquency are mea­ sured at the same time. It is not surprising that Elliott et al. find a strong correlation between self-reported delinquency and involvement with delin­ quent friends. This strong correlation has been reported in similar cross-sec­ tional research for at least 35 years. The Elliott et al. interpretation of the relation, with lags and cross lags, is more complex than those produced by earlier research. Its causal status is not, however, more definitive.

The analytical procedure employed by Elliott et al. is to first regress cur­ rent self-reported delinquency on prior delinquency and then ask whether contemporaneous "peer delinquency" is related to "delinquency." One inter­ pretation of these results is that delinquency is correlated with delinquency, that self-reported peer delinquency is just another measure of self-reported delinquency. In cross-sectional analysis, measures of peer delinquency are related to official delinquency when self-report measures of delinquency are held constant (see Sampson, 1986: Table 1). This "measurement" interpreta­ tion of the results is also consistent with the content of Elliott's "peer delin­ quency" index. This index is composed of answers to two sets of questions. The first measures time spent with other people. The second measures the respondent's estimate of the proportion of his or her close friends who have

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engaged in specific delinquent activities during the previous year. The delin­ quent activities reported for friends are the same delinquent activities previ­ ously reported by the respondent for himself. The method overlap in the two measures of delinquency is thus extreme.

One might reasonably ask the basis of the respondents' answers to ques­ tions about the delinquencies of their friends. Several possibilities come to mind: (1) the respondent may have been at the scene, himself engaging in the activity; (2) the respondent may impute his own qualities to his friends; (3) the respondent may impute friendship to people like himself; (4) the respondent's friends may have told him about delinquencies he did not him­ self witness; and (5) the respondent may have heard about his friend's delin­ quencies from people who witnessed (or heard about) them. If "delinquency of peers" is really "delinquency of respondent" (see numbers 1, 2, and 3), the causal order question is hardly resolved by this research. If "delinquency of peers" is really hearsay or rumor (numbers 4 and 5), the value of the measure is obviously suspect (and is again contaminated by the characteristics of the respondent). In either case, the meaning of this variable, the central variable in the Elliott longitudinal analysis is, to say the least, unclear. What is clear is that longitudinal research, per se, has done little to resolve the key theoreti­ cal dispute in the causation of delinquency (Bordua, 1966; Elliott et al., 1985).

This summary of the social and demographic correlates of crime leads one to conclude that the causal order problem is an illusion that largely disap­ pears when it is addressed one variable at a time. There is no evidence that existing longitudinal research has resolved any issue of causal order more adequately than has cross-sectional research. On the contrary: the complexi­ ties of analysis introduced by longitudinal data have tended to interfere with the straightforward resolution of what tum out to be largely conceptual issues.

TREATMENT AND CRIMINAL JUSTICE INTERVENTION EFFECTS

According to Farrington ( 1979: 310-311 ), "longitudinal studies are useful in investigating the effects of particular events or life experiences on the course of development. A central question in criminology concerns the effects of different penal treatments on criminal careers." Farrington then goes on to describe a research design that blends features of a true experiment (random assignment to treatment and control groups) with the pre- and post­ treatment measures provided by the longitudinal design. Morris, chair of the MacArthur Foundation Justice Program Study Group, finds the Farrington design persuasive and lobbies for its support: "What we now need is new research strategy to be launched by a series of relatively small cohort studies of high risk groups with a variety of experimental treatment modalities attached thereto" (1986: vi).

LONGITUDINAL RESEARCH 599

We do not wish to quarrel with the ideal design for evaluating the effects of treatment in the criminal justice system. Evaluation design issues have been carefully and fully explicated (for example, Cook and Campbell, 1979; Logan, 1972), and the admitted strength of these designs says nothing about the value of longitudinal designs that share none of their features beyond repeated measurement.

Longitudinal research in crime and delinquency is by definition nonexperi­ men tal. Active intervention by the investigator and random assignment of subjects to treatment and control groups are not part of these designs and should not be used to justify them. More importantly, features of longitudi­ nal research should not be presented as though they were part and parcel of powerful experimental or quasi-experimental designs.

