Assignment: Research Designs
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L,earnlngHvvh-**t**D Objectives 1,. Give an example of
a nomothetic causal
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2. Discuss the role of the
I dentifrrrg causes-figuring out why things happen-is the goal of most social I science research. Unfortunately, valid explanations of the causes of social phenomena do not come easily. Why did the rate of homicides rise in the early 1990s and then begin a sustained drop that has continued in the 2000s, even during the2008-2010 recession, to a level last seen in 1968 (Federal Bureau of Investigation 2018) (Exhibit 6.1)? Arizona State Llniversify criminologist Scott Decker points to the low levels of crime committed by illegal immigrants to explain the falling crime rate in his state (Archibold2010), and sociologist RobertJ. Sampson (2008) draws attention to the rising level of immigration in cities through the 1990s to help explain the national decline in the crime rate. Criminal justice advocates in Texas point to the state's invesffnent in communiry treatment and diversion programs (Grissom}Ol1). Police officials in NewYork City point to the effectiveness of CompStat, the city's computer program that indicates to the police where crimes are clustering (Dewan 2004a,M5; Dewan 200+b,A1; Kaplan 2002, A3), but other New Yorkers credit the increase in the ranks of New York's police officers because of its Safe Streets, Safe Cities program (Rashbaum 2002).Yet another possible explanation in New York City was the declining level of crack cocaine use (Dewan 2004b, Cl6).But then should we worry about the increasing number of drug arrests nationally (Bureau ofJustice Statistics 2011) and a rise in the abuse of prescription drugs (Good- nough 2010)? We also know from Desmond, Papachristos, and Kirk (2016) that we should take into account the factors that affectpolice reporting, such as trust in the police. How can we design research that can help us answer these kinds of questions?
In this chapter, we first discuss the meaning of causation from two differ- ent perspectives-nomothetic and idiographic-and then review the criteria for achieving causally valid explanations. During this review, we give special attention to several k.y distinctions in research design that are related to our ability to come to causal conclusions: the use of an experimental or nonexperi- mental design and reliance on a cross-sectional or longitudinal design. By the end of the chapter, you should have a good grasp of the different meanings of causation and be able to ask the right questions to determine whether causal inferences are likely to be valid. You also may have a better answer about the causes of crime and violence.
/.. ulscuss tne role oI itne counterfactual in nomothetic causal explanation.
CAUSATION AND RESEARCH DESIGN
CAUSAL EXPLANATIONS
A cause is an explanation for some characteristic, attitude, or behavior of groups, individuals, or other entities (such as families, organizations, or cities) or for events. Most social scientists seek causal explanations that reflect tests of the tFpes of hypotheses with which you are familiar (see Chapter 2).In these tests, the independent variable is the presumed cause, and the dependent variable is the potential effect. For example, does problem-oriented policing (independent variable) reduce violent crime (dependent variable)? Does experiencing abuse as a child (independent vari- able) increase the likelihood that you will be a violent adult (dependent variable)? This type of causal explanation is termed nomotbetic.
A different type of cause is the focus of some qualitative research (see Chapter 9) and our everyday conversations about causes. In this type of causal explanation, termed idiograpbic, individual events or the behavior of individuals are explained with a series of related, prior events. For example, you might explain a particular crime as resulting from several incidents in the life of the perpetrator that resulted in a tendency toward violence, coupled with stress resulting from a failed marriage and a chance meeting.
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Source: FBI. 2018. Crime in the United States,Table 1.
CHAPTER 6 . CAUSATION AND RESEARCH DESIGN
Exhibit 5.1 Number and Rate of Homicides in the United States, a982-2O76
Nomothetic causal
explanation:
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Counterfactual:
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Quantitative (Nomothetic) Causal Explanation
A nomothetic causal enplanation is one involving the belief that variation in an independent variable will be follovred by variation in the dependent variable, when all other things are equal (ceteris padbus) or when all other potentially infl. uential conditions and factors are taken into consideration. For instance, researchers might claim that the likelihood of committing violent crimes ishigherforindividualswhowere abused as children thanitwould be if these same individ- uals had not been abused as children. Or researchers might daim that the likelihood of committing violent crimes is higher for individuals exposed to media violence than it would be if these same individuals had not been exposed to media violence. The situation as it would have been in the absence of variation in the independent variable is termed the counterfactual (see Exhibit 6.2).
Of course, the fundamental difEculty with this perspective is that we never really know what would have happened at the same time to the same people (or groups, cities, and so on) if the independent variable had not varied, because it did. We catrnot rerun real-life scenarios (King, Keohane, and Verba 1994). We could observe the aggressiveness of people's behavior before and after they were exposed to media violence. But this comparison involves an earlier time period, when, by definition, the people and their circumstances vrere not exacdy the same.
Fornrnately, we can design research to create conditions that are comparable so that we can confidendy assert our conclusions ceteris paribus. We can examine the impact on the dependent variable of variation in the independent variable alone, even though we will not be able to compare the same people at the same time in exacdy the same circumstances except for the variation in the independent variable. And by knowing the ideal standard of compara- bility, we can improve our research designs and strengthen our causal conclusions, even when we cannot come so close to living up to the meaning of ceteris paribus.
Quantitative researchers seek to test nomothetic causal explanations with either experi- mental or nonexperimental research designs. However, the way in which experimental and nonexperimental designs attempt to identif, causes differs quite a bit. It is very hard to meet
lndependent variable: Dependent variable:
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Actual situation: People who watch violence on TV are more likely to commit violent acts.
Dependent variable:
?'q ft?-ft Counterfactual situation: The same people watch nonviolent TV shows at the same time, in the same circumstances. They are not more likely to commit violent acts.
SECTION II . FUNDAMENTALS OF RESEARCH152
Exhibi t 6.2 The Gounterfactual in Gausal Research
some of the criteria for achieving valid nomothetic causal explanations using a nonexperi- mental design. Most of the rest of this chapter is devoted to a review of these causal criteria and a discussion of how experimental and nonexperimental designs can help establish them.
Qualitative (ldiographic) Causal Explanation
The other meaning of the term cowe is one that we have in mind very often in everyday speech. This is idiographic causal explanation: the concrete, individual sequence ofevents, thoughts, or actions that resulted in a particular outcome for a particular individual or that led to a particular event (fIage and Meeker 1988). An idiographic explanation also may be termed an indioidualist or a historici* explanation.
A causal effect from an idiographic perspective includes statements of initial conditions and then relates a series of events at different times that led to the outcome, or causal ffict This narrative ot story is the critical element in an idiographic explanation, which may there- fore be classified as na?Tatiae reasoning @ichardson 1995). Idiographic explanations focus on particular social actors in particular social places at particular social times (Abbott 1992). Idiographic explanations are also typically very concerned with context, with understanding the particular outcome as part ofa larger set ofinterrelated circumstances. Idiographic expla- nations thus can be termed holistic.
