The concept of conditional learning raises the issue of whether adaptive strategies are consciously implemented or whether they automatically arise due to environmental pressures to promote an individual’s survival. Consider the recent finding that individuals who enter military service after high school show relatively little increases in agreeableness over the subsequent six years compared to individuals who enter community service (Jackson, Thoemess, Jonkmann, Lüdtke, & Trautwein, 2012). Stated differently, high school graduates generally increase in agreeableness in the six years following high school, but those who enter the military do not show this developmental trend. The flexible ontogeny framework suggests that, whereas all individuals have the latent capacity to act in an agreeable manner as they enter young adulthood, environmental pressures of military service (e.g., the need to show callousness toward enemies in combat) curb this capacity and cause individuals to adopt a less agreeable strategy. Again, however, we do not know whether these individuals a) consciously chose to act less agreeable given the knowledge that such behavior would increase their likelihood of survival; or b) less agreeable behavior merely emerged due to day-to-day situational pressures inherent in the military. While consideration of these two possibilities risks rekindling the debate on whether behavior is more attributable to persons or situations, a better understanding of the mechanisms driving flexible ontogeny would help elucidate the how and why of personality development.

Things look somewhat less pristine when considering only social psychological phenomena. The same correlation between lab and field effect sizes was .53 for social psychological research, and Mitchell found that 21 out of 80 effect sizes in the lab actually changed sign (i.e., went from negative to positive) when examined in the field. These findings, while certainly refuting the idea that all social psychological lab studies are fabricated, contrived, and not applicable to the real world, suggest that effects seen in the lab exhibit considerable deviation from those found in the field.

Why does social psychological research exhibit more external invalidity when compared to psychology as a whole? The culprit may be small effect sizes. The fact that 21 effect sizes changed sign from lab to field doesn’t necessarily indicate problems with the validity of our research; rather, it could merely reflect an abundance of small effect sizes that—regardless of sign—do not differ from zero more than would be expected by chance. For example, an effect size of r = .09 in the lab might conceivably switch to r = -.04 in the field if the population effect size is actually ρ = 0. Indeed, the correlation between lab and field effect sizes was only .30 for lab studies with small effect sizes—which comprised 66.3% of social psychology lab effects surveyed—compared with a correlation of .57 for lab studies with medium effect sizes. A preliminary conclusion from this report might be to adopt a skeptical view of lab studies with small effect sizes due to the relatively high likelihood that these effects will not translate to the real world.

As a side note, young researchers enamored with the virtues of personality psychology—not naming names—might be tempted to boast about the excellent view of personality research provided by Mitchell’s report: effect sizes in lab and field studies correlated .83 and only 1 of 22 in-lab effect sizes changed sign when examined in the field. Is personality psychology really that much more reliable and externally valid that social psychology? No way! Lab studies falling under the umbrella of personality research do not generally attempt to create complex situations like those classified as social psychological research; in-lab personality research is generally pretty simple and often involves procedures similar to those one would use in the field. For example, a number of studies examining attributional styles of depressed individuals found nearly identical effect sizes in lab and in the field. Few researchers would show much surprise that self-report assessments of attributional style are completed in a similar manner regardless of the setting in which the study was conducted. In contrast, studies examining aggressive behavior—of which Mitchell examined many—may be more hard-pressed to replicate the heat of aggression that we see in the real world when confined to the sterile lab environment. That’s not a fault of the researchers, but rather a necessary evil of scientifically measuring social interaction.

An experimental design such as this one would become far more theoretically rich, however, with the addition of a neutral emotion condition in which participants were not induced to feel any particular mood. This would allow a researcher to ask whether or not any observed difference between the positive mood condition and the negative mood condition is driven by a) the positive mood, b) the negative mood, or c) both. In the first case, we would expect the positive mood group’s ratings to be very positive, whereas the negative and neutral mood group’s ratings would be more negative and roughly equal. In the second case, we would expect the negative mood group’s ratings to be very negative, whereas the positive and neutral mood group’s ratings would be more positive and roughly equal. In the final case, we would expect the positive mood group’s ratings to be more positive than the neutral group’s ratings, which in turn would be more positive than the negative group’s ratings.

The addition of a neutral emotion condition, while adding an important theoretical layer to the study, would introduce an unwanted statistical impediment in the context of an analysis of variance. Let’s assume case “c” would be the result, indicating that both positive and negative mood are theoretically important, and let’s further assume that the mean positivity of each group’s judgments for this sample was 8, 5, and 2 (on a 10-point scale) for positive, neutral, and negative, respectively. An ANOVA tests the ratio of between-groups variance (i.e., meaningful group differences; denoted B for this example) to within-groups variance (i.e., error; denoted W), with larger numbers yielding increasingly significant and meaningful results. B is calculated by summing the difference between grand mean (in this case (8 + 5 + 2) / 3 = 5) of all participants and the mean of a given group for all groups. We also know that, under the traditional homogeneity of variance assumption, each experimental group will have equal within-groups variances; for the purposes of this example, let’s assume that each group’s W is equal to 1.

The equations for the ANOVA components show us that, if positive mood and negative mood were the only two conditions employed in the experiment, the ratio of B/W would equal (3^2 + 3^2)/2 = 9. Now consider the three group design “c” in which the mean positivity of judgments in the positive and negative mood groups are the exact same as in the two-group condition. Our ANOVA would yield a result of (3^2 + 3^2 + 0^2)/3 = 6. Our test just got weaker—and possibly dipped below significance—even though the effect of positive and negative mood did not get weaker! How did this happen? We introduced an additional source of within-groups variance without introducing an additional source of between-groups variance. The neutral mood condition is expected to fall at exactly the grand mean of the entire sample, or half way between the positive and negative mood conditions, because feeling no emotion should not cause systematic shifts in people’s judgments. Thus, for the neutral group, B = 0 and W = 1. The researcher, simply by adding a condition of great theoretical import, has statistically shot himself in the ear with a loaded gun by reducing the chances that he will conduct a statistically significant test of his hypothesis.