Farrington ( 1979: 313) reports that "the Cambridge Study's analyses showed that, both between ages 14 and 18 and between ages 18 and 21, youths who were convicted became more delinquent than those who were not." This finding is interpreted as evidence in favor of "scientific labelling theory." It is, however, contrary to the conclusions of experimental work in the field, which finds no such effects of conviction. It is also contrary to the bulk of evidence on the effects of sanctions (Blumstein et al., 1978; Tittle, 1980). Research that produces results not found by other research designs, especially by stronger designs, must be viewed with caution. Is there a possi­ ble design explanation for the "longitudinal research" finding that efforts to help or punish offenders make them worse?

The design used by Farrington compares a measure of self-reported delin­ quency for individuals convicted of offenses between ages 14 and 18 with the same measure for persons not convicted during this same period. The con­ victed subjects were more delinquent than unconvicted subjects both before and after conviction. In an attempt to control for the prior difference in delinquent behavior, Farrington "matched" convicted and unconvicted sub­ jects on prior level of delinquency. In all of the comparisons reported, sub­ jects formally convicted of offenses had higher self-report delinquency scores than the matched sample of unconvicted youth. (Youths convicted before age 14 were not included in the comparison.)

On their face, these results may be interpreted in two ways: (1) the British Juvenile Justice System reasonably accurately identified and treated the most seriously delinquent boys in the Farrington sample; or (2) Farrington is cor­ rect that conviction increases the likelihood of subsequent delinquent or crim­ inal acts. If the British Juvenile Justice System selects offenders purely on the basis of chance (that is, without regard to the probability of future offending), Farrington's design is a true experiment and his conclusions probably valid. Unfortunately, his own data show that the British Juvenile Justice System is systematically biased toward selection of active delinquents and that such dif­ ferential selection could account for the apparent effects of conviction.

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In an attempt to control for this bias, Farrington matches the convicted and unconvicted groups on prior delinquency scores. The extent to which matching is possible is inversely related to the accuracy of the selection deci­ sions made by the British Juvenile Justice System. The extent to which matching accomplishes its design task is also inversely related to the accuracy of the British Juvenile Justice System selection decisions. Put another way, the better the system, the worse Farrington's design will make it appear to be.

The British System is not accurate enough to preclude finding cases with the same percentile rankings on delinquency scores in the convicted and unconvicted samples. Farrington is thus led to the conclusion that he is able to create groups identical on prior delinquency. It is possible that Farring­ ton's groups are not in fact identical on the variables on which they are osten­ sibly matched. The convicted subjects with self-report scores low enough to overlap with the self-report scores of unconvicted subjects will tend, on remeasurement (by whatever means), to become more delinquent. The unconvicted subjects with self-report scores high enough to overlap with the self-report scores of convicted subjects will tend, on remeasurement (by whatever means), to become less delinquent. (This mathematical necessity is to some extent masked in Farrington's presentation by the use of average percentiles rather than average scores.) A regression artifact explanation of Farrington's results is supported by the finding that conviction subsequent to age 14 predicts (in Farrington's logic, causes) incorrigibility at ages 8 to 10. (That is, when subjects are matched on subsequent self-reported delinquency, those convicted after age 14 have higher incorrigibility scores at earlier ages.)

In another context, the West-Farrington group reports that the "compara­ tively light sentences typically awarded in most cases reflect the generally trivial nature of the offences brought before the London juvenile courts" (1973: 10-11). This suggests the possibility that delinquents learn upon con­ viction that the costs of crime are not as severe as they had imagined and that they therefore increase their criminal activity. Since this possibility too was suggested by the West-Farrington data, it is not clear how Farrington is able to ascribe the same finding to labelling effects. Thus, despite rigorous and sincere effort to analyze an apparent effect of court processing within the con­ text of a true and high-quality longitudinal design, the West-Farrington group is unable to provide a convincing causal analysis or a convincing inter­ pretation of the effect observed.

Clearly, the longitudinal study itself is unable to solve construct validity questions not addressed in the design of initial data collection efforts. (Despite the multiple waves of data collection, the longitudinal researcher enjoys little advantage over the cross-sectional researcher with respect to the flexibility to respond to deficiencies in design or data collection. By the time analysis has revealed problems, the data necessary to resolve them already

LONGITUDINAL RESEARCH 601

were not collected. This problem is not unique to longitudinal research, it is simply more painful in that context.)