Elijah Anderson's (1990) field research in a poor urban community produced a narrative account of how drug addiction can result in a dounrward slide into residential instability and crime:
\44ren addicts deplete tfreir resources, they may go to those closest to them, draw- ing them into their schemes. . . . The family may put up with the person for a while. They provide money if they can. . . . They come to rcalize that the person is on drugs. . . . Slowly the reality sets in more and more completely and the family becomes drained of both financial and emotional resorrces. . . . Close relatives lose faith and begin to see the person as untrustworthy and weak. Eventually the addict begins to "mess up" in a variety of ways, taking furniture from the house [and] any- thing ofvalue. . . . Relatives and friends begin to see the person .. . as "out there" in the streets. . . . One deviant act leads to another. (86-87)
An idiographic explanation such asAnderson's (1990) pays close attention to time order and causal mechanisms. Nonetheless, it is difficult to make a convincing case that one particular causal narrative should be chosen over an alternative narrative (Abbott 1992). Does low self-esteem result in vulnerability to the appeals of drug dealers, or does a chance drug encounter precipitate a slide in self-esteem? The prudent causal analyst remains open to alternative explanations.
Idiographic explanation is deterministic, focusing on what caused a particular event to occur or what caused a particular case to change. fu in nomothetic explanations, idiographic causal explanations can involve counterfactuals by trying to identifi, what would have hap- pened if a different circurnstance had occurred. But unlike in nomothetic explanations, in idiographic explanations, the notion of a probabilistic relationship (an average effect) does not really apply. A deterministic cause has an effect in the case under consideration.
CRITERIA AND GAUTIONS FOR NOMOTHETIC CAUSAL EXPLXANATIONS
MarkTmitchell wanted to be a filmmaker and become famous. One of the short movies he made was about a serial killer. Tritchell also was a big fan of the TV show Dexteti a drama about a serial killer. In 2008, he advanced this fiction to real Iife when he posed as a woman on a dating website to lureJohnnyAltinger on a date. When Altinger showed up for the date on October 8,
ldiographic causal
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CHAPTER 6 . CAUSATION AND RESEARCH DESIGN 153
2008, he was killed and fismembered. Fortunately, the murder was discovered before Tnritch- ell could kil again. Not surprisingly, after his arrest, Tritchell became known as the "Dexter Killer" ('The Mark Tritchell Case" 2015). fu frequendy happens, some attributed Twitchell's violence to media portrayals of violence; in this case, to the series Dexter. How would you evalu- ate this claim? What evidence do we need to develop a valid conclusion about a hypothesized causal effect? Imagine a friend reading about the incident and saying, "See, media violence causes people to cornmit crimes." Of course, after reading Chapter I , you would not be so quick to jump to such a conclusion. "Dont overgeneralize," you would remind yourself. When your friend insiss, "But I recall that type of thing happening before," you might even suspect selec- tive observation. As a blossoming criminological researcher, you now know that if we want to have confidence in the validity of our causal statements, we must meet a higher standard.
FIow research is designed influences our ability to draw causal conclusions. In this sec- tion, we will introduce the features that need to be considered in a research design in order to evaluate how well it can support nomothetic causal conclusions.
Five criteria must be considered when deciding whether a causal connection exists. When a research design leaves one or more of the criteria unmet, we may have some impor- tant doubts about the causal assertions the researcher may have made. The first three of the criteria are generally considered the necessary and most important basis for identiflring a nomothetic causal effect: empirical association, appropriate time order, and nonspuriousness. The other two criteria, identi$ring a causal mechanism and specifring the context in which the effect ocq.rrs, can also considerably strengthen causal explanations, although many do not consider them to be requirements for establishing a causal relationship.
CASE STUDY
Media Violence and Violent Behavior
We will use Bushman's (see Bushman and Huesmann2}l2 for review) experiments on media violence and aggression to illusuate the five criteria for establishing causal relationships. Bushman's study focused in part on this specific research question: Do individuals who view a violent videotape act more aggressively than individuals who view a nonviolent videotape?
Undergraduate psychology students were recruited to watch a l5-minute videotape in a screening room, one student at a time. Half of the students watched a movie excerpt that was violent and half watched a nonviolent movie excerpt. After viewing the videotape, the students were told that they were to compete with another student in a different room on a reaction-time task. When the students saw a light cue, they were to react by rying to click a computer mouse faster than their opponent. On a computer screen, the students set a level of
FUNDAMENTALS OF RESEARCH154 SECTION II
radio static that their opponents would hear when the opponents reacted more slowly. The students themselves heard this same type of noise when they reacted more slowly than their opponenB, at the intensity level supposedly set by their opponens.
Each student in the study participated in 25 trials (competitions) with dre unseen opponent. Their aggressiveness was operationalized. as the intensity of noise that they set for their opponents over the course of the 25 trials. The louder the noise level they set, the more aggressively they were considered to be behaving toward their opponents. The ques- tion that we will focus on first is whether students who watched the violent video behaved more aggressively than those who watched the nonviolent video.
Association
The resuls of Bushman's @ushman and fluesmann 2012) experiment are represented in Exhibit 6.3. The average intensity of noise administered to the opponent was indeed higher for students who watched the violent videotape than for those who watched the nonviolent videoape. But is Bushman justified in concluding from these resuls that viewing a violent videoape increased aggressive behavior in his subjects? Would this conclusion have any greater claim to causal validity than the statement that your friend made in response to the Dexter incident? Perhaps it would.
If for no other reason, we can have greater confidence in Bushman's @ushman and Huesmann 2012) conclusion because he did not observe only one student who watched a violent video and then acted aggressively, as was true in the Dexter lncident. Instead, Bushman observed a number of students, some of whom watched a violent video and some of whom did not. So, his conclusion is based on finding an association between the independent variable (viewing ofa violentvideotape) and the dependentvariable (ikelihood ofaggressive behavior).
Association:
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Students Who Viewed Nonviolent Video
CHAPTER 6 o CAUSATION AND RESEARCH DESIGN 155
Exhibit 6.3 Results of Bushman Experiments on Media Violence and Aggression
Time order:
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fusociation is a necessary criterion for establishing a causal effect, but it is not sufEcient on its own. We must also ensure that the variation in the independent variable ca;me before varia- tion in the dependent variable-the cause must come before the presumed effect. This is the criterion of time order. Bushman's experiment satisfied this criterion because he controlled the variation in the independent variable: All the students saw the movie excerpts (which var- ied in violent content) before their level of aggressiveness was measured. fu you can imagine, we cannot be so sure about time order when we use a srrvey or some other observation done at one point in time. Suppose you find in a survey that most people who have committed vio- lent crimes have also watched the Dexter series, and that most people who have not commit- ted violent crimes have not watched it. You believe you have found an association between watching the Derter series and committing violent crimes. But imagine you learn that the series was released after the crimes were committed. Thus, those people in your survey who said they had seen the series had actually committed their crimes before the TV dharacters had committed th'eir crimes. Watching the series, then, could not possibly have led to the crimes. Perhaps the criminals watched Dexterbecause committing violent crimes made them interested in violent TV programs. This discussion points to the importance of the criterion of time order. To conclude that causation was involved, we must see that cases were erposed to variation in the independent variable before variatton in the dependent variable.
Nonspuriousness
Nonspuriousness is another essential criterion for establishing the existence of a causal effect of an independent variable on a dependent variable; in some respects, it is the most important criterion. We say that a relationship between two variables is not spurious when it is not caused by variation in a third variable. Have you heard the old adage Coryelation does not prooe cawation? It is meant to remind us that an association between two variables might be caused by something other than an effect of the presumed independent variable on the dependent variable-that is, it might be a spurious relationship. If we measure children's shoe sizes and their academic knowledge, for example, we will find a positive association. flowever, the association results from the fact that older children have larger feet as well as more academic knowledge. Shoe size does not cause knowledge, or vice versa.
