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The causes of offending are often investigated in cross-sectional studies and/or between-individual analyses. However, these types of studies yield poor evidence of causality. If X is a cause, changes in X within individuals should be followed by changes in offending within individuals. Therefore, longitudinal data are needed to investigate causes. Causes can be demonstrated convincingly in studies that investigate whether a life event (e.g., getting married) is followed by an increase in offending or that investigate whether changes in a variable (e.g., parental supervision) are followed by changes in offending. Causes can also be demonstrated convincingly in randomized experiments, but few field experiments have attempted to study the causes of offending. Causes could also be demonstrated in prevention or treatment experiments, but it is difficult to disentangle the “active ingredients” in most of these, because the interventions are usually complex and multimodal. Both quasi-experimental analyses within individuals and randomized experiments can address threats to internal validity or valid causal inference such as selection effects (preexisting differences between “treated” and “control” persons). More of these kinds of studies, and of combined longitudinal experimental studies, are needed to advance knowledge about the causes of offending.
What are the causes of offending is a very important topic in criminology. Virtually, all criminological theories include statements about the causes of offending in order to explain, for example, why some individuals commit more offenses than others, why some individuals commit more offenses at some ages rather than other ages, and why some interventions to prevent or reduce offending are more effective than others. But what is the meaning of a cause, and how can causes be established in criminology? This is the topic of this research paper (see also Farrington 1988; Farrington et al. 2010; Loeber and Farrington 2008).
The concept of a cause inevitably involves the concept of change within individual units. A factor X causes a factor Y if, with some specified degree of regularity, and after some specified length of time, changes in X are followed by changes in Y for each individual. For example, the death of a father may cause a decrease in the economic status of his family. As this example shows, the factors X and Y can be dichotomous (father living or dead), continuous (economic status), or of some intermediate kind. The individual unit can be the family rather than an individual person, although this research paper will concentrate on changes within individual persons, in discussing how to study the causes of offending.
Causes are often inferred from variations between individuals rather than from changes within individuals. Many researchers draw causal conclusions from cross-sectional (correctional) data, accepting that one variable causes another if (a) the two variables are statistically associated, (b) one variable occurs before the other, and (c) the association holds independently of other (measured) variables. For example, a project might demonstrate that males were more likely to be convicted offenders than females and that this relationship held after controlling statistically for other measured variables. It might then be concluded that gender was a cause of offending. However, drawing conclusions about causes, or in other words about the effect of changes within individuals, on the basis of variations between individuals, involves a conceptual leap that may not be justifiable. For all practical purposes, one cannot investigate whether changing males into females would lead to a decrease in their offending.
Furthermore, the control of other causal factors that might influence an outcome is usually poorer in studies of variations between individuals than in studies of changes within individuals, where each person essentially acts as his or her own control. Nonexperimental studies of variations between individuals inevitably have low internal validity (a poor ability to establish causal influence convincingly) because of the impossibility of measuring and controlling for all possible factors that might influence offending. This is not true of randomized experiments on variations between individuals because – with large samples – the randomization ensures that the average individual in one condition is equivalent to the average individual in another, on all possible extraneous factors. However, it is difficult to study the causes of offending in randomized experiments (see later).
Our argument is that the causes of offending can be investigated most effectively in studies of changes within individuals. Such studies inevitably require longitudinal rather than cross-sectional data, and their internal validity can be increased by combining experimental or quasiexperimental designs with longitudinal data.
The remainder of this research paper essentially expands the arguments summarized in this introduction. This research paper first discusses the investigation of causes in prospective longitudinal surveys, especially using quasi-experimental methods. Then this research paper discusses the investigation of causes in randomized experiments and finally reviews the advantages of combining the two methods in longitudinal-experimental studies.
The contributions to the study of causes by Cook and Campbell (1979) have been outstanding. They stressed alternative causal explanations (also called threats to internal validity) that plague experimental and quasi-experimental studies. Among these alternative explanations are the following: (a) History: the observed effect is caused by other explanatory variables changing in the same time period; (b) maturation: the observed effect reflects a preexisting trend; (c) testing: the observed effect is caused by previous testing of the participants; (d) instrumentation: the observed effect is caused by changes in measurement techniques; (e) regression: the observed effect is caused by statistical regression of extreme scorers to the mean; (f) selection: the observed effect is caused by preexisting differences between the groups being compared; (g) mortality: the observed effect is caused by differential attrition from experimental and control groups; (h) instability: the observed effect reflects random variation; and (i) causal order: the true causal order is opposite to that hypothesized. When discussing inferences about causality in this research paper, each of these possible threats can serve as a backdrop to the identification of causes. Putative causal effects that can be explained by one of the nine alternatives need to be excluded from further consideration.