How should emotion researchers balance theoretical richness with the necessity of arriving at statistically meaningful conclusions? One potentially fruitful solution would be to conduct planned contrasts between only the groups of interest—here the positive and negative mood groups—as such tests can be employed without first producing a significant omnibus ANOVA. If planned contrasts yielded significant results, this would allow the researcher to conclude that positive mood and negative mood indeed have divergent effects on judgments of others. While this analytic strategy still bypasses the question of whether positive or negative emotion, or a combination of the two, are driving the effect, it allows the researcher to reach an important conclusion from a data set that may look spuriously messy due to the inclusion of the neutral condition. Given that emotion researchers include neutral conditions for the purpose of arriving at the most complete and theoretically meaningful conclusions possible, they should not be penalized for the unwanted statistical byproducts.

Note: Inspired by a late night chat with one Conor M. Steckler in Gastown, Vancouver, BC.

And… lab members in action

Another problem endemic to brief reports, which also received attention in the special section, is the inflation of type-I error rate, both within a specific brief report and in any area of psychology that bases its knowledge largely on brief reports. Consider a basic law of statistics: any psychological phenomena has a true effect size—whether quantified with a t-test, ANOVA, or correlation coefficient—and the sampling distribution of estimates of this effect size should be normally distributed around the true effect with a standard error that decreases as the number of data points (e.g., subjects within studies; studies within papers) used to measure the effect in a given instance increases. In other words, any test of a psychological phenomenon will more closely approximate its true effect size to the extent that it involves a larger number of data points and thus is less susceptible to variation due to sampling error (for further discussion, see LeBel & Peters, 2011, Review of General Psychology, p. 375-376).

Now, consider brief reports. First, brief reports include fewer data points (e.g., fewer subjects overall; fewer studies) than longer articles and thus by definition contain more sampling error. Thus, the effect sizes disseminated in brief reports are likely to vary to a greater degree from the true effect size of the psychological phenomenon in question than the effects reported in longer articles. An immediate consequence of these error-filled effect sizes is that they are more likely to reach magnitudes sufficient to attain statistical significance even if the true effect size of the psychological phenomenon is near-zero. This consequence is similar to the critiques of underpowered studies raised by the authors of the False Positive Psychology paper.

A second, and more often overlooked, consequence is that scientific knowledge based on aggregation of brief reports is likely to contain more variation than knowledge based on aggregation of longer articles. Again, given that brief reports contain fewer data points that longer articles, their estimations of true psychological effect sizes are likely to contain more sampling error. In other words, any given brief report is more likely to misestimate a true psychological effect than a corresponding longer paper. Thus, any area of psychology that is flooded with brief reports is likely to contain wdely divergent estimates of true population effect sizes, thus causing some confusion and misdirection for researchers attempting to systematically advance the field. In addition, due to publication bias toward non-null results, certain of these widely divergent effects (i.e., those that are large and in the direction that previous theory would dictate) are more likely to be published. Such publication bias will further shift the field’s perception of psychological phenomena away from their true effect sizes (for an illustration, see Bertamini & Munafò, 2012, Perspectives on Psychological Science, p. 68-69).

In conclusion, careful consideration of the points raised in the current issue of Perspectives should serve as a cautionary tale regarding publication trends in our field.

Constraints aside, look around the rest of the animal kingdom and you will find morality mostly absent from most species. The capacity to experience empathy and compassion for non-kin seems against the red tooth and claw of nature, and it usually is (hence the absence). It is for this reason altruism presents a paradox for evolutionary thinkers. Defined as any act that reduces an individual’s fitness for the benefit of another, altruism should, on first glance, have a difficult time evolving. Some acts which look like altruism are not altruistic at all. For example, a mother nurturing her young is not an act of altruism because the act increases the likelihood of the survival and reproduction of those offspring (which is directly related to design for passing on genes well).

Is altruistic behavior towards strangers just the brain misfiring?  Was this circuitry shaped for kin? What creative selective forces shaped our moral emotions?

On the surface, moral emotions seem to benefit the group. But as George C. Williams notes in his book, Adaptation and Natural Selection, it is necessary to distinguish between what he calls a population of adapted individuals and an adapted population of individuals. Williams goes on to raise some theoretical problems in ascribing group selection as a major creative force of adaptation. He writes,

“Just as the evolution of even the simplest organic adaptation requires the operation of selection at many loci for many generations, so also would the production of biotic adaptation require the selective substitution of many groups. This is a major theoretical difficulty. Consider how rapid is the turnover of generations in even the slowest breeding organisms, compared to the rate at which populations replace each other. The genesis of biotic adaptation must for this reason be orders of magnitude slower than that of organic adaptation.” (1996/66, pg. 114)

 

To me this means that any benefit for the group at cost to an individual is constrained by the more frequent within-group selection of alternative alleles for benefit of individuals (and ultimately those alleles) at expense of (or at least indifference towards) the group.

If we are looking at a population of adapted individuals, the experience of moral emotions should have an adaptive function that benefits the individual’s fitness. Also, any cognitive shifts, if adaptations, in witnessing the expression of emotion should benefit the perceiver, even when it seems only of benefit to the expresser. If a reaction to an expression was a hindrance to the perceiver I see no reason why perceivers should “buy in” to the expression.  Because humans live in complicated social groups, adaptations to the group environment are likely to have arisen, but the creative force behind them, I suspect, is within-group selection and because of that I do not think many, if any, of our moral emotions will turn out to be altruistic, in the evolutionary sense.