Do storks bring babies? If you believe that correlation proves causation, then you might think so. The more storks that appear in cerain districts in Holland, the more babies are born. But the association in Holland between number of storks and number of babies is spu- rious. In fact, both the number of storks and the birthrate are higher in rural districts than in urban districts. The rural or urban character of the districts (the extraneous variable) causes variation in the other two variables.
In reality, then, the fact that some liked to watch a TV series about a serial killer and then killed someone might be related to the fact that the person was already feeling violent to begin with. This may be the reason he or she sought out violent television dramas for enter- tainment purposes (see Exhibit 6.4). Thus, watching the series Dexter itself tnno way led the person to commit the crime. We must be sure that all three conditions of association, time order, and nonspuriousness are met before we make such claims.
Does Bushman's (Bushman and Huesmann 2012) claim of a causal effect rest on any stronger ground? Jb evaluate nonspuriousness, you need to know about one more feature of his experiment. He assigned students to watch either the violent video or the nonvio- lent video randomly-that is, by the toss of a coin. Because he used random assignment, the characteristics and attitudes that students already possessed when they were recruited for the experiment could not influence which video they watched. As a result, the students' char- acteristics and attitudes could not explain why one group reacted differendy from the other
FUNDAMENTALS OF RESEARCH156 sECTtoN u o
Spurious relationship
after watching the videos. In fact, because Bushman wed296 students in his experiment, it is highly unlikely that the violent video group and the nonviolent video group differed in any relevant way at the outset, even on the basis of chance. This experimental research design meets the criterion of nonspuriousness. Bushman's conclusion that viewing video violence causes aggressive behavior thus rests on firm ground indeed.
Many people believe that causal (internal) validity is achieved by meeting the criteria of association, time order, and nonspuriousness. Others, however, believe that rwo additional criteria should also be considered: mechanism and context.
Mechanism
Confidence in a conclusion that two variables have a causal connection will be strengthened if a mechanisrq some discernible means of creating a connection, can be identified (Cook and Campbell 1979;Marini and Singer 1988). Many social scientists (and scientists in other fields) argue that a causal explanation is not adequate until a causal mechanism is identified. What process or mechanism actually is responsible for the relationship between the independent and dependent variables?
Bushman @ushman and }luesmann 2012) did not empirically identifz a causal mechanism in his experiment, but he did suggest a possible causal mechanism for the effect of watching violent videos. Before we can explain this causal mechanism, we have to tell you about one more aspect of his research. He was not interested simply in whether viewing violent films resulted in aggressive behavior. Actually, his primary hlpothesis was that individuals who were predisposed to aggression before the study began would be more influenced by a violent fi1m than individu- als who were not aggressive at the outset. And that is what happened: Individuals who were predisposed to aggression became more aggressive after watching Bushman's violent video, but individuals who were not predisposed to aggression did not become more aggressive.
After the experimeng Bushman @ushman and lluesmann 2012) proposed a causal mecha- nism to explain why aggressive individuals became even more aggressive after watching the film:
High trait aggressive individuals [people predisposed to aggression] are more suscep- tible to the effects of violent media than are low tait aggressive infividuals because they possess a relatively large network ofaggressive associations that can be activated
Mechanism:
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View the show Dexter
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Commit violent crime
CHAPTER 6 . CAUSATION AND RESEARCH DESIGN 157
Exhibit 6.4 A Spurious Relationship
Contextual effects:
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by violent cues. Habitual exposure to television violence might be partially respon- sible. (959)
Note that this explanation relies more on speculation than on the actual empirical evidence from this particular experiment. Nonetheless, byproposing a reasonable causal mechanism that connects the variation in the independent and dependent variables, Bushman srengthens the argument for the causal validity of his conclusions.
It is often possible to go beyond speculation by designing research to test one or more possible causal mechanisms. Perhaps other researchers will design a new study to measure direcdy the size of individuals' networks of aggressive associations that Bushman contends are part of the mechanism by which video violence influences aggressive behavior.
Context In the social world, it is virtually impossible to claim that one and only one independent vari- able is responsible for causing or affecting a dependent variable. Stated another way, no cause can be separated from the larger context in which it occurs. A cause is really only one ofa set of interrelated factors required for the effect (flage and Meeker 1988; Papineau 1978). When relationships among variables differ across geographic unis such as counties or across other social settings, researchers say there is a contexhrd effect. Identification of the context in which a causal relationship occurs can help us understand that relationship.
Some researchers argue that we do not firlly understand the causal effect of media violence on behavioral aggression unless we have identified these other related factors. As we have just seen, Bushman (Bushman and lluesmann 2012) proposed at the outset of his research at least one other condition: Media violence would increase aggression only among individuals who were already predisposed to aggression.
Identification ofthe context in which a causal effect occurs is not a criterion for a valid causal conclusion. Some contextual factors maynot turn out to be causes ofthe effect being investigated. The question for researchers is "flow many contexts should we investigate?" In a classic study of childrent aggressive behavior in response to media violence, Bandura, Ross, and Ross (1963) examined several contexrual factors. They found that effecs varied with the children's gender and with the gender of the person whom they observed but not with whether they saw a real (acted) or filmed violent incident. For example, children reacted more aggressively after observing men committing violent acts than after observing women committing these same acts. But Bandura et al. fid not address the role of violence within the children's families or the role of participation in sports or many other factors that could be involved in children's responses to media violence. Bandura et al. strengthened their conclu- sions by focusing on a few likely contextudl factors.
Speci$,ing the context for a causal effect helps us understand that effect, but it is a process that can never really be complete. We can always ask wtrat else might be important: In which counbT was the study conducted? What are the ages of the study participans? We need to carefirlly review the results ofprior research and the implications ofrelevant theory to deter- mine what contexflral factors are likely to be important in a causal relationship. Our confidence in causal conclusions will be stronger when we lnow these factors are taken into account.
RESEARCH DESIGNS AND CAUSALITY
flow research is designed influences our ability to draw causal conclusions. Obviously, if you conclude that playing violent video games causes violent behavior after watching your eight-year-old nephew playrng a violent video game and then hitting his four-year-old
158 SECTION II O FUNDAMENTALS OF RESEARCH
brother, you would be on shalcy empirical ground. In this section, we will introduce features that need to be considered in a research design in order to evaluate how well it can support nomothetic causal conclusions.
True Experiments
In a true experiment, the time order is determined by the researcher. The experimenul design provides the most powerful design for testing causal hlpotheses about the effect of a treatrnent or some other variable whose values can be manipulated by the researchers. It is so powerful for testing causal hypotheses because it allows us to establish the three criteria for causality with a great deal of confidence. The Bushman @ushman and Huesmann 2012) study we examined in the last section was a true experiment.
Ti'ue experiments must have at least three things:
1. fivo comparison groups: one receiving the experimental condition (e.g., treatrnent or intervention), termed the experimental group, and the other receiving no treatrnent or intervention or another form thereof, termed the control or comparison group.
2. Random assignment to the two (or more) comparison groups. 3. Assessment of change in the dependent variable for both groups after the
experimental condition has been received.
