Discussion 5: Research Design III

LONGITUDINAL AND CRIMINAL CAREER RESEARCH: FURTHER CLARIFICATIONS

ALFRED BLUMSTEIN Carnegie Mellon University

JACQUELINE COHEN Carnegie Mellon University

DAVID P. FARRINGTON Cambridge University

We appreciate the opportunity provided by Criminology to present some of our work in this forum and to respond to Gottfredson and Hirschi's critiques of our work. We did not have an opportunity to review the comments by Tittle and by Hagan and Palloni that appear in this volume, and so cannot address them.

Our response to Gottfredson and Hirschi is presented in two parts. The first is a response to their critique (Gottfredson and Hirschi, this volume!) of our paper (Blumstein, Cohen, and Farrington, this volume2). It seems from their remarks that GH88 have not understood the concepts we are using in our treatment of criminal careers.3 This misunderstanding contributes to the continuing disagreement between them and ourselves on the interpretation of available research evidence, especially the evidence of a decline in offending with age, regarding which the distinction between participation and frequency is crucial. Their misunderstanding is also central to our differing views on the implications of criminal career research for theory. The second part of our response addresses issues raised in a very recent paper by

I. Hereafter referred to as GH88. 2. Hereafter referred to as BCF88. 3. Their critique (GH88), as was their original paper (Gottfredson and Hirschi,

1986) and their more recent paper (GH87), is replete with assertions about our purposes and about the assumptions we make. For example, GH88 (p. 50) continue to insist that we are searching "for evidence that 'lambda' remains constant with age" despite our explicit assertion that we have no such intent (BCF88: 14). They interpreted (GH88: 38) "career" as a way of earning a livelihood, despite our explicit statement (BCF88: 2) that we use it in the sense of a progress or course through life. They also challenge our use of an average A. and claim that this undermines our interest in "individual offenders" (GH88: 42). Clearly, A. can be measured first for each individual offender (e.g., Chaiken and Chaiken, 1982). The individual values can then be aggregated to obtain means for population subgroups. This is no different from the treatment of any other individual attribute.

Space limitations preclude our replying to every one of their statements individually. Many of their assertions derive from a misunderstanding of either our purpose or our methods.

CRIMINOLOGY VOLUME 26 NUMBER 1 1988 57

58 BLUMSTEIN, COHEN AND FARRINGTON

Gottfredson and Hirschi (1987)4 that criticizes some of our work on longitudinal research designs. This paper is referred to in GH88, and the issues raised in it are highly relevant to criminal career research.

DISTINGUISHING PARTICIPATION AND FREQUENCY: ONE MORE TIME

In reviewing Gottfredson and Hirschi's criticisms of criminal career research in GH88, it has become clear that they do not understand the basic constructs and the conceptual issues involved in using those constructs. They (GH88: 38) complain that our paper "largely repeats the distinctions," but then they fail to appreciate those distinctions. We will try one more time to clarify the conceptual distinction that is at the heart of a criminal career framework.

DEFINING THE CONCEPTS

Participation distinguishes between offenders and nonoffenders, thereby reflecting the breadth of involvement in crime within a population. It indi­ cates how widespread or limited offending is. On this concept, we and GH88 seem to agree. The problems in understanding arise over the concept of "individual crime rate," "frequency," or "lambda"-all terms that we have used to denote the same concept. Rather than merely characterizing the existence or absence of offending, frequency (or A) characterizes a very spe­ cific feature of offending by individual offenders, namely, its magnitude as measured by the number of crimes an active offender commits in a unit of time. To avoid ambiguity we will use the symbol A to refer to this rate of offending.

The discussion in GH88 repeatedly demonstrates a failure to understand the meaning and application of A. This is most evident in the discussion of their Table 1 (GH88: 42-44). Despite our repeated efforts to explain the meaning of A as the rate at which offenders commit crimes in a unit of time, their Table 1 confuses this concept with the standard statistical concept of a frequency distribution of the number of persons with each count of total arrests-or total self-reported crimes-during a measurement period. Their third column in Table 1 is not A or frequency (in our terms), as they have labeled it, but rather the distribution of subjects with each number of offenses. So, for example, 111 subjects had a total of three officially recorded offenses.

Since a rate involves a count of events per unit of time, it would be possible to convert the number of offenses in their Table 1 to values of A if we knew the length of the active period for each of the individuals who had one or more offenses. This information is not provided, however. The official record

4. Hereafter referred to as GH87.

FURTHER CLARIFICATIONS 59

data covered a period of 2 years and 10 months (January 1963 to October 1965; see Hirschi, 1969: 298). Hence, the offending frequency might be approximated by assuming that all individuals who committed any offenses were active and free in the community throughout the entire period. s If this assumption were true, then the number of offenses in their first column would reflect the value of A (arrests per two years and ten months) for the desig­ nated number of individuals in their A column. Their self-report data referred to the number of different acts ever committed.

