Genes,Childhood Trauma,and Late Life Depressive Symptoms

Abstract

Objectives: Findings on gene-environment correlations suggest childhood “environments” may reflect genetic liabilities. The independent psychosocial influence of childhood trauma is unclear. This study examined such effects on adulthood depressive symptoms. Methods: Data were from the Health and Retirement Study. Trauma items included childhood physical abuse and parental substance abuse. Multinomial logit models examined genetic effects on stable and unstable reports. Linear growth models tested associations of stable trauma responses, genes, and their interaction with current depressive symptoms. Results: Genetic risk predicted both stable and unstable trauma reports. With genes controlled, stable responses were associated with life course variations but not late life change in depression. The exception was women’s physical abuse, which moderated genetic effects but had no independent influence. Discussion: Apparent gene-trauma correlations may be driven by flawed retrospective reports. Research is needed to distinguish true from artifactual genetic effects on other environmental factors and establish psychosocial implications.

Keywords

depressive symptoms older adults gene-environment correlation childhood trauma HRS

Introduction

The literature has long indicated that both genes (G) and childhood trauma (CT) influence subsequent depressive symptoms (Halldorsdottir & Binder, 2017; McLaughlin et al., 2010; Norman et al., 2012; Springer, Sheridan, Kuo, & Carnes, 2007). As explained below, these effects persist into later life (American Psychiatric Association [APA], 2013). Recent studies suggest, however, that genes can also shape experienced childhood environments. Such “gene-environment correlations” (rGE) apparently extend to a range of ecological dimensions, including parenting characteristics, family chaos, and broad socioeconomic factors (Butcher & Plomin, 2008; Krapohl et al., 2017). Plausibly, then, they may also apply to early traumatic experiences. If so, rather than being an autonomous cause of depression, CT may simply mediate genetic effects. Alternately, CT effects may be confounded by genes, such that at least a portion of previous estimates is spurious. No population representative studies have queried these patterns.

Genes, CT, and Lifetime Depressive Symptoms

CT is a major public health problem (Stoltenborgh, Bakermans-Kranenburg, van IJzendoorn, & Alink, 2013). Annually, 4% to 16% of children are physically abused worldwide (Gilbert et al., 2009; Ip et al., 2016). Parental substance abuse—increasingly recognized as a distinct trauma subtype (Becci, Brook, & Lloyd, 2015; Parolin, Simonelli, Mapelli, Sacco, & Cristofalo, 2016) as well as a precursor for direct maltreatment (Clemens et al., 2019)—seems even more common. A recent nationally representative U.S. study reports prevalences of 24.3% among women and 21.4% among men (Cavanaugh, Petras, & Martins, 2015).

In turn, such experiences generate long-term mental health problems. Specifically, these seem to reflect Axis II rather than Axis I disorders (Ip et al., 2016; Norman et al., 2012). Axis I disorders include conditions that have acute symptoms and are generally treatable, such as mood disorder, anxiety disorder, attention-deficit and disruptive behavior disorders, sleep disorder, and schizophrenia. In contrast, Axis II disorders, such as personality disorders, are usually lifelong problems that arise in childhood (APA, 2013). A recent meta-analysis suggests an odds ratio of 1.54 for physical abuse as a predictor of depressive disorders (Norman et al., 2012). Similarly, in an administrative data set of all individuals born in Sweden between 1984 and 1988, parental substance abuse strongly predicts clinical depression (hazard ratio = 2.09; Björkenstam, Vinnerljung, & Hjern, 2017). Other population representative studies—both United States (McLaughlin et al., 2010; Springer et al., 2007) and international (Lee & Song, 2017)—support these linkages.

Studies also indicate genetic effects on depression. As with other complex psychiatric traits, such influences are polygenic—reflecting the aggregate effects of many different genes (Okbay et al., 2016). Polygenic risk scores (PRSs)—additive indexes of hundreds of thousands or millions of single nucleotide polymorphisms (SNPs) from across the genome—are thus becoming a common way of capturing them (Conley, 2016; Halldorsdottir & Binder, 2017). Recent literature suggests that these genetic substrates may influence not just depression but also proximal life environments—and hence, arguably, confound their mutual linkages. The next section describes these patterns.