The combination of these features permits us to have much greater confidence in the valid- ity of causal conclusions than is possible in other research designs. Confidence in the validity
True experiment:
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CHAPTER 6 T CAUSATION AND RESEARCH DESIGN 159
AmandaAykanian,ResealchAgsoeieteied"r,b Human-Potential
Amanda Aykanian majored in psychology at Framingham State University and found that she enjoyed the rou- tine and organization of research. She wrote an undergrad thesis to answer the following research question: How does the way in which course con- tent is presented affect
the content and the rate at
materials to entering research data, cleaning data, and proofing reports. As she contributed more to project reports, she began to think about data from a more theo- retical standpoint.
During her seven years at AHP, Aykanian has helped Iead program evaluation research, design surveys and write,survey questions, conduct phone and qualitative interviews,
Td lead focys groups. Her program evalu-
ation res'earch'almost always uses a mixed-methods J
approach, so,Aykanian has learned a lot about how qualitative and quantitative methods can complement each other. She has received a lot of on-the-job train- ing in data analysis and has learned how to think about and write a proposal in response to federal funding opportunities.
Aykanian was promoted to research associate and ,describes her current role as part program evaluation coordinator and part data analyst. She has also returned to graduate school, earning a master's degree in applied sociology and then starting a PhD program in social welfare.
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Source : Amand a Aykanian
students' feelings about which they retain it?
After graduating, Aykanian didn't want to go to graduate school right away; instead, she wanted to e.xplore her interests and get a sense of what she could do with research. Advocates for Human Potential (AHP) was the last research assistant (RA) job that Aykanian applied for. Her initial tasks as an RA at AHP ranged from taking notes, writing agendas, and assembling project
1..
of an experiment's findings is frrther enhanced by identification of the causal mechanism and control over the context of an experiment. W'e will discuss experimental designs in more detail in Chapter 7. For now, we want to highlight how true experimental designs lend themselves to meeting the criteria necessary for causality.
Causality and True Experimental Designs
A prerequisite for meeting each of the three criteria to identify causal relations is maintaining control over the conditions subjects are exposed to after they are assigned to the experimental and comparison groups. If these conditions begin to differ, the variation between the experimental and comparison groups will not be what was intended. Even a subsequent difference in the distribution of cases on the dependent variable will not provide clear evidence ofthe effect ofthe independent variable. Such unintended variation is often not much of a problem in laboratory experiments, where the researcher has almost complete control over the conditions and can ensure that these conditions are nearly identical for both groups. But control over conditions can become a very big concern for experiments that are conducted in the field in real-world settings, such as Sherman and Berk's (1984) study ofthe deterrent effects ofarrest on intimate partner assaults.
Let us examine how well true experiments meet the criteria necessary for establishing causality in greater detail:
Association Between the Hypothesized lndependent and DependentVariables, As you have seen, experiments can provide unambiguous evidence of association by randomly assigning subjects to experimental and comparison groups.
Time Order of Effects of One Variable on the Others, Unquestionably, the independent variable (teatrnent of condition) preceded the posttest measures in the experiments described so far. For example, arrest for partler abuse preceded recidivism in the Sherman and Berk (1984) study, and exposure to media violence preceded aggression in the Bushman experiments (Bushman and Huesmann 2012).Tn experiments with a pretest, time order can be established by comparing posttest to pretest scores. In experiments with random assignment of subjects to the experimental and comparison groups, time order can be established by comparison of posttest scores only.
Nonspurious Relationships Between Variables. Nonspuriousness is difEcult to establish; some would say it is impossible to establish in nonexperimental designs. The random assignment of subjects to experimental and comparison groups makes true experiments powerfril designs for testing causal hypotheses. Random assignment controls a host of possible extraneous influences that can create misleading, spurious relationships in both experimental and nonexperimental data. If we determine that a design has used randomization successfully, we can be much more confident in the causal conclusions.
Mechanism That Creates thte Causal Effect, The features of a true experiment do not, in themselves, allow identification of causal mechanisms; as a result, there can be some ambiguity about how the independent variable influenced the dependent variable and the causal conclusions.
Context in Which Change Occurs. Control over conditions is more feasible in many erperimenal designs than it is in nonerperimenal designs, but it is often difficult to control conditions in field experiments. In the next chapter, you will learn how the lack of control over experimental conditions can threaten internal validity.
SECTION II ; FUNDAMENTALS OF RESEARCH160
Nonexperimental Designs
Nonexperimental research designs can be either cross-sectional or longitudinal. In a cross-sectional research design, all data are collected at one point in time. Identi$ring the time order of effects-what happened first and so on-is critical for developing a causal analysis but can be an insurmountable problem with a cross-sectional design. In longi- tudinal research designs, data are collected at two or more points in time, and so, the identification of the time order of effects can be quite straightforward. You can think of an experiment as a type of longitudinal design because subjects are observed at two or more points in time.
Cross-Sectional Designs
Much of the research you have encountered so far in this text has been cross-sectional. Although each survey or interview takes some time to carry out, if it measures the actions, attitudes, and characteristics ofrespondents at only one time, it is considered cross-sectional. The name comes from the idea that a snapshot from a cross section of the population is obtained at one point in time.
fu you learned in Chapter 4, Sampson and Raudenbush (1999) used a very ambitious cross-sectional design to study the effect ofvisible public social and physical disorder on the crime rate in Chicago neighborhoods. Their theoretical framework focused on the concept of informal social control: the ability of residents to regulate social activity in their neigh- borhoods through their collective efform according to desired principles. They believed that informal social control would vary among neighborhoods, and they hypothesized that it was the strength of informal social control that would explain variation in crime rates rather than only the visible sign of disorder. They contrasted this prediction with the "broken windows" theory: the belief that signs of disorder themselves cause crime. Their findings supported their hypothesis: Both visible disorder and crime vrere consequences of low levels of informal social control (measured with an index of collective effrcacy). One did not cause the other (see Exhibit 6.5).
In spite of these compelling findings (see Exhibit 6.6), Sampson and Raudenbush's (1999) cross-sectional design could not establish direcdy that the variation in the crime rate occurred after the variation in informal social control. Mryb. it was a high crime rate that led residents to stop trying to exert much control over deviant activities in the neighborhood,
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CHAPTER 6 . CAUSATION AND RESEARCH DESIGN 161
Exhibit 5.5 The Effect of Informal Social Control
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perhaps because of fear of crime. It is difficult to discount such a possibility when only cross-sectional data are available.
There are four special circumstances in which we can be more confident in drawing conclusions about time order on the basis of cross-sectional daa. Because in these special circumstances the data can be ordered in time, they might even be thought of as longitudinal designs (Campbell 1992).
The lndependentVariable ls Fixed at Some Point Prior to theVariation in the Dependent Variable. So-called demographic variables that are determined at birth-such as sex, race, and age-are fixed in this way. So are variables such as education and marital status, if we know when the value of cases on these variables was established and if we lnow that the value of cases on the dependent variable was set some time afterward. For example, say we hypothesize that educational opportunities in prison affect recidivism rates. Let us say we believe those inmates who are provided with greater educational and vocational opportunities in prison will be less likely to reoffend after release from prison. If we lnow that respondents completed their vocational or other educational training before leaving prison, we would satisS, the time order requirement, even if we were to measure education at the same time we measure recidirrism after release. However, if there is a possibility that some respondents went back to school after prison release, the time order requirement would not be satisfied.
We BelieveThat Respondents Can Give tJs Reliabte Reports of What Happened toThem or What They Thought at Some Earlier Point in Time. The reliability of recall is based on many factors, including how far back in time respondents are queried and the events they are asked to recall.
