Pornographic Socialization as “Selective‑Exposure”: Let it Go, Let it Go II (2021), by Paul J. Wright, PhD

Wright, P.J. Arch Sex Behav 50, 387–392 (2021).

“Let it go, let it go

Can’t hold it back anymore

Let it go, let it go

Turn away and slam the door” (Elsa – Disney’s Frozen)

The wisdom of Elsa’s self-admonition to let go of her attempts at overcontrol struck me as an important life-lesson the first time I watched Frozen with my nieces and nephews. I am hoping my own young daughter (just over a year old, and a first time listener to Frozen songs this week) can also learn the important principle of letting go.

Kohut, Landripet, and Stulhofer’s (2020) recent article on pornography and sexual aggression reminded me that I’ve wanted to suggest the same to my fellow pornography researchers for at least a few years now regarding the use of “control” variables (S. Perry, personal communication, June 26, 2018). Specifically, the purpose of this letter is to encourage my colleagues to “let go” and “slam the door” on the prevailing approach to the treatment of third variables in pornography effects research (i.e., the predominate conceptualization of third variables as potential confounds, rather than as predictors, mediators, or moderators).

I outline several problems with the current approach. I indict my own work as specific illustration, rather than cite by name the work of others, as I too have been guilty of overcontrol. Because I am friend, fellow Kinsey Institute affiliate, and collaborator to Stulhofer (Milas, Wright, & Stulhofer, 2020; Wright & Stulhofer, 2019), and because his article was the final prompt that motivated this letter, I also use Kohut et al. (2020) as a specific example with which to illustrate my points. My goal is to encourage research practices that will facilitate our understanding of the effects of pornography, not to excoriate or incite. I believe this is accomplished best through constructive evaluation of oneself and one’s friends, rather than personally unknown others.

Current Approach and Its Problems

Pornography effects research is a subfield of media effects research, wherein social scientists use quantitative methods to investigate the impact of pornography on users’ beliefs, attitudes, and behaviors (Wright, 2020a). I would be hard-pressed to recommend a more effective way to become exhaustively (and exhaustingly, in both the physical and mental sense) familiar with a body of research than to conduct regular narrative reviews (e.g., Wright, 2019, 2020a; Wright & Bae, 2016) and meta-analyses (e.g., Wright & Tokunaga, 2018; Wright, Tokunaga, & Kraus, 2016; Wright, Tokunaga, Kraus, & Klann, 2017). Through such literature syntheses, I have observed that (1) the vast majority of pornography effects studies from the 1990s on have been conducted using survey methods and (2) the predominate analytical paradigm in this body of research is to ask if pornography use (X) is still correlated with some belief, attitude, or behavior (Y) after statistically adjusting for an ever increasing and ever more peculiar list of “control” variables (Zad infinitum).

Here are just a few examples of variables that researchers have deemed necessary to include as controls: sexual experience, pubertal status, age, relationship status, sexual orientation, gender, education, socioeconomic status, race, perceptions of religious texts, emotional connectedness with caregiver, exposure to spousal violence, substance use, marital status, political affiliation, hours of work in a week, parents’ marital status, sex drive, ethnic identity, antisociality, depression symptoms, PTSD symptoms, relationship satisfaction, peer attachment, sex talk with peers, attachment to parents, television viewing, parental control, perceived sexual experience of peers, sensation seeking, sexual sensation seeking, life satisfaction, family background, sexual self-esteem, sexual assertiveness, attitudes toward sexual coercion, age of friends, social integration, internet use, music video viewing, religious affiliation, relationship length, immigrant background, living in a large city, parental employment, smoking, history of theft, truancy, conduct problems at school, age of sexual debut, dating activity, telling lies, cheating on tests, social comparison orientation, geographical location of residence, masturbation frequency, religious service attendance, sexual satisfaction, satisfaction with decision making, number of children, ever divorced, employment status, number of religious friends, frequency of sex in the past week, and enrollment in a postsecondary school.

Again–these are just a few examples.