The identification of causes is more difficult in some cases than in others. Of the known risk factors for delinquency, some concern discrete events, such as getting married, getting divorced, leaving home, or joining a gang. Establishing the causal effects of these life events tends to be more straightforward than establishing the causal effects of processes that often take place over months or years, such as poor communication between parents and children or poor child-rearing practices. It should be noted, however, that even discrete causes may correlate with and sometimes operate through long-term processes. An example is becoming a single parent, which may be preceded by prolonged periods of conflict between partners and disagreements about parenting practices. This research paper discusses both risk factors that predict a high probability of offending and “promotive” factors that predict a low probability of offending.
Prospective Longitudinal Surveys
The main focus of this research paper is on investigating causes in prospective longitudinal surveys which involve repeated measures of the same people. Therefore, they involve at least two data collection points. The word “prospective” implies that risk and promotive factors are measured before outcomes. The most important surveys focus on community samples of hundreds of people, with repeated personal interviews spanning a period of at least 5 years. This research paper focusses on community surveys (as opposed to surveys of offenders) because they are needed to study the natural history of offending and the effects of risk/promotive factors and life events. In order to avoid retrospective bias, it is important to measure risk and promotive factors before the development of offending and to calculate prospective probabilities. A minimum of a 5-year time period was set because such a period is needed to provide adequate information about the natural history of the development of offending. Interview data was a requirement because official record data cannot provide adequate information on offending, risk and promotive factors, and life events.
In criminology, the main advantage of these longitudinal surveys is that they provide information about the development of offending over time, including data on ages of onset and desistance, the frequency and seriousness of offending, the duration of criminal careers, continuity or discontinuity in offending, and specialization and escalation. They also provide information about developmental sequences, within-individual change, effects of life events, and effects of risk and promotive factors at different ages on offending at different ages. A great advantage of longitudinal compared with cross-sectional surveys is that longitudinal surveys provide information about time ordering, which is needed in trying to draw conclusions about causes. An investigation of causes leads to an emphasis on change. However, it should not be forgotten that longitudinal data are also useful in studying the opposite of change: the degree of consistency and continuity in behavior over time.
While prospective longitudinal surveys have many advantages, they also have problems. The main challenge in these surveys is to draw convincing conclusions about causal effects. Because of their focus on naturalistic observation, longitudinal surveys find it difficult to disentangle the impact of any particular variable from the effects of numerous others. It is particularly difficult to rule out selection effects; for example, child abuse may predict delinquency because antisocial parents are more likely to abuse their children and are more likely to have delinquent children, without there being any causal effect of child abuse on delinquency. Also, the infrequency of data collection often makes it difficult to pinpoint causal order.
A quasi-experimental analysis tries to isolate the impact of a naturally occurring presumed causal factor (e.g., joining a gang) by treating it as though it was experimentally manipulated and then trying to eliminate the plausible alternative explanations of observed effects discussed above. Prospective longitudinal data constitute the foundation for quasi-experimental approaches in studying the causes of offending.
Sometimes a catastrophe or a major beneficial event occurring to a population may trigger vast changes in criminality. For example, Costello et al. (2003) examined the impact of the opening of a casino on an American Indian reservation, which took place in the course of a longitudinal study by the authors (the Great Smoky Mountains Study of Youth). The revenue from the casino was shared by every adult and child tribe member. This led to a reduction in the number of Indian families with income below the federal poverty line, while non-Indian families did not benefit from the casino revenue. They found that children in Indian families showed a significant improvement in behavioral symptoms of oppositional/defiant and conduct disorder. This study is exemplary in that it takes advantage of a natural event that affected some families compared to other families, established temporal order, and shed light on mediating factors.
