Nov 052008
 
ResearchBlogging.orgThe latest evidence in the debate over the effects of video game violence has arrived in the November edition of the journal Pediatrics. Japanese and American psychologists, including well-known media violence researchers Craig Anderson and Douglas Gentile, report that violent video games constitute a causal risk factor for physical aggression. Perhaps unsurprisingly, the gaming internets have already expressed their disagreement with these results via angry blog postings based on secondary reporting (calmer coverage can be found at Gamasutra). A more professional critique has also been offered, in the form of a post-publication peer review by Texas A&M International University Professor Christopher Ferguson. The paper tries to sell itself as a significant piece of new proof, which it is not. Anderson et al. have found an interesting, if weak, correlation that they cannot prove to be causal, due to the limitations of the methods employed.

The study has two key advantages that, in principle, make it a unique addition to our knowledge about the effects of video game violence. Firstly, it attempts to correlate physical aggression (PA) in teens and kids with habitual exposure to video game violence (HVGV) 3-6 months earlier. While the use of a timecourse alone cannot prove causation, long-term correlations are thought to suggest a causal relationship more strongly than instantaneous correlations. Secondly, the study involves several age groups from two countries, the United States and Japan. Although more children play video games in Japan than in the US, the rate of violent crime in Japanese society is much lower than in the US. This has occasionally been held out as disproof of an HVGV-PA link, but all it really establishes is that other factors play a significant role. Therefore it would be interesting to determine whether cultural differences between the US and Japan alter the effect of HVGV on PA.

Three sets of children (two in Japan, one in the US) filled out questionnaires querying their gaming habits and physical aggression levels. Some months later, these same children were surveyed again to see whether their physical aggression levels had changed. The authors found that HVGV levels at the first time point had a weak correlation (r= 0.28) with PA at the second time point. This effect varied significantly over the individual datasets and was strongest in the youngest age group. However, the r value did not exceed 0.5 for any of these datasets.

In layman’s terms, one could see these results as evidence that HVGV predicts between 8% and 16% of the level of physical aggression, depending on the age group and nationality. I caution my readers that this interpretation is an oversimplification that depends on certain assumptions about the data to have any validity. Because no statistics of the underlying matrices are provided I cannot substantiate those assumptions, so this should not be taken as a definitive description of the study’s findings. Statistics (even averages) imply a model, and should not be trusted if it cannot be proved that the model is appropriate.

These results are interesting and indicate that, although the magnitude of the effect may differ between societies, there is nonetheless a universal positive correlation between HVGV and subsequent physical aggression. Despite the elaborate discussion of youth violence in the paper, this does not directly indicate a linkage to criminal behavior. Moreover, this correlation is difficult to interpret due to the study’s numerous flaws.

There are good reasons to wonder whether the interpretation of the questionnaires produced a valid measure of HVGV at all, the assignment of violence level by genre being particularly suspect. A more significant problem may be that HVGV and PA were assessed by different means in every single group. Each group used different delays between surveys, and each involved differently-aged children. This doesn’t necessarily mean that conclusions drawn by aggregating the three are wrong, and the authors contend that agreement across the varying methodologies indicates robustness. However, the differences in method and subjects multiply the potential sources of error considerably. Since the derived correlations are so weak, this is a significant concern. In addition, because the populations differ substantially in respects other than nationality, it is impossible to accurately assess the effect of culture on the relationship between HVGV and PA. Doubtless future longitudinal studies will apply more uniform methods.

This brings me to another weakness of the study. Scientists will occasionally joke that the best possible set of correlational data is the one that contains only two points, the reason being that you are assured of being able to draw a perfect, straight line through all your data. In practice, however, we know that having limited numbers of data points makes our interpretations much more likely to be wrong. A “longitudinal” study involving two questionnaires given a couple of months apart hardly provides firm footing for a long-term correlation or a causal relationship. The authors acknowledge that the study is limited in this regard, but argue that the short wait would most likely depress correlations from their true value. Still, a longer timecourse with more measurement points would be highly desirable.

The authors make no attempt to account for any confounding factors other than gender. They do not seem to have taken data on family situation, peer influence, parental involvement, or school performance, although all of these factors are known to correlate to greater or lesser degrees with both PA and video game habits. If we only wish to establish that there is a correlation between HVGV and PA that’s not a huge problem. However, Anderson et al. clearly mean to establish video games as a causal factor for aggression. In the absence of controls for confounding factors, that is impossible.