This major reformulation is necessary to use the data in their Table 1 to learn about individual frequency rates. Unfortunately, however, data on the frequency distribution of incidence, like that in their Table l, are rarely reported in studies of offending, especially for high values of incidence, which even they truncate at "6 or more." Moreover, such detailed data are almost never reported for subsamples, and this omission has precluded comparisons of A among different population subgroups.

Assuming that all official offenders are active for the full measurement period, and following GH88's definition of incidence (per capita), the essen­ tial difference between incidence rates and A is that people who have no arrests are included in the incidence calculation and excluded from the fre­ quency calculation. In the criminal career framework, having no crimes (or arrests) is viewed as qualitatively different from having some crimes; "zero crimes" is not on the same continuum as other positive numbers of crimes (see below).

In comparing the incidence of crime in population subgroups, we are inter­ ested in determining the relative contributions of participation and A. Popu­ lation subgroups with identical incidence rates may be very different with respect to their participation and ..l; and alternatively, populations with differ­ ent incidence rates may have identical ..l's, but vary widely in their participa­ tion. These differences can only be detected by looking beyond aggregate measures of incidence. GH88's conflation of participation and A is most bla­ tant when they refer to a "serious-offense-participation lambda" (p. 49), a concept that links participation and A in a way that denies their separate meanings.

5. The value of A. should be calculated for each individual only for that period when he is an active offender. Since it is reasonable to expect that a number of the teenagers were not active throughout the observation period, this precludes simply dividing the total number of offenses by the length of the observation period to estimate an annual rate. The best estimate of the rate is the reciprocal of the average interval between each individual's recorded offenses, which can only be calculated for offenders who have at least two events. This is the reason for the sampling procedures referred to by GH88 (p. 41). As we indi­ cated in our paper (BCF88: 17), such procedures will not artifactually induce stability in the measurement of A..

60 BLUMSTEIN, COHEN AND FARRINGTON

SOME EMPIRICAL EVIDENCE

In their critique of our work, GH88 (pp. 37 and SO) claim that we have "ignored research contrary to [criminal career] assumptions." This is simply untrue: We do not ignore or deny the various research evidence. However, we do differ fundamentally from Gottfredson and Hirschi in the interpreta­ tion of that evidence.

ESCALATION AND SERIOUSNESS DURING CAREERS

We disagree that invoking the paradigm of a "career" to characterize the longitudinal life history of crimes by an individual implies any particular pat­ terned trajectories, like escalation in seriousness or specialization in types of offenses (GH88: 38-39). Such are possible trajectories during a career that are substantively interesting and that certainly have merited empirical investi­ gation to confirm or disconfirm them. We agree with GH88 (p. 39) that the accumulating body of evidence generally contradicts the existence of these particular patterns. This failure to find escalation or specialization, however, provides valuable information about the nature of criminal careers. It does not invalidate the usefulness of examining criminal careers.

CORRELA TES OF PARTICIPATION AND A

Another key question inherent in the disagreement between Gottfredson and Hirschi and ourselves is whether the predictors and/or correlates of par­ ticipation are similar to, or different from, the factors related to .A. Contrary to the claims of GH88 (p. 46), the findings in their Table 2 do not resolve the issue, and they are not "the most heavily replicated in the field," at least not with respect to the correlates of A (which are largely unknown). If there is a "substantial consensus on the basic correlates of crime" (GH88: 46), it can only apply to correlates of incidence and of participation. Few researchers have even attempted to measure the correlates of A.

Data From the Cambridge Study in Delinquent Development. We pursue this issue in a limited way here with data collected in the Cambridge Study in Delinquent Development, a prospective longitudinal survey of 411 London males. Because of the small sample size, only nonoffenders, one-time offend­ ers, and recidivist offenders are contrasted. West and Farrington (1973: Appendix C) listed 12 factors, measured at ages 8 to 10, as the most impor­ tant predictors of offending identified in their survey (and in numerous other surveys: see Farrington, 1987). These factors were chosen 1 S years ago, not specially selected for this analysis.

