Reading I NEED HELP ON MY HOMEWORK
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Sara Prot and Craig A. Anderson
Th e 20th century witnessed a mass media explo- sion after the invention of television, digital com- puters, and the Internet. Th is rapid technological development was followed by rapid growth in the fi eld of media psychology.
Researchers have gone from asking relatively sim- ple, basic questions such as, “Does observing fi lmed aggression increase aggressive behavior?” (Bandura, Ross, & Ross, 1963a) to asking complex and highly specifi c questions, such as, “Th rough which cogni- tive and aff ective mechanisms do violent media exert their infl uence on aggression?” (Anderson et al., 2003), “How robust and consistent are media violence eff ects on diff erent outcomes?” (Anderson & Bushman, 2001; Anderson et al., 2010) and “What are the long-term consequences of habitual media violence exposure?” (Huesmann et al., 2003; Bartholow, Bushman, & Sestir, 2005).
Th is chapter off ers a broad review of contemporary methodology used in the fi eld of media psychology
Abstract
This chapter provides an overview of contemporary research methods used in the field of media
psychology. Basic scientific principles are discussed. Commonly used research designs are described.
Some methodological pitfalls in media psychology research are explained and suggestions are given on
how to avoid them. Finally, guidelines are given on how to convey scientific methodology and findings
to the general public (see Chapter 26). We hope that this chapter will aid readers from other fields in
becoming informed consumers of media psychology research and aid media psychology researchers in
continuing the trend toward better methodological quality in the field.
Key Words: media psychology, research designs, research methods
in studying the eff ects of exposure to media violence on the consumer of such media. Although the basic prin- ciples and ideas described here apply more broadly to other domains of media-related research, such as motivations underlying media choices and prefer- ences (e.g., Ryan, Rigby, & Przybylski, 2006), we focus on the eff ects of exposure domain—and within this domain, we focus on media violence eff ects.
We discuss basic scientifi c principles that are at the foundation of all psychological research. An overview of widely used research designs is given. Common methodological pitfalls in media psychol- ogy are described as well as some suggestions on how to avoid them. Finally, guidelines are given on how to convey scientifi c methodology and fi ndings to the general public. We hope that this chapter will aid media psychology researchers in continuing the trend toward better methodological quality in the fi eld, aid journal editors and reviewers in doing a better job of screening out weak and promoting
7 C H A P T E R
Research Methods, Design, and Statistics In Media Psychology
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strong research, and aid readers from other fi elds in becoming informed consumers of media psychology research.
Science, Causality, and Media Psychology Empirical Research and Th eory Development test/revise/test/revise cycle
Research in the fi eld of media psychology can generally be divided into two approaches: quanti- tative and qualitative. Qualitative methods (e.g., content analyses, ethnographic studies and phe- nomenological studies) generate descriptive fi nd- ings and are usually conducted without forming a priori hypotheses (for a discussion of qualitative methods see Chapters 8 and 23). Th e majority of media eff ects research, however, is quantitative and follows a diff erent pattern, progressing through a cyclic interaction between theory and empirical research. Researchers identify a question of inter- est (e.g., What eff ects does media violence have on viewers?). One or more hypotheses are generated (e.g., Observing media violence will increase the likelihood of later aggression. Exposure to media violence will decrease helping.) and tested using multiple research methods. Empirical results lead to revisions and refi nement of the original hypotheses. Over time, a set of related hypotheses and empirical fi ndings is developed, a set that can be integrated into a larger conceptual model or theory. Th e theory can then be used to develop novel hypotheses that can be tested further through empirical research. Th e cycle is repeated, leading to further refi nement of the theory. Th is extensive test/revise/test/revise process leads to the development of theoretical mod- els based on sound principles which are unlikely to be invalidated by future research. For example, the general aggression model (GAM) (Anderson & Bushman, 2002b; Anderson & Huesmann, 2003; DeWall & Anderson, 2011) and the general learn- ing model (GLM) (Buckley & Anderson, 2006; Barlett, Anderson, & Swing, 2009; Gentile et al., 2009) integrate a number of earlier models and are based on more than 100 years of psychologi- cal research on learning, emotion, cognition, and behavior. Well-tested models such as these provide a solid foundation for interpreting fi ndings, mak- ing new predictions, and developing interventions. Nonetheless, specifi c interpretations can always be changed as a result of new discoveries. It is for this reason that scientists are reluctant to use the words fact, or proven, or truth, even when speaking with audiences and individuals who do not understand
this perpetual cycle of theory and data. Th us, the general public may view the “theory” of evolution as a mere guess or hypothesis, whereas the scientifi c community knows that the basic tenants of the the- ory are as well established and as factual and basic as the law of gravity. Th is diff erential understand- ing of the meaning of “theory” and other common words leads to much unnecessary miscommunica- tion among scientists and nonscientists, a topic that is addressed in a later section of this chapter.
translations from conceptual to empirical
One frequently overlooked (or underevaluated) aspect of scientifi c theory development and testing concerns the multiple translations that take place between the conceptual/theoretical level and the spe- cifi c procedures used to conduct empirical tests. Th at is, one must translate the conceptual hypothesis into specifi c empirical realizations of the independent and dependent variables (Carlsmith, Ellsworth, & Aronson, 1976; Anderson & Anderson, 1996). Figure 7.1 illustrates some of the multiple levels and translations that underlie an experimental manipula- tion of violent versus nonviolent violent game expo- sure. As can be seen, there are lots of levels between the most basic (and therefore the conceptually broad- est) theoretical level and the specifi c manipulation that a researcher creates in an empirical study. Keep in mind that a similar set of translations are needed to get from the conceptual dependent variable (e.g., aggression) and its empirical realization. Th us, there are lots of ways one can test the same conceptual hypothesis. Furthermore, although theory provides many constraints on what should be considered reasonable tests of any given conceptual hypothesis, there is no such thing as a perfect empirical realiza- tion of that hypothesis. For this reason, multiple studies using multiple methods give a better overall picture of the validity of any conceptual hypothesis than any single method or study can give. Further discussion of this appears in the next section.
Causality Th e majority of scientifi c theories and models in
nomothetic scientifi c disciplines (those that seek to uncover general laws that underlie phenomena, such as natural sciences and psychology; M ü nsterberg, 1899) are causal. Widely used theories in media eff ects psychology such as social learning theory and social cognitive theory (Bandura, 1973, 1983), general aggression model (Anderson & Bushman, 2002b; Anderson & Huesmann, 2003), cultivation
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theory (Comstock & Scharrer, 2007), and social information processing theory (Crick & Dodge, 1994) all imply causal relationships among vari- ables. Th e central characteristics of any good theory, the ability to predict and control outcomes, require causal models. Of course, establishing causality is often a diffi cult task, one that is seldom understood by public policy makers or the general public, and too often is misunderstood even by members of the scientifi c community. What follows is a partial list- ing of the most common diffi culties.
scientific causality is probabilistic Th e old Logic 101 principles of establishing cau-
sality do not apply to most modern science (Anderson & Bushman, 2002a). Scientifi c causality is probabilis- tic, instead of “necessary and suffi cient.” Stating that X causes Y means that variable X causes an increase in the likelihood of outcome Y (Anderson, 2004). For example, saying that smoking causes lung cancer means that smoking increases the likelihood of devel- oping lung cancer. Th is does not mean that all smok- ers get lung cancer; many do not (a violation of the principle of “suffi cient” causality). Furthermore, some nonsmokers do get lung cancer (a violation of the principle of “necessary” causality). Correspondingly, saying that violent video games cause aggression does not mean that every person who plays violent video games will necessarily become aggressive, or that all aggressive behavior is a result of violent video game play. It means that exposure to violent video games increases the likelihood of future aggression.
Probabilistic causality is a result of the fact that most (if not all) biological outcomes, disease pro- cesses, and human behaviors are multicausal (Gentile & Sesma, 2003). Complex behaviors of interest, such as prosocial behavior and aggression, are infl u- enced by a large number of factors (e.g., genetic pre- dispositions, parental practices, cultural infl uences) (Anderson & Huesmann, 2003; DeWall, Anderson, & Bushman, 2012). Media use is just one of many relevant factors that infl uence the likelihood of these behaviors. In most cases, it is neither a necessary nor a suffi cient cause. Nonetheless, media eff ects are not negligible and have important practical consequences in many domains, including aggression among oth- ers (Anderson & Dill, 2000; Gentile et al., 2004; Anderson et al., 2010), helping (Greitemeyer, 2009; Greitemeyer & Osswald, 2010), risk taking (Fischer et al., 2011), and school performance (Sharif & Sargent, 2006; Anderson, Gentile, & Buckley, 2007; Rideout, Foehr, & Roberts, 2010).
A methodological diffi culty in the fi eld of media psychology stems from the fact that many media eff ects are subtle, cumulative, and unintentional. For example, advertisements can have a subtle infl u- ence on viewers without their awareness (Gentile & Sesma, 2003). Although such short-term infl u- ences may be small, over time they can produce large cumulative eff ects. To use the cigarette smok- ing analogy, although short-term eff ects of smok- ing are relatively harmless and transient, long-term cumulative eff ects of this risk factor are lasting and severe. Likewise, although eff ects of watching
Learning Theory
Social Learning
Other types of Learning
Direct Experience
Observational Learning
Other Observational
Sources
Stories
Video Games
Violent
Nonviolent
IV Empirical Realization:
Specific games,
instructions, context
Stories
Other Types
Figure 7.1 Illustration of Multiple Translation Levels from Learning Th eory to Empirical Realization of the Independent Variable: Experimental Manipulation of Video Game Violence.
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a single violent TV show dissipate fairly quickly, habitual exposure to violent media has long-lasting eff ects on desensitization to violence (Bartholow, Bushman, & Sestir, 2005), hostile attribution biases (Anderson, Gentile, & Buckley, 2007), development of an aggressive personality (Bartholow, Sestir, & Davis, 2005), and aggressive behavior (Huesmann, Moise-Titus, Podolski, & Eron, 2003; Anderson, Sakamoto, Gentile, Ihori, Shibuya, Yukawa, Naito, & Kobayashi, 2008; M ö ller & Krah é , 2009).
An interesting solution to the methodological diffi culty of studying cumulative eff ects of media exposure is proposed by Potter (see Chapter 23). Th e author suggests that, instead of measuring group diff erences in eff ects of media exposure, as is done in the majority of media eff ects studies, attention should be shifted to patterns of eff ect score changes for individuals over time. Th is approach would allow researchers to directly examine the course of long-term changes produced by media infl uences, identifying how mass media infl uences gradually change a person’s baseline. Indeed, this is essentially what longitudinal studies of media violence do (e.g., Huesmann, Moise-Titus, Podolski, & Eron, 2003; Anderson, Sakamoto, et al., 2008).
role of plausible alternative explanations
Testing scientifi c theories largely involves creat- ing alternative explanations for a given phenomenon and then empirically testing whether the originally hypothesized relations among variables fi ts the data better than the alternative explanation. In essence, establishing causality involves testing and ruling out plausible alternative explanations. We emphasize “plausible” because the total number of alternative explanations—plausible + implausible—approaches infi nity. Furthermore, only alternative explanations that are empirically testable (at least in principle) qualify as plausible. Alternative explanations that cannot be empirically tested (e.g., god did it) usu- ally fall outside the realm of science. Of course, technological advances often create opportunities to test alternative hypotheses that previously had been untestable, which is why the “in principle” aspect of plausible alternative explanations is important. For example, recent advances in genetics and in neuroimaging have allowed tests of numerous new hypotheses about aggression and violence (DeWall, Anderson, & Bushman, 2011, 2012).