In this connection, it is instructive to compare the Farrington conclusion about the effects of the criminal justice system with the conclusions reached by Tracy, Wolfgang, and Figlio in their longitudinal study in the United States: "Failure to impose sanctions-failure to impose necessary controls early---<:an encourage further delinquency. This situation is apparently what happened in Cohort II. Initial Index offenses were not singled out for severe dispositions early enough to have had a deterrent or rehabilitative effect" (1985: 24). The design leading Tracy et al. to their assertions about how young offenders should be treated in the criminal justice system is the design used by Farrington to reach a contrary conclusion. It is also the design advo­ cated by the Blumstein et al. panel and by Farrington et al. (1986).

The "Cohort II" study was, in essence, a replication of the Philadelphia cohort study described in Delinquency in a Birth Cohort (Wolfgang et. al., 1972). The earlier study led the authors to a rather different conclusion about the effects of justice system interventions:

It appears that the juvenile justice system has been able to isolate the hard core offender fairly well. Unfortunately, the product of this encounter with sanctioning authorities is far from desirable. Not only do a greater number of those who receive punitive treatment (institutional­ ization, fine, or probation) continue to violate the law, but they also com­ mit more serious crimes with greater rapidity than those who experience a less constraining contact with the judicial and correctional systems. Thus, we must conclude that the juvenile justice system, at its best, has no effect on the subsequent behavior of adolescent boys and, at its worst, has a deleterious effect on future behavior (1972: 252).

These inconsistencies in the results of longitudinal research about the impact of justice system processing may be resolved in several ways. The effects of processing in London at one point in time is similar to the effects in Philadelphia at one point in time and different from the effects in Philadel­ phia at another point in time. Or, one or another of the Philadelphia cohorts may have gone through some life experience that makes its members unusual in their reactions to the sanctions imposed by the justice system. Of course, neither of these alternatives is attractive on scientific or policy grounds. For­ tunately, a third alternative exists: all longitudinal or cohort studies appar­ ently produce the same finding. Interpretation of this finding is contingent on current theoretical or policy fashions. It one day reflects the leniency of the criminal justice system and another day the harshness of the same system. Neither interpretation can be tested or refuted by the longitudinal or cohort design. The best guess, based on logic and evidence collected by better designs, is that neither interpretation is correct. The apparent "effect" of

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criminal justice processing is merely an artifact of selection "bias" in the lon­ gitudinal design. The fact that a judge does or does not "sustain" the findings against a juvenile has little or no impact on his subsequent behavior (Hirschi and Gottfredson, 1986).

The passive observational longitudinal design has obvious difficulty resolv­ ing questions about the causal impact of treatment efforts. Would it be worthwhile to append experimental interventions to ongoing longitudinal designs as a device for resolving problems of causal order-as recently sug­ gested by Farrington et al. (1986)? As proposed by Farrington et al., "the best method for advancing knowledge about ... key issues is by means of longitudinal-experimental surveys. . . . [I]n these kinds of studies, people are followed up over a period, and the effects on them of experimental interven­ tions are investigated" ( 1986: 151 ). Farrington et al. propose numerous potentially valuable treatments that might be studied by criminologists. For example, they propose studies of the effects of employment services for teen­ agers, drug counseling, head start programs, learning skills to oppose peer pressures, court dispositions (compare the discussion above), and postprison income maintenance, but they do not explicitly discuss their reasons for thinking that such studies would be strenthened by addition of a longitudinal component. Given the thrust of their discussion, one guess is that they believe a longitudinal study would identify subjects for whom a particular treatment was or was not effective. What works for 10-year-olds may not work for 15-year-olds. If an effect is found subsequent to early marriage, it may not be found subsequent to late marriage.

In terms of the plain practicalities of research limited by time and money, it makes little sense to worry about the conditions under which a treatment program is effective before it has been established that the treatment is effec­ tive at all (Zeise!, 1982). The longitudinal-experimental design, in other words, appears to assume what it is designed to show-a most risky assump­ tion, especially when it requires a long-term commitment of research resources.