West and Farrington (1973) provide more detailed explanation of the predictors. Briefly, troublesomeness, daring, and dishonesty were ratings of

FURTHER CLARIFICATIONS 61

the boy's behavior by his teachers, parents, and peers. Convictions of biologi­ cal parents were obtained from official records. Poor parental child-rearing behavior (reflecting harsh and erratic discipline), low family income, separa­ tion of a boy from his parents for reasons other than death or hospitalization, and poor parental supervision were ratings based on interviews with parents. Large family size (four or more siblings) was based on information from par­ ents and school records. Psychomotor clumsiness and low nonverbal intelli­ gence were measured in tests completed by the boys, and parental authoritarianism was measured using questionnaires completed by the parents.

In Table 1, phi correlations summarize the bivariate relationships of each dichotomized predictor with (a) conviction as a juvenile (84 boys) versus non­ conviction (327 boys) and (b) reconviction as a juvenile (37 boys) versus one­ time conviction (47 boys) among those convicted at least once. The relative ability of these factors to predict conviction was very different from their rela­ tive efficiency in predicting reconviction among those convicted at least once. In fact, the rank correlation between factors predicting conviction and those predicting reconviction was negative ( - .126).

Table 1. The Prediction of Juvenile Conviction and Reconviction

Factor Measured at Conviction Reconviction Ages 8 - 10 Phi Rank Phi Rank

Troublesomeness .321 1 .333 2 Daring .293 2 .111 9 Dishonesty .266 3 -.066 11 Convicted Parent .232 4 -.180 12 Poor Parental Child- rearing Behavior .184 5 .329 3 Low Family Income .173 6 .315 4 Large Family Size .166 7 .143 8 Psychomotor Clumsiness .163 8 .170 7 Separations from Parent .155 9 .190 5 Low Nonverbal Intelligence .152 10 .341 1 Poor Parental Supervision .146 11 .100 10 Parental Authoritarianism .138 12 .175 6

NOTE: Phi correlations are derived from 2 x 2 tables linking the factor at ages 8 to 10 with (a) convicted or not as a juvenile and (b) reconvicted as a juvenile or one-time offender.

62 BLUMSTEIN, COHEN AND FARRINGTON

Parental conviction was the fourth best predictor of a first conviction: of boys with a convicted parent, 36.5% were convicted compared with 15% of those with unconvicted parents. Parental conviction, however, was negatively related to reconviction (34.2% of those with convicted parents were recon­ victed, in comparison with 52.2% of those with unconvicted parents). Simi­ larly, dishonesty was the third best predictor of a first conviction, but it was negatively related to reconviction. In contrast, low intelligence was only the tenth best predictor of a first conviction, but it was the best predictor of reconviction.

It is plausible to suggest that whether a youth is ever convicted reflects participation in offending, and whether a youth is reconvicted reflects some combination of A and career length. These results, at least in these data, show that the predictors of participation were quite different from the predictors of other dimensions of a criminal career, and this suggests that participation, ..1., and career length may well reflect different theoretical constructs.

Data from the Richmond Youth Project. Table 2 in GH88 is also an attempt to investigate the correlates of participation and ..1.. For reasons men­ tioned above, however, especially the failure to account for the length of active periods for individual offenders, the measure GH88 called A (fre­ quency) in their Tables 1 and 2 is not a measure of ..1.. Offenders with a larger total count of offenses may also have longer active periods, and this will affect their relative frequencies. Thus, the correlations reported in Table 2 of GH88 do not indicate correlates of A. In addition, the results in their Table 2 are by no means contradictory with our own research on the covariates of A and participation. We have concluded that demographic attributes are associated primarily with participation, and not with A; those conclusions derive from comparisons of the average magnitude of participation and A across race, sex, and age subgroups. The differences in the magnitude of participation are stark for the various demographic subgroups. Participation for males, for blacks, and for teenagers is usually several times higher than participation for females, for whites, and for older adults. In contrast to these large differ­ ences in magnitude for participation, the average magnitudes for A are much more similar across demographic subgroups, usually well within a factor of two (Blumstein et al., 1986).

These patterns with respect to the average magnitudes of participation and A for different subgroups are compatible with the correlation findings reported by GH88 in their Table 2. The measures of association for their "frequency" in official records are always lower, and are usually only one-half the level of association for participation. GH88 (p. 44) suggest that the decline in association as one moves from participation to frequency, and from aggregate rates to crime-specific rates, may be due (at least in part) to "restricting the range of the dependent variable for correlation coefficients."

FURTHER CLARIFICATIONS 63

Our experience, however, is that as one restricts the measurement of il to periods of time free for active offenders, il can be very widely distributed and can take on very large values. Moreover, except for very small samples that limit the number of observations (say, under 10), the range of variation in a variable need not be reduced by a reduction in sample size.