The (ostensible) logic underlying the current approach is that pornography may not be an actual source of social influence; rather, some third-variable may cause individuals to both consume pornography and express/engage in the belief, attitude, or behavior in question. Few authors, however, explicitly identify how each variable they selected as a control could cause both pornography consumption and the outcome being studied. Sometimes, a general statement is made (sometimes with citations, sometimes without) that prior research has identified the variables as potential confounds and this is why they are included. Other times, no explanation is offered other than to list the various control variables. It is very difficult to find studies that identify a specific theoretical perspective as justifying the selection of controls (more on this point later). It is even rarer to find a study that justifies why the variables were modeled as controls rather than predictors, mediators, or moderators (I don’t believe I’ve ever seen this).

As promised, I confess that I too have included a battery of underjustified controls in several studies. As one example, in Wright and Funk (2014), I included seven control variables with no more justification than the statement that “prior research” indicated the “importance of controlling” for them (p. 211). As another example, in Tokunaga, Wright, and McKinley (2015) I included 10 control variables with the only justification being that they were “potential confounding variables” suggested “in previous research” (p. 581). In my defense, at least I actually cited the “prior/previous research” that had suggested these variables…

In sum, when the pornography effects research landscape is considered in totality, it is my contention that the inclusion of controls is idiosyncratic, inconsistent, atheoretical, and overdone. My best guess is that researchers either include controls because prior researchers have, they believe editors or reviewers will expect it (Bernerth & Aguinis, 2016), or because they have fallen victim to the “methodological urban legend” that “relationships with control variables are closer to the truth than without control variables” (Spector & Brannick, 2011, p. 296). I know that earlier in my career each of these applied to me.

The problems with this “everything but the kitchen sink approach” to control variable inclusion (Becker, 2005, p. 285) are manifold. But the two that are most relevant to the way controls are used in the pornography effects literature are:

  1. The chance of Type II error increasing due to true variance being partialled from the pornography–outcome correlation (Becker, 2005). Becker also notes that Type I errors can increase if the controls are associated with the predictor but not the criterion. However, I am not aware of this as a problem in the pornography effects literature. The question is always whether the statistically significant pornography–outcome bivariate correlation holds after controlling for Zad infinitum.
  2. The chance of totally missing and/or misunderstanding the actual “antecedents-contexts-effects” in the pornography– outcome dynamic dramatically increasing (Campbell & Kohut, 2017, p. 8). The progression of knowledge is not only stagnated but obfuscated every time variance is incorrectly attributed to “confounding” when the third-variable is, in reality, a predictor, mediator, or moderator in the ponography effects process (Spector & Brannick, 2011). It is partly for this reason that Meehl (1971) identified the current approach to third variables in the pornography effects literature (i.e., overwhelmingly modeled as controls, not predictors, mediators, or moderators) as a “methodological vice” that leads to “grossly erroneous inferences” (p. 147).

These problems can sometimes compound each other. For example, if what is actually a mediator is modeled as a control, processual misunderstanding increases as does the chance of a Type II error regarding a now increasingly likely null pornography–outcome partial correlation.

Religiosity and sensation seeking are prime examples. These variables are taken for granted as potential confounds that must be “controlled” when, in fact, there is evidence that they are part of the pornography effects process. Perry (2017, 2019; see also Perry & Hayward, 2017) has found in several longitudinal studies across different samples that pornography viewing prospectively predicts decreases in religiosity for both adolescents and adults. Thus, rather than religiosity confounding associations between, for instance, pornography use and recreational attitudes toward sex (e.g., Peter & Valkenburg, 2006), it may be a mediator (pornography → decreases in religiosity → more favorable attitudes toward recreational sex).