Our Measures Are Based on Records That Contain lnformation on Cases in Earlier Periods, Government agency and organizational records are an excellent source of time-ordereddataafterthefact.Iloweveqsloppyrecordkeepingandchangesindaa-collection policies can lead to inconsistencies, which must be taken into account. Another weakness of
SECTION ll . FUNDAMENTALS OF RESEARCH
disorder Collective
162
Exhibit 6.6 Effect of Social Disorder and Gollective Efficary on Personal Violent Grimes
such archival data is that they usually contain measures of only a fraction of the variables that we think are important. This caution applies to the arrest records obtained by Lo and colleagues (Lo, Kim, and Cheng 2008), described in the next section. For example, their research did not obtain arrest records from states other than Ohio, and for this reason, they may have missed important incidents that could have affected their results.
We Know That the Value of the Dependent Variable Was Similar for All Cases Prior to the Treatmenf. For example, we may hlpothesize that an anger management program (independent variable) improves the conflict resolution abilities (dependent variable) of individuals arrested for intimate partner assault. If we know that none of the arrested individuals could employ verbal techniques for resolving conflict prior to the training program, we can be confident that any subsequent variation in their ability to do so did not precede exposure to the training program. This is one way that traditional experiments establish time order: fivo or more equivalent groups are formed prior to exposing one of them to some treatment.
CASE STUDY
Using Life Galendars: Do Offenders Specialize in Different Crimes? Lo and colleagues (2008) provide an interesting example of the use of such retrospective daa. The researchers wanted to examine the characteristics of offenders that would lead them to repeat ceftain crimes. Specifically, they wanted to know if the type of crime committed early in someone's life was a reliable predictor of offenses committed later. Stated differendy, do offenders specialize in different qpes of crime? Lo et al. obtained official arrest records from the age of I 8 to the time of the study (typically around age 2 5) for a sample of young offend- ers who were incarcerated in county jails in Ohio. They then asked the inmates to reconstruct their drug and alcohol use, among other things, monthly for the same time period using a life calendar instrument based on the Amestee Drug Abuse Monitoring (ADAM) interview schedule. This life calendar instrument helps respondents recall events in their past by display- ing each month of a given year along with key dates noted within the calendar, such as birth- days, arrests, holidays, anniversaries, and so on. Respondents are given a calendar that displays these key dates, typically called anchors, and then are asked to recall the variables of interest (i.e., drug use, victimizations) that also occurred during the specified time frame. The use of a life calendar has been shown to improve the ability of respondents to recall events ix the past compared to the use of basic questions without a calendar (Belli, Stafford, and Alwin 2009).
Results of t-he research by Lo et al. (2008) were somewhat mixed regarding offender specialization. Most offenders engaged in a variety of offenses prior to their current arrest. Ilowever, compared to drug and property offenders, violent offenders vr'ere more likely to specialize, as they were the most likely to have had violent arrest records prior to their cur- rent offenses.
It is imporunt to note that retrospective daa such as these are often inadequate for measuring variation in past pqychological sates or behaviors, because what we recall about our feeling or actions in the past is likely to be influenced by what we feel in the present. For example, retrospective reports by both adult alcoholics and their parens appear to gready overestimate the frequency of childhood problems (Taillant 1995). People cannot report reliably the frequenry and timing of many past events, from hospialization to hours worked. FIowever, retrospective data tend to be reliable when they concern major, persistent experiences in the pasg such as what type of school someone went to or how a person's family was strucnrred (Campbell 1992).
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CHAPTER 6 e CAUSATION AND RESEARCH DESIGN 163
Longitudinal Designs
In longitudinal research, data are collected at two or more points in time and, for this reason, can be ordered in time. By measuring the value of cases on an independent variable and a dependent variable at different times, the researcher can determine whether variation in the independent variable precedes variation in the dependent variable.
In some longitudinal designs, the same sample (or panel) is followed over time; in other designs, sample members are rotated or completely replaced. The population from which the sample is selected may be defined broadly, as when a longitudinal survey of the general population is conducted. Or the population may be defined narrowly, as when members of a specific age group are sampled at multiple points in time. The frequency of follow-up measurement c n vary, ranging from a before-and-after design with only one follow-up to studies in which various indicators are measured every month for many years.
Collecting data at two or more points in time can prove difficult for a number of reasons-lack of long-term funding, not being able to locate the original participants, and so on. But think of the many research questions that really should involve a much longer follow-up period: Does community-oriented policing decrease rates of violent crime? What is the impact of job uaining in prison on recidivism rates? IIow effective are batterer treatment programs for individuals convicted of intimate partrler assault? Do parenting programs for young mothers and fathers reduce the likelihood of their children becoming delinquent? It is safe to say that we will never have enough longitudinal data to answer many important research questions. Nonetheless, the value of longitudinal data is so great that every effort should be made to develop longitudinal research designs when they are appropriate for the research question asked. The following discussion of the three major types of longitudinal designs will give you a sense of the possibilities (see Exhibit 6.7).
Repeated Cross-Sectional Design (Trend Study)
Fixed-Sample Panel Design (Panel Study)
Time 1
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SECTION II . FUNDAMENTALS OF RESEARCH
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Exhibit 6.7 Three Tlrpes of Longitudinal Design
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Repeated Cross-Seclional Designs Studies that use x repeated cross-sectional desigrl also known as trend studieg have become fixtures of the political arena around election time. Particularly in presidential election years, we accustom ourselves to reading weekly or even daily reports on the percentage ofthe population that supports each candidate. Similar polls are conducted to track sentiment on many other social issues, such as attitudes toward marijuana legalization and trust in the police.
Repeated cross-sectional surveys are conducted as follows:
1. A sample is drawn from a population atTime 1, and data are collected from the sample.
2. As time passes, some people leave the population, and others enter it.
3. AtTime 2, a different sample is drawn from this population.
These features make the repeated cross-sectional design appropriate when the goal is to determine whether a population has changed over time. Has racial tolerance increased among Americans in the past 20 years? Are prisons more likely to have drug-treatrnent programs avail- able today than they were in the 1950s? These questions concern changes in the population as a whole, not changes in individuals within the population. We want to know whether racial tolerance increased in society, not whether this change was due to migration that brought more racially tolerant people into the country or to individual U.S. citizens becoming more tolerant. We are asking whether state prisons overall are more likely to have drug-treaffnent programs available today than they were a decade or two ago, not whether any such increase was due to an increase in prisoner needs or to individual prisons changing their program availability. When we do need to know whether individuals in the population changed, we must turn to a panel design.
Fixed-Sample Panel Designs Panel designs allow us to identifz changes in individuals, groups, or whatever we are studying. This is the process for conducting fixed-sample panel designg also known as panel studies:
1 . A sample (called a panel) is drawn from a population at Time 1 , and data are collected from the sample.
2. As time passes, some panel members become unavailable for follow-up, and the population changes.
3. AtTime 2, data are collected from the same people as atTime 1 (the panel), except for those people who cannot be located.
