Thursday, November 28, 2019

Switzerland: Those exposed to civil conflict/mass killing during childhood are 35 pct more prone to violent crime; effect is mostly confined to co-nationals, consistent with inter-group hostility persisting over time

Couttenier, Mathieu, Veronica Petrencu, Dominic Rohner, and Mathias Thoenig. 2019. "The Violent Legacy of Conflict: Evidence on Asylum Seekers, Crime, and Public Policy in Switzerland." American Economic Review, 109 (12): 4378-4425. DOI: 10.1257/aer.20170263

Abstract: We study empirically how past exposure to conflict in origin countries makes migrants more violence-prone in their host country, focusing on asylum seekers in Switzerland. We exploit a novel and unique dataset on all crimes reported in Switzerland by the nationalities of perpetrators and of victims over 2009–2016. Our baseline result is that cohorts exposed to civil conflict/mass killing during childhood are 35 percent more prone to violent crime than the average cohort. This effect is particularly strong for early childhood exposure and is mostly confined to co-nationals, consistent with inter-group hostility persisting over time. We exploit cross-region heterogeneity in public policies within Switzerland to document which integration policies are best able to mitigate the detrimental effect of past conflict exposure on violent criminality. We find that offering labor market access to asylum seekers eliminates two-thirds of the effect.

Could they be lying?: Vegetarian women reported that they are more prosocially motivated to follow their diet & adhere to their diet more strictly (i.e., are less likely to cheat & eat meat)

Gender Differences in Vegetarian Identity: How Men and Women Construe Meatless Dieting. Daniel L.Rosenfeld. Food Quality and Preference, November 28 2019, 103859.

• This research evaluated psychological differences between vegetarian men and women.
• Women are more prosocially motivated to follow a vegetarian diet than men are.
• Women adhere to their vegetarian diet more strictly than men do.

Abstract: Meat is deeply associated with masculine identity. As such, it is unsurprising that women are more likely than men are to become vegetarian. Given the gendered nature of vegetarianism, might men and women who become vegetarian express distinct identities around their diets? Through two highly powered preregistered studies (Ns = 890 and 1,775) of self-identified vegetarians, combining both frequentist and Bayesian approaches, I found that men and women differ along two dimensions of vegetarian identity: (1) dietary motivation and (2) dietary adherence. Compared to vegetarian men, vegetarian women reported that they are more prosocially motivated to follow their diet and adhere to their diet more strictly (i.e., are less likely to cheat and eat meat). By considering differences in how men and women construe vegetarian dieting, investigators can generate deeper insights into the gendered nature of eating behavior.

Keywords: vegetarianismfood choicedietinggenderidentity

About lies and prosociality in women, nonreligion is socially risky, atheism is more socially risky than other forms of nonreligion, & women and members of other marginalized groups avoid the most socially risky forms of nonreligion: From Existential to Social Understandings of Risk: Examining Gender Differences in Nonreligion. Penny Edgell, Jacqui Frost, Evan Stewart. Social Currents, Dec 2018.

Check also Taste and health concerns trump anticipated stigma as barriers to vegetarianism. Daniel L.Rosenfeld, A. JanetTomiyama. Appetite, Volume 144, January 1 2020, 104469.

And Relationships between Vegetarian Dietary Habits and Daily Well-Being. John B. Nezlek, Catherine A. Forestell & David B. Newman. Ecology of Food and Nutrition,

And Psychology of Men & Masculinity: Eating meat makes you sexy / Conformity to dietary gender norms and attractiveness. Timeo, S., & Suitner, C. (2018). Eating meat makes you sexy: Conformity to dietary gender norms and attractiveness. Psychology of Men & Masculinity, 19(3), 418-429.

Great interest exists in identifying methods to predict neuropsychiatric disease states and treatment outcomes from high-dimensional data, including neuroimaging and genomics data; best practices are discussed

Establishment of Best Practices for Evidence for Prediction: A Review. Russell A. Poldrack, Grace Huckins, Gael Varoquaux. JAMA Psychiatry, November 27, 2019. doi:

Importance  Great interest exists in identifying methods to predict neuropsychiatric disease states and treatment outcomes from high-dimensional data, including neuroimaging and genomics data. The goal of this review is to highlight several potential problems that can arise in studies that aim to establish prediction.

Observations  A number of neuroimaging studies have claimed to establish prediction while establishing only correlation, which is an inappropriate use of the statistical meaning of prediction. Statistical associations do not necessarily imply the ability to make predictions in a generalized manner; establishing evidence for prediction thus requires testing of the model on data separate from those used to estimate the model’s parameters. This article discusses various measures of predictive performance and the limitations of some commonly used measures, with a focus on the importance of using multiple measures when assessing performance. For classification, the area under the receiver operating characteristic curve is an appropriate measure; for regression analysis, correlation should be avoided, and median absolute error is preferred.

Conclusions and Relevance  To ensure accurate estimates of predictive validity, the recommended best practices for predictive modeling include the following: (1) in-sample model fit indices should not be reported as evidence for predictive accuracy, (2) the cross-validation procedure should encompass all operations applied to the data, (3) prediction analyses should not be performed with samples smaller than several hundred observations, (4) multiple measures of prediction accuracy should be examined and reported, (5) the coefficient of determination should be computed using the sums of squares formulation and not the correlation coefficient, and (6) k-fold cross-validation rather than leave-one-out cross-validation should be used.