There are no advantages to the Farrington et al. research design, and there are many problems with it. Following subjects for years in advance of attempts to treat them would add greatly to the cost of program evaluation but would not add to its validity. The very purpose of the randomized experi­ ment is to make irrelevant the prior history of the subjects and to do so in the most efficient manner possible. Given the large amount of nonrandom sam­ ple loss typically suffered by longitudinal surveys in the United States, the results of such "experiments" could not be generalized as efficiently as those with an ordinary (that is, nonlongitudinal) design. Researchers who do not trust randomization or who do not believe its effects may "feel better" if they know something about the subjects prior to intervention, but it is a mistake to confuse such feelings with the requirements of scientific research.

LONGITUDINAL RESEARCH 603

THE EFFECTS OF ORDINARY LIFE EVENTS

A considerable source of the attraction of the longitudinal design is its abil­ ity to track individuals through ordinary institutional experiences-entering and leaving school, entering and leaving marriage, finding and losing a job, becoming a parent, and so on. The design assumes that these events may have a causal impact on criminal behavior, and that the task is to study the interplay between subject characteristics (for example, social class) and char­ acteristics of the institutional experience (for example, marriage to a delin­ quent as opposed to a nondelinquent woman (Farrington, l 986a) as they jointly influence the probability of delinquency.

As noted in the discussion of the effects of the criminal justice system, it seems that concern with the conditions under which life events affect criminal behavior should follow evidence that such events do in fact affect criminal behavior. The evidence for such speculation is not nearly as strong as advo­ cates of developmental studies of crime and delinquency would have one believe. In logic, the problem of determining the effect of these ordinary life experiences is identical to that encountered in efforts to determine the effects of delinquent peers on delinquent behavior. Associations with delinquents are not "accidental" or, in research terminology, random. Neither, it may be argued, is marriage to a good woman, persistence in a good job, or in an educational or vocational program. Nor, it may be argued, is the age at which these events take place accidental or random. In fact, many theories would argue that the characteristics of people associated with these events are also associated with crime and delinquency. Indeed, some theories go so far as to argue that crime-relevant characteristics of people cause all of these events (Olweus, 1979; Hirschi and Gottfredson, 1986).

If these theories are true, reports from longitudinal research of a causal impact of ordinary life events on crime are wrong. Neither perspective is unambiguously supported or refuted by a correlation between ordinary events and delinquency. What is required is either random assignment to such events (or complete assignment to them-as in the World War II "assign­ ment" of almost all young men to a "job") or careful control of relevant personal characteristics (coupled with adequate variation in assignment-that is, there must be enough "good workers" out of work and enough "bad work­ ers" continuously employed to allow the relevant comparisons). The obvious difficulty in finding the requisite natural variation seems to be evidence for the view that the longitudinal/developmental assumption that such events are important neglects its own evidence on the stability of personal characteris­ tics (Loeber, 1982; West and Farrington, 1977; Farrington, 1979, 1986a). In the latter case, the "cross-sectional" survey (which can, it might be recalled, ask people "when" and "how long" questions) is more likely to be adequate than the longitudinal study with an equivalent budget. The funds used to

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follow the same people over an extended period of time can be used to collect more information on more people at one point in time, thus facilitating the application of modern, sophisticated multivariate statistics to such problems. Advociates of longitudinal research acknowledge the utility of such tech­ niques (Farrington, 1979), but the design of existing longitudinal studies unfortunately inhibits their application, in part by creating the illusion that the longitudinal design somehow makes them unnecessary. Given the cen­ trality of the dispute between the personality and the institutional views of crime causation, unqualified recommendations for more longitudinal studies (Farrington, 1979, l 986a, 1986b; Farrington et al., 1986; Blumstein et al., 1986; Tracy et al., 1985) are once more hard to justify.