Relevant empirical results can cast doubt on alternative explanations and lend support to the tar- get theory. Or, such tests can support an alternative
explanation, thereby pointing to parts of the theory that need further revision. As the number of plausi- ble alternative explanations is reduced, the strength of the remaining theoretical explanation increases.
triangulation and alternative explanations
No single test of a theory-based hypothesis is defi nitive, irrespective of whether it confi rms or disconfi rms the prediction (Anderson & Anderson, 1996). One reason for this is because theoretical models involve abstract conceptual variables, whereas empirical tests involve concrete operationalizations of those variables (Carlsmith, Ellsworth, & Aronson, 1976). In other words (and as noted earlier), there are multiple levels of interpretation and specifi ca- tion between the theoretical model and empirical tests of the implications of that model (see Anderson & Anderson, 1996, for an example concerning the heat/aggression hypothesis). Operationalization of a conceptual hypothesis involves making several assumptions concerning the empirical methods being used (e.g., reliability and validity of the mea- sures, adequacy of the sample of variables and par- ticipants). Because of this, null results are often less informative than confi rming results, especially when new measures or procedures are used. Findings that are in line with theory-based predictions give sup- port not only to the target conceptual hypothesis, but also to various implicit assumptions made in the study. If, on the other hand, the study fails to support the hypothesis, a common reaction of researchers is to acknowledge that there are many possible reasons for those fi ndings. Th e unexpected results possibly refl ect the fact that the original hypothesis is wrong, but also might be a product of methodological weak- nesses of the specifi c study. Typically, for null results to be informative and result in a major change in theory they have to be replicated many times, shown to be not the result of mere poor methods or small samples, and have to lead to a more comprehensive theory that accounts not only for the null results but also accounts for the many results explained by the original theory (Kuhn, 1962). Unfortunately, occasional unreplicated null results based on small samples or poor methods, are frequently misinter- preted in the media violence domain as evidence of a lack of eff ects overall. Nonsignifi cant fi ndings from specifi c studies have been regularly used by media industry apologists to question the validity of stud- ies showing signifi cant harmful media eff ects, a criti- cism media violence scholars have faced many times (Huesmann & Taylor, 2003; Bushman, Rothstein,
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& Anderson, 2010). For example, one of the meth- odologically poorest media violence studies ever published (Williams & Skoric, 2005) is frequently promoted by the video game industry and gamers as proof that violent games don’t increase aggression. Th ey conveniently ignore that fact that that study didn’t measure aggression, had severe dropout rate problems, had diff erential dropout rates in the two conditions, and failed to show that the “violent” and “nonviolent” game conditions actually diff ered on the amount of exposure to violent games. 1
Far greater support for a conceptual hypothesis is given if conceptual relations are repeatedly tested and confi rmed using diff erent methodologies in diff erent contexts. Th is is the logic of multiple operationalism or triangulation (Campbell & Fiske, 1959; Anderson, 1987, 1989; Anderson, Gentile, & Buckley, 2007). Diff erent types of research designs make diff erent methodological assumptions, so if a conceptual rela- tionship is confi rmed time after time in studies using diff erent designs, it is extremely unlikely that the results are just a byproduct of methodological fl aws. Similarly, conceptual relationships that yield similar results using diff erent (but theoretically compatible) measures or manipulations greatly strengthen one’s confi dence in the basic conceptual model. When weaknesses of a particular type of study do not apply to other types, this enables researchers to triangu- late or home in on a true causal factor (Anderson, 1989). When a hypothesis survives many potential falsifi cations using varied methods, a robust eff ect is established. For example, Bandura’s initial fi nd- ings concerning the eff ect of televised violence on modeling of aggressive behavior may have been falsifi ed by several possible alternative explanations (Bandura, Ross, & Ross, 1961, 1963a). However, today researchers have no doubt that televised vio- lence increases aggression because this eff ect has been repeatedly shown using correlational studies (Eron, Huesmann, Lefkowitz, & Walder, 1972; McLeod, Atkin, & Chaff ee, 1972), experimental studies (Bjorkqvist, 1985; Josephson, 1987), and longitu- dinal studies (Huesmann, Moise-Titus, Podolski, & Eron, 2003). Th e interpretation of Bandura’s early studies has changed slightly as a result of changes in defi nitions of aggression. But our main point in this example is that when studies using various research designs and measures, done in a number of diff er- ent contexts and with samples from diverse popu- lations all converge on the same answer, we can be much more confi dent that this answer is indeed true. In the words of Richard Cardinal Cushing when asked about the propriety of calling Fidel Castro a
communist, “When I see a bird that walks like a duck and swims like a duck and quacks like a duck, I call that bird a duck” ( Th e New York Times, 1964).
Although this chapter is focused almost exclu- sively on quantitative research methods, it is impor- tant to emphasize that qualitative methods also play a signifi cant role in the fi eld of media eff ects, providing rich knowledge on the content of media messages and people’s individual experiences that cannot be obtained through experimentation or other forms of quantitative research (see Chapter 8). Also note that the line between qualitative and quantitative research is sometimes quite blurry.
Outcome Measures, Research Designs, and Review Types Outcome Measures
Choice of outcome measure is crucial to any study, both because it infl uences the likelihood that the study will yield useful results and because of the- oretical relevance. A measure of aggressive behavior that is appropriate in one research context may well be inappropriate in another. For example, a count of how often each child trips, pushes, or bites another child in a daycare setting can be a useful measure of physical aggression in that research context (i.e., young children at daycare), but would not be a valid measure of physical aggression for college students in a laboratory setting. A less obvious but equally important example frequently arises in the study of violent video game eff ects. Because violent video games involve a lot of physical aggression and almost no indirect or relational aggression, the dominant theoretical models of social learning and develop- ment all predict that playing such games is most likely to infl uence physical aggression. Measures of verbal and indirect aggression are unlikely to provide sensitive tests of the main hypothesis that exposure to violent video games increases the likeli- hood of aggressive behavior. Similarly, the measure of physical aggression has to match the age of the participants and the research context. For example, a measure of trait physical aggression in which the participant reports the frequency of aggressive acts over the past year is inappropriate as the main out- come measure in a short-term experimental study in which participants have just played a randomly assigned violent or nonviolent video game. Th e recent game play cannot change the frequency of aggressive acts that the person committed in the year before the game play, unless of course time travel is involved. Of course, such a trait physical aggression measure might be infl uenced by the content (violent
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versus nonviolent) of a recently played game, but in such a case it would represent some type of memory or reporting bias, not a true measure of the video game eff ect on physical aggression (Anderson & Bushman, 2001). Yet, several short-term experimen- tal studies have used traitlike measures of aggression as the main dependent variable.
It is impossible to succinctly describe all of the measures that have been used or could be used in the study of the eff ects that media have on consum- ers. We focus here on a few of the measures related to antisocial eff ects (e.g., aggressive behavior, cogni- tion, and aff ect) and to prosocial behaviors, cogni- tions, and aff ect.
aggressive behavior measures Because defi nitions of conceptual variables such
as “aggression” and “violence” diff er somewhat between disciplines and even over time, clarity of defi nition is critical in theory development and in translating conceptual variables into empirical real- izations (e.g., Carlsmith et al., 1976). Social psy- chologists have come to rely on a specifi c defi nition that is much narrower than what is used by the gen- eral public and in some other areas of psychology. Specifi cally, human aggression is “ . . . any behavior directed toward another individual that is carried out with the proximate (immediate) intent to cause harm. In addition, the perpetrator must believe that the behavior will harm the target, and that the tar- get is motivated to avoid the behavior” (Anderson & Bushman, 2002b, p. 28; see also Berkowitz, 1993; Baron & Richardson, 1994; Geen, 2001). Aggression and aggressive behavior are used inter- changeably throughout this chapter. It is important to note that aggression is always a behavior; it is not an emotion, thought, or desire. Also note that it is not the outcome of a behavior that defi nes it as aggressive or not, but the intent of the behavior, that is, the intent to harm. Th us, shooting an arrow at another person with the intent to harm them is an act of aggression, regardless of whether the arrow strikes or missed the target person. A shortcoming of many media eff ects studies arises from failure to use this defi nition.
Physical Aggression in a Lab Setting Numerous methods have been developed that
allow direct observation and measurement of aggres- sive behavior in laboratory settings. A common pro- cedure used to measure physical aggression is the teacher/learner paradigm , sometimes known as the Buss aggression machine paradigm (Buss, 1961; Geen
& O’Neal, 1969; Milgram, 1974; Donnerstein & Berkowitz, 1981). In this procedure, participants are told that purpose of the study is to explore eff ects of punishment on learning. Th ey are paired with a supposed second participant (actually a con- federate). Th e real participant is selected to be the “teacher” and the confederate is selected to be the “learner.” Th e participant presents stimuli to the confederate who seemingly tries to learn them. When the “learner” gives an incorrect response, the participant is supposed to punish him or her with an electric shock. Aggression is measured by the intensity and/or the duration of the shock the par- ticipant chooses to give the confederate. For exam- ple, Donnerstein and Berkowitz (1981) used this procedure to measure eff ects of combining violent and sexual content on aggression of males toward a female target. Participants who had viewed a violent, sexual fi lm delivered shocks of a higher intensity to a female “learner” than did those who viewed fi lms containing only violent or sexual content. Th ere have been many variations of this task, including use of diff erent types of punishments (e.g., hand in ice water instead of electric shock) (Ballard & Lineberger, 1999) and diff erent rationales for why the participant is delivering punishments (Baron & Richardson, 1994, pp. 69–75).
Another common method of measuring physi- cal aggression in the laboratory is the competitive reaction time task (Taylor, 1967; Bushman, 1995; Giancola & Parrott, 2008). Participants in this task compete against a supposed opponent on a reac- tion time task in which the winner delivers aversive stimulation (an electric shock or a noise blast) to the loser. In actuality, the pattern of wins and losses is predetermined by the experimenter. Provocation can be manipulated by increasing the intensity of shocks set by the “opponent.” Aggression can be measured as the intensity, duration, or number of high-intensity blasts given. For example, Anderson and Carnagey (2009) used this paradigm to test the eff ects of violent and nonviolent sports video games on aggression. Th ey found that playing violent sports games increased aggressive behav- ior, even after controlling for competitiveness. In other words, competitive reaction time task mea- sures aggression, not competitiveness (Gaebelein & Taylor, 1971; Bernstein, Richardson, & Hammock, 1987). Like the teacher/learner paradigm described in the preceding, the competitive reaction time task has been used in various modifi ed forms in hun- dreds of studies, and is one of the most extensively validated measures of physical aggression.