Excerpts (full paper, references, etc., at the DOI above):


The development of biomarkers for disease is attracting increasing interest in many domains of biomedicine. Interest is particularly high in neuropsychiatry owing to the current lack of biologically validated diagnostic or therapeutic measures.1 An essential aspect of biomarker development is demonstration that a putative marker is predictive of relevant behavioral outcomes,2 disease prognosis,3 or therapeutic outcomes.4 As the size and complexity of data sets have increased (as in neuroimaging and genomics studies), it has become increasingly common that predictive analyses have been performed using methods from the field of machine learning, with techniques that are purpose-built for generating accurate predictions on new data sets.

Despite the potential utility of prediction-based research, its successful application in neuropsychiatry—and medicine more generally—remains challenging. In this article, we review a number of challenges in establishing evidence for prediction, with the goal of providing simple recommendations to avoid common errors. Although most of these challenges are well known within the machine learning and statistics communities, awareness is less widespread among research practitioners.

We begin by outlining the meaning of the concept of prediction from the standpoint of machine learning. We highlight the fact that predictive accuracy cannot be established by using the same data both to fit and test the model, which our literature review found to be a common error in published claims of prediction. We then turn to the question of how accuracy should be quantified for categorical and continuous outcome measures. We outline the ways in which naive use of particular predictive accuracy measures and cross-validation methods can lead to biased estimates of predictive accuracy. We conclude with a set of best practices to establish valid claims of successful prediction.

Code to reproduce all simulations and figures is available at

Association vs Prediction

A claim of prediction is ultimately judged by its ability to generalize data to new situations; the term implies that it is possible to successfully predict outcomes in data sets other than the one used to generate the claim. When a statistical model is applied to data, the goodness of fit of that model to those data will in part reflect the underlying data-generating mechanism, which should generalize to new data sets sampled from the same population, but it will also include a contribution from noise (ie, unexplained variation or randomness) that is specific to the particular sample.5 For this reason, a model will usually fit better to the sample used to estimate it than it will to a new sample, a phenomenon known in machine learning as overfitting and in statistics as shrinkage.

Because of overfitting, it is not possible to draw useful estimates of predictive accuracy simply from a model’s goodness of fit to a data set; such estimates will necessarily be inflated, and their degree of optimism will depend on many factors, including the complexity of the statistical model and the size of the data set. The fit of a model to a specific data set can be improved by increasing the number of parameters in the model; any data set can be fit with 0 error if the model has as many parameters as data points. However, as the model becomes more complex than the process that generates the data, the fit of the model starts to reflect the specific noise values in the data set. A sign of overfitting is that the model fits well to the specific data set used to estimate the model but fits poorly to new data sets sampled from the same population. Figure 1 presents a simulated example, in which increasing model complexity results in decreased error for the data used to fit the model, but the fit to new data becomes increasingly poor as the model grows more complex than the true data-generating process.

Because we do not generally have a separate test data set to assess generalization performance, the standard approach in machine learning to address overfitting is to assess model fit via cross-validation, a process that uses subsets of the data to iteratively train and test the predictive performance of the model. The simplest form of cross-validation is known as leave-one-out, in which the model is successively fit on every data point but 1 and is then tested on that left-out point. A more general cross-validation approach is known as k-fold cross-validation, in which the data are split into k different subsets, or folds. The model is successively trained on every subset but 1 and is then tested on the held-out subset. Cross-validation can also help discover the model that will provide the best predictive performance on a new sample (Figure 1).

One might ask how poorly inflated the in-sample association is as an estimate of out-of-sample prediction; if the inflation is small, or only occurs with complex models, then perhaps it can be ignored for practical purposes. Figure 2 shows an example of how the optimism of in-sample fits depends on the complexity of the statistical model; in this case, we use a simple linear model but vary the number of irrelevant independent variables in the model. As the number of variables increases, the fit of the model to the sample increases owing to overfitting. However, even for a single predictor in the model, the fit of the model is inflated compared with new data or cross-validation. The optimism of in-sample fits is also a function of sample size (Figure 2). This example demonstrates the utility of using cross-validation to estimate predictive accuracy on a new sample.

Statistical Significance vs Useful Prediction

A second reason that significant statistical association does not imply practically useful prediction is exemplified by the psychiatric genetic literature. Large genome-wide association studies have now identified significant associations between genetic variants and mental illness diagnoses. For example, Ripke et al6 compared more than 21 000 patients with schizophrenia with more than 38 000 patients without schizophrenia and found 22 genetic variants significant at a genome-wide level (P = 5 × 10−8), the strongest of which (rs9268895) had a combined P value of 9.14 × 10−14. However, this strongest association would be useless on its own as a predictor of schizophrenia. The combined odds ratio for this risk variant was 1.167; assuming a population prevalence of schizophrenia of 1 in 196 individuals as the baseline risk,7 possessing the risk allele for this strongest variant would raise an individual’s risk to 1 in 167. Such an effect is far from clinically actionable. In fact, the increased availability of large samples has made clear the point that Meehl8 raised more than 50 years ago, which stated that in the context of null hypothesis testing, as samples become larger, even trivial associations become statistically significant.