Because a panel design follows the same individuals, it is better than a repeated cross-sectional design for testing causal hl.potheses. For example, Schreck, Steward, and Fisher (2006) wanted to identifiz predictors of adolescent victimization and wondered if the cross-sectional studies that had been conducted about victimization might have provided mis- leading results. Specifically, they suspected that adolescenc w'ith lower levels of self-control might be more prone to victimization and so needed to collect or find longitudinal data in vrhich self-control was measured before experiences of victimization. The theoretical model they proposed to test included several other concepts that criminologists have identified as related to delinquenry and that also might be influenced by levels of self-control: having delinquent peers, engaging in more delinquenry, and being less attached to parents and school (see Exhibit 6.8). Schreck et al. anilyzed data available from a panel study of delinquenry and found that low self-control at an earlier time made it more likely that adolescents would
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CHAPTER 6 o CAUSATION AND RESEARCH DESIGN 165
Delinquent peers
Delinquency
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Social bonds
Source: Schreck, Christopher J., Eric A. Steward, and Bonnie S. Fisher. 2006. "Self-control, Victimization, and their Influence on Risky Lifestyles: A Longitudinal Analysis Using Panel Data.",fournal of Quantitctiue Criminology 22:319-340. Reprinted with permission from Springer Nature.
subsequendy experience victimization, even accounting for other influences. The researchers' use of a panel design allowed them to be more confident that the self-control-victimization relationship was causal than ifthey had used a cross-sectional design.
Panel designs are also a challenge to implement successfirlly-and often are not even attempted-because of two major difEculties:
Expense and Attrition, It can be difEcult and very expensive to keep track of individuals over a long period, and ineviably, the proportion of panel members who can be located for follow-up will decline over time. Panel studies often lose more than one quarter of their members through aurition (Miller 1991), and those who are lost are often not necessarily similar to those who remain in the panel. As a resrlg a high rate of subject attrition may mean that the follow-up sample will no longer be representative of the population from which it was drawn and may no longer provide a sound basis for estimating change. Subjecs who were lost to follow-up may have been those who changed the most, or the leasg over time. For orample, between 5o/o and 66% of subjects are lost in substance abuse prevention studies, and the dropous typically begin such studies with higher rates of tobacco and marijuana use (Snow, Tebes, and Arthur 1992).
It does help to compare the baseline characteristics of those who are interviewed at follow-up with characteristics of those lost to follow-up.If these two groups of panel members were not very different at baseline, it is less likely that changes had anything to do with the characteristics of the missing panel members. Even better, subject attrition can be reduced subsantially if sufficient staff can be used to keep track of panel members. In their panel study, Sampson and Laub (1993) lost only 12 of the juveniles in the original sample (eight, if you do not count those who died).
Subject Fatigue. Panel members may grow vreary of repeated interviews and drop out of the study, or they may become so used to answering the sandard questions in the survey that they
166 SECTION II . FUNDAMENTALS OF RESEARCH
Exhibit 6.8 Explanatory Model of Adolescent Victimization Using Fixed-Sample Panel Design
start giving stock answers rather than actually thinking about their current feelings or actions (Campbell 1992). This is called the problem of subject fatigue. Fortunately, subjects do not often seem to become fatigued in this way, particularly if the researchers have maintained positive relations with the subjects.
Because panel snrdies are so usefirl, social researchers have developed increasingly effective techniques for keeping rack of individuals and overcoming subject fatigue. But when resources do not permit use of these techniques to mainain an adequate panel, repeated cross-sectional designs uzuallycanbe employed ata costthatis nota greatdealhigherthan thatofa one-time-only cross-sectional study. The payoffin explanatory power should be well worth the cost.
CASE STUDY
Offending Over the Life Course Sampson and Laub (1993) used a fixed-sample panel design to investigate the effect of child- hood deviance on adult crime. They studied a sample of white males in Boston when the sub- jects were between l0 and 17 years old and then followed up when the subjecs were in their adultyears. Data were collected from multiple sources, including the subjects themselves and criminal justice records. Sampson and Laub found that children who had been committed to a correctional school for persistent delinquency were much more likely than other children in the study to commit crimes as adults: 6l% were arrested between the ages of 25 and32, compared to 14olo of those who had not been in correctional schools as juveniles. In this study, juvenile delinquenry unquestionably occurred before adult criminality. Ifthe researchers had used a cross-sectional design to study adults' pasts, the juvenile delinquenry measure might have been biased by memory lapses, by self-serving recollections about behavior as juveniles,
or by loss of agenry records.
Event-Based Designs In an event-based design, often called a cohort study, the follow-up samples (at one or more times) are selected from the same cohort (people who all have experienced a similar event or a common starting point). Examples include the following:
o Birth cohorts: those who share a common period of birth (those born in the 1940s, 1950s, 1960s, etc.)
o Seniority cohom: thosewho have worked at the same place for about 5 years, about 10 years, and so on
o School coborts: freshmen, sophomores, juniors, and seniors
An event-based design can be a type of repeated cross-sectional design or a type of panel design. In an event-based repeated cross-sectional design, separate samples are drawn from the same cohort at two or more different times. In an event-based panel design, the same individuals from the same cohort are studied at two or more different times.
Determining Gausation Using Nonexperimental Designs
How well do the research designs described earlier satisfi, the criteria necessary to deter- mine causality? Although it is relatively easy to establish that an empirical association exists between an independent and a dependent variable in these designs, the other criteria are much more difEcult to assess.
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CHAPTER 6 . CAUSATION AND RESEARCH DESIGN 167
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CASE STUDY
Gender, Social Control, and Grime
Let us first illustrate the importance of time order and nonspuriousness using research that has examined the factors related to the gender and crime relationship. Based on both victimization data and official police reports, data indicate that males commit the majority of all crimes. Why is this? Gottfredson and Hirschi's (1990) general theory of crime (GTC) contends that the reason males engage in more criminality is that they have lower levels of self-control than females. The researchers also contend that socialization of children by parents is the primary factor in the development of self-control. However, based on a critique of the GTC by Miller and Burack (1993) and the power-conrol theory (llagan, Gillis, and Simpson 1985), Blackwell and Piquero (2005) hypothesized that the power relationships that exist between parents in a household (e.g., patriarchy) would also affect the socialization experiences of boys and girls and, ultimately, their levels of self-control.
To summarize briefly, Blackwell and Piquero (2005) examined the factors related to self-control acquisition in childhood using a sample of adults. Using this same sample of adults, they then examined the extent to which low self-conuol predicted the propensity for criminal offending. In a nutshell, they sought to explain the origins of self-control as well as the effects of self-control on criminal offending and how all this may be dif- ferent for males and females from patriarchal families and for males and females from more egalitarian families. Using a random sample of 350 adults from Oklahoma City, Oklahoma, they found that there were indeed differences in the way power relationships between parents affected the acquisition of self-control for males and females. They also found, however, that there were essentially no differences in the ability of self-control to predict criminal aspirations; males and females with low self-control levels were more likely to self-report that they would engage in criminal behavior than their counterparts with higher self-conuol levels.
Do these findings establish that low self-control leads to crime through poor socializa- tion of children by parents? Well, there are many assumptions being made here that we hope you can see right away. First, this study relied on the recollections of adults about their child- hood socialization. It also assumed that levels oflow self-control were subsequent to parental socialization and came before individuals' aspirations to offend (time order). This may very well be the case. It may be that those adults who were more likely to offend had inadequate socialization, which created low self-control. Howeveq it may also be that offending behavior during their adolescence led to weak attachments to family and high attachments to other delinquent peers similar to themselves, which also decreased levels of self-control. In this case, the delinquent offending and peer associations would be a third variable responsible for both the low self-control and the criminal aspirations in adulthood (spurious relation- ship). The problem, of course, is that with cross-sectional data such as these, the correct time order cannot be established, and it is difficult to control for the effects of all important factors. Jb reduce the risk ofspuriousness, Blackwell and Piquero (2005) used the technique of statistical control Howevbr, they still stated clearly the need for longitudinal research, "Future research should attempt to examine the changing nature of parental socialization and self-control across gender in longitudinal studies" (l 5).