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Another commonly employed method to study direct physical aggression is to place the participant and the confederate in a situation that requires the confederate to evaluate the participant and later requires the participant to evaluate the confederate. In the evaluation paradigm (Berkowitz, 1962), for example, participants are led to believe that they will be evaluating another student’s performance on an assigned task. Solutions are evaluated using any- where from one to ten electric shocks, in which one shock indicates a very favorable evaluation and ten shocks indicates a very unfavorable evaluation. In some studies, the confederate evaluates the partici- pant’s solution. Generally, half of the participants receive a positive evaluation from the confederate (e.g., one shock), whereas the other half receive a negative evaluation (e.g., seven shocks). After expo- sure to some treatment (e.g., a violent or nonviolent fi lm), the participant then evaluates the confeder- ate’s solution. Th e measure of aggression is the num- ber of shocks the participant gives the confederate.
Barlett, Branch, Rodeheff er, and Harris (2009) used a more recently developed laboratory mea- sure of physical aggression, the hot sauce paradigm (developed by Lieberman, Solomon, Greenberg, & McGregor, 1999) to measure how long the eff ects of brief exposure to violent video games persist. In this procedure, participants decide how much hot sauce another person (known to dislike spicy food) must consume. Alternatively, one can have the participant determine the degree of hotness of the sauce that the other person must consume. Aggression is measured as the amount of hot sauce given to the target and/ or the degree of hotness of the sauce selected.
Indirect, Verbal, and Other Laboratory Aggression Measures
Some laboratory based studies use verbal aggres- sion measures. For example, in some studies the participant is given the opportunity to provide a potentially harmful written or verbal evaluation of another person (e.g., another participant, a confed- erate, or the experimenter), and does so knowing that the evaluation could hurt the other person. Sometimes the verbal aggression is direct, meaning that the participants believe that the target of their harmful evaluations will see or hear it. For exam- ple, Wheeler and Caggiula (1966) had participants listen and later evaluate another person’s (actually, a confederate’s) extreme and socially undesirable statements. Th e participants believed that the other person would hear their evaluations, so anything negative in the evaluations would presumably cause
some harm. Th ese evaluations were recorded and later coded for the degree of hostility.
Sometimes the evaluation is in the form of rat- ings that the target will not see, but that the par- ticipant believes will harm the target indirectly . For example, Berkowitz (1970) randomly assigned some female undergraduates to an anger induction con- dition (in which they listened to a job applicant’s insulting statements about university women) or a control condition. Half in each condition then lis- tened to either a hostile or a nonhostile comedian. All participants then rated the job applicant on sev- eral measures, with the knowledge that their ratings could aff ect the applicant’s chances of getting the job. Interestingly, the women who had heard the hostile humor gave the applicant worse ratings than those who had heard the neutral humor. Other simi- lar indirect verbal aggression measures have ranged from ratings of competence, to liking, job perfor- mance, and grades (Obuchi, Kameda, & Agarie, 1989; Dill & Anderson, 1995).
Perhaps the most recent addition to the list of lab- oratory aggression tasks is the tangram task (Gentile et al., 2009). In one study Gentile et al. randomly assigned participants to play a violent video game, a prosocial video game, or a game that was neither violent nor prosocial. Later, participants assigned an anonymous partner a set of 11 easy, moderately complex, or diffi cult tangram puzzles to attempt to solve within 10 minutes. Participants were led to believe that the partner would win a prize if they completed a suffi cient number of puzzles in 10 min- utes. Th e number of hard puzzles chosen constituted a measure of aggression, whereas the number of easy puzzles measured helping behavior. As expected, the violent video games increased aggressive choices, whereas the prosocial games increased helpful choices. Because this measurement task is the new- est, it has received less empirical attention that the older measures described earlier, and thus does not yet have the extensive network of validation studies.
Aggression Measures Outside the Lab Th e variety of ways that one can measure aggres-
sive behavior outside of controlled laboratory setting is huge, limited only by the combination of the con- ceptual defi nition and the creativity of researchers. Generally, they can be categorized as self-reports, other reports, and archival.
Self-reports may be very specifi c, such as report- ing how many physical fi ghts one has been in during the past school year. Or, they may be broad trait- like measures of habitual aggressiveness. Th ey may
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include any type of aggression (e.g., verbal, physi- cal) at any severity level (e.g., said mean things about a classmate, attacked a peer with a knife or gun). Common self-report measures of trait aggression in the media eff ects domain include the physical and verbal aggression subscales of the Buss and Perry (1992) Aggression Questionnaire and the physical violence subscale from the National Youth Survey (Elliot, Huizinga, & Ageton, 1985; Anderson & Dill, 2000). Other commonly used self-report trait aggression scales that include relatively more items that are not strictly aggressive behaviors are the Caprara Irritability scale (Caprara et al., 1985) and the Cook-Medley Hostility Inventory (Cook & Medley, 1954). Of course, there are many self-report measures, and researchers create new ones as the empirical and theoretical need arises.
Others’ reports of aggression include a wide range of measures, usually subcategorized into peer reports, teacher/supervisor reports, parent reports, and direct observation. Peer reports are frequently used in pre– high school settings. Often these involve asking each student in a classroom to rate each of their classmates on specifi c behaviors, or to nominate classmates who do certain aggressive behaviors. For example, it is common to ask, “Who pushes, shoves, or hits other kids to get what they want?” Teacher and supervisor reports ask similar questions about those under their care or supervision. Parent reports often ask about the frequency with which their child has done specifi c aggressive behaviors; other parent reports are vaguer, asking for ratings of “how aggressive” is your child. Direct observation studies often involve the record- ing of behavior in some naturalistic setting, followed by standardized coding of the recorded behavior. Sometimes, however, trained observers watch and code behaviors directly in the setting, such as while watching children on a playground.
Archival measures are derived from written records, such as crime reports and school incident records. Frequently archival measures are combined with other types of aggression measures.
aggressive cognition measures Exposure to violent media has a host of cognitive
consequences, which in turn can lead to aggressive behavior. A number of outcome measures have been used to assess infl uences of violent media on cogni- tion in both short- and long-term contexts.
Aggressive Cognition in Lab Settings Laboratory experiments measure short-term
infl uences of exposure to violent media on cognitive
processing. Such short-term eff ects mainly occur through priming of aggressive knowledge struc- tures, making them more accessible (Anderson & Huesmann, 2003). Various methods have been successfully used in laboratory settings to measure these increases in aggressive thinking.
A number of studies have shown an increased frequency of aggressive thought content during or immediately after media violence exposure. For exam- ple, Calvert and Tan (1994) used a thought-listing questionnaire to measure diff erences in aggressive thoughts while observing or playing a violent game in virtual reality. In a study by Bushman (1998), par- ticipants made free associations to nonaggressive words and to homonyms with one meaning more aggressive than the other (e.g., cuff , mug). More aggressive associations were made to both types of words by participants who had just watched a violent video.
Several studies have used a word completion task to measure accessibility of aggressive thoughts (Anderson, Carnagey, & Eubanks, 2003; Anderson, Carnagey, Flanagan,, Benjamin, Eubanks, & Valentine, 2004; Barlett et al., 2008). In this kind of task, participants are given a list of word frag- ments and are asked to fi ll in the missing letters to form the word. Some of the fragments can be completed to form either an aggressive word or a nonaggressive word (e.g., “h_t” can become hit or hat ). Aggressive thought accessibility can be calcu- lated as the proportion of word completions that were aggressive. Similar tasks have been commonly used to measure implicit memory (e.g., Roediger, Weldon, Stadler, & Riegler, 1992), and have been used to assess accessibility of prosocial thoughts as well (e.g., Greitemeyer, 2011).
A number of studies have used reading reaction times to aggressive and nonaggressive words as a measure of accessibility of aggressive cognitions (also called the word pronunciation task ) (e.g. (Bushman, 1998; Anderson & Dill, 2000; Anderson, Carnagey, & Eubanks, 2003). In the reading reaction time task (e.g. (Anderson et al., 1996; Anderson, 1997; Anderson, Benjamin, & Bartholow, 1998), partici- pants are timed as they read aggressive and nonag- gressive words. Average reaction times to aggressive and nonaggressive words can be compared to assess relative accessibility of aggressive thoughts. An advan- tage of this task is that suspicion or hypothesis-related demand characteristics are unlikely to infl uence responses because participants are taxed with trying to read all words as quickly as possible (Anderson, 1997). Furthermore, attempts by suspicious partici- pants to bias the results in either direction can be
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detected by examining the distribution of reaction times, because such biasing attempts typically yield unusually long reaction times.
In a somewhat diff erent approach, Uhlmann and Swanson (2004) measured the eff ects of violent video game play on automatic aggressive thoughts using the implicit association test. Th is study showed that media violence exposure can teach a person to automatically associate the self with aggressive traits and actions. More recently, Saleem and Anderson (in press) have used another version of this task to assess anti-Arab bias.
Interesting methods have been used to assess cog- nitive biases that result from media violence expo- sure. For example, to assess hostile expectation bias Bushman and Anderson (2002) had participants read ambiguous story stems about potential inter- personal confl icts. Participants were then asked to list what the main character will think, feel, say, and do next and their responses were coded for aggres- sive content. Several media eff ect studies (Kirsh, 1998; Anderson, Gentile, & Buckley, 2007; M ö ller & Krah é , 2009) have also used ambiguous provoca- tion stories to assess hostile attribution bias. In each story, an actor causes a negative event to happen, but the intent of the actor is unclear. After each story, participants are asked a series of questions concern- ing the provocateur’s intent. It has been shown that exposure to media violence leads to the development of a hostile attribution bias, a tendency to interpret ambiguous behaviors of others as malevolent (Kirsh, 1998).
Yet another method of assessing accessibility of aggressive cognitions is the word pair similarity rating task. Th is task was originally developed by Bushman (1996) to assess individual diff erences in aggressive cognitive-associative networks. But a minor revision to the task has been used to examine the eff ects of short-term experimental manipulations of variables, including pain (K. Anderson, Anderson, Dill, & Deuser, 1998), cooperative versus competi- tive video game instructions (Anderson & Morrow, 1995), and violent versus nonviolent music lyrics (Anderson, Carnagey, & Eubanks, 2003). Th is task consists of rating the degree of meaning similarity of each paired combinations of 20 words. Ten of these words have both aggressive and nonaggressive con- notations (e.g., bottle, night, stick). Th ese words are referred to as ambiguous words. Th e remaining ten words are more obviously related to aggression (e.g., butcher, choke, hatchet). Ratings of each word pair are made on a 1 to 7 scale of how “similar, associ- ated, or related” they are. Each participant gets three
scores, the average similarity rating of all ambiguous/ aggressive word pairs, ambiguous/ambiguous pairs, and aggressive/aggressive word pairs. Anderson, Carnagey, and Eubanks (2003) found that partici- pants who had just listened to songs with violent lyrics gave higher similarity ratings to ambiguous/ aggressive word pairs than did participants who had just listened to nonviolent songs. In other words, the violent lyrics increased the accessibility of the aggres- sive meaning of the ambiguous word pairs.