A more general challenge exists regarding the prediction of uncommon outcomes, such as a diagnosis of schizophrenia. Consider the case in which a researcher has developed a test for schizophrenia that has 99% sensitivity (ie, a 99% likelihood that the test will return a positive result for someone with the disease) and 99% specificity (ie, a 99% likelihood that the test will return a negative result for someone without the disease). These are performance levels that any test developer would be thrilled to obtain; in comparison, mammography has a sensitivity of 87.8% and a specificity of 90.5% for the detection of breast cancer.9 If this test for schizophrenia were used to screen 1 million people, it would detect 99% of those with schizophrenia (5049 individuals) but would also incorrectly detect 9949 individuals without schizophrenia; thus, even with exceedingly high sensitivity and specificity, the predictive value of a positive test result remains well below 50%. As we can straightforwardly deduce from the Bayes theorem, false alarm rates will usually be high when testing for events with low baseline rates of occurrence.

Misinterpretation of Association as Prediction

A significant statistical association is insufficient to establish a claim of prediction. However, in our experience, it is common for investigators in the functional neuroimaging literature to use the term prediction when describing a significant in-sample statistical association. To quantify the prevalence of this practice, we identified 100 published studies between December 24, 2017, and October 30, 2018, in PubMed by using the search terms fMRI prediction and fMRI predict. For each study, we identified whether the purported prediction was based on a statistical association, such as a significant correlation or regression effect, or whether the researchers used a statistical procedure specifically designed to measure prediction, such as cross-validation or out-of-sample validation. We only included studies that purported to predict an individual-level outcome based on fMRI data and excluded other uses of the term prediction, such as studies examining reward prediction error. A detailed description of these studies is presented in the eTable in the Supplement.

Of the 100 studies assessed, 45 reported an in-sample statistical association as the sole support for the claims of prediction, suggesting that the conflation of statistical association and predictive accuracy is common.10 The remaining studies used a mixture of cross-validation strategies, as shown in Figure 3.

Factors That Can Bias Assessment of Prediction

Although performing some type of assessment of an out-of-sample prediction is essential, it is also clear that cross-validation still leaves room for errors when establishing predictive validity. We now turn to issues that can affect the estimation of predictive accuracy even when using appropriate predictive modeling methods.

- Small Samples

The use of cross-validation with small samples can lead to highly variable estimates of predictive accuracy. Varoquaux11 noted that a general decrease in the level of reported prediction accuracy can be observed as sample sizes increase. Given the flexibility of analysis methods12 and publication bias for positive results, such that only the top tail of accuracy measures is reported, the high variability of estimates with small samples can lead to a body of literature with inflated estimates of predictive accuracy.

Our literature review found a high prevalence of small samples, with more than half of the samples comprising fewer than 50 people and 15% of the studies with samples comprising fewer than 20 people (Figure 3). Most studies that use small samples are likely to exhibit highly variable estimates. This finding suggests that many of the claims of predictive accuracy in the neuroimaging literature may be exaggerated and/or not valid.

- Leakage of Test Data

To give a valid measure of predictive accuracy, cross-validation needs to build on a clean isolation of the test data during the fitting of models to the training data. If information leaks from the testing set into the model-fitting procedure, then estimates of predictive accuracy will be inflated, sometimes wildly. For example, any variable selection that is applied to the data before application of cross-validation will bias the results if the selection involves knowledge of the variable being predicted. Of the 57 studies in our review that used cross-validation procedures, 10 may have applied dimensionality reduction methods that involved the outcome measure (eg, thresholding based on correlation) to the entire data set. This lack of clarity raises concerns regarding the level of methodological reporting in these studies.13

In addition, any search across analytic methods, such as selecting the best model or the model parameters, must be performed using nested cross-validation, in which a second cross-validation loop is used within the training data to determine the optimal method or parameters. The best practice is to include all processing operations within the cross-validation loop to prevent any potential for leakage. This practice is increasingly possible using cross-validation pipeline tools, such as those available within the scikit-learn software package (scikit-learn Developers).14

- Model Selection Outside of Cross-validation

Selecting a predictive method based on the data creates an opportunity for bias that could involve the potential use of a number of different classifiers, hyperparameters for those classifiers, or various preprocessing methods. As in standard data analysis, there is a potential garden of forking paths,15 such that data-driven modeling decisions can bias the resulting outcomes even if there is no explicit search for methods providing the best results. The outcomes are substantially more biased if an explicit search for the best methods is performed without a held-out validation set.