Sensation seeking has also been conceptualized as an immutable trait that could only confound pornography–outcome correlations. The taken-for-granted narrative is that sensation seeking could affect pornography consumption and (insert sexual risk outcome here) and therefore be a confound, but could not be impacted by pornography consumption. The empirical record suggests otherwise, however. In the realm of sexual media in general, Stoolmiller, Gerrard, Sargent, Worth, and Gibbons (2010) found in their four-wave, multiple year longitudinal study of adolescents that R-rated movie viewing predicted later sensation seeking, while earlier sensation seeking did not predict later R-rated movie viewing. Stoolmiller et al. note that their results “provide empirical evidence of an environmental media effect on sensation seeking” (p. 1). Subsequent analyses of these data focusing on sexual content specifically found that sexual content exposure predicted increases in sensation seeking, which in turn predicted risky sexual behavior (O’Hara, Gibbons, Gerrard, Li, & Sargent, 2012). In the realm of pornography specifically, our recent meta-analysis on pornography and condomless sex explicitly tested whether sensation seeking is better conceptualized as a confound or a mediator (Tokunaga, Wright, & Vangeel, 2020). The data supported a mediation conceptualization, not a confounding conceptualization.

“Preexisting” sexual attitudes have also been assumed to confound pornography–sexual behavior associations. However, using four national probability metasamples of adults, two measures of pornography consumption, two measures of sexual attitudes, and two measures of sexual behavior, I found in a recent study that sexual attitudes did not confound pornography—sexual behavior associations; they mediated them (pornography → sexual attitudes → sexual behavior) (Wright, 2020b). Likewise, our meta-analysis of the pornography and impersonal sex literature found that pornography use predicted impersonal sexual behavior through impersonal sexual attitudes (i.e., impersonal sexual attitudes were a mediator). No evidence was found for the prediction that associations between pornography and impersonal sexual behavior were confounded by sexual attitudes (Tokunaga, Wright, & Roskos, 2019).

But certain variables–for instance, demographics–must surely be confounds only, one might retort. I suggest that even “demographic” variables be carefully evaluated. Consider sexual orientation, a variable taken for granted as a control in the pornography effects literature. Interview data are fairly clear that pornography can affect both the awareness and expression of a sexually diverse identity. For example, a man in Giano’s (2019) study of how online sexual experiences shape gay men’s identities stated:

I remember the first time I went to a gay porn site and saw two men engaging in sex. I remember thinking I shouldn’t be turned on if I wasn’t gay, but I was. It was at that moment when I realized that this is real–I’m gay. It was equally exciting and scary. (p. 8)

Similarly, Bond, Hefner, and Drogos (2009) reported that “young males in the pre-coming out stage used Internet pornography to understand and develop their same-sex feelings” (p. 34).

In sum, with the current approach to controls in the pornography effects literature, (1) “power might be reduced [which] could lead to a Type II error (Becker, 2005, p. 287) and (2) “it is possible that the [third variables rotely modeled as controls] play a substantive rather than extraneous role in the network of relations the researcher is studying,” but we are regrettably unaware of this (Becker et al., 2016, p. 160).

Kohut et al. (2020) reported results on pornography consumption and sexual aggression from two samples of adolescent males. Their selection and justification of controls follows the predominate pattern in the pornography effects literature and is not my primary point of emphasis. Like many others, including myself (see Tokunaga et al., 2019 and Wright, 2020b, for exceptions), they did not identify any theory as guiding their identification of controls. They simply cited their own previous lament (Baer, Kohut, & Fisher, 2015) about previous studies “failing to account for potential confounds” (p. 2) and began to list several variables that prior studies had found to be correlated with pornography use or sexual aggression (e.g., sensation seeking, impulsiveness, sex drive). As the number of variables that prior studies have found to correlate with pornography use or sexual aggression easily numbers in the hundreds, it is not clear how the five control variables listed were identified among the sea of possibilities.

Ultimately, Kohut et al. concluded their section on controls with the argument that their inclusion provided a more rigorous test than would have been the case without their inclusion: “Failing to control for constructs that jointly influence pornography use and sexual aggression may substantially affect estimations of the activating effects of pornography use on sexual aggression” (p. 3). No mention is made of the possibility that these “confounds” could actually be mediators (e.g., sensation seeking–pornography consumption increasing sensation seeking, which subsequently increases sexual aggression) or moderators (e.g., impulsiveness–pornography consumption predicting sexual aggression, but only for men who are impulsive). Nor is any mention made of Bernerth and Aguinis’ (2016) “best-practice recommendations for control variable usage,” which are to “Stop” and not use controls if the only rationales for inclusion are either (1) “to provide conservative or rigorous tests of my hypotheses” or (2) “because previous research finds empirical relationships between this variable and variables in my study” (p. 273).