In general, the differences in magnitude that have been the focus of our research are not adequately reflected in measures of association (e.g., correla­ tion and gamma). Correlation coefficients measure the extent of a linear rela­ tionship between two variables; the size of the correlation is affected both by the slope of the relationship (which in our data is indicated by the magnitude of the ratio between groups) and by the amount of dispersion, or variance, around that slope. A low slope (i.e., a low ratio between groups) can have a similar correlation to a high slope (i.e., a high ratio between groups). Ordinal measures of association, like gamma, are only sensitive to gross similarities or differences in order; they ignore the magnitude of differences between catego­ ries. Large and important differences in magnitude could be masked when comparisons are based only mechanically on such measures of association.

The data presented in their Table 2 do not support their conclusion that the results are "substantively the same from one career measure to another" (GH88: 44). Their participation and frequency measures are highly corre­ lated for self-reports, have lower positive correlations for theft, and are nega­ tively correlated for serious officially recorded offenses, where the gammas of the six variables had a Spearman· rank correlation between participation and frequency of -.43 while the corresponding correlation for the r's was -.04.6 Hence, even accepting their data, the correlates of participation are some­ times very different from the correlates of frequency.

AGE & CRIME

The remainder of the evidence offered in GH88 relates to the relationship between age and crime. Once more, we do not deny the evidence of a distinc­ tive age-crime curve for aggregate population arrest rates. We do, however, differ with Gottfredson and Hirschi on the interpretation of those data. As GH88 (p. 48) note, in discussing the age-crime curve in our paper, we focused on the differences between the curves for various subgroups in such things as magnitude, skew, and the location of the peak rates. We did this because we find that the hypothesis of an invariant age-crime curve does not hold up in the face of these variations among population subgroups. Highlighting such differences is crucial to pursuing the social, cultural, economic, psychological,

6. In assigning ranks the sign of each GP A association measure was reversed to make this variable consistent with the direction of effect for the other variables by reflecting the contribution of low GPA to criminal activity.

64 BLUMSTEIN, COHEN AND FARRINGTON

environmental, and other factors that might account for differences in the age-crime relationship among different subgroups.

In denying the stability of A. over age, GH88 (pp. 49-50) cite numerous examples of declines in offending with age. We do not deny the existence of such declines. The question, however, is just what is declining: Are still­ active offenders (i.e., those who are still committing crimes) committing crimes at lower frequencies, or are increasing numbers of offenders ending their careers and ceasing to commit crimes altogether? The former is a change in A., and the latter is a change in participation, and measuring these changes with age is an empirical issue.

Insofar as the decrease in the percentage of serious offenders among all offenders cited from the Gluecks' data (GH88: 49) measures anything, it measures a participation rate. Hence, this is evidence of a decrease in partici­ pation with age, not of a decrease in A.. Similarly, decreases in offending after release on parole (GH88: 50) could reflect termination of careers rather than decreases in A.. The decline in the frequency of charges with age reported in Haapanen (1987) is based on changing samples of offenders at each age. Those observed at older ages are active for many more years before their last charge in the follow-up, and those observed at younger ages include many offenders with only one charge before their last charge as young adults. The decline with age, then, could reflect a negative relationship between frequency and career length, whereby offenders with long careers commit crimes at lower frequencies. 7 In acknowledging that crime decreases with age (GH88: 50), we require that criminal careers be disaggregated into distinct compo­ nents, like participation, frequency (A.), and termination, so that the sources of the decline can be more precisely identified.

THEORETICAL ISSUES

On a conceptual level, it seems that understanding crime-in the sense of knowing its causes and potential "remedies" -requires identification of the sources of variation in crime. Those might be variations in offending by indi­ viduals over time (e.g., changes in participation or A with age), variations among offenders, and differences between offenders and nonoffenders. Investi­ gating these variations sets a major research agenda. Moreover, the particu­ lar aspects of offending that vary will have profound implications for the nature of theories of crime and criminal behavior.

We find Gottfredson and Hirschi's theory of individual offending (as expli­ cated in GH88) rather puzzling. In view of the age variation in aggregate

7. In raising this alternative hypothesis we are not denying the possibility that fre­ quency (A) does in fact decline with age for individual offenders. However, this conclusion should not be drawn without considering and testing other plausible explanations for the observed aggregate decline.

FURTHER CLARIFICATIONS 65

offending, the presumption of stable and common causes of each crime com­ mitted by an individual (GH88: 41) raises the question of whether situational factors are meant to explain the totality of the age-crime curve. If criminal propensity is stable, as Hirschi and Gottfredson (1986: 57-59) have sug­ gested, and if the causes of each crime are stable over time for an individual, does this mean that situational factors account for the observed age variation in crime? But how could situational factors vary so consistently with age?

