Please note that ethical standards of peer reviewing constrain me [JP] to give you the original manuscript. I also had to anonymize identifying information in the review. This review is meant as an example of the style used in writing a review; you do not have to understand all the details. Please note that this review is longer than the one you are requested to write.
This is a highly interesting study on a timely subject, the impact of pornography use in adolescence on relationship intimacy in early adulthood. Based on Zillman’s programmatic piece about the “influence of unrestrained pornography” on adolescents and more recent research on teenagers’ use of internet pornography, the study develops a model on how adolescent pornography use may affect relationship intimacy in young adulthood. The study concludes that there is, “at best, minimal support for Zillmann’s claim that prolonged exposure to pornography is associated with sexual callousness” (p. 13). The strengths of the study include, in my view, the focus on an under-researched dependent variable; its attempt to build and test a model; and the (attempted) investigation of gender differences. The weaknesses include, in my view, the theoretical underdevelopment of the model and several severe methodological problems.
Theoretical development of the model
By the standards of Journal [ANONYMIZED], the theory section (pp. 2-4) is very short. While in journals of other disciplines (e.g., Journal of Adolescent Health) such a short introduction is requested, pieces in [ANONYMIZED] are expected to be more specific about the theoretical underpinnings of the study. Although brevity is always preferable, a study that develops and tests a new model does require a somewhat more thorough conceptual definition of the various influences in the model and, most importantly, a rationale for these influences.
Conceptual definitions and rationale for the components in the model: The model has four components, exposure to pornography, pornographic realism, acceptance of recreational sex, and relationship intimacy. However, on p. 2, many more concepts are outlined (based on Zillmann’s paper): habituation, cultivation effects in terms of perceived sexual behaviors, distrust in intimate partners, abandonment of exclusivity as a norm of romantic relationships, and greater endorsement of promiscuity. None of these concepts is tested. Moreover, on p. 3, several other concepts are mentioned, including cynical attitudes about love, sexual pleasure without affection, sexual callousness, and decreasing emotional attachment.
While the latter concepts are related to what is tested, they are not the same. Scanning through the studies that Zillmann and Bryant published in the 1980s, it becomes clear that they have probably something else in mind when they talk about *sexual* callousness than “an impaired ability to form intimate relationships” (p. 4). Finally, it remains unclear why pornographic realism is an important addition to the model suggested by Zillmann. This is certainly not to say that the paper’s model is unrelated to Zillmann’s ideas, but the paper should aim for more conceptual clarity. Key concepts need to be defined. Moreover, it needs to be outlined how the key concepts of the model relate to Zillmann’s ideas as well as when and why they differ.
Rationale for the influences hypothesized in the model:
The model hypothesizes that recreational attitudes toward sex mediate the effect of pornography on intimacy. Pornographic realism is included as a covariate of pornography use (although it is claimed that it is investigated as a mediator, p. 4). However, the rationale for hypothesizing these processes remains vague. First, how precisely are recreational attitudes related to sexual socialization and the sexual script concept (p. 3)? How, and why, are these attitudes affected by pornography? These questions should not be answered on the basis of empirical regularities (as done on pp. 3-4), but on the basis of more elaborate theorizing. Second, why is pornographic realism a covariate (at least in the model tested)? From the quote on p. 4, it rather seems a mediator. This needs some clarification and elaboration, too.
The analysis of gender differences occupies considerable space in the analysis and discussion. However, a rationale is largely lacking why such differences need to be investigated. There is sufficient evidence that females use pornography less often than males do (i.e., gender as a direct predictor), but it is crucial to outline why the processes hypothesized may differ by gender (i.e., gender as a moderator).
I would like to stress that any research on the issue of the study is admirable, given the enormous ethical, practical, methodological, statistical issues involved. In my evaluation, I take this into account. That said, I do have to raise some potentially unpleasant questions about the design of the study; operationalization of the key measure; procedure/ sample; and analysis.
Design and operationalization of key measure
The paper aims at testing a causal model, but relies on cross-sectional data. The paper outlines on p. 4 that the study includes a time component by asking respondents to indicate their pornography use at ages 14 and 17. Several problems arise. First, cross-sectional data do not permit causal conclusions related to media effects. At the very least, this needs to be acknowledged explicitly and prominently. Also, language suggesting causal relations should be avoided. Second, asking respondents retrospectively about their pornography use at the ages of 14 and 17 raises some questions. Why at ages 14 and 17? Adolescence usually spans the period between age 12 and 17. Why was exposure not measured, for instance, for age 12 (early adolescence), age 15 (middle), and age 17 (late)? Third, self-reported retrospective measures of sensitive behavior are prone to multiple biases, most notably memory bias and social desirability bias.