Gene-Environment Linkages

Measured environments—particularly, when fashioned by parents who also transmit their genes to study participants—may be correlated with unmeasured genetic variation (Conley, 2016). In other words, “nurture” itself may have a “nature” component (Butcher & Plomin, 2008; Kong et al., 2018). Evidence for such gene-environment correlation comes from a range of family, twin, and adoption studies, which demonstrate that individuals’ exposure to childhood environments partially depends on their genotype. Affected environments include parenting characteristics, troubled family or social contexts, and parental socioeconomic status (Butcher & Plomin, 2008; Krapohl et al., 2017). Moreover, findings largely reflect “actual parental behavior” rather than just a child’s perceptions (Kendler & Baker, 2007).

Four nonmutually exclusive mechanisms have been suggested for rGE (Avinun & Knafo, 2014; Krapohl et al., 2017). (a) Many observed associations between offspring genotype and environment-providing parental traits are outside the offspring’s influence (e.g., parental age and education level at childbirth), and hence likely to reflect “passive rGE.” Specifically, parental genetic propensities that were passed down to offspring are also associated with their own environment-providing behavior. (b) Some childhood environments may also reflect “active rGE”—individuals selecting their social environment (e.g., friendship networks) based on their genetic tendencies. (c) Parental behaviors could partially be “evoked” by offspring genetic propensities (McGuire, Segal, & Hershberger, 2012). Previous studies using polygenic scores have found linkages of adolescents’ genetic risk for aggression with low family cohesion (Elam, Chassin, & Pandika, 2018), for behavioral undercontrol with poorer parental monitoring (Elam et al., 2017) and for poor response inhibition with mothers’ inconsistent parenting (Wang et al., 2017). Such patterns are broadly in keeping with an established “stress generation” literature, which suggests individuals with psychiatric disorders may actively contribute to the production of ongoing stressors in their lives (Hammen, 2005). And finally, (d) rGE could be induced by environmentally mediated genetic effects. For instance, if education-associated genetic variation influenced mothers’ predisposition to smoke during pregnancy—and prenatal nicotine exposure had an environmental effect on offspring attention problems—this could induce associations of the offspring’s own education-associated polygenic variation with maternal smoking, as well as capture part of its correlation with offspring attention problems (Krapohl et al., 2017).

If rGE holds for CT, the latter’s autonomous psychosocial influence becomes unclear. In extreme cases, if G is not controlled, the entire apparent CT effect might be spurious. Even if the CT influence is “real,” it might just reflect this exposure’s mediation of genetic effects. An established “stress diathesis” literature also indicates that factors like CT may amplify genetic risk (Assary, Vincent, Keers, & Pluess, 2018; Shanahan & Hofer, 2005). As explained below, work in causal modeling demonstrates that estimates of direct as well as indirect genetic effects may be incorrect if such gene-environment (GxE) interactions are not taken into account.

Finally, each of these components may differentially influence life course divergences and late life change in depressive symptoms. The next section lays out these arguments.

Late Life Effects: Levels or Trends?

Early genetic and environmental pressures may lead not just to divergent affect trajectories—manifesting in late life as between-person differences in mental health—but to continued within-person decline. As long-term sensitizing factors, they can make people more reactive to recent stressors, and/or less able to cope with them (Boyce & Ellis, 2005). Older adults, in particular, face increasing exposure to such pressures (Waite & Das, 2010). These may include, for instance, incipient frailty, new or worsening health conditions, age discrimination, and financial concerns. Simultaneously, they also experience a generalized loss of stress-buffering social assets, through fundamental changes in the structure of both their families and their broader social networks. Children leave home, retirement terminates workplace relationships, parents and elders pass away, and health problems begin impeding social interaction (Hughes, Waite, Hawkley, & Cacioppo, 2004). Preexisting sensitization, then, may interact with these proximal pressures to worsen one’s depressive symptoms.

The recent availability of polygenic scores for depressive symptoms as well as CT items in the U.S. Health and Retirement Study (HRS) offers a unique opportunity to examine the patterns above. As of this writing, HRS is the only publicly available population representative data set of older adults with externally validated genetic scores. The current study used data from four recent waves (2006 and 2010-2014) to address the following questions: (a) Is CT predicted by one’s depressive symptoms PRS? (b) Does CT predict late life depressive symptoms, net of this PRS? (c) Are genetic effects on these outcomes mediated by CT?