In an earlier elaboration of the theory they argue that criminal propensity is constant over time (GH87: 609-610), that crime is a consequence of rela­ tively stable characteristics of people (GH87: 608), and that age has a "direct influence" on-which we interpret to mean that age causes-crime (GH87: 590). Do these statements mean that criminal propensity and crime are bio­ logically determined? Gottfredson and Hirschi also argue that all variables have the same effect on crime at all ages. Their response to the argument that factors such as truancy and marriage can apply only at certain ages is to suggest that these factors may have functional equivalents at other ages (GH87: 605). We wonder, however, what the functional equivalent of mar­ riage might be at age 8.

Their argument that the causes of offending are the same for each crime and stable over time seems to ignore the various selection factors that distin­ guish offenders from nonoffenders and that distinguish offenders with very different A's. This selection effect is illustrated, for example, when a strong correlation between measured IQ and economic success in the general popu­ lation is likely to be significantly diminished among those who attend highly selective universities, who will tend to have less variation in both variables. Similarly, once the population eligible for offending is filtered to include only active offenders-particularly for the highly selected offenders who commit serious offenses-the factors that distinguish among these offenders could certainly be different from the ones that contributed to the offending in the first place.

To the extent that GH88 (p. 41) claim that "researchers assume that the causes of one offense are the same as the causes of others," this probably reflects the traditionally narrow focus of research on offending. s Some researchers deal only with general population samples, in which serious offending is rare, and so focus on factors associated with participation. Other researchers focus only on an offender population, as in studies of recidivism.

8. We find it somewhat surprising that Gottfredson and Hirschi look to traditional criminological research for support of their position. Hirschi, in particular, has often vigor­ ously challenged the beliefs of traditional criminology (Hindelang and Hirschi, 1977; Hir­ schi, 1973, 1983). We do not agree that the parameters ofa model of criminal careers-or any other empirical question-could or should be determined by asking a traditional crimi­ nologist (GH88: 53).

66 BLUMSTEIN, COHEN AND FARRINGTON

Neither approach has had to address the full range of factors contributing to both participation and A..

LONGITUDINAL RESEARCH

LONGITUDINAL AND CROSS-SECTIONAL DESIGNS

Research to identify patterns of variation or stability during criminal careers inherently requires longitudinal data-simply because a "career" is longitudinal by definition, and longitudinal information is necessary to address a longitudinal phenomenon. Despite this fact, there is nothing that inherently requires a prospective longitudinal survey to collect such informa­ tion. Such longitudinal data can be collected retrospectively in a cross-sec­ tional survey, as GH87 (p. 587) pointed out. For example, as we pointed out (BCF88: 29), offending from age 10 to age 19 could be studied by asking a sample of people on their 20th birthday to recall the dates of their offending and other key life events from ages 10 to 19. If the respondents were totally cooperative, and if they had sufficiently good powers of recall, they would provide precisely the kind of information that would be needed for research on criminal careers. Of course, this approach is inadequate precisely because the recall is simply not good enough.

On the contrary, retrospective recall over long time periods is likely to be inaccurate and biased. For example, Yarrow et al. (1970) carried out a landmark study of the retrospective method. They compared contemporane­ ous information on children in detailed nursery school records with mother and child recollections between 3 and 30 years later. They found low agree­ ment between contemporaneous and retrospective data, and the agreement decreased as the interval before recall lengthened.9

The importance of such recall errors is the main justification for carrying out a prospective longitudinal survey, in which data is collected more proxi­ mate to the events and before important outcomes are known.10 One of the most telling criticisms of the cross-sectional survey of Glueck and Glueck (1950) was that many of the differences noted between their delinquents and nondelinquents could have been artifactually produced by retrospective bias, since the variables were often subjective ratings by interviewers who knew whether they were dealing with the families of delinquents or nondelinquents. 11

9. In view of such errors we would question the validity of long-term retrospective information such as that collected by Felson and Gottfredson (1984). They asked a ran­ dom sample of adults about their activities at age 17, in some cases requiring recollection of events that happened over forty years earlier.

10. Oversampling subjects likely to be delinquent (GH87: 585) does not solve-and indeed has no relevance to-the problem of retrospective biases.

11. The large number of citations of Glueck and Glueck (1950) noted by GH87 (p.

FURTHER CLARIFICATIONS 67

If accurate longitudinal data can be collected retrospectively, then a pro­ spective survey is not needed. Accurate data on official offending (e.g., the dates of arrests and convictions) can often be collected retrospectively from criminal records because this information was recorded contemporaneously with the events. However, there are many known limitations to such retro­ spective data collection. For example, records may be partially destroyed or lost, or events may be inconsistently classified resulting in errors in estimates of participation and A. Such errors also make it difficult to even specify the samples of first offenders who are at risk of reoffending. Perhaps more impor­ tant, researchers are limited to the recorded information, and so have less freedom to choose theoretical constructs and their operational definitions.