Aggressive Cognition Outside the Lab Correlational studies and longitudinal studies
provide an opportunity to explore long-term infl u- ences of violent media on cognition. Repeated expo- sure to media violence strengthens aggression-related knowledge structures and can make them chroni- cally accessible. Additionally, long-term exposure reinforces normative beliefs that violence is com- mon and appropriate (Carnagey & Anderson, 2003; Bushman & Huesmann, 2006). Dependent variables in correlational and longitudinal studies of aggres- sive cognition often include normative beliefs about violence (Gerbner, Gross, Jackson-Beeck, Jeff ries- Fox, & Signorelli, 1978; Gerbner, Gross, Morgan, & Signorelli, 1980; Bryant, Carveth, & Brown, 1981), positive attitudes toward violence (Funk et al., 2004; Anderson, Gentile, & Buckley, 2007) and hostile attribution bias (Anderson, Gentile, & Buckley, 2007). Th ese long-term consequences are can be assessed using self-report measures, such as the Normative Aggressive Beliefs Scale (Anderson, 2004; Anderson, Gentile, & Buckley, 2007), Huesmann’s NOBAGS scales (Huesmann et al., 1992), Funk’s Attitudes toward Violence Scales (Funk, Elliott, Urman, Flores, & Mock, 1999), and the Revised Attitudes toward Violence Scale (Anderson, Benjamin, Wood, & Bonacci, 2006). Some studies also use trait measures of aggressive cognition, such as the hostility subscale of the Buss-Perry Aggression Questionnaire (Anderson, Carnagey, Flanagan, Benjamin, Eubanks, & Valentine, 2004; Shibuya, Sakamoto, Ihori, & Yukawa, 2004; Bartholow, Sestir, & Davis, 2005).
aggressive affect measures Another route through which violent media
can increase aggression is by producing feelings of anger and hostility (Anderson et al., 2003; Swing & Anderson, 2010). Brief exposure to media vio- lence has been shown to lead to temporary increases in aggressive aff ect (Barlett et al., 2009), whereas chronic exposure leads to the development of a
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hostile personality (Bartholow, Sestir, & Davis, 2005; Bushman & Huesmann, 2006).
Aggressive Aff ect in Lab Settings Experimental studies in laboratory settings mea-
sure eff ects of media violence exposure on short-term aff ective states. Short-term aff ective consequences are most often assessed using self-report scales such as the State Hostility Scale (SHS) (Anderson, Deuser, & DeNeve, 1995), the Multiple Aff ect Adjective Checklist (Zuckerman, 1960; Zuckerman, Lubin, Vogel, & Valerius, 1964), or the State Anger sub- scale of the State-Trait Anger Expression Inventory (STAXI) (Spielberger, 1988). Many other studies have used the Positive and Negative Aff ect Schedule (PANAS) (Watson, Clark, & Tellegen, 1988). Th is widely used self-report scale has the advantage of assessing both positive and negative aff ect, as well as several more specifi c subtypes of aff ect. However, it is a less sensitive measure of hostility/anger, most likely because of fewer items for this more specifi c aff ective state (Anderson, Deuser, & DeNeve, 1995; Anderson, Anderson, & Deuser, 1996; Anderson, Anderson, Dorr, DeNeve, & Flanagan, 2000).
Such self-report measures can be complemented with physiological indicators such as heart rate, blood pressure, or skin conductance (Ballard, Hamby, Panee, & Nivens, 2006; Carnagey, Anderson, & Bushman, 2007). Additionally, researchers have started examining neural bases of short- and long- term media eff ects on emotional processing by using techniques such as magnetic resonance imaging (Weber, Ritterfeld, & Mathiak, 2006) and event- related brain potentials (Bartholow, Bushman, & Sestir, 2005; Bailey, West, & Anderson, 2011a).
Aggressive Aff ect Outside the Lab Long-term changes in aff ective processing as a
result of habitual media violence exposure can be assessed outside the laboratory using trait measures such as the Caprara Irritability Scale (CIS) (Caprara et al., 1985), the Cook-Medley Hostility Inventory (Cook & Medley, 1954), and the anger subscale of the Buss-Perry Aggression Questionnaire (Buss & Perry, 1992). Once again, more general trait-aff ect scales may be appropriate in some research contexts, but researchers need to be aware that general mea- sures of positive and negative aff ect usually are less sensitive measures of any give specifi c aff ect type.
physiological arousal measures For most people, exposure to media violence
tends to produce physiological arousal (Anderson
et al., 2003; Swing, Gentile, & Anderson, 2008). Arousal can be measured in experimental studies using indicators such as heart rate, blood pressure, or skin conductance (Ballard & Wiest, 1996; Fleming & Rickwood, 2001; Anderson et al., 2004; Barlett et al., 2008).
How lasting are these eff ects? Barlett et al. (2009) showed that heightened arousal immediately after playing a violent video game lasts between 4 and 9 minutes. However, these short-term changes can start aggression promoting processes that last much longer than 4 to 9 minutes, such as long-term desen- sitization to violence. Even within a short-term con- text, exposure to violent media may increase arousal (and hostile aff ect) for longer periods of time if the violent media episode increases processes that typi- cally last long and that increase anger arousal, such as rumination on a perceived unjust harm.
A popular belief in our culture is that playing violent video games or watching violent television and fi lms allows people to “vent” their aggression, decreasing arousal and reducing subsequent aggres- sive behavior (Anderson, Gentile, & Buckley, 2007). According to the catharsis hypothesis, engaging in real or imagined aggression helps relieve angry feel- ings, leaving us emotionally calmed (Dollard et al., 1939; Campbell, 1993). However, the bulk of research evidence opposes the catharsis hypothesis (Mallick & McCandless, 1966; Geen, Stonner & Shope, 1975; Geen & Quanty, 1977; Bushman, Baumeister, & Stack, 1999; Geen & Quanty, 1977Bushman, 2002). Although physiological arousal can decrease after the initial aggressive act, later aggressive behavior does not (Geen & Quanty, 1977). Instead, studies show that viewing, think- ing about or performing aggressive acts increases the likelihood of aggressive behavior (Dill & Dill, 1998; Geen, 2001).
desensitization/empathy measures Repeated exposure to violence can lead to desen-
sitization, best defi ned as a reduction in emotional and physiological reactivity to violence (Carnagey, Anderson, & Bushman, 2007). Empathy can be defi ned as the degree to which a person identifi es and commiserates with a victim and feels emotional distress (Anderson et al., 2010). A small number of high-quality studies exist in this domain (Anderson et al., 2010). However, media violence has been clearly linked to both short-term desensitization as a result of brief exposure (Carnagey, Anderson & Bushman, 2007), and chronic desensitization and decreased empathy as a result of habitual, long-term
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exposure (Mullin & Linz, 1995; Funk et al., 2003; Bartholow, Bushman, & Sestir, 2006).
Short-Term Eff ects on Desensitization/Empathy Desensitization to violence after brief periods of
exposure is typically explored in experimental stud- ies using physiological indicators such as heart rate, blood pressure, and galvanic skin response (Th omas, Horton, Lippincott, & Drabman, 1977; Linz, Donnerstein, & Adams, 1989; Carnagey, Anderson & Bushman, 2007). For example, participants in the Carnagey et al. (2007) experiment played a violent or nonviolent video game, and then watched fi lm clips of real violent behavior, including shootings, stabbings, and fi ghts. Heart rate and skin conduc- tance were recorded before and during video game play, and during observation of the violent fi lm clips. Both physiological indicators of emotional arousal increased in both game conditions while playing the assigned video games, but only those who had played a violent game showed decreases in arousal while watching the violent fi lm clips.
Long-Term Eff ects on Desensitization/Empathy Neurological evidence of chronic desensitiza-
tion to violence through playing video games also exists. Bartholow, Bushman, and Sestir (2005) found that habitual violent game players have reduced amplitudes of the P300 component of the event-related brain potential while viewing vio- lent images. Other laboratory studies have found similar eff ects (Kronenberger et al., 2005; Bailey et al., 2011a). Outside the laboratory, long-term eff ects on desensitization and empathy can be measured using self-report scales such as the Basic Empathy Scale (Jolliff e & Farrington, 2006), the Interpersonal Reactivity Index (Davis, 1980), the Index of Empathy for Children and Adolescents (Bryant, 1982) or Children’s Empathic Attitudes Questionnaire (Funk et al., 2008). Indeed, longi- tudinal studies have yielded evidence of long-term changes in desensitization/empathy as a result of media violence exposure (see Anderson et al., 2010, for the video game case).
prosocial behavior/helping measures Prosocial behavior involves helping or reward-
ing others, especially when this behavior brings no benefi t to the helper (Barlett, Anderson, & Swing, 2009). Eff ects of violent media on prosocial behav- ior have been less frequently explored than eff ects on aggression. In spite of this, several measures have been developed that make it possible to perform
reliable and valid measurement of prosocial behav- ior and helping.
Prosocial Behavior in Lab Settings Several procedures have been used in media vio-
lence research that allow direct observation and mea- surement of prosocial behavior in the laboratory. For example, Chambers and Ascione (1987) showed that children who had played a violent game donated less to charity. Ballard and Lineberger (1999) employed a variation of the teacher/learner paradigm in which participants could award jelly beans to their partner. Th e number of jelly beans awarded served as a mea- sure of helping and it was shown that participants who had just played a violent game tended to award a smaller number of jelly beans.
Bushman and Anderson (2009) simulated a fi ght in a laboratory experiment and found that partici- pants who had played a violent video game were less likely to help and took more time to help the “vic- tim.” Th ese participants perceived the fi ght as less serious and were less likely to notice the fi ght than the participants who played a nonviolent game.
Sheese and Graziano (2005) used a prisoner’s dilemma game in which participants were given a choice to cooperate with their partner for mutual gain, exploit their partner for their own benefi t or withdraw. Participants in the violent condition were signifi cantly more likely to choose to exploit their partner.
Gentile et al. (2009) developed a new task to measure helping—the previously mentioned tan- gram task . In this task, participants are asked to assign easy, moderately complex or diffi cult tan- gram puzzles to an anonymous partner. Participants are told that the partner will win a prize if they com- plete a suffi cient number of puzzles in 10 minutes. Th e number of easy puzzles represents a measure of helping behavior. Participants who had just played a prosocial video game assigned the most easy tan- grams, where as those who had just played a violent game assigned the fewest.
Prosocial Behavior Outside the Lab Th e most common type of measure chosen out-
side laboratory settings are self-report questionnaires such as the Prosocial Orientation Questionnaire (Cheung, Ma, & Shek, 1998). For example, a cor- relational study by Gentile et al. (2009) assessed video game habits of a large sample of children, along with several prosocial measures. Playing vio- lent video games was negatively related to helping behavior, whereas prosocial gaming was positively associated with helping.