Data

HRS is an ongoing longitudinal survey nationally representative of the U.S. population over 50 years of age, conducted every 2 years since 1992. The overall response rate is about 87%. The survey uses multistage sampling of households with an oversample of Blacks and Hispanics (Sonnega et al., 2014). This study utilized data from four recent waves (2006 and 2010-2014). Models were limited to those over 50 years of age as HRS is only population representative for these ages. HRS genetic principal components (PCs), crucial to the polygenic analyses, are specific to African or European ancestry groups (see below). The longitudinal sample for the former was too low for robust analysis—especially not only for men (n = 243) but also women (n = 444). Among other issues, lack of significant associations could have been due to low statistical power rather than absent empirical linkages. In preference of robust findings over comprehensive ethnic coverage, analysis was restricted to White respondents with available genetic data (maximum n = 2,660 for women and 1,984 for men).

The original race measure in HRS was a self-assessment. Respondents were able to identify themselves as belonging to more than one racial category. Those who indicated multiple races were then asked, “Do you consider yourself primarily (first mention, second mention, etc.)?” In a second stage, the HRS team used principal components analysis (PCA) of genome-wide SNP data to more deeply investigate population structure. For several of the subjects in which self-identified race (Black or White) strongly contrasted with the PCA results, the self-assessment was corrected after review by the HRS (2012) group.

Measures

Table S1 in the e-supplement shows summary statistics for the variables below.

Dependent variables: CT

A first set of multinomial logit models tested genetic effects on trauma reports (Table 1). CT items came from a leave-behind instrument. Specifically, a random half sample was assigned to as an enhanced face-to-face interview (EFTF) in 2006—with the same subpopulation assessed again in 2010. The module included a leave-behind questionnaire on psychosocial topics. Questions on CT tapped events before age of 18 years, and allowed dichotomous “yes/no” responses. Specifically, respondents were asked whether they had experienced “physical abuse by a parent.” Parental substance abuse was indicated by reports of parents who “drank or used drugs so often that it caused problems in the family.”

Table 1.

Genetic Effects on Childhood Trauma : Coefficients (Standard Errors).

	Childhood physical abuse				Parental substance abuse
	Multinomial logit (ref: no report in either wave)			Dichotomous logit^a	Multinomial logit (ref: no report in either wave)			Dichotomous logit^a
	Reported in both waves	Reported in one wave, denied in other	Reported in one wave, missing in other	Any report (ref: none)	Reported in both waves	Reported in one wave, denied in other	Reported in one wave, missing in other	Any report (ref: none)
Women
Depressive symptoms PRS	0.31* (0.14)	0.29* (0.14)	0.07 (0.06)	0.32** (0.10)	0.09 (0.07)	0.23** (0.08)	0.07 (0.06)	0.13* (0.05)
n	2,659			2,047	2,655			2,104
Men
Depressive symptoms PRS	0.31 (0.17)	0.14 (0.14)	0.18* (0.08)	0.32** (0.11)	0.07 (0.09)	−0.16 (0.14)	0.17* (0.08)	0.08 (0.08)
n	1,984			1,499	1,984			1,544

Note. All analyses were restricted to White adults over age of 50 years with available genetic data. Figures in bold represent estimates significant at at least p < .05. Estimates were weighted to adjust for differential probabilities of selection, nonresponse, and attrition. Models adjusted for a respondent age, a PRS for educational attainment, and 10 genetic principal components. PRS = polygenic risk score.

Those missing observations in either wave were dropped. Hence the smaller sample size than in the corresponding multinomial logit model.

p < .05. **p < .01.

For each of the two CT types, responses from 2006 and 2010 were combined to generate a nominal dependent variable with four categories (Table 1): “no report in either wave” (the baseline category); “reported in both waves”; “reported in one wave, denied in other”; and “reported in one wave, missing in other.” The goal was to at least partly distinguish stable portions of these retrospective self-reports from those contradictory or of uncertain stability, and potentially more affected by response bias. For comparison, “any report” over that period (versus none) was examined as a separate dichotomous outcome. Those missing observations in either wave were dropped from this measure.

Dependent variables: Depressive symptoms

Depressive symptoms were measured through an eight-item version of the Center for Epidemiologic Studies–Depression (CES-D) scale, indicating negative affect and somatic complaints in the preceding week (Turvey, Wallace, & Herzog, 1999). The variable was an additive score of dichotomous “yes/no” responses—ranging from 0 (no symptoms) to 8 (all symptoms reported). To minimize endogeneity, only CES-D measures from the 2010, 2012, and 2014 waves were used as outcomes (Tables 2 and 3).

Table 2.

Additive Linear Growth Models for Depressive Symptoms: Coefficients (Standard Errors).