Another way of investigating offending from ages 10 to 19 would be to ask 10 samples of people, one sample at each age from 11 to 20, to recall their offending in the previous year. This would be an example of cross-sectional data collected in a cross-sectional survey. This contrasts markedly with a design in which one sample of people is surveyed annually at each birthday from their 11th to their 20th and asked to recall their offending in the previ­ ous year-longitudinal data collected in a longitudinal survey. To avoid ambiguity in the remainder of this discussion, we will contrast these two types of surveys: longitudinal surveys collecting longitudinal data, and cross­ sectional surveys collecting cross-sectional data.

Longitudinal surveys involve repeated measures of the same people. The main advantage of such surveys of crime and delinquency lies in their ability to provide detailed information about the natural history and course of devel­ opment of offending. In particular, longitudinal surveys can show the extent of continuity or discontinuity between offending at different ages, the extent to which one event precedes or follows another in developmental sequences, and how well later events can be predicted by earlier ones. They can also provide information about the time ordering of different events, which can be useful in drawing conclusions about cause and effect, and they can show the effects of different events on the course of development of criminal careers. 12

Ultimately, a longitudinal survey will be needed to investigate the extent to which behavior is stable or unstable over time. It is not true, however, that "some stability" is required to justify such a survey (GH87: 585). Longitudi­ nal surveys are useful in studying both stability and change over time. GH87 (p. 592) are correct that stability coefficients for offending are often on the order of .5 or .6. However, in interpreting that to mean that there is "little change" (GH87: 593), they exaggerate the degree of stability indicated by

582) reflects to some extent the large number of criticisms of their cross-sectional research, many of which are set out in great detail in Hirschi and Selvin (1967).

12. Contrary to GH87's (p. 608) arguments, longitudinal researchers do not assume that events such as marriage have an effect on criminal careers; rather, they carry out research to investigate whether these events have an effect.

68 BLUMSTEIN, COHEN AND FARRINGTON

these figures. A correlation of .6, representing 36% of the variance explained, is compatible with a great deal of change in the relative ranking of individuals from one age to the next. There is certainly enough change to require the kinds of explanations that could be provided in a longitudinal survey.

Criminological research can and should profitably draw on many research methods. Longitudinal surveys are usually contrasted with cross-sectional surveys. The two methods, however, should not be viewed as mutually exclu­ sive; they have different strengths and limitations, and so both should be used to complement each other. For example, Glenn (1981: 362-363), in the con­ text of a discussion of resolving aging, period, and cohort effects, pointed out that aging and cohort effects were often confounded in cross-sectional surveys and that aging and period effects were often confounded in longitudinal surveys. Thus, Glenn, like many other researchers (e.g. Farrington et al., 1986) stressed the advantages of combining longitudinal and cross-sectional methods by following multiple cohorts.

In comparing longitudinal and cross-sectional research, it is important to distinguish features in practice from features in principle. In practice, many longitudinal surveys have extended over long time periods, but this is not inherent in principle. Many longitudinal surveys have not included quasi­ experimental analyses that rely on changes within subjects, and many of the theories proposed by longitudinal researchers (GH87: 608) have been based on earlier theories proposed by cross-sectional researchers, but neither of these features is essential in principle. The implementation deficiencies of any particular longitudinal survey are not an adequate basis for rejecting the lon­ gitudinal method. In contrast, testing effects resulting from repeated observa­ tions of the same subjects could be a problem in principle in any prospective longitudinal survey. The literature (e.g., Bachman et al., 1978; Douglas, 1970), however, does not support GH87's (p. 585) contention that "testing effects are often substantial," at least not in existing longitudinal surveys in criminology.

THE ROLE OF EXPERIMENT AL DESIGNS

In their 1987 paper Gottfredson and Hirschi seem to imply that the most important purpose of research is to test causal hypotheses and that all meth­ ods should be evaluated according to their adequacy on this criterion. This naturally draws their attention to experimental and quasi-experimental meth­ ods that are specifically designed to test such hypotheses. However, docu­ menting the natural history and course of development of a phenomenon (description) and investigating how well future behavior can be anticipated on the basis of present knowledge (prediction) are also legitimate and important aims of research, and these naturally draw our attention to the longitudinal method. There are other legitimate aims of research as well, such as generat­ ing plausible causal hypotheses. For hypothesis generation, such methods as

FURTHER CLARIFICATIONS 69

participant or unobtrusive observation, ethnography, or unstructured inter­ viewing may be particularly useful.