Almost all studies of the causes of offending have carried out analyses between individuals showing, for example, that unemployed people commit more crimes than employed people and that this relationship holds after controlling for measured extraneous variables. However, as mentioned, analyses within individuals are more relevant to the concept of cause, which suggests that changes within individuals in a causal factor (e.g., from employment to unemployment) tend to be followed by changes within individuals in offending (Farrington 1988). Similarly, analyses within individuals are more relevant to prevention or treatment research (which requires within individual change). Quasi-experimental analyses within individuals control for individual factors that do not change over time (e.g., gender and race). For example, in the Pittsburgh Youth Study (Loeber et al. 2008), which is a prospective longitudinal survey of over 1,500 Pittsburgh males from age 7 to age 35, Gordon et al. (2004) found that the boys’ offending increased after they joined a gang and decreased after they left a gang. The researchers controlled for selection effects, since the boys who joined gangs were more delinquent beforehand than those who did not join.
The Cambridge Study In Delinquent Development
Quasi-experimental analyses within individuals have been carried out in the Cambridge Study in Delinquent Development, which is a prospective longitudinal survey of over 400 London males from age 8 to age 48 (Farrington et al. 2009). One analysis attempted to test labelling theory (Farrington 1977). According to this theory, one effect of a conviction should be to amplify delinquent behavior, perhaps because of the effect of stigmatization on a person’s self-concept. However, an alternative causal sequence is proposed by deterrence theory. According to this theory, the effect of a conviction should be to decrease delinquent behavior, because detected offenders become more afraid of the possible consequences of offending.
In comparing these theories, the basic design was to investigate the self-reported offending of boys before and after they were convicted for the first time (between ages 14 and 18). All boys were assigned percentile scores between 0 and 100 according to the number of their admitted offenses, and it was found that the average score of convicted youths increased significantly, from 59 before the conviction to 69 after. In this test, each youth acted as his own control, and it was clear that the convicted youths became relatively more delinquent. This was especially true when they were compared with an individually matched sample of unconvicted youths, whose average scores decreased from 59 to 51 during the same period. However, it was necessary to test a number of plausible alternative explanations of this effect (or threats to internal validity).
The results could not have been caused by maturation (processes within the individuals operating as a function of the passage of time), history (events occurring between the first and the second test), testing (the effect of taking one test on the scores in a second), or instrumentation (changes in the measuring instruments of scoring methods). Each of these factors would have been expected to affect the whole sample equally. The results could not have been caused by mortality (differential loss of individuals from the comparison groups) because the analysis was based only on youths interviewed at all three ages (14, 16, and 18). Furthermore, statistical regression to the mean could not explain the results because the scores of the convicted youths became even more extreme at 18 than they had been at 14.
The major plausible alternative explanation of the results was selection: the convicted youths could possibly have differed from the unconvicted ones in some factor unrelated to conviction that caused an increase in offending. However, no other factor was found that caused such an increase. The convicted youths were individually matched with unconvicted ones at age 14 not only on self-reported offending but also on a prediction score based on the best predictors of delinquency (troublesomeness, low family income, large family size, parental criminality, poor parental child-rearing behavior, and low intelligence). This did not significantly change the results. While these factors predicted high self-reported delinquency at age 18, they did not predict an increase in percentile scores between 14 and 18.
One key advantage of this kind of within individual analysis is that all individual difference factors are controlled for. Another is that causal-order questions can be resolved more satisfactorily than in a between-individual analysis. The main problem of causal order here was whether the conviction preceded the increase in offending or whether the increase in offending preceded the conviction. The percentile self-report scores at age 16 showed that there was no sign of an increase in offending by convicted boys before the conviction occurred, and so it was concluded that the conviction preceded the increased offending.
Some remaining uncertainties about the interpretation of these results center on the theoretical constructs underlying the empirical variables. Did offending increase, or did the likelihood of admitting offending increase? A study of the dates of reported offenses suggested that both effects happened, since the convicted youths at age 16 were more likely to admit offenses committed before age 14 but not admitted at that age. What constructs intervened between convictions and increased offending? One construct that increased in the same way as self-reported offending was a hostile attitude to the police, and so this may have been one link in the causal chain. Finally, did the increase in offending reflect labelling or decreased deterrence? A later study by Farrington et al. (1978) was able to replicate the delinquency-amplifying effects of convictions between ages 18 and 21 and suggested that decreased deterrence was happening. The increase in offending was most marked for those who received the lightest possible sentences, whereas labelling theory might have predicted the opposite.