	Women		Men
	Model 1		Model 1
	Depressive symptoms^a		Depressive symptoms^a
	Intercept growth factor^b	Slope growth factor^b	Intercept growth factor^b	Slope growth factor^b
Depressive symptoms PRS	0.15** (0.05)	−0.01 (0.02)	0.00 (0.06)	0.02 (0.03)
Childhood physical abuse^c	0.42 (0.22)	−0.10 (0.09)	1.17** (0.23)	−0.08 (0.11)
	Childhood physical abuse^c,d		Childhood physical abuse^c,d
Depressive symptoms PRS	0.35* (0.15)		0.26 (0.19)
Indirect effect of PRS on intercept growth factor	0.02 (0.01)		0.06 (0.05)
n	2,204		1,580
	Model 2		Model 2
	Depressive symptoms^a		Depressive symptoms^a
	Intercept growth factor^b	Slope growth factor^b	Intercept growth factor^b	Slope growth factor^b
Depressive symptoms PRS	0.16** (0.05)	−0.02 (0.02)	0.00 (0.07)	0.02 (0.03)
Parental substance abuse^c	0.42** (0.13)	−0.02 (0.05)	0.60** (0.14)	−0.10 (0.07)
	Parental substance abuse^c,d		Parental substance abuse^c,d
Depressive symptoms PRS	0.11 (0.07)		0.06 (0.10)
Indirect effect of PRS on intercept growth factor	0.00 (0.00)		0.01 (0.01)
n	2,206		1,580

Note. All analyses were restricted to White adults over age of 50 years with available genetic data. Figures in bold represent estimates significant at at least p < .05. Estimates were weighted to adjust for differential probabilities of selection, nonresponse, and attrition. Models controlled a respondent’s age, an educational attainment PRS, and 10 genetic principal components. PRS = polygenic risk score; OLS = ordinary least squares.

Count variable. Linked to growth factors through negative binomial distribution function.

Continuous outcome. Estimates are OLS coefficients.

Dichotomous measure, comprised solely of stable trauma reports.

Estimates are logit coefficients.

p < .05. **p < .01.

Table 3.

Multiplicative Linear Growth Models for Depressive Symptoms: Coefficients (Standard Errors).

	Women		Men
	Model 1		Model 1
	Depressive symptoms^a		Depressive symptoms^a
	Intercept growth factor^b	Slope growth factor^b	Intercept growth factor^b	Slope growth factor^b
Depressive symptoms PRS	0.13* (0.05)	−0.01 (0.02)	−0.00 (0.07)	0.02 (0.04)
Childhood physical abuse	0.29 (0.24)	−0.10 (0.12)	1.26** (0.27)	−0.09 (0.11)
PRS × physical abuse	0.39* (0.20)	−0.02 (0.06)	−0.12 (0.25)	0.09 (0.06)
	Childhood physical abuse^c		Childhood physical abuse^c
Depressive symptoms PRS	0.35* (0.15)		0.26 (0.19)
Counterfactually defined indirect effects of PRS on intercept growth factor
Total natural indirect effect	0.03 (0.02)		0.06 (0.05)
Pure natural indirect effect	0.01 (0.01)		0.07 (0.05)
n	1,815		1,303
	Model 2		Model 2
	Depressive symptoms^a		Depressive symptoms^a
	Intercept growth factor^b	Slope growth factor^b	Intercept growth factor^b	Slope growth factor^b
Depressive symptoms PRS	0.17** (0.06)	−0.00 (0.02)	0.01 (0.07)	0.01 (0.04)
Parental substance abuse	0.41** (0.13)	−0.02 (0.05)	0.58** (0.14)	−0.14 (0.08)
PRS x parental substance abuse	0.08 (0.11)	−0.06 (0.04)	0.27 (0.16)	0.09 (0.10)
	Parental substance abuse^c		Parental substance abuse^c
Counterfactually defined indirect effects of PRS on intercept growth factor
Depressive symptoms PRS	0.11 (0.07)		0.06 (0.10)
Total natural indirect effect	0.01 (0.00)		0.01 (0.02)
Pure natural indirect effect	0.00 (0.00)		0.01 (0.01)
n	1,765		1,281

Note. Sample sizes were smaller than in additive models due to FIML handling of interactions. All analyses were restricted to White adults over age of 50 years with available genetic data. Figures in bold represent estimates significant at at least p < .05. Estimates were weighted to adjust for differential probabilities of selection, nonresponse, and attrition. Models controlled a respondent’s age, an educational attainment PRS, and 10 genetic principal components. PRS = polygenic risk score; OLS = ordinary least squares; FIML = full information maximum likelihood.