The problems facing the researcher can be illustrated by consideration of the effects of marriage on crime. As is extensively documented, crime rates tend to rise until late adolescence and then decline. The general decline in crime is coincident with a variety of life events that seem inconsistent with criminal behavior, such as a job, marriage, and the accumulation of material goods. This coincidence has suggested to many criminologists (for example, Greenberg, 1977, 1985; Farrington, 1986a; Baldwin, 1985) that these events are responsible for the decline in crime. Existing research, however, contra­ dicts the hypothesis that the decline in crime with age is due to such events, since the decline occurs whether or not these events occur (Hirschi and Gott­ fredson, 1983). The inability of life events to explain the age distribution of crime suggests that these events are not themselves causes of crime. This conclusion is contrary to the basic substantive justification for the longitudi­ nal design.

Longitudinal researchers counter with the following argument: "Some fac­ tors only apply at certain ages. For example, the relation between marriage and crime cannot be studied among 10-year-olds, who cannot get married, any more than the relation between truancy and crime can be studied among 60-year-olds. Other factors may have different meanings at different ages .... It seems implausible to argue that all variables are related to crime in the same way at all ages" (Farrington, 1986: 229). Similarly, Farrington et al. (1986: 27) argue that

... there are different relationships with offending at different ages. For example ... Farrington (1986) reported that if a child, up to age 10, had parents who had been convicted, this was one of the best predictors of that child offending at ages 14 through 16 and 17 through 20, but did not predict offending at ages 10 to 13. West (1982) reported that if a delin­ quent married between ages 18 and 21 marriage had no effect on offend­ ing between these ages, while marriage between 21 and 24 (to a noncriminal woman) led to a decrease in offending between these ages.

LONGITUDINAL RESEARCH 605

It is implausible to propose that a variable such a marriage should have the same effect on offending at all ages. s

This combination of logical and data-based argument is at first glance per­ suasive. Marriage and truancy would not be expected to have the same effect or the same meaning for children as for old people. The issue, however, is their empirical relation to crime, a relation that needs to be established before it can be used as part of a logical refutation of the age invariance thesis. If truancy, marriage, and stable employment are causes of crime at an early age and if there are no equivalents of these variables at later ages, then the causes of crime indeed vary from one age to another. What needs to be established in the first instance, therefore, is the causal influence of these variables at any age. This has not been done, and arguments that assume it has been or could be done remain speculative rather than logical.

The empirical evidence cited by Farrington ( 1986a) and by Farrington et al. ( 1986) in favor of the argument that the causes of crime vary by age is not persuasive. Both findings of differential causation by age come from the West and Farrington longitudinal study. The finding of a differential effect of parental criminality depending on the age of the child is not convincing because all differences are in the same direction, and the differences among the differences are insignificant. (No test of the statistical significance of the difference is reported.) The correct conclusion from these data is that the effect of parental criminality is the same at all ages. If it were not the same, if one were required to interpret the Farrington et al. finding, one would have to explain why one of the major causes of crime is not correlated with "early onset" and appears to produce its effects from 4 to 10 years after exposure to it.

The marriage finding reported by Farrington and his colleagues is even less persuasive. The subjects in the London study were not randomly assigned to marital statuses, let alone to delinquent and nondelinquent wives, and there is therefore no reason to believe that a meaningful age by marriage by type of marriage interaction has been discovered in the London longitudinal study. When such an interaction is discovered, the burden is on the researcher to show that it is replicable and theoretically nontrivial.

8. Farrington, Ohlin, and Wilson (1986: 27) report that "most research on crime and delinquency has been and is cross-sectional in design. Nevertheless, most of our firm knowledge about criminal careers derives from longitudinal studies." Although this state­ ment is tautological (since "criminal careers" are not studied cross-sectionally), a more worthwhile statement might be: "The principal finding of well-designed longitudinal research is that its results replicate those of cross-sectional research."

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PREVALENCE AND INCIDENCE, PARTICIPATION AND LAMBDA

A major attraction in the contemporary call for longitudinal research is that it offers the opportunity to distinguish clearly between ordinary offenders and so-called career criminals: in other words, the opportunity to study "the dimensions of active criminal careers" (Blumstein et al., 1986: 55). Advo­ cates of the longitudinal design stress the fact that the "crime rate" can be "decomposed" into several components. The crime rate is a function of (1) the number of persons in the population committing crimes (the preva­ lence of crime) and (2) the number of crimes they commit. When the denom­ inator of the rate consists of the total number of people in the population, the first rate is traditionally called the prevalence rate and the second the inci­ dence rate of crime. Modern criminal career researchers alter the traditional incidence measure by using "the number of active criminals" as the denomi­ nator to produce individual frequency rates, or what they call lambda.