As reported in studies by Skocik et al16 using simulations and Varoquaux11 using fMRI data, it is possible to obtain substantial apparent predictive accuracy from data without any true association if a researcher capitalizes on random fluctuations in classifier performance and searches across a large parameter space. A true held-out validation sample is a good solution to this problem. A more general solution to the problem of analytic flexibility is the preregistration of analysis plans before any analysis, as is increasingly common in other areas of science.17

- Nonindependence Between Training and Testing Sets

Like any statistical technique, the use of cross-validation to estimate predictive accuracy involves assumptions, the failure of which can undermine the validity of the results. An important assumption of cross-validation is that observations in the training and testing sets are independent. While this assumption is often valid, it can break down when there are systematic relationships between observations. For example, the Human Connectome Project data set includes data from families, and it is reasonable to expect that family members will be closer to each other in brain structure and function than will individuals who are not biologically related.

Similarly, data collected as a time series will often exhibit autocorrelation, such that observations closer in time are more similar. In these cases, there are special cross-validation strategies that must be used to address this structure. For example, in the presence of family structure, such as the sample used in the Human Connectome Project, a researcher might cross-validate across families (ie, leave-k-families-out) rather than individuals to address the nonindependence potentially induced by family structure.18

- Quantification of Predictive Accuracy

Two main categories of problems occur in predictive modeling. The first, classification accuracy, involves the prediction of discrete class membership, such as the presence or absence of a disease diagnosis; the second, regression accuracy, involves the prediction of a continuous outcome variable, such as a test score or disease severity measure. In our literature review, we found that 37 studies performed classification while 64 performed regression to determine predictive accuracy. These strategies generally involve different methods for quantification of accuracy, but in each case, potential problems can arise through the naive use of common methods.

- Quantifying Classification Accuracy

In a classification problem, we aim to quantify our ability to accurately predict class membership, such as the presence of a disease or a cognitive state. When the number of members in each class is equal, then average accuracy (ie, the proportion of correct classifications, as used in the examples in Figure 2) is a reasonable measure of predictive accuracy. However, if any imbalance exists between the frequencies of the different classes, then average accuracy is a misleading measure. Consider the example of a predictive model for schizophrenia, which has a prevalence of 0.5% in the population; the classifier can achieve average accuracy of 99.5% across all cases by predicting that no one has the disease, simply owing to the low frequency of the disease.

A standard method to address the class imbalance problem is to use the receiver operating characteristic curve from signal detection theory.19 A receiver operating characteristic curve can be constructed given any continuous measure of evidence, as provided by most classification models. A threshold is then applied to this measure of evidence, systematically ranging from low (in which most cases will be assigned to the positive class, and the number of false positives will be high) to high (in which most cases will be assigned to the negative class, and the number of false positives will be low). The area under the curve can then be used as an integrated measure of classification accuracy. A perfect prediction leads to an area under the curve of 1.0, while a fully random prediction leads to an area under the curve of 0.5. Importantly, the area under the curve value of 0.5 expected by chance is not biased by imbalanced frequencies of positive and negative cases in the way that simple measures of accuracy would be. It is also useful to separately present the sensitivity (ie, the proportion of positive cases correctly identified as positive) and specificity (ie, the proportion of negative cases correctly identified as negative) of the classifier, to allow assessment of the relative balance of false positives and false negatives.

- Quantifying Regression Accuracy

It is increasingly common to apply predictive modeling in cases in which the outcome variable is continuous rather than discrete—that is, in regression rather than classification problems. For example, a number of studies in cognitive neuroscience have attempted to predict phenotypic measures, such as age,20 personality,21 or behavioral outcomes.22 For continuous predictions, accuracy can be quantified either by the relation between the predicted and actual values, relative to perfect prediction, or by a measure of the absolute difference between predicted and actual values (ie, the error). A relative measure is useful because its value can easily be related to the success of the prediction. For this purpose, a useful measure is the fraction of explained variance, often called the coefficient of determination or R2. If a model makes perfect predictions, its associated R2 value will be 1.0, whereas a model making random predictions should have an R2 value of approximately 0. If a model is particularly poor, to the point that its predictions are less accurate than they would be if the model simply returned the mean value for the data set, the R2 value can be negative, despite the fact that it is called R2. The disadvantage of this measure is that it does not support comparisons of the quality of predictions across different data sets because the variance of the outcome variable may differ between one data set and another. For this purpose, absolute error measurements, such as the mean absolute error, which has the benefit of quantifying error in the units of the original measure (such as IQ points), are useful.

It is common in the literature to use the correlation between predicted and actual values as a measure of predictive performance; of the 64 studies in our literature review that performed prediction analyses on continuous outcomes, 30 reported such correlations as a measure of predictive performance. This reporting is problematic for several reasons. First, correlation is not sensitive to scaling of the data; thus, a high correlation can exist even when predicted values are discrepant from actual values. Second, correlation can sometimes be biased, particularly in the case of leave-one-out cross-validation. As demonstrated in Figure 4, the correlation between predicted and actual values can be strongly negative when no predictive information is present in the model. A further problem arises when the variance explained (R2) is incorrectly computed by squaring the correlation coefficient. Although this computation is appropriate when the model is obtained using the same data, it is not appropriate for out-of-sample testing23; instead, the amount of variance explained should be computed using the sum-of-squares formulation (as implemented in software packages such as scikit-learn).