In comparing longitudinal surveys with randomized experiments, GH87 (p. 599) claim that "longitudinal research in crime and delinquency is by defi­ nition nonexperimental." On the contrary, there are some existing longitudi­ nal surveys that combine the longitudinal and experimental methods (e.g., McCord, 1978, 1979, quoted by GH87: 582). Moreover, Farrington et al. (1986) have argued in great detail that a "next generation" of longitudinal surveys should contain planned experimental interventions. In addition, quasi-experimental analyses have been used in many longitudinal surveys. No one could deny that randomized experimentation represents the best method of testing causal hypotheses (see, e.g., Farrington, 1983). However, in the majority of instances in which such experiments are not feasible, longi­ tudinal surveys analyzed as quasi-experiments can provide the most compel­ ling evidence of causal effects (see Cook and Campbell, 1979). Even though people cannot be randomly assigned to be married or unmarried (GH87: 605), it is still possible to draw valid inferences about the effects of mar­ riage.13 To believe otherwise implies that most causal hypotheses in crimi­ nology could not be tested.

In GH87 (p. 602) the authors complain that Farrington et al. (1986) did not explicitly state why experiments would be strengthened by the addition of a longitudinal component. However, Farrington et al. (1986: 92) list four main reasons: (1) The impact of interventions would be better understood in the context of preexisting trends or developmental sequences, which would help in assessing maturation, instability, and regression effects in before-and­ after comparisons. (2) The equivalence of persons in different experimental conditions could be studied in more detail. (3) Interactions between subjects' earlier experiences and types of treatment could be investigated more fully. (4) A long-term follow-up would show the effects of intervention that do not become apparent immediately, but may be displayed much later, and hence could help to explicate intervening variables in causal chains. Farrington et al. also pointed out that a longitudinal-experimental survey has two aims: to document the course of development and to investigate the impact of the intervention. Even when a randomized experiment is feasible, there is a cer­ tain risk that it will not be carried through successfully (e.g., because the random assignment breaks down; see Farrington, 1983). In this eventuality, the study could still provide useful data on the course of development, and the effect of the intervention could then be investigated by a quasi-experimen­ tal analysis.

13. Offending declines more quickly for men who marry than it does for men who remain unmarried, contrary to the equal decline implied by the statement "the decline occurs whether or not these events occur" (GH87: 604).

70 BLUMSTEIN, COHEN AND FARRINGTON

Farrington's (1977) research on the effect of convictions on offending was an example of the use of quasi-experimental analysis in a longitudinal survey. The key feature of this design was to compare before-and-after measures of (self-reported) offending within individuals and, hence, to detect changes using each person as his own control. Farrington found that the offending rates of convicted youths increased after they had been convicted, relative to the rest of the sample, and he investigated various alternative explanations of this increase.14 To control for selection effects, the convicted youths were matched with an equal number of unconvicted youths on self-reported offend­ ing, as well as on other behavioral and social background factors, before the conviction. However, the matched unconvicted youths decreased in their subsequent offending. 1 s

CAUSAL INFERENCES

The three criteria of causation listed by GH87 (p. 583)-association, tem­ poral order, and nonspuriousness-are rather weak, and may have been spe­ cifically devised to deal with problems of drawing causal inferences from cross-sectional surveys. A stronger definition of causation would require changes in one factor to be followed by changes in another factor, at least with a reasonably high probability and within a reasonable time interval. Cross­ sectional surveys can only show that variations (between subjects) in one fac­ tor are associated with variations in another factor. In contrast, longitudinal surveys can show that changes (within subjects) in one factor are followed by changes in another factor.16

Gottfredson and Hirschi argue that burglary, robbery, and all forms of delinquency and drug use are measuring the same underlying theoretical con­ struct (GH87: 596), and they insist-with no supporting evidence-that

14. GH87 are correct in their statement that the theoretical links in the causal chain between conviction and increased offending in this study have not been fully explicated. As Farrington et al. ( 1978) noted later, the explanation of the causal effect may lie in decreased deterrence rather than in labelling. However, the major result that conviction leads to increased offending, which survived all the quasi-experimental analyses, is not threatened by these alternative interpretations.

15. Contrary to GH87's (p. 600) statement, regression to a higher mean by convicted youths could not have explained their increased scores. All convicted youths were included in the matching analysis; there was no sampling that might have identified only those con­ victed youths who artifactually displayed low self-reported offending prior to conviction. Regression could explain the decreased scores of the unconvicted youths, and this was fully discussed by Farrington (1977).