Developmental and life-course criminology aims to investigate the effects of life events on the course of development of antisocial behavior. In the Cambridge Study, going to a high delinquency-rate school at age 11 did not seem to amplify the risk of offending, since badly behaved boys tended to go to high delinquencyrate schools (Farrington 1972). The boys committed more offenses during periods when they were unemployed than when they were employed, suggesting that unemployment caused crime (Farrington et al. 1986a). However, there was only an increase in crimes leading to financial gain, such as theft, burglary, robbery, and fraud. There was no effect of unemployment on other offenses such as violence, vandalism, or drug use, suggesting that the link between unemployment and offending was mediated by a lack of money rather than by boredom.
It is often believed that marriage to a good woman is one of the most effective treatments for male offending, and indeed, Theobald and Farrington (2009) found that getting married led to a decrease in offending compared with staying single. Also, later separation from a wife led to an increase in offending compared with staying married, and the separated men were particularly likely to be violent (Farrington and West 1995). Another protective life event was moving out of London, which led to a decrease in self-reported violence (Osborn 1980). This was probably because of the effect of the move in breaking up delinquent groups.
One currently popular method of controlling for selection effects is to use propensity score matching. For example, in their investigation of the effect of marriage on offending in the Cambridge Study, Theobald and Farrington (2009) calculated propensity scores indicating the probability of getting married and matched married and unmarried men both on these and on prior offending. They found that convictions decreased after marriage, but only for men who married at relatively young ages (under age 25). Just as randomization equates the probability of each person receiving a treatment, matching on propensity scores aims to equate treated and untreated persons on their prior probability of receiving the “treatment” (here, marriage).
Comparing Changes Within Individuals With Variations Between Individuals
Only one article in criminology has compared whether causes identified by means of within individual analyses were similar to or different from causes identified by means of between individual analyses. Farrington et al. (2002) examined the course of offending of over 500 boys in the oldest sample of the Pittsburgh Youth Study over seven data waves between ages 14 and 18 on average. Putative causes were only examined if they were available at each data wave. These putative causes were hyperactivity impulsivity-attention problems, low school achievement, depressed mood, poor parental supervision, low parental reinforcement, poor parent-boy communication, low family involvement, low social class, poor housing, and peer delinquency. The between-individual correlations were computed for each wave and then averaged across the seven waves. In contrast, the within-individual correlations were calculated for each boy (based on seven waves) resulting in 370–380 correlations for boys who had admitted at least one delinquent act.
All ten variables were significantly correlated with delinquency in the between-individual analyses. The within-individual correlations with delinquency were on average lower and statistically significant for only four variables: peer delinquency, poor parental supervision, low involvement in family activities, and poor parent-boy communication. To test whether the associations held prospectively, subsequent analyses investigated whether variables in one wave predicted delinquency in the next wave. Only poor supervision, low reinforcement, and low involvement predicted within individuals. In conclusion, although peer delinquency was correlated with offending between individuals, it was not a within-individual cause of offending. However, poor parental supervision, low involvement in family activities, and low parental reinforcement appeared to be causes in that as they rose or fell over time, the delinquency of most participants would subsequently rise and fall as well. Thus, temporal covariation between putative risk factors and offending is one of the most convincing demonstrations of causal status.
The results also showed that individuals varied considerably in their within-individual correlations between predictors and delinquency. For some, the correlation was negative, for others it was zero, and for others it was positive. Averaged across individuals, the within-individual correlation tended to be in the direction of the between individual correlation. The point, however, is that causal factors that explain between-individual differences in offending are not necessarily operating in the same way for all individuals. Thus, the causal status of a particular variable may vary from individual to individual. For example, poor housing was positively related to delinquency for boys living in bad neighborhoods but not for boys living in good neighborhoods.
An experiment is a systematic attempt to investigate the effect of variations in one factor (the independent or explanatory variable) on another (the dependent or outcome variable). In criminology, the independent variable is often some kind of intervention, and the dependent variable is some measure of offending. Most criminological experiments are pragmatic trials designed to test the effectiveness of an intervention rather than explanatory trials designed to test causal hypotheses. The independent variable is under the control of the experimenter; in other words, the experimenter decides which people receive which treatment (using the word “treatment” very widely to include all kinds of interventions).