Similarly, Sampson and Raudenbush (1999) designed their study, in part, to determine whether the apparent effect of visible disorder on crime-the "broken windows" thesis-was spurious due to the effect of informal social control. Exhibit 6.9 shows how statistical control was used to test this possibility. The data for all neighborhoods show that neighborhoods with more visible disorder had higher crime rates than those with less visible disorder. Ilowever, when we examine the relationship between visible disorder and neighborhood crime rates
FUNDAMENTALS OF RESEARCH168 sECTroN n
separately for neighborhoods with high and low levels of informal social control-that is, when we statistically control for social control level-we see thar the crime rate no longer varies with visible disorder. Therefore, we must conclude that the apparent effect of broken windows was spurious, due to level of informal social control. Neighborhoods with low levels of social control were more likely to have high levels of visible social and physical disorder, and they were also more likely to have a high crime rate, but the visible disorder itself did not alter the crime rate.
Our confidence in causal conclusions based on nonexperimental research also increases with identification of a causal mechanism. These mechanisms are called inter- vening variables in nonexperimental research and help us understand how variation in the independent variable results in variation in the dependent variable. For example, in a study that reanalyzed data from Glueck and Glueck's (1950) path-breaking study of juvenile delinquency, Sampson and Laub (1993) found that children who grew up with such structural disadvantages as family poverty and geographic mobility were more likely to become juvenile delinquents. Why did this occur? Their analysis indicated that these structural disadvantages led to lower levels of informal social control in the family (less parent-child attachment, less maternal supervision, and more erratic or harsh discipline). Lower levels of informal social control resulted in a higher probability of delinquency (see Exhibit 6.10). Informal social control intervened in the relationship between struc- tural context and delinquency.
Of coursq, identification of one (or two or three) intervening variables does not end the possibilities for clari$ring the causal mechanisms. You might ask why structural disadvantage tends to result in lower levels of family social control or how family social control iafluences delinquenry. You could then conduct research to identifiz the mechanisms that link family social control and juvenile delinquenry-perhaps the children feel they are not cared for, so
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Crime Rate
High Low
Amount of Visible Disorder
Source:Based on Sampson and Raudenbush 1999.
Crime Rate
lnformal Social Control
Crime Rate
High
High Low Amount of Visible
Disorder
High Low
Amount of Visible Disorder
CHAPTER 6 . CAUSATION AND R ESEARCH DESIGN 169
Exhibit 6.9 The Use of Statistical Gontrol to Reduce Spuriousness
disadvantage Family poverty
Geographic
lndependent Variable
lntervening Variable (causal mechanism)
Dependent Variable
lnformal social control:
Low parent-child attachment
Low maternal supervision
More erratic or harsh discipline
Source: Based on Sampson and Laub 1993.
they become less concerned with conforming to social expecations. This process could go on and on. The point is that identification of a mechanism through which the independent variable influences the dependent variable increases our confidence in the conclusion that a causal connection does indeed exist.
When you think about the role of variables in causal relationships, do not confuse vari- ables that cause spurious relationships with variables that intervene in causal relationships, even though both are third variables that do not appear in the initial hypothesis. fnterven- ing variables help explain the relationship berween the independent variable (uvenile delin- quenry) and the dependent variable (adult criminality).
Nonexperimental research can be a very effective tool for exploring the context in which causal effects occur. Administering surveys in many different settings and to different types of individuals is usually much easier than administering various experiments. The difficulty of establishing nonspuriousness does not rule out using nonexperimental data to evaluate causal hypotheses. In fact, when enough nonexperimenal data are collected to allow tests of multiple implications of the same causal hlpothesis, the results can be very convincing @reedman 1991).
h roy case, nonexperimental tests of causal hlpotheses will continue to be popular, because the practical and ethical problems in randornly assigning people to different condi- tions preclude testing many important hypotheses with an experimental design.Just remem- ber to carefirlly consider possible sources of spuriousness and other problems when evaluating causal claims based on individual nonexperimental studies.
UNITS OFANALYSIS AND ERRORS IN CAUSAL REASONING
In criminological research, we obtain samples from many different units, including individuals, groups, cities, prisons, countries, and so on, When we make generalizations from a sample to the population, it is very important to keep in mind the units under study, which are referred to as the units of analysis. These unis of analysis are the level of social life on which the research question is focused, such as individuals, groups, or nations.
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170 SECTION I FUNDAMENTALS OF RESEARCH
Exhibit 6.10 Intenrening Variables in Nonexperimental Research: Structural Disadvantage and Juvenile Delinquency
lndividual and Group Units of Analysis In many research studies, the units of analysis are individuals. The researcher may collect survey data from individuals, analyze the data, and then report on how many individu- als felt socially isolated and whether recidivism by individuals related to their feelings of social isolation. Data are collected from individuals, and the focus of analysis is on tlre individual.
In other instances, however, the units of analysis may be groups, such as families, schools, prisons, towns, states, or countries. For example, a researcher may collect data from town and police records on the number of DIII accidents and the presence or absence of a server liability law, which makes those who serve liquor liable for accidents caused by those they served. The researcher can then analyze the relationship between server liability laws and the frequenry of accidents due to drunk driving (perhaps also taking into account town population). Because the data describe the towns, towns are the units of analysis.
In some studies, groups are the units of analysis, but data are collected from individuals. For example, Sampson, Raudenbush, and Earls (1997) studied influences on violent crime
171CHAPTER 6 e CAUSATION AND RESEARCH DESIGN
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in Chicago neighborhoods. Collectiae fficary was one variable they hypothesized as an influ- ence on the neighborhood crime rate. This variable was a characteristic of the neighborhood residents who were likely to help other residents and were trusted by other residens, so they measured this variable in a survey of individuals. The responses of individual residents about their perceptions of their neighbors' helpfulness and trusmrorthiness were averaged to create a collective efficary score for each neighborhood. It was this neighborhood measure of collec- tive efEcacy that was used to explain variation in the rate of violent crime between neighbor- hoods. The data were collected from individuals and were about individuals, but they were combined or aggregated to describe neighborhoods. The units of analysis were thus groups (neighborhoods).
In a study such as this, we can distinguish the concept of unix of analysis from the units of observation. Data were collected from individuals (the units of observation) and then the data were aggregated and analyzed at the group level. In most studies, however, the units of observation and the units of analysis are the same. For example, Xu, Fiedler, and Flaming (2005), in collaboration with the Colorado Springs Police Department, srr- veyed a stratified random sample of 904 residents to test whether their sense of collective efficary and other characteristics would predict their perceptions of crime, fear of crime, and satisfaction with police. Their data were collected from individuals and analyzed at the individual level. They concluded that collective efficacy was not as important as in Sampson et al.'s (1997) study.
The important point is to know when this is true. A conclusion that crime increases with joblessness could imply that individuals who lose their jobs are more likely to commit a crime, that a community *ith a high unemployment rate is likely to have a high crime rate, or both. Whether we are drawing conclusions from data or interpreting others' conclusions, we have to be clear about which relationship is referenced.