As discussed previously in this section, leave-one-out cross-validation is problematic because it allows for the possibility of negative R2 values. For classification settings, the effect is the same; in a perfectly balanced data set, leave-one-out cross-validation creates a testing set comprising a single observation that is in the minority class of the training set. A simple prediction rule, such as majority vote, would thus lead to predictions that would be incorrect.24 Rather, the preferred method of performing cross-validation is to leave out 10% to 20% of the data, using k-fold or shuffle-split techniques that repeatedly split the data randomly. Larger testing sets enable a good computation of measurements, such as the coefficient of determination or area under the receiver operating characteristic curve.

Best Practices for Predictive Modeling

We have several suggestions for researchers engaged in predictive modeling to ensure accurate estimates of predictive validity:

.    In-sample model fit indices should not be reported as evidence for predictive accuracy because they can greatly overstate evidence for prediction and take on positive values even in the absence of true generalizable predictive ability.

.    The cross-validation procedure should encompass all operations applied to the data. In particular, predictive analyses should not be performed on data after variable selection if the variable selection was informed to any degree by the data themselves (ie, post hoc cross-validation). Otherwise, estimated predictive accuracy will be inflated owing to circularity.25

.    Prediction analyses should not be performed with samples smaller than several hundred observations, based on the finding that predictive accuracy estimates with small samples are inflated and highly variable.26

.    Multiple measures of prediction accuracy should be examined and reported. For regression analyses, measures of variance, such as R2, should be accompanied by measures of unsigned error, such as mean squared error or mean absolute error. For classification analyses, accuracy should be reported separately for each class, and a measure of accuracy that is insensitive to relative class frequencies, such as area under the receiver operating characteristic curve, should be reported.

.    The coefficient of determination should be computed by using the sums-of-squares formulation rather than by squaring the correlation coefficient.

.    k-fold cross-validation, with k in the range of 5 to 10,27 should be used rather than leave-one-out cross-validation because the testing set in leave-one-out cross-validation is not representative of the whole data and is often anticorrelated with the training set.

Author Contributions: Dr Poldrack and Ms Huckins had full access to all of the data in the study and take responsibility for the integrity of the data and the accuracy of the data analysis.

Concept and design: Poldrack, Varoquaux.

Acquisition, analysis, or interpretation of data: Poldrack, Huckins.

Drafting of the manuscript: Poldrack.

Critical revision of the manuscript for important intellectual content: Huckins, Varoquaux.

Statistical analysis: All authors.

Administrative, technical, or material support: Poldrack.

Among well-nourished populations of Westerners, men's high testosterone levels represent an outlier of cross‐cultural variation; probably due to intrasexual competition in reproductive contexts; it increases prostate cancer risk

From 2012... Do evolutionary life‐history trade‐offs influence prostate cancer risk? A review of population variation in testosterone levels and prostate cancer disparities. Louis Calistro Alvarado. Evolutionary Applications, December 11 2012.

Abstract: An accumulation of evidence suggests that increased exposure to androgens is associated with prostate cancer risk. The unrestricted energy budget that is typical of Western diets represents a novel departure from the conditions in which men's steroid physiology evolved and is capable of supporting distinctly elevated testosterone levels. Although nutritional constraints likely underlie divergent patterns of testosterone secretion between Westernized and non‐Western men, considerable variability exists in men's testosterone levels and prostate cancer rates within Westernized populations. Here, I use evolutionary life history theory as a framework to examine prostate cancer risk. Life history theory posits trade-offs between investment in early reproduction and long-term survival. One corollary of life history theory is the ‘challenge hypothesis’, which predicts that males augment testosterone levels in response to intrasexual competition occurring within reproductive contexts. Understanding men's evolved steroid physiology may contribute toward understanding susceptibility to prostate cancer. Among well-nourished populations of Westerners, men's testosterone levels already represent an outlier of cross‐cultural variation. I hypothesize that Westernized men in aggressive social environments, characterized by intense male–male competition, will further augment testosterone production aggravating prostate cancer risk.


Modern Westernized environments represent a clear deviation from the environment in which male reproductive physiology evolved. Largely removed from energetic constraint and pathogen burden, Westernized men are capable of supporting distinctly elevated testosterone at the upper limit of human variability and amplifying the incidence of hormone‐sensitive cancer. Variation in nutritional status can largely account for observed disparities in men's testosterone levels and prostate cancer between Westernized and non‐Western populations, but not within Westernized populations—the populations at highest risk of prostate cancer. By incorporating a challenge hypothesis framework, another source of lifetime variation in testosterone exposure was proposed: Aggressive social environments affect prostate cancer incidence through the responsiveness of male androgen physiology to challenges, specifically among Westerners who are able to support the energetic costs of high testosterone levels. I reviewed literature which showed that ancestry, a widely recognized risk factor for prostate cancer, is in and of itself biologically unimportant when accounting for lifestyle factors. For instance, population disparities in testosterone levels of black‐and white‐American men become attenuated and nonsignificant when comparing among college‐educated men from similar backgrounds (Mazur 1995, 2006). And in a nationally representative sample, there was no significant difference in testosterone levels of black‐and white‐American men after accounting for differences in anthropometry (age and body fat percentage) and lifestyle factors (drug use and physical activity) (Rohrmann et al. 2007). To reiterate, there is surprisingly little evidence to suggest that testosterone levels are a direct consequence of ancestry. And as discussed earlier, men of lower SES, regardless of ethnicity, demonstrate higher rates of male–male violence, higher testosterone levels, and higher prostate cancer. Using ancestry as a putative biomarker of prostate cancer risk is effective only to the extent which it tracks environmental circumstances and living conditions that influence cancer risk.