The focus here is on randomized experiments, where people are randomly assigned to different treatments. Provided that a large enough number of people are assigned (e.g., at least 50 per condition), randomization ensures that the average person receiving one treatment is equivalent (on all possible measured and unmeasured extraneous variables) to the average person receiving another treatment, within the limits of small statistical fluctuations. Therefore, it is possible to isolate and disentangle the effect of the independent variable (the intervention) from the effects of all other extraneous variables (Farrington and Welsh 2005). However, it is also desirable to investigate intervening mechanisms or causal chains (mediators). The main strength of randomized experiments is in excluding selection effects (preexisting differences between persons in different conditions) as a possible explanation.
Few field experiments have been designed to investigate the causes of offending. However, in experiments on stealing, Farrington and Knight (1979, 1980) left stamped, addressed, apparently lost, unsealed letters on the street, each containing a handwritten note and also (except for control conditions) a sum of money. The experimenter, who was blind to the condition of each letter, observed the personal characteristics and behavior of each person who picked up the letter. Each person could honestly mail the letter and money to the intended recipient or could steal the money.
Behavior after picking up the letter predicted stealing. Almost all of the participants were observed to take out the note and read it. Those who then walked along holding the letter were likely to return it, whereas those who put the letter in a pocket or handbag were likely to steal it. This suggested that the decision to steal was made immediately. The prevalence of stealing varied remarkably, from about 20 % to 80 % in different conditions. This suggested that, depending on the experimental conditions, almost everyone would steal or almost no one would steal.
Our experiments were designed to test ideas of deterrence and were inspired by subjective expected utility theories (Farrington 1979). The study found that stealing increased as the amount of money that could be stolen increased, decreased when the apparent victim was an impoverished old lady (high cost) compared with an affluent young man (low cost), and decreased when the probability of detection was greater (with a postal order compared to cash). The study also found that younger people were more likely to steal than older ones, although in most cases (except when there was a large amount of money) there were few gender differences in stealing.
Experiments are usually designed to investigate only immediate or short-term causal effects. However, some interventions may have long-term rather than short-term effects, and in some cases the long-term effects may differ from the short-term ones (Farrington and Welsh 2013). More fundamentally, researchers rarely know the likely time delay between cause and effect, suggesting that follow-up measurements at several different time intervals are desirable. A longitudinal-experimental study deals with many of these problems.
More than two decades ago, Farrington et al. (1986b) in their book Understanding and Controlling Crime: Toward a New Research Strategy argued that:
- The most important information about the development, explanation, prevention, and treatment of offending has been obtained in longitudinal and experimental studies.
- New studies are needed in which these two important methods are combined, by embedding experimental interventions in longitudinal studies.
Longitudinal-experimental studies are needed to advance knowledge about the causes of offending.
There have been a number of longitudinal- experimental studies in criminology in which persons who did or did not receive an experimental intervention were followed up for several years (Farrington 2006). It is not controversial to argue for the desirability of adding a long-term follow-up to a randomized experiment. What is much more controversial is the desirability of embedding an experiment within an ongoing longitudinal survey, essentially because of concerns that the experiment might interfere with the aims of the longitudinal survey such as documenting the natural history of development.
Strictly speaking, every experiment is prospective and longitudinal in nature, since it involves a minimum of two contacts or data collections with the participants: one consisting of the experimental intervention (the independent variable) and one consisting of the outcome measurement (the dependent variable). However, the time interval covered by the typical experiment is relatively short. Farrington et al. (1986b) argued that longitudinal-experimental studies were needed with three elements: (1) several data collections, covering several years; (2) the experimental intervention; and (3) several more data collections, covering several years, afterwards. No study of this kind has ever been carried out on offending using interview data. A few experiments collected official record data retrospectively for a few years before an intervention and prospectively for a few years after the intervention, but these did not assess the effect of the intervention on criminal career trajectories or developmental sequences of offending.
An important advantage of a combined longitudinal-experimental study in comparison with separate longitudinal and experimental projects is economy. It is cheaper to carry out both studies with the same individuals than with different individuals. For example, the effect of interventions and the effect of risk or promotive factors can be compared on the same people. The number of individuals and separate data collections (e.g., interviews) is greater in two studies than in one (other things being equal).