However, although problematic, it was not the specific controls or their inclusion rationale in this particular study that ultimately led me to (finally) write this letter. As I have admitted, I have been guilty of the same. No, the tipping point was Kohut et al.’s statements about our meta-analysis on pornography and sexually aggressive behavior (Wright et al., 2016) in relation to a recent meta-analysis by Ferguson and Hartley (2020). Given that the influence and importance of meta-analyses are significantly larger than any one study, these statements were the ultimate impetus for writing.

Kohut et al. (2020, p. 15) stated that our meta-analysis’ use of bivariate (rather than third-variable adjusted) correlations resulted in a “likely inflating [of] the focal associations” [we found that pornography use was a robust predictor of both verbal and physical sexual aggression]. They go on to say that their “observations of Wright et al.’s over-reliance on inflated effect sizes are corroborated by more recent meta-analytic findings which indicate that once control variables are properly accounted for, nonviolent pornography use is generally not associated with sexual aggression (Ferguson & Hartley, 2020)” (p. 16).

Two elements of these unfortunate statements are in need of redress.

Firstly, the notion that bivariate correlations are “inflated” while covariate-adjusted correlations are indicative of the true nature of the relationship in question is a classic illustration of the fallacy that Spector and Brannick (2011) called the “purification principle”:

The implicit belief that statistical controls can yield more accurate estimates of relationships among variables of interest, which we will call the “purification principle,” is so widespread, and is so accepted in practice, that we argue it qualifies as methodological urban legend— something accepted without question because researchers and reviewers of their work have seen it used so often that they do not question the validity of the approach. (p. 288)

Meehl (1971) said this about the erroneous notion that the inclusion of control variables leads to a more accurate conclusion about the nature of the XY association in question:

One cannot label a methodological rule as playing it safe when it is likely to produce pseudo-falsifications, unless we have a strange philosophy of science that says we want wrongly to abandon good theories. (p. 147)

I contend that the theories that have been used to predict that the use of pornography increases the likelihood of sexual aggression (e.g., classical conditioning, operant learning, behavioral modeling, sexual scripting, construct activation, gendered power) are good ones that we should not wrongly abandon because of the regrettably widespread application of the purification principle in pornography effects research.

This segues directly to the second unfortunate element of these statements. According to Kohut et al. (2020), “control variables are properly accounted for” by Ferguson and Hartley (2020). As Kohut et al. do not explain why they perceive Ferguson and Hartley’s use of controls as “proper,” we must go directly to the source. Upon doing so, one becomes confused as to how Kohut et al. evaluated Ferguson and Hartley’s list of controls as “proper,” since no such list is provided. The only specific mention of controls regards an index of “best-practice analysis” in which studies that adjusted for “mental health,” “family environment,” and “gender” are given “1 point” (p. 4). What is found is the repeated rhetorical reassurance from Ferguson and Hartley that their unarticulated and unexplained controls are “theoretically relevant.” What is also found is that the “standardized regression coefficients (βs)” used in their meta-analysis “were calculated from the most conservative value (e.g., involving the greatest number of theoretically relevant controls)” (p. 3).

Before circling back to the question of what theory or theories Ferguson and Hartley (2020) used to identify “theoretically relevant” controls (since no identificatory theory is mentioned in their paper), here are a few statements from methodologists pertinent to the singling out of “the most conservative value” for analysis:

We take exception to the common viewpoint that larger numbers of CVs [control variables] constitute a better, more rigorous methodological approach than including fewer or no CVs. This viewpoint is based on the flawed assumption that adding CVs necessarily produces more conservative tests of hypotheses and reveals the true relations among variables of interest. (Becker et al., 2016, p. 159)

Many researchers…presume that adding controls is conservative and likely to lead to a conclusion that is at least closer to the truth than omitting them. As Meehl (1971) notes, this practice is far from conservative. In fact it is in many cases quite reckless. (Spector & Brannick, 2011, p. 296)

A second answer that should also stop control consideration surrounds the rationale of conservative, rigorous, or stringent” tests of study hypotheses. This is a fallacy initially debunked years ago (Meehl, 1971; Spector & Brannick, 2011) with enough accumulated evidence at present to conclude there is nothing conservative or rigorous about including statistical controls (Carlson & Wu, 2012). (Bernerth & Aguinis, 2016, p. 275)

In sum, it is difficult to deduce how Ferguson and Hartley’s nonexistent list of controls was determined as “proper” unless guided by the usual regrettable assumption that “more controls = a more accurate result.”