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A longitudinal study by Anderson, Gentile, and Buckley (2007) measured children’s media violence exposure and prosocial behaviors twice during a school year and showed that video game violence at time 1 signifi cantly predicted a relative decrease in prosocial behavior over time. In this study, prosocial behavior was measured using teacher ratings and peer ratings.
Another less common measurement procedure is naturalistic observation. In an unusual fi eld experi- ment by Bushman and Anderson (2009), violent and nonviolent movie attendees saw a young woman with an injured leg struggle to pick up her crutches. Participants who had just watched a violent movie took longer to help than those who had just watched a nonviolent movie. Violent and nonviolent movie- goers did not diff er in their helpfulness before seeing the movie.
It is important to emphasize that prosocial and antisocial behaviors are not simply opposite sides of the same coin. Measures of aggressive and prosocial behavior tend to be negatively correlated, but not strongly so. One can be high both in helpful and in hurtful behaviors—for example, hostile toward ene- mies and kind toward friends (Gentile et al., 2009).
Research Designs Researchers generally use three broad types of
research designs: experimental studies, cross-sectional correlational studies, and longitudinal studies (Anderson & Bushman, 2001; Swing & Anderson, 2010). Each design has its own advantages and dis- advantages and is appropriate for certain kinds of research problems. Findings from diff erent kinds of studies complement each other and help researchers form a complete picture of media eff ects.
experimental studies Advantages
In experimental studies, researchers manipu- late exposure to media content and measure brief, short-term eff ects. Participants are randomly assigned to treatment and control groups; for example, play- ing a violent or nonviolent video game (Anderson & Dill, 2000). With all other factors controlled, a diff er- ence between two groups, for example, in aggression, establishes a causal link between violent media and subsequent aggression. Random assignment ensures that there are no preexisting diff erences between the two comparison groups (within certain statisti- cal limits) and allows researchers to rule out a host of alternative explanations. If a diff erence in aggres- sive behavior of the two groups is found, it is very
likely that this diff erence was caused by experimental manipulation (exposure to video game violence). It is very improbable (although not impossible) that highly aggressive individuals just happened to be ran- domly assigned to the experimental group and non- aggressive individuals were assigned to the control group. Th e larger the sample size, the less likely it is that a disproportionate percentage of highly aggres- sive people were randomly assigned to any one condi- tion, just as tossing a coin 100 times is less likely to yield 80% “heads” than tossing it only ten times.
If the researcher has additional information about the research participants before they are assigned to condition, information that may be relevant to the dependent variables of interest such as gender or trait aggressiveness, they may decide to “block” on these other variables in the random assignment pro- cedure. For example, they may separately random- ize males and females to the diff erent experimental conditions to ensure that each gender is represented equally across the conditions; but the logic and power of true experiments does not require this.
Methodologically sound experimental stud- ies in the fi eld of media psychology share several characteristics—they are designed so that they con- trol for many possible alternative explanations (i.e., high internal validity), have adequate sample sizes, employ eff ective experimental manipulation, and use a reliable and valid measure of the dependent variable.
High-quality laboratory experiments use well-validated paradigms to test relevant hypotheses. For example, Anderson and Dill (2000) conducted a laboratory experiment to test short-term eff ects of playing a violent video game on aggressive thoughts and behavior. In this study, a large sample of 227 college students participated. Participants were ran- domly assigned to play a violent or a nonviolent game. Games used in the study were carefully pretested and matched on several relevant dimensions (e.g., diffi - culty, frustration, and the physiological arousal lev- els they produce). Aggressive behavior was measured using a modifi ed version of the Competitive Reaction Time Task (Taylor, 1967), a widely used measure of aggressive behavior that has well-established internal and external validity (Carlson, Marcus-Newhall, & Miller, 1989; Anderson & Bushman, 1997; Giancola & Chermack, 1998; Anderson, Lindsay, & Bushman, 1999). Aggressive cognition was measured with a reading reaction time task that had been successfully used in previous aggression studies (Anderson, 1997; Anderson, Benjamin, & Bartholow, 1998) as well as in many studies in cognitive psychology. Violent
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video game play led to signifi cant increases in aggres- sive cognition and aggressive behavior. Th is study made an important contribution to the violent video game eff ects literature because previous experimental studies in this area had methodological weaknesses that put their results into question. A number of early experiments testing for violent video game eff ects (Cooper & Mackie, 1986; Silvern & Williamson, 1987; Schutte, Malouff , Post-Gorden, & Rodasta, 1988; Irwin & Gross, 1995) did not match violent and nonviolent games on important dimensions and thus could not rule out the possibility that other vari- ables such as arousal, diffi culty, or frustration caused the observed diff erence in aggressive behavior.
High-quality fi eld experiments use measures of real-life behavior in natural settings. For example, as mentioned earlier, Bushman and Anderson (2009) tested eff ects of media violence on helping behavior by staging a minor emergency outside movie the- aters that were showing either a violent or a nonvio- lent movie. Moviegoers saw a young woman with a wrapped ankle “accidentally” drop her crutches outside the theater and struggle to pick them up. Th e emergency was staged either before the movie (to control for helpfulness of people who choose to view violent versus nonviolent movies) or after the movie (to test for the eff ect of viewing media vio- lence on helping). In this case, the randomization was whether the measure of helpfulness occurred before or after viewing the movie. Before watch- ing a movie, no diff erences in helping were found between those going to a violent versus nonviolent movie. However, after the movie, participants who had just viewed a violent movie took signifi cantly longer to help the confederate than those who had viewed a nonviolent movie.
Disadvantages Th e main advantage of experimental studies is
that they enable strong causal inferences. A poten- tial disadvantage concerns the ability to generalize results to real-life conditions. Field experiments don’t suff er this concern. But, because most experi- ments are conducted in the laboratory, the general- izability of fi ndings from such studies to real-world settings is sometimes questioned. However, such doubts have been challenged and refuted both by rational arguments (e.g., Mook, 1983) and empiri- cal studies of external validity of laboratory experi- ments (e.g., Anderson & Bushman, 1997).
Th e main purpose of most laboratory studies is to explore conceptual relationships between variables and thus test and develop theories. Th e goal is to be
able to generalize these underlying theoretical prin- ciples, not specifi c features of the sample, manipula- tion, or measure (Berkowitz & Donnerstein, 1982; Henshel, 1980; Mook, 1983; Banaji & Crowder, 1989; Anderson & Bushman, 1997). Conceptual relationships between variables generalize, even if specifi c operationalizations do not.
Th e external validity of laboratory experiments is also supported by empirical fi ndings from several studies. For example, in the aggression domain it has been shown that laboratory measures of aggression are positively associated with each other, and that variables that infl uence aggression and violence in the real world have the same kind of eff ects on laboratory measures of aggression (Carlson, Marcus-Newhall, & Miller, 1989; Anderson & Bushman, 1997; Bushman & Anderson, 1998). Similarly, Anderson, Lindsay, and Bushman (1999) explored the consis- tency between fi ndings obtained in laboratory and fi eld settings across several domains in psychology (e.g., aggression, helping, leadership style, social loafi ng, self-effi cacy, depression, and memory). Th is study found considerable correspondence between lab- and fi eld-based eff ect sizes, suggesting that labo- ratory experiments have high external validity.
Laboratory settings also enable researchers to explore relationships between variables that may never be suffi ciently isolated in real life to enable precise testing (Mook, 1983). If increasing the similarity of the laboratory situation to real-world conditions interferes with the internal validity of the study, external dissimilarity (to achieve high internal validity) is strongly favored (Anderson & Bushman, 1997).
Th ere are two additional potential disadvantages of experimental designs in media eff ects studies. Both involve ethical considerations. First, one cannot ethically conduct an experiment in which one of the experimental treatments is expected to increase a seri- ously harmful behavior, such as aggravated assault or homicide. One can’t randomly assign a group of 10 year olds to play either a violent or nonviolent video game, then give each a handgun, and turn them loose on the playground to see which group does the most killing during recess. For this reason, alternative measures of aggressive behavior have been developed and used. Field experiments typically measure milder forms of physical aggression, such as hitting, pushing, shoving, and biting. Laboratory experiments use a variety of measures of aggression, including measures of physical and verbal aggression. And as noted ear- lier, these measures have been well validated, showing high levels of external validity.
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Th e second potential disadvantage of experi- mental designs in this domain concerns duration of the manipulation. It is not ethical to intentionally expose a group of participants to a long-term high media violence diet to see whether this randomly assigned group becomes more aggressive than a ran- domly assigned control group. One can’t randomly assign a group of 4 year olds to grow up in either a high or low media violence household, and then measure their level of aggressiveness in school or criminal records at age 18. One can, however, use a long-term experimental design to see if an interven- tion designed to reduce exposure to media violence has any eff ect on aggression. A few such experi- mental intervention studies have been done (e.g., Huesmann, Eron, Klein, Brice, & Fischer, 1983; Robinson, Wilde, Navracruz, Haydel, & Varady, 2001), and have found that such interventions can reduce aggression.
cross-sectional correlational studies Advantages
Cross-sectional correlational studies explore the direction and magnitude of associations among relevant variables. Th e independent variable is measured instead of manipulated, and both the independent and dependent variable are measured once, usually at the same point in time. Strengths of correlational studies include the ability to measure real-world outcomes, test diff erent alternative expla- nations, and suggest new hypotheses about causal relationship.
Disadvantages Th e main weakness of correlational research is
diffi culty in establishing causality. Results of a single correlational study in which variables are measured at the same single point in time cannot ascertain cause-and-eff ect relationships. In other words, corre- lational studies generally have lower internal validity than experimental studies (Anderson & Bushman, 1997). Of course, some correlational studies are more informative about causality than others. For example, some of the early violent video game eff ect studies had serious methodological diffi culties (Dominick, 1984; Lin & Lepper, 1987; Fling et al., 1992). Th ese studies showed signifi cant associations between playing video games and aggression, but did not distinguish between playing violent versus nonviolent games. In contrast, Anderson, Gentile, and Buckley (2007) tested the strength of the asso- ciation between aggression and violent video game play, while controlling for several key competitor
variables (total screen time, normative aggression beliefs, positive orientation toward violence and sex). Th is example leads us to the important con- cept of destructive testing.
Destructive Testing Because of the critical role played by testing plau-
sible alternative explanations in theory development, even cross-sectional correlational studies can play an important part in testing causal hypotheses. Th ey can provide an opportunity for falsifi cation of the causal hypothesis as well as for testing and ruling out alter- native hypotheses. Well-designed correlational stud- ies can measure many theoretically relevant variables along with the target independent variable and the target dependent variable, and then statistically con- trol for eff ects of those other variables. For example, Anderson and Dill (2000, Study 1) used the destruc- tive testing approach (Anderson & Anderson, 1996) to assess the strength of the relationship between violent video game exposure and aggression. In this approach, a predicted relationship between variables is fi rst established. Th en one attempts to break the relationship by adding competitor variables. Th e key question is not whether the relationship can be bro- ken—even strong truly causal links can eventually be rendered nonsignifi cant in a correlational study by adding more correlated predictors into the model. Instead, the focus of destructive testing is on how diffi cult it is to break the relation, considering the theoretical and empirical strength of the competitor variables used to test it. If the inclusion of several rel- evant competitor variables fails to break the relation- ship, this gives strong support to the validity of the target link. For example, in the study by Anderson and Dill (2000), the eff ect of violent video game play on aggression remained signifi cant even with the inclusion of variables such as time spent playing any kind of video game and sex. Statistically controlling for these covariates invalidated several possible alter- native explanations of the video game violence eff ect, thereby strongly supporting the authors’ prediction that playing violent games will increase aggression. When using destructive testing, relevant covariates may include confounds (e.g., sex), potential com- petitors (e.g., total time spent playing), and potential mediators (e.g., aggressive personality). Occasionally, researchers also have mistakenly included as covari- ates variables that are better conceived as additional outcome (dependent) variables.