Curiously, the authors also do not seem to have measured HVGV at the later time point. One objection to existing research linking HVGV to real-world violence has been that the observed correlations exist because people predisposed to violence choose to enjoy violent media. Testing the hypothesis that PA at the initial timepoint predicts HVGV at the second timepoint seems like an obvious thing to do, if only to squelch this objection. This seems to me particularly worthwhile, because the predictive power of HVGV for later aggression appears to be less than the instantaneous correlation between HVGV and aggression, significantly so for the older group. In light of these facts, the choice not to assess HVGV at the later time seems extremely odd.

Despite these flaws, this research is a step in the right direction. We need longitudinal studies, carefully controlled for confounding factors, over a range of ages and nationalities to parse out the true effects of video games on aggressive behavior in teens and adults. I do not find the present study terribly convincing, and I particularly dislike the more sensationalistic high points of its discussion section. Nonetheless, I hope that the authors will take criticisms like those of Dr. Ferguson into account as they design studies that will more rigorously investigate the causal relationship between HVGV and PA.

Only a particularly obstinate person would deny that there is a correlation between the intake of violent media, including video games, and aggressive behavior. They may inspire aggressive behavior, or serve as an outlet for existing aggression; either way, the correlation ought not be ignored. However, video games are just one, and doubtless not the most important one, of a constellation of potential factors affecting child behavior. Without a genuine analysis of the complicated causal relationships among these it is impossible to provide good advice to parents, doctors, and psychologists. The present study does not fill that gap in our understanding; it is doomed by its single-minded focus on video games and failure to account for confounding factors. While it is of value to know that the correlation between violent video games and aggression transcends national and cultural boundaries, it would be of greater value to know whether excessive playing of violent video games is a cause of aggressive behavior, a result of pre-existing aggression, or both. That is a question this research does not adequately, much less conclusively, address.

C. A. Anderson, A. Sakamoto, D. A. Gentile, N. Ihori, A. Shibuya, S. Yukawa, M. Naito, K. Kobayashi (2008). Longitudinal Effects of Violent Video Games on Aggression in Japan and the United States PEDIATRICS, 122 (5) DOI: 10.1542/peds.2008-1425

  3 Responses to “Video games and violence: grasping at causality”

  1. It is stated that the two key advantages to the study of the effects of video game violence are to correlate PA in teens and kids with HVGV and also that several age groups from two countries are involved. However, how is one to know where a childs aggression truly comes from? Can a simple questionnaire really determine a noticeable difference in a child’s aggression and link it to video games?

  2. Well, you bring up a couple of separate research concerns, some of which are handled well by the paper's authors and others not so well. The surveys used may not be accurate measures of the absolute value (if such a thing exists) of a child's aggression, but by comparing identical measures at each timepoint it should be possible to accurately extrapolate relative changes in aggression levels. However, I'm not really sure that's what they did. Their description indicates that they correlated HVGV at time 1 with PA at time 2, but other parts of the paper are argued as if they had correlated HVGV at time 1 with the change in PA. If the former is the truth, then it would seem to be disingenuous to claim that HVGV at 1 correlated with increases in PA. Some clarification on this point is probably in order.

    Another data problem here is that the measures of HVGV and PA were totally different for each group. That makes any comparison between the groups, or aggregation of the data, somewhat suspect. For instance, the youngest age group in the US had by far the highest correlation between HVGV and PA (r = 0.40). Was that because they were younger, because they were in the US, because the methodology for that group produced better estimates of HVGV and PA, or because systematic errors in the methodology for that group produced an erroneously high correlation? There's not really any way to tell from these data. I am not so concerned about the use of surveys per se as I am about the inconsistent measurement techniques.

    The second question, whether aggression can be linked to video games, is handled less well. If we only look at video game violence and aggression we can establish whether a high level of one is correlated with an high levels of another. What this paper is missing in this regard is any sort of attention to other possible causes of aggression. Without doing any work to rule out other possible origins of aggression, you simply can't come to any sort of firm conclusions about causality.

    There are some good questions to be asked about the data here, but I am willing to trust them, provided this PA(2) vs. ΔPA thing gets cleared up. My main problem is that the interpretation, particularly the interpretation the authors seem to be spinning to the press, really goes beyond what those data would support even if we were absolutely certain about their accuracy.

  3. The availability of video games has led to an epidemic of youth violence. The debate around video games and violence rears its head every few months. In every group, children who were exposed to more video game violence did become more aggressive over time than their peers who had less exposure.

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    jnnywllms

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