And finally, back to the question of whether we should be assured by Ferguson and Hartley’s (2020) reassurance that the controls they included in their meta-analysis were derived theoretically. Since, as I mentioned, they neither provide their full list of controls or the theory or theories that were used to identify these controls in the primary studies they meta-analyzed, I searched the studies common to our meta-analysis (Wright et al., 2016) for the words “control,” “confound,” “covariate,” and “theory” to see if any theory was named to guide the selection of controls in these primary studies. I did not find any evidence that these studies used theory to guide their selection of controls (third variables in confluence model research [e.g., Malamuth, Addison, & Koss, 2000] are sometimes modeled as controls and other times as moderators). A key “best-practice” for control variable usage common to all of the control variable methodologists cited previously is the explicit guidance of theory. Without it, the use of controls is highly likely to result in Type II errors and/or model misspecification.


Where to go from here? There are two possibilities. I’ll start with my secondary preference.

One possibility is for pornography effects researchers to continue to control for “potential confounds,” but to do so following the best-practice recommendations from control variable methodologists (e.g., Becker et al., 2016; Bernerth & Aguinis, 2016; Spector & Brannick, 2011). These include reporting results with and without controls, explicitly incorporating controls into hypotheses and research questions, and subjecting controls to the same reliability and validity standards expected of focal measures. I note, however, that the #1 suggestion of Becker et al. (2016) is “When in doubt, leave them out!”

My first preference is for pornography effects researchers to let go of the “potential confound” paradigm completely and move into what might be called a “predictors, processes, and contingencies” paradigm. In other words, instead of considering third variables as extraneous to and contaminant of the effects of pornography on beliefs, attitudes, and behaviors, I would prefer if pornography researchers incorporated third variables into causal models as antecedents, mediators, and moderators. This preference aligns with Slater’s (2015) Reinforcing Spirals Model (RSM) of media use and effects:

Traditional media effects analyses attempt to assess cause-effect relations by controlling away as many other variables as might be implicated in the causal process, to minimize the threat of third-variable, alternative causal explanations. The RSM, in contrast, would suggest that further insight can be gained by incorporating variables, such as individual differences and social influences as predictors of media use rather than as statistical controls. One can then consider the total effect of media use as summed across all the direct and indirect effects. In other words, RSM suggests that traditional media effects analyses, by trying to control for variables that are part of the causal process and are not really third variables providing competing causal explanations, in fact are likely to reduce the actual effects that should be attributed to the role of media use. (p. 376)

Although social science rests on fewer unverifiable assumptions than other methods of knowing about human behavior, if we are honest with ourselves, we must acknowledge that our studies proceed from certain assumptions that can never be irrefutably confirmed or falsified to the satisfaction of 100% of scholars. I was born in 1979. There were social scientists who believed pornography could not affect its users before I was born and I guarantee there will be social scientists when I’m gone (hopefully, at least another forty or so years) who will believe the same.

While it is an existential possibility that pornography is the lone communicative domain where messages and meanings have zero impact, and that any correlation between pornography use and beliefs, attitudes, and behaviors is always spurious and due entirely to some other independent and immutable causal agent, I believe there is sufficient theoretical reasoning and empirical evidence to assume that this is not the case. Accordingly, I echo Elsa once again in asking my colleagues to “turn away and slam the door” on the “does pornography still predict (outcome) after controlling for the kitchen sink?” approach. Instead, I ask that we direct our attention to third variables that differentiate the frequency and type of pornography consumed, the mechanisms that lead to particular outcomes, and the people and contexts for whom those outcomes are more or less likely.


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