Additionally, I argued that poverty and compromised male investment lead to prioritized mating effort and increased male–male competition, culminating into chronically elevated testosterone and higher rates of prostate cancer. This general trend would be expected only if inequity in wealth distribution translated into more agonistic interactions between males at the population level. In other words, if the relationship between poverty and aggressive social environments is moderated, then there would be little expectation for lower SES to contribute to prostate cancer risk. Norwegian men, for example, deviate from the normally observed correlation between low SES and increased prostate cancer risk. This is particularly interesting because of the sizeable welfare program that is characteristic of Nordic social policy (Sachs 2006), which is associated with some of the lowest crime rates, violent or otherwise (Barclay et al. 2001). As such, Norway invests heavily in poverty reduction, boasts the lowest homicide rate within the developed world, and does not exhibit a concentration of prostate cancer among men of lower SES. Taken together, it would appear that comprehensive social programs might decouple socioeconomic differentials from male–male violence and prostate cancer risk, and may provide a surprising example of how improved social policies and poverty alleviation strategies are fundamental to the interest of public health.

And finally, the challenge hypothesis framework developed in this review may have occupational health implications, considering that men's testosterone levels vary according to occupational status (Dabbs 1992), and that some professions carry a disproportionate risk of prostate cancer (Demers et al. 1994; Zeegers et al. 2004). Dabbs (1992) and colleagues (1998) found that blue‐collar workers have higher salivary and serum testosterone than white‐collar workers. However, distinct social contexts within a profession can also give rise to differences in testosterone levels. Although lawyers as a group are white‐collar workers, trial lawyers have significantly higher salivary testosterone than nontrial lawyers, which has been attributed to the polemical nature of face‐to‐face litigation (Dabbs et al. 1998). If this pattern of elevated testosterone from agonistic interactions persists across occupations, it seems reasonable to expect that men in professions with a higher intensity of competitive interaction would exhibit a greater incidence of prostate cancer. Findings from an extensive cohort study of 58,279 Western European men (ages 55–69 years) from 20 separate occupations are consistent with this reasoning (Zeegers et al. 2004). After accounting for individual characteristics and lifestyle factors (age, diet, drug and alcohol use, education, family disease history, and physical activity), it was police officers who showed the highest relative risk for prostate cancer. Indeed, prostate cancer risk increased 67% for each 10 years of occupational duty as a policeman. The framework proposed here can explain these seemingly peculiar associations between career choice and prostate cancer risk.

Liberals & conservatives are similarly obedient to their own authorities & condemn perceived abuses of their ideology’s sacralized objects & and heroes; liberals & conservatives seem made up of the same psychological stuff

Do liberals and conservatives use different moral languages? Two replications and six extensions of Graham, Haidt, and Nosek’s (2009) moral text analysis. Jeremy A. Frimer. Journal of Research in Personality, November 28 2019, 103906.

Abstract: Do liberals and conservatives tend to use different moral languages? The Moral Foundations Hypothesis states that liberals rely more on foundations of care/harm and fairness/cheating whereas conservatives rely more on loyalty/betrayal, authority/subversion, and purity/degradation in their moral functioning. In support, Graham, Haidt, and Nosek (2009; Study 4) showed that sermons delivered by liberal and conservative pastors differed as predicted in their moral word usage, except for the loyalty foundation. I present two high-powered replication studies in religious contexts and six extension studies in politics, the media, and organizations to test ideological differences in moral language usage. On average, replication success rate was 30% and effect sizes were 38 times smaller than those in the original study. A meta-analysis (N=303,680) found that compared to liberals, conservatives used more authority r=.05, 95% confidence interval=[.02,.09] and purity words, r=.14 [.09,.19], fewer loyalty words, r=-.08 [-.10,-.05], and no more or less harm, r=.00 [-.02,.02], or fairness words, r=-.03 [-.06,.01].

Keywords: morality, language, ideology, conservatism, replication, moral foundations theory

General Discussion

Two replications and six extensions found limited support for the MFH in terms of language usage. Whereas a close replication of sermons from the same two U.S. Christian denominations as those in the original was successful (Study 1), a conceptual replication with 12 other U.S. Christian denominations was largely unsuccessful (Study 2), meaning that the two denominations studied in Graham et al. (2009) may not be representative of Christian denominations in general. This suggests that even within the context of religious sermons by U.S. Christian pastors, liberals and conservatives may not use different moral languages as much as previously thought. Although Graham et al. (2009) suggested that political speeches may not be the ideal context for detecting the different moral languages of liberals and conservatives, conceptual replications with four political samples were successful in aggregate for four of the five foundations (Study 3). A moderation analysis found that the differences in the moral languages of liberals and conservatives changed when moving from a religious to a political context for two of the five foundations only, meaning that the distinction between religion and politics may not be as important as Graham et al. (2009) suggested.