If the target link is broken by a single competitor variable or a single confounded variable, this puts the validity of the original causal hypothesis into
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question. However, mediating variables and second- ary outcome variables have a very diff erent theoreti- cal status in correlational studies. Mediating variables are those that theoretically link the predictor vari- able to the outcome variable. In essence, they are another outcome variable of the same independent variable. For example, repeated exposure to violent video games (the predictor or independent vari- able) may increase aggressive behavior (outcome or dependent variable) because such exposure increases trait aggressiveness (the mediator variable). Th us, a proposed mediator variable should signifi cantly weaken or even break the link between the predic- tor and outcome variables, even when that link is causal. When this happens, it lends support for the predicted theoretical model. Unfortunately, some gamers/media researchers (e.g., Ferguson et al., in press) either don’t understand this principle or they choose to ignore it when promoting their position. Th ey have incorrectly concluded that when mediator variables such as trait aggressiveness weaken the cor- relation between habitual exposure to violent video games and aggressive behavior, this weakening of the key link contradicts the main theoretical hypothesis; in reality, such a result supports the causal model.
Figure 7.2A displays this issue with a Venn dia- gram. Th e three circles represent the variance of three variables, media violence, trait aggression, and bullying behavior. Th e area represented by sec- tions A + B represents the correlation (or overlap) between media violence and trait aggression. C + B represents the correlation between media violence and bullying. B + D is the correlation between trait
aggression and bullying behavior. Signifi cance tests of the various relations can be thought of tests of whether overlapping areas are signifi cantly greater than zero. If media violence truly causes an increase in the likelihood of bullying behavior, and it does so at least in part because it increases trait aggres- sion as a mediating variable, then the theoretically most appropriate test of whether media violence is signifi cantly related to bullying is the B + C area. But when trait aggression is treated as a nuisance variable that is statistically controlled, then the test of the hypothesis includes only area C, an unrealisti- cally conservative test. By adding more restrictions on what gets counted as media violence/bullying variance, such as by adding additional covariates that themselves are theoretical outcomes of high media violence exposure, one can further inappro- priately reduce the “unique” overlap between media violence and bullying.
A related problem occurs when two conceptu- ally related predictors are used in the same regression model. For example, one study included both tele- vision violence and video game violence as separate predictors of aggression (Ferguson, San Miguel, & Hartley, 2009). Th is also removes considerable pre- dictive variance inappropriately because television violence and video game violence are highly corre- lated (in that sample: r (602) = .47, p < .001) yet both contribute to the same theoretical explanation (i.e., media violence increases aggression). Figure 7.2B displays this problem. Testing the video game eff ect on aggression after controlling for the televi- sion violence eff ect, that is, testing area B, is overly
Media Violence
Trait Aggression
Bullying Behavior
A
B
C
D
Panel A.
Video Game Violence
Television Violence Aggression
A
B
C
D
Panel B.
Figure 7.2 Inappropriate Uses of Covariates in Regression AnalysesA. When a mediator variable is added as a covariate, it can signifi - cantly weaken or even break the link between the predictor and outcome variables, even when that link is causal. B. When two concep- tually related predictors are used in the same regression model, considerable predictive variance is removed which results in an overly conservative signifi cance test.
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conservative. It may be appropriate to include two conceptually and empirically overlapping predictors in a model if one wants specifi cally to compare the unique contributions of these two predictors (as in Anderson et al., 2007 tests of the relative strength of old versus new media), but otherwise the hypoth- esis that media violence increases aggression is better tested by including these two variables in separate regression models or by statistically combining them into a single “media violence” predictor. Th us, mod- els that test the hypothesis of media violence eff ects on aggression with more than one distinct media violence predictor are unnecessarily biased against this hypothesis, losing a substantial portion of the eff ect(s) of interest to a covariate that is not an alter- native explanation at all.
A third version of this problem concerns cases in which a control variable (e.g., sex of participant) is correlated with both the main independent variable (e.g., video game violence) and the main dependent variable (e.g., physical aggression). Males spend more time playing violent video games than females, and also are more likely to use physical aggression in many contexts. If playing violent video games is truly a causal risk factor for later physical aggression, then at least part of the confounded variance pre- dicting physical aggression truly belongs to the vio- lent video game eff ect. Controlling for the sex eff ect in essence overcorrects for the confound between sex and exposure to violent video games. Th us, cor- relational studies that control for sex likely underes- timate the true eff ect size of violent video games on physical aggression (Anderson et al., 2010).
Th is problem is not unique to the media vio- lence domain; indeed, this is pretty basic to research design, statistics, and methodology. Th is diagram also illustrates another point. Although the media violence critics are quick to note that “correlation is not causation,” they seem to miss the necessary counterpoint that “lack of correlation is not lack of causation.” Th at is, the same third variable problems that make it risky to conclude on the basis of one or several cross-sectional studies showing signifi cant overlap between X and Y that “X causes Y,” also make it risky to conclude that “X is not a cause of Y” based on studies showing that X and Y do not signifi cantly overlap, especially if theoretically inappropriate cova- riates are fi rst controlled for the overlap tests.
longitudinal studies Advantages
In longitudinal studies, independent and depen- dent variables are measured at two or more points in
time. Such studies provide an opportunity to assess real-life consequences of long-term media expo- sure. Causality is easier to establish in longitudinal studies than in cross-sectional correlational studies because temporal relations among variables make it possible to rule out a host of alternative explana- tions. For example, media habits and school perfor- mance can be assessed both early and late in a school year (as was done in a study by Anderson, Gentile, & Buckley, 2007). Results can be analyzed to see if the amount of habitual entertainment screen time (television, fi lm, video games . . . ) at measurement Time 1 predicts school performance at Time 2 after statistically controlling for Time 1 school perfor- mance. Th e fi nding that total habitual screen time measured at Time 1 is a signifi cant negative pre- dictor of grades at Time 2 provides much stronger support for the hypothesis that time spent on televi- sion and video games has a negative eff ect on school performance than results from cross-sectional cor- relational studies showing a signifi cant association at a single point in time (Anderson & Dill, 2000; Gentile et al., 2004; Sharif & Sargent, 2006).
In cases in which experimentally manipulating a particular independent variable would be diffi cult or unethical, longitudinal studies represent an excellent way for making sound causal inferences. For exam- ple, in a study by Hopf, Huber, and Wei ß (2008), cumulative long-term infl uences of media violence exposure on adolescents’ violence and delinquency were investigated—two behaviors that cannot be ethically investigated in an experimental study. Th e frequency of adolescents’ exposure to media violence was measured over a 2-year period as well as expo- sure to eight other risk factors. Exposure to media violence at age 12 was a signifi cant predictor of vio- lence ( b = .28) and delinquency ( b = .39) at age 14, even after controlling for earlier levels of violence and delinquency and several other relevant variables.
Disadvantages Th e main disadvantages of longitudinal designs
are that they are time consuming and expensive. Repeated measurement requires researchers to keep track of participants and pay them to stay in the study. Large samples need to be taken to com- pensate for dropout rates. Another potential con- cern is nonrandom attrition. For example, in a 3-year study of television violence eff ects commis- sioned by the NBC television company (Milavsky, Kessler, Stipp, & Rubens, 1982), data from a large portion of the most aggressive participants in the sample were deleted because they allegedly had not
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given accurate reports of their television viewing. Although the original authors concluded that there was little evidence of a television violence eff ect, closer examination of this study reveals diff erent conclusions (Kenny, 1984; Anderson et al., 2003; Huesmann & Taylor, 2003).
mixed designs Many high-quality media eff ects studies com-
bine multiple design features. Adding a correla- tional component in experimental designs can have several advantages. Including measures of relevant covariates makes it possible to perform additional tests of key hypotheses and explore eff ects of pos- sible mediating and moderating variables. Including individual diff erence variables can also decrease error variance and increase the precision or power of statistical analyses, maximizing the likelihood that true eff ects will be detected. For example, an experi- mental study by Konijn, Bijvank, and Bushman (2007) elucidated the role of wishful identifi ca- tion as a possible moderator/mediator of violent video game eff ects. In this study, exposure to video game violence was experimentally manipulated. In addition to the dependent variable (aggressive behavior), several relevant covariates were measured (e.g., trait aggressiveness, general exposure to video games, immersion, and wishful identifi cation). It was shown that playing a violent video game had the strongest eff ect on aggression for participants who wished they were like a violent character in the game. Furthermore, identifi cation was associated with realism of the game and with immersion.
Some experimental studies also include a lon- gitudinal component. For example, Huesmann, Eron, Klein, Brice, and Fischer (1983) conducted a 2-year intervention study that aimed to mitigate eff ects of television violence on aggressive behavior of school-aged children. Children selected because of their high exposure to violent television were ran- domly assigned either to a control group or an exper- imental group that received treatments designed to decrease eff ects of television violence (lessons about the unreality of television violence and an attitude change treatment). After the intervention, children in the experimental group were rated as signifi cantly less aggressive by peers and showed a lower associa- tion between viewing violence and aggression.
A potential methodological diffi culty in long- term experiments concerns the eff ective manipula- tion of the independent variable and control and measurement of possible confounds over a period of time. For example, an experimental study by
Williams and Skoric (2005) attempted to measure eff ects of violence in a massively multiplayer online role-playing game (MMORPG, a type of online game in which a large number of players interact and play the roles of diff erent characters) on aggres- sion after 1 month of game play. However, exposure to other violent games was not controlled or mea- sured during this 1-month period so no evidence existed that participants in the violent game condi- tion actually spent more time playing violent video games than participants in the control condition. Furthermore, the MMORPG used in this study was not very popular, which apparently resulted in play- ers being unable to do much fi ghting in the game because of a lack of opponents. Th e participants in this study were recruited from online gaming sites. Furthermore, the overall dropout rate was huge, especially in the control condition, thus ruining the main advantage of experimental studies. Th erefore, it is possible that during the study period partici- pants in the control condition were exposed to as much (or even more) violent video game play than those in the violent game condition.