All of these statistics can be computed from cross-sectional and longitudi­ nal designs. For example, the annual crime rates reported by the Uniform Crime Reports and the National Crime Survey are cross-sectional estimates of the incidence of crime. When researchers divide subjects into delinquents and nondelinquents (however delinquency is measured), a prevalence statistic may be calculated. When the number of persons committing at least one criminal act and the number of acts they have committed are known, one can calculate lambda, whatever the research design. The traditional tendency among researchers has been to treat prevalence and incidence as interchange­ able and "lambda" as derivative (Gottfredson and Hirschi, 1986). The cur­ rent preference among longitudinal researchers is for prevalence and lambda, with the traditional incidence measure being seen as derivative (Farrington, 1979; Wilson and Herrnstein, 1985; Blumstein et al., 1986).

The interest in prevalence and lambda stems not from the idea of inter­ changeability but from the idea that these measures have distinct causes. "The factors that distinguish participants from nonparticipants could well be different from the factors that distinguish among participants, in terms of their offending frequency" (Blumstein et al., 1986: 54). (For empirical evi­ dence to the contrary, see Riley and Shaw, 1985.) Put in other terms, the criminal career researcher assumes that the causes of the second crime may differ from the causes of the first and third crime; that those offenders who commit 5 crimes may differ from those who commit 2 or 12; that, in other words, differences among offenders are as significant for the causation of crime as differences between offenders and nonoffenders. Nor does this exhaust the complexities introduced by interest in differences among offend­ ers over time. The offender who moves from petty theft to rape to vandalism may differ in causal terms from the offender who starts with aggravated

LONGITUDINAL RESEARCH 607

assault and moves from there to bicycle theft and shoplifting. Since such sequences are significant to criminal career research and by definition take place over time, they help justify longitudinal research. Lambda is also attractive to those interested in crime control policies that focus on the indi­ vidual offender.

The career criminal perspective introduces a distinction not unlike that found routinely in medical research. Consider heart disease. Medical researchers studying the causes of heart disease can focus their attention on those who have suffered heart attacks and attempt to find factors indicative of multiple attacks, or they can focus on the general population and attempt to find factors distinguishing those who suffer from those who do not suffer heart attacks. In the first case they deal with a population whose behavior and treatment has been much affected by the initial heart attack. In the sec­ ond case they deal with a population whose "causal history" has not been contaminated by efforts to correct the medical problem of interest. Those concentrating on the first group will likely formulate policies for the individu­ alized treatment of heart attack patients and will explore all sorts of operative techniques, drugs, and mechanical devices. (Thereby attracting great atten­ tion and resources for their research.) To the extent they are successful, the lives of some heart attack victims will be prolonged. Those who study the prevalence of heart attacks, in contrast, will attempt to identify manipulable causes of heart attacks, such as smoking, lack of exercise, and excessive cho­ lesterol. To the extent they are successful, they will prolong the lives of a great many people, including, in all likelihood, heart attack victims. The sta­ tistics of human longevity are driven much more by "prevalence" than by "lambda" factors.

There is no reason to believe that the same logic does not apply to crime. All correlates of the prevalence of crime are also correlates of crime incidence (as traditionally assumed). At the same time, the correlates of lambda appear to be of limited significance. For example, the finding that drug use predicts lambda is equivalent to the finding that stroke history is related to heart attacks-that is, neither correlation has causal significance.

At first glance, it seems reasonable to argue in favor of both approaches to research and policy. If time and money were unlimited, and if there were no "prevention costs" from a policy focusing on lambda, we would agree with this position. Since this is not the case, the present emphasis on longitudinal research leads one to overlook more promising avenues for criminal justice policy. Criminal career researchers argue that criminal justice policy is restricted to criminal offenders, and cannot attend to the general population. According to this line of reasoning, policies directed at family, school, and environmental design are not "criminal justice" policies, and are therefore irrelevant topics of research for federal agencies charged with crime control. Obviously, we do not agree.