The main advantages of longitudinal experimental research have been summarized by Blumstein et al. (1988). The impact of interventions can 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. The prior information about participants would help to verify that comparison groups were equivalent, to set baseline measures, to investigate interactions between types of persons (and their risk/ promotive factors and prior histories) and types of interventions, to establish eligibility for inclusion in the experiment, and to estimate the impact of differential attrition from experimental conditions. The long-term follow-up information would show effects of the intervention that were not immediately apparent, facilitate the study of different age-appropriate outcomes over time, and make it possible to compare short-term and long-term effects and to investigate the developmental sequences linking them. The experimental intervention could help to distinguish causal or developmental sequences from different age-appropriate behavioral manifestations of the same underlying construct.
Longitudinal data make it possible to study both changes within individuals and variations between individuals separately. Because of this distinction, and because of the high internal validity of quasi-experimental analyses, longitudinal data are much more suitable than cross-sectional data for testing causal hypotheses. Furthermore, causal conclusions based on changes within individuals in longitudinal data could in principle have practical implications for preventive or rehabilitative treatment designed to change people, providing that the construct that varies within individuals is manipulable. No possible treatment implications could follow from the argument that a construct that varied only between individuals – such as gender or race – was a cause of offending, since one cannot change a person’s gender or race. However, variables that are associated with gender or race could be causes of offending. Similarly, no possible treatment implications could follow from the argument that a non-manipulable construct that varied within individuals – such as age – was a cause of offending.
Treatment implications can readily be drawn from manipulable theoretical constructs. For example, it could be predicted that a decrease in school failure would cause a decrease in offending. This prediction was indeed supported in the Perry Program (Schweinhart et al. 2005). They found that a preschool intellectual enrichment program led to decreases in school failure and decreases in offending. In many respects, a good way to test a hypothesis about the causes of offending is to carry out a prevention or treatment experiment (Robins 1992). This clearly requires a manipulable theoretical construct. However, it is difficult to disentangle the “active ingredients” in most intervention experiments, because the “treatment” is usually complex and multimodal.
Criminologists should attempt to carry out more field experiments to investigate theories of offending, using a realistic measure of offending as the dependent variable. The most feasible dependent variables are probably stealing and vandalism; it is hard to imagine conducting an experiment with real violence as the dependent variable, although verbal aggression might possibly be studied. Most criminological experiments have investigated policing, early prevention, corrections, courts, or community treatment (Farrington and Welsh 2005). There is surely a need for field experiments that try to test theories of offending (Farrington 2008).
In reviewing causality problems arising in longitudinal studies several years ago, Loeber and Farrington (1994) stressed that the major issues were attrition, testing effects, the distinction between aging, period, and cohort effects, and establishing causes with high internal validity. All these issues remain crucial. The authors also stressed the need to combine longitudinal and experimental studies or, at a minimum, to turn experimental studies into longitudinal studies so that the long-term impact of change agents can be ascertained. In addition, there is an urgent need to reinvigorate the search for causes in at least the following ways:
- A web-based inventory is needed of what is known about the causal status of the 60 or more known putative causes of delinquency. Such an inventory should not only summarize effect sizes but should also investigate which of the several crucial tests have succeeded in narrowing down risk factors into causes. Ideally, such a website should also contain information about promotive causes that foster nondelinquency and can aid in explaining desistance. The Handbook of Crime Correlates (Ellis et al. 2009) would be a useful source of references.
- Systematic reviews and meta-analyses of putative causes of offending should be carried out. These reviews should investigate not only to what extent risk factors predict offending but also to what extent they predict offending after controlling for other putative causes (see, e.g., Ttofi et al. 2011).
- A systematic survey is needed of the moderators and mediators of causes of delinquency. This will be of immense help in documenting processes that unfold over time.
- Causes that operate within individuals should be more vigorously investigated so that eventually meta-analyses across different studies can be undertaken, leading to better generalizations about what is known about within individual causes and their implications for interventions.
Unfortunately, there is very little solid evidence about the causes of offending. More within-individual quasi-experimental analyses in longitudinal surveys, and more randomized experiments, are needed to draw convincing conclusions and advance knowledge significantly.
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