Scientifi c Literature Reviews Each research design plays an important role in
the study of media eff ects. Sound causal conclu- sions are based on consistent results across each of these designs (Abelson, 1995; Swing & Anderson, 2010). When a suffi cient number of studies have been done on a specifi c topic, the results can be combined in a literature review. Such a review can answer additional questions, support or refute theo- retical models, and point toward areas that are in need of further research. Reviews enable researchers to draw more advanced conclusions than would be possible on the basis of results from any single study. Two types of reviews can be performed—narrative and meta – analytic reviews.
narrative reviews In traditional narrative literature reviews fi nd-
ings from relevant published empirical studies are described, categorized, and summarized. Possible goals of narrative reviews include providing an overview and integration of an area, theory evalua- tion and development, identifi cation of weaknesses or contradictions in a specifi c fi eld of investiga- tion, and generating new problems and hypoth- eses (Baumeister & Leary, 1997). By searching for connections among a large number of empirical fi ndings, narrative reviews can address much wider questions than any single empirical study. Th e major
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strength of narrative literature reviews is their focus on conceptual relationships between key variables that can lead to rich theoretical and methodological insights (Anderson, Gentile, & Buckley, 2007).
However, diff erent studies necessarily yield some- what diff erent fi ndings. Even if a study was repli- cated perfectly using the exact same methods, the results would be diff erent because of eff ects of ran- dom factors. How should these diff ering results be interpreted and what conclusions should be drawn? A weakness of narrative literature reviews is that many critical decisions that are made while selecting and interpreting studies are subjective. Th is opens the door for reviewer biases that can result in drasti- cally diff erent interpretations of the empirical fi nd- ings by diff erent reviewers. People generally have a tendency to disregard evidence that contradicts their beliefs (Lord, Ross, & Lepper, 1979; Kunda, 1990; Koehler 1993), and reviewers are not exempt from such biases. Diff ering theoretical and empiri- cal orientations can lead reviewers to form diff er- ent inclusion criteria and organizational schemes, leading to diff erent conclusions (Dill & Dill, 1998; Griffi ths, 1999). Because of this, it’s important that reviewers pay attention to counterexamples and allow themselves to be led by evidence rather than rigidly imposing a priori beliefs and expectations (Baumeister & Leary, 1997).
meta-analytic reviews Meta-analytic reviews use statistical techniques to
combine the results of a number of empirical stud- ies that tested the same hypothesis. Meta-analyses describe the typical strength of an eff ect, its vari- ability, its statistical signifi cance, and variables that moderate it (Rosenthal, 1995). When a suffi ciently large number of studies are available that tested the same hypothesis and a meta-analysis is usable, it is generally the preferred review method (Baumeister & Leary, 1997). By combining results from mul- tiple studies, meta-analytic reviews can resolve inconsistencies caused by small sample sizes. Th e main strength of meta-analytic reviews is objectiv- ity (Anderson, Gentile & Buckley, 2007). Unlike narrative reviews, meta-analyses done to answer a particular research question tend to give similar answers irrespective of diff erent perspectives held by diff erent reviewers. However, the meta-analytic reviewer still has to make important decisions con- cerning what studies to include and what studies to exclude from the sample. Th us, poorly conducted meta-analyses, those that do not include all relevant studies (Ferguson et al., in press), can be just as
misleading as a biased narrative review. Th e major weakness of meta-analyses is that the focus on sta- tistical aspects sometimes leads the researchers to ignore important conceptual aspects.
In well-conducted meta-analyses, researchers attempt to fi nd all available published and unpub- lished studies that might be eligible for inclusion in the sample, construct a clear and explicit set of inclusion criteria, and conduct publication bias analyses. For example, the most recent and com- prehensive meta-analysis in the violent video game eff ects domain was conducted by Anderson et al. (2010). Th is meta-analysis combined a total of 136 research papers with 381 eff ect size estimates involv- ing more than 130,000 participants from Eastern and Western countries. Six outcome variables were included in the meta-analysis: aggressive behavior, aggressive cognition, aggressive aff ect, physiological arousal, desensitization/low empathy, and prosocial (helping) behavior. Newer studies of higher method- ological quality made it possible to use more strin- gent inclusion criteria in this meta-analytic review than in prior reviews, and allowed tests of the eff ects of a number of relevant moderators (e.g., sex, cul- ture, player’s point of view). Both the best practices sample and the full sample yielded the same results: Violent video games had signifi cant eff ects on all six outcome variables, showing that video game violence is indeed a causal risk factor for increased aggression and decreased prosocial behavior.
Methodological Pitfalls in the Field of Media Psychology Conducting Studies in a “Th eoretical Vacuum”
When attempting to understand underlying processes of media eff ects, it’s important to keep in mind general knowledge in the fi eld of psychol- ogy concerning mechanisms of memory, learning, social cognition, and development. Media eff ects research is informed by extensively replicated fi nd- ings and well-validated theoretical models from sev- eral disciplines, including, among others, cognitive psychology, developmental psychology, personality psychology, social psychology, and neuroscience. Well-tested and generally accepted theories such as schema theory (Alba & Hasher, 1983; Schmidt & Sherman, 1984), social learning theory and social cognitive theory (Bandura, 1973, 1983), script theory (Huesmann, 1986, 1988, 1998), and risk and resilience models (Glantz & Johnson, 1999; Gentile & Sesma, 2003) provide a solid foundation for predicting and explaining fi ndings in the fi eld
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of media psychology. As Kurt Lewin (1951) put it, “Th ere is nothing so practical as a good theory.” However, even though there are well-developed and well-validated theoretical models behind media vio- lence eff ects (Anderson et al., 2003), some other research domains involving media eff ects suff er from a lack of theoretical focus (see Chapter 23).
A dangerous error sometimes made by media eff ects researchers is planning studies and interpreting results as if they are completely disconnected from the fi eld’s general knowledge of psychological function- ing. For example, researchers who deny the existence of media violence eff ects on aggression are ignoring reliable and extensively replicated fi ndings regard- ing priming (Bargh, 1982; Bargh & Pietromonaco, 1982), observational learning and imitation (Bandura, Ross, & Ross, 1961, 1963a,b; Meltzoff & Moore, 1977), excitation transfer (Zillmann, 1971, 1983) and desensitization (Wolpe, 1982). Given this extensive literature concerning ways that aggressive and nonaggressive social behaviors are learned and induced, it would indeed be very surprising if media violence did not aff ect us.
Using Inadequate Sample Sizes Because most eff ects found in media psychology
are small or medium in size, adequately large sam- ples are needed to detect media eff ects. If the average eff ect size is about r = .20 (Anderson & Bushman, 2001), a sample of at least 200 participants should be taken to have .80 power. If sample sizes being used are too small, this will lead to results that are unstable and seemingly inconsistent. More reliable estimates can be obtained through combining such studies using meta-analytic techniques, of course, but researchers need to use adequate sample sizes in every study.
Using Inappropriate Experimental Manipulations
Any experimental manipulation represents an attempt by the researcher to construct a valid empirical realization of the conceptual independent variable (Carlsmith et al., 1976). Ideally, the various experimental manipulations: (1) diff er from each other on the conceptual independent variables that they are supposed to represent, and (2) do not diff er on other aspects that might (theoretically) infl uence responses on the dependent variable. For example, an experimental study to test the theoretical hypothesis that violent video game content increases the likeli- hood or amount of physical aggression minimally requires two conditions that diff er in the amount
of violent content (one should have a lot, the other should have none). Some early experiments (which shall remain nameless) did not successfully do this, in part because the researcher used an inappropriate defi nition of “violent content.” Th at is some experi- ments used violent video games in the nonviolent control condition, because the researcher defi ned violent content as content that contained blood and gore, rather than the now-accepted defi nition of violent content as content in which player–charac- ters try to harm other game characters. Also, recall our earlier comments on the failure of the Williams and Skoric (2005) “experiment” to appropriately manipulate exposure to violent video games.
Th e second requirement of the ideal case, that the relevant comparison conditions do not diff er in aspects that might infl uence the dependent variable, also requires careful attention. We know, for example, that variables such as excitement, arousal, and frus- tration can sometimes increase aggressive behavior in some circumstances. Th erefore, such extraneous factors (extraneous to the violent content T physical aggression hypothesis) need to be controlled.
Th ere are two basic strategies for controlling such extraneous factors. One is to pretest several possible empirical realizations of the independent variable on the extraneous factors (using the same participant population as will be used in the main experiment), and then choose those that meet the theoretical and empirical requirements for use in the main experi- ment. For example, in a pilot study one could use several violent and several nonviolent video games, measure excitement, arousal, and frustration, and then select games that diff er in violent content but that do not diff er in induced excitement, arousal, and frustration for use in the main experiment (e.g., Anderson et al., 2004).
Th e second strategy is measure the extraneous fac- tors in the main experiment on the main participants, and then statistically control for those factors in anal- yses of the violent content manipulation on aggres- sive behavior. If it turns out that an extraneous factor (e.g., excitement) doesn’t contribute signifi cantly to aggressive behavior, then one doesn’t need to control for it. However, if it does relate to aggressive behavior, then one can use the measure of excitement as a cova- riate in the statistical analysis. And of course, both of these strategies can be used in the same program of research as has been done in many of the meth- odologically strongest studies (e.g., Anderson & Dill, 2000, Study 2; Anderson et al., 2004).
It is important to keep in mind that the com- parison conditions still will likely diff er in other
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ways. Th is is especially likely in media psychology studies and any domain in which the stimuli tend to be selected rather than created. Although beyond the scope of this article, one solution to this issue is to use multiple stimuli (e.g., games) of each type (violent and nonviolent) such as in Anderson and Carnagey’s (2009) study of violent and nonviolent competitive games. In addition, if one uses many examples of each game type, one could use random eff ects statistical models rather than the more com- mon fi xed-eff ect models.
Yet another approach to equating experimental conditions on extraneous factors is to use the same stimuli with changes only to the violent content. For example, Carnagey and Anderson (2005) repro- grammed the violent video game Carmageddon (a driving game in which one gets points for running over pedestrians) so that in the nonviolent condi- tion there were no pedestrians to kill. Similarly, Anderson et al. (2004, Experiment 3) modifi ed the violent video game Marathon 2 . However, even this approach guarantees that the comparison games will be “equal” on relevant extraneous factors. So, it is useful to control such factors by pretests, mea- suring and statistically controlling for them in the main study, or both.
Finally, combining the eff ects of well-designed experiments in a meta-analysis also helps eliminate alternative explanations based on potential extrane- ous factors coinciding with the experimental vari- able of interest. Because diff erent researchers have used a wide range of violent and nonviolent video games in their experiments, the likelihood that some extraneous factor existing in all or most of them is quite remote. Indeed, if one comes up with a plau- sible alternative explanation that might account for some of the results, one can test that alternative in a meta-analysis. For example, some gamer/scholars have proposed that the violent video game eff ect in experimental studies only works with the competi- tive reaction time task. Anderson et al. (2010) tested this alternative hypothesis, and found that the aver- age eff ect size of such CRT studies is actually slightly smaller than the average eff ect found in the other experimental studies of violent video games, thus disproving that alternative explanation.