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RESEARCH DESIGN AND THE THEORY OF CRIME

The longitudinal study is a consequence of particular theories or orienta­ tions toward the causes of crime. Theories that see crime as a consequence of developmental processes or stages, theories that see crime as an occupation or state one moves into and out of, or theories that see crime as the consequence of positive learning by always malleable individuals-all suggest the desirabil­ ity or necessity of following individuals over time.

Other theories see crime as a consequence of relatively stable characteris­ tics of people and the predictable situations and opportunities they experi­ ence. These theories do not presume that major changes in criminal activity are associated with entry into or exit from roles, institutions, or organiza­ tions. Such theories are therefore adequately tested at any point in the life course, the particular point selected by reference to expected distributions of the important variables.

What is clear, therefore, is that the theoretical point being tested has impli­ cations for the appropriateness of a particular research design, and vice versa. That is, advocacy of a particular research design almost by definition entails acceptance of one side or the other of this dispute. Thus, researchers favoring longitudinal research designs must assume that transitions from one state to another (for example, from being single to being married) produce changes in crime. They must assume that the specific character of institutional arrange­ ments or social relations will have an impact on crime (for example, that being married to a nondelinquent wife will have good consequences while being married to a delinquent wife will have bad consequences independent of the initial propensities of the husband). Such theories may be correct or incorrect. But their truth is problematic, and what needs to be understood is that these theories and not methodological virtue may be behind the prefer­ ence for the longitudinal design.

Although theoretical notions are implicit in the decision to advocate longi­ tudinal designs, explicit theories of crime are extremely rare among longitudi­ nal researchers. One finds them proposing to examine the effects of becoming unemployed or dropping out of school or getting married, but the theoretical justification for these interests appears typically to be nothing more than the common sense notion that these factors "should make a difference." When pressed, longitudinal researchers tend to be eclectic and to fall back on theo­ ries traditionally used to explain cross-sectional results. Thus, for example, in his attempt to explain changes in crime over the life course, Greenberg ( 1977) proposes a model combining traditional strain and social control ideas. Elli­ ott et al. ( 1985) combine three standard sociological theories (strain, control, and differential association) to provide structure to the National Youth Sur­ vey. And Farrington (1986b) combines subcultural, opportunity, social

LONGITUDINAL RESEARCH 609

learning, social control, and differential association theories to produce a four-stage processual model of delinquency.

The "theoretical" appeal of longitudinal research apparently lies in its implicit promise to take one to the scene of the crime, to allow study of the person before, during, and after the event. Frequent measurement is inter­ preted as measurement directly relevant to the causal chain involving crime, and as measurement sufficiently detailed to allow us to understand the mean­ ing of events to those participating in them.

In practice, "frequent" measurement becomes once-a-year or once-every­ six-months measurement. More frequent measurement would be prohibi­ tively expensive, even if the size of the study sample were not increased to provide the cases necessary to study the rare combinations of life events pro­ duced by such frequent measurement. For example, in any given week, only a very small portion of an adolescent sample would be expected to drop out of school, or to use marijuana for the first time, or to acquire new prodelinquent friends. Even assuming perfect correlations between such activities and sub­ sequent crime, the sample sizes would in all likelihood be too small to allow rejection of the null hypothesis. Thus, even if the theory guiding such fre­ quent-measurement research were true, the data collected to test it could not falsify or verify the theory.

However, frequent measurement remains a seductive justification for longi­ tudinal research. Because one tends to equate behavioral and causal sequences, one imagines that observation of the former will automatically reveal the latter. Put another way, one assumes that "complete" observation is all that is necessary to understand causal processes. Unfortunately, noth­ ing could be further from the truth. One can observe offenders every hour of every day and still not know the causes of their behavior. Facts require a context for their interpretation. Even longitudinal facts do not speak for themselves. Observation, as Darwin reminded us, must be for or against some view if it is to be useful. As of now, the longitudinal research tradition has no unique findings nor compelling theory about the causes of crime it could use to justify more detailed or more frequent observation.