Samples drawn from the media and organizations, contexts not ruled out by Graham et al. (2009), allowed for a novel assessment of whether liberal and conservative commoners (broadly defined) use different moral languages (Studies 4-5). Tests of the MFH in these contexts were predominantly unsuccessful. Across all samples, metrics, foundations, and dictionaries, replication success rate was just 30%, meaning that 70% of replications failed. A meta-analysis (Study 6) of all the available data found support for the MFH for the authority and purity foundations, no evidence to support the MFH for harm and fairness, and evidence that is counter to the MFH for the loyalty foundation. Effect sizes were 38 times smaller on average. The most generous viable conclusion is that these results offer limited support for the MFH in the language of liberals and conservatives.

Analytical Considerations

The present analyses revealed that most distributions generated by the moral foundations dictionaries have a large number of identically-zero entries and are skewed. Correcting for this skew had relatively little effect on replication success and the resulting effect sizes. Thus, this analytic issue ended up being relatively inconsequential vis-à-vis replication considerations. Another analytical question concerned the dictionaries themselves. I used both the original MFD1 and the more recent and more valid MFD2. While results were not always the same, they tended to be largely similar. Analyses of non-skewed distributions stemming from the MFD2 are probably the most valid due to enhanced normality and predictive validity of this analytical set up.

Both GHN and the present studies relied on a simple word counting program to operationalize the usage of moral languages (GHN also coded the speakers’ attitudes towards those words). For more than a century, psychologists have drawn inferences about topics of conversation and speakers’ internal states and traits through methods like these. And word counting procedures have generally been shown to be valid. However, topics are not fully reducible to the presence of certain words. Future work might use other linguistic techniques to assess whether liberals and conservatives have similar or different attitudes toward moral languages and use them in similar or different ways.

Theoretical Considerations

Graham et al. (2009) found that liberals used more loyalty words than conservatives, a finding that is at variance with the MFH. The present analyses suggested that although this effect is weak, it is robust. Why liberals talk more about a topic upon which their morality is not based remains an important and pressing question for MFT.

The present and recent empirical findings motivate the revisiting of a fundamental question: what is a moral foundation, psychologically speaking? Proponents of the theory have advocated for construct pluralism in the sense that foundations are general mental modules that manifest in multiple psychological forms, including values, perceptions, behavioral orientations, language, and so on. The present findings, along with other work, raise questions about this tenet of Moral Foundations Theory. Results from the present studies suggest that differences in the moral language usage of liberals and conservatives are generally small. Moreover, for three foundations, the MFH was unsupported. It would probably be more accurate to conclude that liberals and conservatives use similar moral languages than that they use different languages.

Along with their similar languages, liberals and conservatives may not be as different as previously thought in terms of their general action orientations: liberals and conservatives are similarly obedient to their own authorities (Frimer, Gaucher, & Schaefer, 2014) and condemn perceived abuses of their ideology’s sacralized objects (Frimer et al. 2015, 2016) and heroes (Frimer, Biesanz, Walker, & MacKinley, 2013). This growing body of evidence is in line with idea that liberals and conservatives are made up of the same psychological stuff, but each ideology has its own set of cherished values and symbols. Whereas conservatism tends to cherish religion and the military, liberalism champions social justice and the environment (Frimer et al. 2015, 2016). Psychologically speaking, liberals and conservatives may cut from the same cloth.

They meta-analyze whether race or ethnicity moderate the heritability of intelligence in the US; find moderate to high heritabilities that do not substantially differ by race or ethnicity

Racial and ethnic group differences in the heritability of intelligence: A systematic review and meta-analysis. Bryan J.Pesta et al. Intelligence, Volume 78, January–February 2020, 101408.

•    We meta-analyze whether race or ethnicity moderate the heritability of intelligence.
•    The main sample (k = 16) was comprised of Whites Blacks, and Hispanics from the USA.
•    We found moderate to high heritabilities for both groups.
•    Heritabilities, however, did not substantially differ by race or ethnicity.
•    Results are largely inconsistent with predictions from the Scarr-Rowe hypothesis.

Abstract: Via meta-analysis, we examined whether the heritability of intelligence varies across racial or ethnic groups. Specifically, we tested a hypothesis predicting an interaction whereby those racial and ethnic groups living in relatively disadvantaged environments display lower heritability and higher environmentality. The reasoning behind this prediction is that people (or groups of people) raised in poor environments may not be able to realize their full genetic potentials. Our sample (k = 16) comprised 84,897 Whites, 37,160 Blacks, and 17,678 Hispanics residing in the United States. We found that White, Black, and Hispanic heritabilities were consistently moderate to high, and that these heritabilities did not differ across groups. At least in the United States, Race/Ethnicity × Heritability interactions likely do not exist.