It is important to keep in mind that this type of reasoning, development, and assessment of experi- mental manipulations, and theory testing can and should be done in other media psychology domains, once suffi cient numbers of studies are available. We use the media violence domain as an example because it is large, has had many excellently designed
and executed studies published, has had a number of poorly executed studies published, and also because we are most familiar with this domain.
Using Poor or Inappropriate Measures Diff erences in the direction of fi ndings and in
eff ect sizes can sometimes be a result of diff erent measures of the independent, the dependent, or the control variables in particular studies. To detect eff ects and accurately assess their magnitude, reliable and valid measures need to be used. For example, the meta-analysis by Anderson et al. (2010) showed that the way one measures violent video game expo- sure in nonexperimental studies signifi cantly infl u- ences the magnitude of eff ects found. Using specifi c measures of the length of exposure and violence levels in particular games (Anderson & Dill, 2000) yielded larger eff ect sizes than did other methods of assessing exposure to violent games.
Another potential pitfall involves using depen- dent measures that don’t fi t the research context. Th is can happen in multiple ways. For example, some short-term experimental studies of violent media eff ects have used traitlike measures as the depen- dent variable. Such traitlike measures essentially assess how frequently one has behaved aggressively in recent years. How can a 15-minute experimental manipulation today (violent versus nonviolent video game) infl uence how often one has behaved aggres- sively before today? Another version of this problem concerns what is an appropriate measure of aggres- sion. Is having an argument with a friend or spouse a measure of aggression, as claimed by Williams and Skoric? Is the proximal intent of such an argument to harm the friend or spouse? In most cases, the answer is probably “no,” so this is a very poor measure of the conceptual variable “aggression.” It is even more inappropriate in a study designed to test the eff ects of violent video games on the kinds of aggression most frequently modeled in violent games, physical aggression. And it is even more inappropriate when the most of the participants don’t have a spouse with which to argue (Williams & Skoric, 2005). Certainly, there is evidence that school children arguing with teachers and other authority fi gures is one valid aspect of antisocial tendencies, but that is very diff erent from using arguments with friends/ spouses as a measure of video game–induced aggres- sion in adult participants.
Often, the most important fi ndings are acquired by using multiple measures. For example, in a lon- gitudinal study of media violence eff ects, Anderson, Gentile, and Buckley (2007) obtained multiple
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measures of children’s aggressive behavior through self-report, peer nominations, and teacher nomina- tions. Sometimes such measures can be usefully com- bined into an overall index of aggression (Study 3).
An interesting recent direction in the media psy- chology fi eld concerns examining neurocognitive bases of media eff ects through techniques such as event-related brain potentials (ERPs) and functional magnetic resonance imaging (fMRI). For example, Bartholow, Bushman, and Sestir (2005) showed that habitual violent video game players have reduced amplitudes of the P300 component of the event-related brain potential while viewing violent images and that this reduced response predicts more aggressive behavior. Research by Kronenberger et al. (2005) has shown similar fMRI and Stroop attention diff erences in conduct disordered and high violent gaming adolescents (Mathews et al., 2005; Weber et al., 2006). Similarly, Bailey, West, and Anderson (2010, 2011a,b) have used ERPs, Stroop tasks, and photo rating tasks to compare high and low action gamers on their attention control and emotional reactions to violence. Relative to low gamers, high gamers show defi cits in proactive control, other more general attention defi cits, and brain activa- tion patterns suggesting desensitization to violent images. Overall, these various fi ndings, each using multiple ways to measure theoretically related pro- cesses, provide converging support on desensitizion and decreased empathy as results of media violence exposure (Mullin & Linz, 1995; Dexter, Penrod, Linz, & Saunders 1997).
However, obtaining multiple measures some- times comes at a cost. A potential pitfall stems from the fact that measurement of one variable of interest may infl uence the values of other related variables. Similar to the Heisenberg uncertainty principle in physics, the psychological uncertainty principle states that that measurement of one variable may change the psychological processes at work and thus change the values of downstream variables (Lindsay & Anderson, 2000). For example, measuring attitudes toward aggression after watching a violent movie may reveal the purpose of the study to participants and infl uence their later behavior. Th e possibility of such an infl uence can be controlled by experimen- tally varying the order in which variables are assessed and then testing for order eff ects. If signifi cant order eff ects are found, this shows that the psychological uncertainty principle is at work. To test for media- tion eff ects in such cases, multiple experiments need to be conducted, each of which assesses one of the key variables (Lindsay & Anderson, 2000).
Signifi cance Testing A problematic statistical practice employed
in many media violence studies consists of using null-hypothesis signifi cance testing without report- ing eff ect sizes and confi dence intervals. Th is widely used approach (in psychology as well as other social sciences) has been the subject of much criticism (Rozeboom, 1960; Cohen, 1994; Kirk, 1996; Th ompson, 1998; Bonett & Wright, 2007). Unfortunately, null hypothesis tests are often misin- terpreted (Nickerson, 2000). Failing to reject the null hypothesis is frequently viewed as proof that the null hypothesis is true, whereas rejection of a null hypoth- esis is taken as evidence of a practically and theoreti- cally relevant fi nding (Bonett & Wright, 2007).
In the media violence domain, in which eff ect sizes are in a small to medium range (Anderson & Bushman, 2001; Anderson et al., 2010), interesting fi ndings may be overlooked because of Type II errors (failure to reject the null hypothesis when it is true) and may go unpublished. Th e absence of signifi cant diff erences found in particular studies are some- times misinterpreted as evidence that there indeed are no eff ects, without taking into account other possible reasons for the nonsignifi cant result (e.g., inadequate control of extraneous variables, inappro- priate overcontrol of mediating outcome variables, unreliable measurement techniques, and small sam- ple sizes). A wide confi dence interval immediately indicates to the reader that the sample estimate may not be reliable and may be quite diff erent from the true eff ect in the population. Meta-analytic tech- nique can then be used to combine such studies and enable researchers to draw fi rmer conclusions.
Th e American Psychological Association (APA) Task Force on Statistical Inference advocated for an improvement of statistical practices by including eff ect size estimates along with confi dence inter- vals more than 10 years ago (Wilkinson & the Task Force on Statistical Inference, 1999). However, these changes have not yet been widely implemented in psychology journals (Finch et al., 2004; Cumming & Finch, 2005; Cumming et al., 2007). As the APA Publication Manual now strongly encour- ages authors to include confi dence intervals (APA, 2011), it is our hope that this change in reporting styles will reduce miscommunication and misun- derstanding in the media violence literature.
Eff ect Size Interpretation Media eff ects research has sometimes been
criticized on the grounds that eff ect sizes found in most studies are small and are thus unimportant
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(Ferguson & Kilburn, 2010). However, it is danger- ous to assume that just because most studies fi nd small eff ect sizes, media do not have important prac- tical consequences.
Th e eff ect sizes found in most media eff ects stud- ies conform to the range of eff ect sizes usually found in social psychology studies in general (Richard, Bond, & Stokes-Zoota, 2003). Because complex behaviors are determined by a multitude of personal and situational factors, no one causal factor by itself can explain more than a small proportion of the vari- ance in a particular behavior. Because of this, some authors suggest that eff ect size conventions should be revised so that r = .1 is small, r = .2 is medium, and r = .3 is large (Hemphill, 2003).
Some of the eff ects found in media psychol- ogy are, in fact, considerably larger than eff ect sizes found in medical research that are seen as extremely important (Bushman & Huesmann, 2001). For example, the eff ect of violent video games on aggres- sion outweighs eff ects of substance use, abusive par- ents, and poverty (U.S. Department of Health and Human Services, 2001) and is larger than the eff ects of passive smoking on lung cancer and the eff ect of calcium intake on bone mass (Anderson, 2004). Furthermore, because a large proportion of the pop- ulation is exposed to violent mass media, even small statistical eff ects can have important societal conse- quences (Abelson, 1985; Rosenthal, 1986; Prentice & Miller, 1992; Anderson et al., 2003).
Communicating Research Findings and Methodology to the General Public
An important role for many scientists involves disseminating knowledge gained from their research not only among the scientifi c community, but also among the general public. Indeed, several American Psychological Association presidents have urged its members to “give psychology away” to the public. One of the goals of media psychology as an applied fi eld is to benefi t society with its insights, a goal that requires eff ective communication between media researchers and the media, public policy makers, parents, teachers, and so on. Unfortunately, the sci- entifi c community has not always been successful in communicating research fi ndings to the general pub- lic. For example, a content analysis of research papers and newspaper articles conducted by Bushman and Anderson (2001) revealed a large disparity between news reports and the actual state of scientifi c knowl- edge concerning media violence eff ects.
Researchers often do not see themselves as pub- lic educators. Diff erences in terminology and basic
assumptions between scientists and nonscientists can impede eff ective communication and contrib- ute to misinterpretation of scientifi c fi ndings in the general public. Additionally, public involvement comes with costs (e.g., time, eff ort, money, and personal costs)—a price that researchers frequently are unwilling to pay. Th e costs are especially large when the research suggests that certain products are harmful (e.g., lead, tobacco, violent media), and when there is a large and committed group of product users and industry leaders who are highly threatened (e.g., by threats to self-image, profi ts) by the research fi ndings. Th ere is a long history of industries in the United States spending large sums of money attacking research fi ndings that they don’t like, attacking the integrity or scientifi c reputations of researchers whose work discovered the harmful eff ects. Th ere is such a history in the television and fi lm violence domain. For example, both Albert Bandura and Leonard Berkowitz were excluded from key governmental review panels on media violence because of pressure brought by the entertainment media industry. Similar attacks are widespread in the video game violence domain, and with the rise of the Internet, the personal attacks on and outright fabrications about key researchers has taken on a new dimension. One need only Google the names of the leading video game violence researchers to fi nd such fabrications about them and their research.
However, it is our belief that the benefi t of eff ec- tive communication between scientists and the gen- eral public outweighs such costs. Th erefore, a fi nal task of successful researchers in the fi eld of media psychology is to be able to clearly and eff ectively inform general audiences concerning their fi ndings and methods used to obtain them.
Notes 1 . We fi nd it ironic that the lead author of that study,
Dmitri Williams, in 2005 criticized the experimental study reported in Anderson and Dill (2000) for selecting a violent and a nonviolent game based on pilot testing of several games that included self-reported ratings on a variety of dimensions and physiological measures of arousal. Williams apparently didn’t like the two games chosen because they didn’t fi t his intuitions about excitement levels induced by the games. What he fails to note is that: (1) Anderson and Dill reported that there were diff erences in self-reported excitement; (2) there were not diff erences in heart rate or blood pressure; (3) excite- ment was statistically controlled in the main experiment; (4) the excitement did not infl uence the results of the main exper- iment. Furthermore, in science when intuition confl icts with empirical data, it is intuition that has to yield. In fact, the Anderson and Dill studies set the methodological standard for
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later video game studies (both experimental and correlational), and their basic fi ndings have been replicated numerous times by numerous research teams from many countries around the world. We are not saying that this early experimental study was perfect; no single study is perfect. In fact, several more recent studies from our and other labs are, in our view, stronger methodologically; they built on the insights and knowledge gained from the earlier study.
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