In the "cross-sectional" view of crime, differences across people and their life circumstances are sufficiently stable over time that day-to-day variability is uninteresting or likely to be nothing more than measurement error. In this view, apparently large changes in circumstance are themselves perfectly pre­ dictable from the explanation of crime itself. Lack of perserverence in school or in a job or in an interpersonal relationship are simply different manifesta­ tions of the personal factors assumed to cause crime in the first place. Taking up with delinquent friends is another example of an event without causal sig­ nificance. Since such "events" are predictable consequences of the causes of crime, there is little or no point in monitoring them.

Differences in propensity to crime are also sufficiently stable over time that

610 GOTTFREDSON AND HIRSCHI

they need not be continually reassessed. Given basic stability in the causal system, the particular slice of it that one examines is determined by consider­ ations of (I) sampling efficiency-that is, it makes sense to concentrate research at the point in life where the crime rate is maximally variable; (2) measurement adequacy-for example, some subjects are more suitable than others for questionnaire surveys, record searches, or experimental inter­ ventions; (3) policy relevance-for example, understanding crime among the elderly is of limited practical significance; and (4) sampling costs-for exam­ ple, young people are preferred because they are easier to find and to induce to cooperate.

In one version of the cross-sectional view, differences in crime rates by age are due to age itself (Hirschi and Gottfredson, 1983, 1986). This view leads to interest in causes of crime that do not operate on the propensity to crime previously mentioned, but on the differences in the likelihood of criminal acts among persons equal in criminal propensities. For example, holding constant propensity, areas with a curfew for teenagers would be expected to have lower crime rates than areas without such a curfew. Holding constant propensity, communities in which schools enforce attendance rules would be expected to have lower crime rates than communities in which such rules are ignored. Interest in such questions, questions of obvious policy relevance, can only be satisfied by research based on samples sufficiently large and variable to allow control for differences in propensity to crime, samples far beyond the reach of feasible longitudinal designs. (Since such findings can be produced without delay, they are likely to be of greater policy relevance than those produced by standard longitudinal research.)

CONCLUSIONS

Neither the results of current longitudinal research in criminology nor rea­ sonable expectations about proposed longitudinal research in the area justifies the dominance this design has achieved. The most credible facts generated by this research simply confirm long-standing "cross-sectional" findings. Facts unique to the longitudinal method turn out on careful inspection to be suffi­ ciently problematic that they should not be used to advertise its virtues. Attention to longitudinal designs diverts attention from policy-relevant and theoretically important issues. Indeed, current advocates of longitudinal studies blur the distinction between theory and method to such an extent that they seem to be making important substantive and logical assertions when in fact they are merely repeating an extremely narrow conception of crime and its causation. As a consequence, the cost of longitudinal thinking to the study of crime is not restricted to the large sums necessary for its execution. 9

9. The longitudinal research "community" envisions a single super study to be car­ ried out by a consortium of investigators with funding provided by combining the resources

LONGITUDINAL RESEARCH 611

One of the consequences of increased specialization among social science disciplines is that communication across disciplinary boundaries becomes increasingly infrequent and difficult. Were this not true, criminology might have avoided at least some of the misguided enthusiasm it has shown for the longitudinal method. Experience in other areas has shown that while longitu­ dinal methods are perfectly proper and indeed necessary for the study of some phenomena, they are not suitable or useful for others; it has shown that justified criticisms of cross-sectional methods do not justify uncritical faith in longitudinal methods. For example, according to Glenn, "the most impor­ tant recent development among researchers in the aging field has been the widespread, though not universal, recognition of the limitations of longitudi­ nal data" (1981: 363). These limitations should be recognized by criminolo­ gists as well.

of several agencies (Blumstein et al., 1986; see also Farrington et al., 1986). According to Morris, Chair of the MacArthur Foundation Study Group, "We came to the firm conclu­ sion that criminal justice research in the United States has reached a stage at which an increasing investment in more ambitious longitudinal studies is essential" (1986: v). In the authors' view, science is better advanced by broad dissemination of research funds under a rigorous peer review process.

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Michael Gottfredson is Associate Professor of Management and Policy and Psychology at the University of Arizona.

Travis Hirschi is Professor of Sociology and Management and Policy at the University of Arizona.