1. Introduction

In behavioral genetic research, individual variance in cognitive ability is commonly partitioned into three components. The first is the additive genetic component (a2, also known as h2), which refers to genetic effects on a trait that act additively. This component is called (narrow) “heritability.” The second component is the common or shared environment (c2), which denotes environmental effects that make family members more similar. The third component is the unshared environment (e2), which consists of non-genetic effects (plus measurement error) that are not shared between family members, but which instead differentiate them from each other. Collectively, the last two components are known as “environmentality” (Plomin, DeFries, Knopik, & Neiderhiser, 2014).

These three components together comprise the “ACE” model of behavioral genetics. The model represents one basic, biometric framework behavioral geneticists may use when studying the heritability of human traits, including intelligence. The ACE model assumes that environmental and genetic influences are additive, but allows that interactions (e.g., A × E) may also exist between components; these can be estimated as well (Plomin et al., 2014; Vinkhuyzen, van der Sluis, Maes, & Posthuma, 2012). Moreover, the model is useful in intelligence research because the behavioral genetic architecture of the trait is “surprisingly simple” (Plomin et al., 2014, p. 200). Finally, the ACE model nicely fits IQ data, and ACE estimates do not require the use of cumbersome kinship designs.

The relative importance of genetic and environmental sources of individual differences in cognitive ability has been extensively studied. Results for the general population show that the proportion of variance in IQ explained by genes increases with age (Plomin et al., 2014). Specifically, in early childhood, genetic effects explain less than 50% of IQ variance, and the effect of the shared environment is relatively strong. As children age, though, genetic effects become increasingly prominent, and the environmental variance due to factors common to siblings decreases. In adults, the heritability of intelligence is 60–80%, while the effect of common environment is small, if not zero (Plomin et al., 2014). The unshared environment explains the rest.

The degree to which one can generalize heritability estimates to other populations has been debated (see, e.g., Sesardic, 2005). It is clear, though, that some variables (e.g., age; Plomin et al., 2014) moderate the heritability of cognitive ability. One putative moderator is the quality of one’s environment. Poorer (richer) environments supposedly correspond to lower (higher) heritability, to a presumably measurable degree. Said differently, “natural potentials for adaptive functioning are more fully expressed in the context of more nourishing environmental experiences” (Tucker-Drob & Bates, 2016, p. 1). This prediction is known as the Scarr-Rowe hypothesis (Scarr-Salapatek, 1971; Turkheimer, Harden, D’onofrio, & Gottesman, 2011).

The Scarr-Rowe hypothesis predicts lower heritabilities for lower performing social classes and racial/ethnic groups (Scarr-Salapatek, 1971, p. 1286). Scarr-Salapatek’s (1971) original hypothesis and related ones – examples include the “Threshold Hypothesis” (Jensen, 1968), the “Bio-ecological Model” (Bronfenbrenner & Ceci, 1994), and the “Gene–Gini Hypothesis” (Selita & Kovas, 2019) – predict that Scarr-Rowe interactions will result when there are environmental differences. Assuming that social class and racial/ethnic differences are largely environmental in origin, Scarr-Salapatek (1971) and others have predicted lower heritabilities for the lower scoring groups.

Does the heritability of human intelligence differ by either social class or race/ethnicity? The answer is complicated because variables like age and the country sampled can moderate the effects. For example, a meta-analysis by Tucker-Drob and Bates (2016) found greater heritability with higher socioeconomic status, but these effects existed only with participants from the United States. Regarding age, recent data from Germany suggest the existence of a Scarr-Rowe interaction, but one which declines with increasing age (Gottschling et al., 2019).

While Scarr-Rowe interactions for social class are relatively well-studied, interactions for race or ethnicity are less so. Hence, whether Scarr-Rowe interactions for race or ethnicity exist is unclear. Some reviews suggest that the heritability of intelligence is similar across cultures (Plomin et al., 2014) and ethnic groups (Jensen, 1998; Rushton & Jensen, 2005). Others suggest differently (Turkheimer, Harden, & Nisbett, 2017).

The issue is relevant for several reasons, including evaluating the trans-ethnic validity of polygenic scores. Recently, Lee et al. (2018) developed polygenic scores for both intelligence and educational levels. These scores were derived from European samples and they showed lower predictive accuracy in non-European groups such as African Americans. The typical explanation offered for attenuated predictive accuracy is decay of linkage disequilibrium (LD) which results in differences in the correlations between SNPs across different ancestry groups (Zanetti & Weale, 2018). Another hypothesis appeals to lower within-group heritability in non-White groups (see, e.g., Rabinowitz et al., 2019). Both explanations are plausible since the predictive accuracy of polygenic scores is a joint function of (1) the validity of the scores as predictors of the traits, and (2) the within-group heritability of the traits in question (i.e., the association between the genotype and the phenotype; Daetwyler, Villanueva, & Woolliams, 2008). While LD decay might be a theoretically adequate explanation for attenuated predictive accuracy of PGS (Zanetti & Weale, 2018), whether it is the actual explanation can only be properly evaluated when the heritabilities of the trait within the different subgroups are known.

Our aim is to shed light on these matters by conducting a systematic review and meta-analysis. The goal is to test for the presence of Scarr-Rowe interactions with respect to race/ethnicity. Our specific research question is whether the heritability of intelligence differs across racial/ethnic groups residing in the United States (we searched for studies worldwide but found only samples from this country).