These biases already plague measures that relate, for instance, to the “past week.” But how can such measures meaningfully be applied to behavior that happened, for the oldest respondents, 11 years ago? Fourth, what exactly were the response categories? “Never” suggests a vague-quantifier scale (e.g., never, rarely, sometimes, often, very often), which carries a lot of problems, most notably the problem that vague quantifiers leave it up to the respondent to decide what the categories mean. However, the positive anchor of the scale is “every day.” Was the scale thus a scale asking about specific frequencies (e.g., once a week, less than once a week). Again, how can such frequencies be assessed validly after so much time? Any information on the validity and reliability of the measure along with a rationale for the operationalization is highly welcome.
Fifth, how does this measurement strategy assess “prolonged” exposure, the key concept in Zillmann’s paper? Assessing retrospectively the use of pornography does not tell us much about the trajectory of porn use. Finally, a retrospective measure is not the same as a measure taken at a certain point in the past, in contrast to what is claimed on p. 4. I perfectly understand that longitudinal research is cumbersome, particularly in that area. That said, it seems difficult to see how the retrospective measurement of pornography use tackles the causal problems inherent in cross-sectional research. In sum, there are several serious issues with the operationalization of one of the key variables, which urgently need to be addressed.
The paper is unfortunately very brief about the procedure and sample of the survey. Given the self-selection problems in sex research, I was surprised to read that few precautions were taken to minimize this bias. Why was snowballing not avoided, but even encouraged (p. 5)? Why did the study not include some simple quotas, most notably for gender (see below)? Was there a control of whether a particular respondent filled in the survey multiple times? In addition, I assume that informed consent was explicitly asked for, but this should be mentioned briefly. Finally, is there an indication of how many respondents were contacted and what the response rate was? There are also several important questions about the sample. First, why was the study limited to sexually active students? Sexual experience may create a limiting boundary condition for what the paper is interested in.
Second, why was the age frame limited to 18- to 25-year olds? Is this related to the theory of emerging adulthood? Third, why was the study limited to university students? We complain about such convenience samples in experimental research. There may be even more concerns about such samples in survey research. While the concerns raised in the previous paragraphs address very severe shortcomings, they may even be multiplied by the fact that twice as many women as men filled in the questionnaire. This is a crucial problem because the basic conclusion of the paper is that the model only works for women, but not for men. To be sure, the paper mentions these shortcomings in the discussion section, but that does unfortunately not reduce its importance.
Table 2 shows small to moderate zero-order correlations for men and women. However, with twice as many women as men in the sample, an r = -.11 is significant for women, while an r = .13 is not significant for men. Both for men and women, the correlations are in the same direction. I guess that, with an equal number of men and women (e.g., 350 each), the model would largely hold for both. This would also be a more reasonable sample size in terms of statistical power consideration. In conclusion, there is reason to believe that one of the main conclusions of the paper is a result of a severe shortcoming in the sample procedure of the study.
The general problems with the gender analysis notwithstanding, I was wondering why the paper does not apply a multiple-group analysis. This is a more rigorous way of testing whether the various paths differ between women and men than the strategy currently employed. I was wondering whether the SEM analysis used item-parceling strategies. Otherwise, there need to be more manifest indicators in the models. Finally, the statistical testing of indirect effects (i.e., whether they differ significantly from zero) has become a standard procedure and should be included. Discussion
In the light of the problems raised above, some of the conclusions raised in the discussion section may need some reconsideration. (This is my opinion, and the authors may or may not follow them). First, I am hesitant to agree with the paper that the findings have “little if any practical significance” (p. 10). The discussions about effect sizes in media effects research in particular and the social sciences in general have been outlined elsewhere and do not have to be repeated here. Against that backdrop, an explained variance of 8% (with two predictor variables related to pornography) in recreational attitudes and of 16% in relationship intimacy does not seem trivial to me. It may indeed be that other variables (family, peers etc.) have a greater influence, but this needs some more backing in order to contextualize the effects found.
I agree with the paper that the moral panic that surrounds pornography finds no support in any research published so far. However, this does not mean that the effects found in this paper and elsewhere are trivial, at least when considered in the context of media effects research and against the backdrop of the methodological and statistical problems that this kind of research faces. Second, it seems to me that the paper contradicts itself when, on the one hand, it rejects main effects as too simplistic (p. 3) and, on the other hand, describes the found indirect effects as practically insignificant. No serious media effects researcher would disagree that media effects are typically not direct and that a focus on the “how” and “why” of such effects is important. If we can explain how precisely media affect people, then this may have enormous practical significance, especially if we can outline which people may be affected and which may not (in line with Malamuth’s ideas).
Third, I agree that love maps and sexual scripts may explain sexual attitudes and behavior, probably even better than media use (p. 11). But it remains unclear to me where, precisely, this is tested in the model. Some clarification may be helpful. Fourth, it may also be helpful to specify how the distinction between imagined and real sex lives relates to the model tested, apart from outlining that perceptions of pornographic realism may never fully translate into people’s actual sex lives.
In sum, this is important and interesting research. However, the theoretical, conceptual, and methodological weaknesses currently outweigh the strengths of the paper so that its contribution to our knowledge about how the use of pornography affects relationship intimacy in adulthood is limited.
Courtney from Study Moose
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