16. These arguments have been expounded in detail by Farrington (1988). This study of change requires relatively frequent data collection. We do not agree that "more data are not necessarily better than less data, especially if they are essentially the same data" (GH87: 584-585). Measures at one age do not yield essentially the same data as measures at another age, and repeated measures are needed to detect when changes occur.

FURTHER CLARIFICATIONS 71

studying their sequencing would be "without causal import." Knowing sequences of events seems to be extremely important for understanding the factors leading to the development of offending and some kinds of deviant behavior. Lee Robins has indeed studied such paths with considerable suc­ cess (e.g., Robins and Ratcliff 1980; Robins and Wish, 1977).

Longitudinal surveys make it possible to study both changes within subjects and variations between subjects. Consider an example. Suppose that a cross­ sectional survey shows that juveniles exposed to relatively high degrees of parental disharmony tend to have relatively high offending rates. Clearly, there are problems of temporal order in this association: Which came first? Also, there are problems of spuriousness: Does the association merely reflect the fact that high degrees of parental disharmony are associated with some other factor that is related to high offending rates? It is possible to demon­ strate that the association between high parental disharmony and high offend­ ing rates holds independently of other measured factors. 11 It could always be argued, however, regardless of research design, that some unmeasured theo­ retical construct accounted for this relationship and, hence, could not be con­ trolled statistically.

On the basis of a cross-sectional survey that survived the three criteria of causation posited by GH87, one could not be very confident that prevention or treatment efforts that decreased parental disharmony would result in a decrease in offending rates. Statements about prevention or treatment are essentially statements about changes within subjects, not about variation across subjects. Generalizing from variation across subjects to changes within subjects involves an inferential conceptual leap that is often unjustified.

In contrast, consider a longitudinal survey that demonstrates that increases in parental disharmony are followed by increases in offending rates. The problems of causal order are avoided, and the problems of control of extrane­ ous personal variables are largely eliminated because each person acts as his or her own control. Hence, the problem of statistical control is much reduced in longitudinal surveys. is

The main threats to valid causal inference (or internal validity) in longitu­ dinal surveys are those processes listed by Cook and Campbell ( 1979), namely, maturation, regression, history, selection, instrumentation, mortality,

17. However, this is often studied using multivariate techniques that are not appropri­ ate to the data. Least-squares multiple regression techniques are often used inappropriately with highly skewed or categorical data.

18. Similarly, randomization eliminates the problem in true experiments. Mul­ tivariate analyses would only be needed in this example if "history" factors change at the same time as parental disharmony. However, since parental disharmony will change at a different time for each person, it seems likely that other factors that change with parental disharmony will be part of the same causal chain.

72 BLUMSTEIN, COHEN AND FARRINGTON

and testing. Most of these are also problematic in cross-sectional surveys. Causal inferences can be drawn with more confidence from longitudinal surveys because of better control of extraneous variables and better determi­ nation of temporal order. In addition, since the longitudinal survey demon­ strates changes within subjects, prevention and treatment implications can be drawn with much greater confidence.

While longitudinal surveys are superior in drawing causal inferences when variables vary within subjects, longitudinal surveys are no better than cross­ sectional ones in establishing causal effects of factors (such as sex19 or race) that can only vary between subjects. However, to the extent that the relation between such factors and offending is mediated by factors (such as parental supervision) that do vary within subjects, this interaction could be addressed more effectively by longitudinal surveys.

CONCLUSION A fundamental concern for contemporary criminological research is identi­

fying the different factors affecting crime. We are confident that our approach of separating the different aspects of a criminal career-including participation, frequency (A.), and termination-is likely to produce more pre­ cise knowledge about offending and its causes than a single aggregated con­ struct like "criminal propensity." By disaggregating various aspects of offending, it will be possible to isolate the effects of different factors on differ­ ent aspects of criminal activity. Although the relative merit of this approach remains an empirical matter, we anticipate from our work so far that different effects will emerge and will be important.

While we agree with GH87 that randomized experiments and quasi-experi­ ments are the best methods of testing causal hypotheses (and so should be used whenever possible and appropriate-including within longitudinal surveys), we find nothing in the GH87 paper that undermines longitudinal surveys as an important method for pursuing research relating to criminal careers. They are markedly superior to cross-sectional surveys in describing the natural history and course of development of a phenomenon, in studying developmental sequences, in studying prediction, and in drawing causal inferences.

19. Sex differences in crime are not "the same at every age" (GH87: 589). Males are more likely than females to offend at every age, but the male-to-female ratio varies consid­ erably with age (Farrington, 1986).

FURTHER CLARIFICATIONS

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