We also have to know what the units of analysis are to interpret statistics properly. Mea- sures ofassociation tend to be stronger for group-level than for individual-level data, because measrrement errors at the individual level tend to cancel out at the group level (Bridges and Weis 1989).
The Ecological Fallacy and Reductionism Researchers should make sure that their causal conclusions reflect the units of analysis in their study. Conclusions about processes at the individual level should be based on individual-level data; conclusions about group-level processes should be based on data collected about groups. When this rule is violated, we can often be misled about the existence of an association between two variables.
A researcher who draws conclusions about individual-level processes from groupJevel data is constructing an ecological fallacy (see Exhibit 6.11). The conclusions may or may not be correct, but we must recognize that group-level data do not describe individual-level processes. For example, a researcher may examine prison employee records and find that the higher the percentage ofcorrectional workers without college education in prisons, the higher the rate of inmate complains of brutality by officers in prisons. But the researcher would commit an ecological fatlacy if she then concluded that individual correctional officers without a college education were more Iikely to engage in acts of brutality against inmates. This conclusion is about an individual-level causal process (the relationship between the edu- cation and criminal propensities of individuals), whereas the data describe groups (prisons). It could actually be that college-educated officers are the ones more likely to commit acts of brutality. If more officers in prison are not college educated, perhaps the college-educated ofEcers feel they would not be suspected.
172 SECTION II . FUNDAMENTALS OF RESEARCH
You Collect Data From
Groups lndividuals
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Conversely, when data about individuals are used to make inferences about group-level processes, a problem occurs that can be thought of as the mirror image of the ecological fallacy the reductionist fallacy, or reductionism, also known as the indiztid.ualist fallacy (see Exhibit 6.11). For example, a reductionist explanation of individual vjolence would focus on biological factors, such as genes or hormones, rather than on the community's level of poverty. Wilson (1987) also notes that we can be misled into concluding from individual-level data that race has a causal effect on violence. Although African Americans may be disproportionately represented in arrest statistics, they are also disproportionately represented in poor communities. That is, they are significandy more likely to live in com- munities with concentrated disadvantage compared to whites. The concentration ofAfrican Americans in poverty areas, not the race or other characteristics of the individuals in these areas, may be the cause of higher rates of violence. Explaining violence in this case requires community-level data.
The fact that errors in causal reasoning can be made should not deter you from con- ducting research with aggregate data, nor should it make you unduly critical ofresearchers who make inferences about individuals on the basis of aggregate data. When considered broadly, many research questions point to relationships that could be manifested in many ways and on many levels. The study of urban violence by Sampson et al. (1997) is a case in point. Their analysis involved only aggregate data about cities, and they explained their research approach as, in part, a response to the failure ofother researchers to examine this problem at the structural, aggregate level. Moreover, Sampson et al. argued that the rates of
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CHAPTER 6 . CAUSATION AND RESEARCH DESIGN 173
'' ...' : Exhibit 6.L1 Errors in Gausal Gonclusions
joblessness and family disruption in communities influence community social processes, not only the behavior of the specific individuals who are unemployed or who grew up without two parents.
The solution is to know what the units of analysis and units of observation were in a study and to take these into account when weighing the credibility of the researcher's conclusions. For example, if a study tses cities as the units of analysis and finds that cit- ies with higher levels ofpoverty (independent variable) also tend to have higher levels of violent crime (dependent variable), they should be cautious in concluding that individuals who live below the poverty level are also more likely to commit violent acts. This would be an ecological fallacy unless data at the individual level suggested this conclusion was accurate.
The goal is not to reject conclusions that refer to a level of analysis different from what was actually studied. Instead, the goal is to consider the likelihood that an ecological fallaey or a reductionist fallary has been made when estimating the causal validity of the conclusions.
CONCLUSION
In this chapter, you have learned about two alternative meanings of causation (nomo- thetic and idiographic). You have studied the five criteria used to evaluate the extent to which particular research designs may achieve causally valid findings. You have learned how our ability to meet these criteria is shaped by research design features, including the use of true experimental designs, the use of cross-sectional or longitudinal designs, and the use of statistical control to deal with the problem of spuriousness. You have also seen why the distinction between experimental and nonexperimental designs has so many consequences for how, and how well, we are able to meet nomothetic criteria for causation.
It is important to remember that the results of any particular study are part of an always-changing body of empirical knowledge about social reality. Thus, our understand- ings of causal relationships are always partial. Researchers always wonder whether they have omitted some relevant variables from their controls, whether their experimental results would differ if the experiment were conducted in another setting, or whether they have overlooked a critical historical event. But by using consistent definitions of terms and maintaining clear standards for establishing the validity of research results and by expecting the same of others who do research, social researchers can contribute to a growing body ofknowledge that can reliably guide social poliry and social understanding.
When you read the results of a social scientific study, you should now be able to evalu- ate critically the validity of the study's findinp. If you plan to eng"ge in social research, you should now be able to plan an approach that will lead to valid findings. And with a good understanding of three dimensions of validity (measurement validity, generalizability, rnd causal [internal] validity) under your belt, you are ready to focus on the major methods of data collection used by social scientists.
174 SECTION II . FUNDAMENTALS OF RESEARCH
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176 SECTION II . FUNDAMENTALS OF RESEARCH
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the replication studies to randomly assign individuals
accused of domestic violence to an arrest or nonarrest #t#ttl ,r rbo,rt i",i,iab##;+ s dr;i* ., students like yourielf? Do io" tlink it *ould be ethical td es$i$fii$HdenrS..feil;d9 l gl.i{ifftibnt' fo.nprl *i$ sorne receiving suessful stimuli iuch as loud noises?
f " Think of at least three intervening variables/causal mechanisms through which parents' education might influen.. ,hli, children's risk of poor school performance.
3. Let'S elaborate on this by accounting for a potential confounder. Some have argued that race is critical to understanding school discipline. They suggest that low parent educatior, ,rrd suspension are both correlated with a parent/respondent's race. Therefore, race may be a confounder in this relationship, raising the possibiliry that education doesn't matter after all. We can control for the effect of race by constructing alayered cross-tab, which will look at the relationship between parent educarion and school suspension in whites and blacks separately.
a. Go back to the cross-tab menu. This time, add the variable whiteto the "layer" field.
ill be a bit daunting at firstb. The result here w glance, but what
{ou are looking forls whether the
pattern you found in Exercise 2 is present in the nonwhite subgroup and the white subgroup. If the effect is not present for one group, you have a partial corufounder, where the relationship benareen the two variables is present only for certain groups. If the relationship goes away *ir.n you ,..o,rrrt for this new variable: 1rou have found a confounder,
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Dataset Description
Monitori ng the f utu re 2A13 grade 10,sav
This dataset contains variables f rom the 2013 Monitoring the Future (MIF) study. This dataset covers a national sample of tenth graders, with a f ocus on monitoring substance use and abtrse.
Variable Name Description
An ordinal variable where 0 indicates that both parents have high school educations or greater, '1 indicates that one parent has less than a high school education, and 2 indicates that both parents have less than a high school indication
A binary variable based on a question asking if the respondent had ever been suspended from school, whereO = no, 1 = yes
Race dichotomy where 0 = nonwhite, 1 = whiteWhite
178