Count variable. Linked to growth factors through negative binomial distribution function.

Continuous outcome. Estimates are OLS coefficients.

Dichotomous measure, comprised solely of stable trauma reports. Estimates are logit coefficients.

p < .05. **p < .01.

Independent variables: CT

As covariates, CT measures included only the stable component of each type of report (Tables 2 and 3). This measure was arguably less susceptible to response bias and feedback from contemporaneous depressive symptoms. Separate dichotomous items indexed reports of childhood physical abuse and of parental substance abuse in both 2006 and 2010, with responses of “no” in both waves comprising the reference. Those with discrepant reports, or missing observations in either wave, were dropped from this measure.

Independent variables: PRS

Continuous PRSs were available for HRS respondents who provided salivary DNA in 2006 and 2010. Samples were collected during the EFTF. Given the repeat administration of the 2006 EFTF in 2010, this half sample had the highest genetic coverage (73% of White adults over age of 50 years). In combination with inverse probability weighting to handle missing data (see below), this coverage was arguably sufficient to ensure population representativeness.

PRSs for each phenotype were based on a single, replicated, and externally validated genome-wide association study (GWAS). DNA data collection was through the Oragene DNA Collection Kit. Genotyping was conducted by the Center for Inherited Disease Research in 2011, 2012, and 2015. Scores were calculated using the PRSice and PLINK software packages. The European ancestry PRS used in the present study contained 1,147,841 SNPs (Okbay et al., 2016; Ware, Schmitz, Gard, & Faul, 2018). The score was standardized within ancestry group.

Control variables

Controls were limited to time-invariant measures known not to be “post treatment”—that is, not influenced by either the genetic score or CT (Pearl, 2009). Thus, childhood or life course factors were left out. Among viable controls, a participant’s age (in years) in 2006 was entered linearly as a continuous variable. In addition, two sets of genetic covariates were included, starting with an educational attainment PRS comprised of 1,329,385 SNPs. This genetic measure is strongly correlated with that for depressive symptoms (Pearson’s r = –.13, p < .001). It is now also known to contribute to multiple supposed environmental “exposures” as well as to developmental outcomes (Krapohl et al., 2017). Scholars therefore recommend controlling it through multipolygenic models, to isolate other polygenic effects (Krapohl et al., 2017). A second set of variables adjusted for population stratification—systematic differentials in allele frequencies across subgroups due to distinct histories. It was comprised of 10 HRS-provided genetic PCs designed for the European ancestry group (Ware et al., 2018). The PCs accounted for any ancestry differences in genetic structures within populations that could bias estimates.

Analytic Approach

The literature suggests women and men may have differential reactivity to the same stressors (Dedovic, Wadiwalla, Engert, & Pruessner, 2009; Hammen, 2005). Mechanisms remain unclear but could involve sex differences in peripheral and central nervous system aspects of hypothalamic–pituitary–adrenal (HPA) axis regulation (Dedovic et al., 2009). Such variations may in turn be due to effects of sex steroids, and hence sensitive to the menstrual cycle or use of oral contraceptives. Differences in socialization have also been implicated. Accordingly, all analyses were gender specific.

CT measures were retrospective reports of childhood events, with unknowable correspondence with real experiences. To at least partly distinguish “true” exposures from response bias, initial multinomial logit models regressed the four category nominal CT measure on the PRS (Table 1). For comparison, a separate logit model examined the same genetic linkage with “any report” (versus none).

Next, linear growth models examined additive associations of the PRS and of stable CT reports with a respondent’s depressive symptoms (Table 2)—both between-person variation in 2010 (indexed by the intercept growth factor) and within-person change through 2014 (slope growth factor; Bollen & Curran, 2006). As CES-D was a count measure, a negative binomial distribution function was used for the measurement part (linking growth factors to responses). Growth factors, in turn, were continuous latent variables; hence, their associations with covariates were assessed through ordinary least squares (OLS) coefficients. To incorporate rGE, CT was simultaneously regressed on the genetic score through a logit submodel. Indirect effects from these analyses were then used to examine mediation.

To extract mediation estimates that also accounted for any gene-CT interactions, the final models included these two factors multiplicatively (Table 3). As above, trauma was simultaneously regressed on the genetic score. Counterfactually defined indirect effects from these models were then examined. The e-supplement explains the logic both visually (Supplemental Figure S1) and through equations (Muthén & Asparouhov, 2015). Briefly, the standard mediation estimates in Table 2 rest on the assumption that genetic effects on depressive symptoms are the same among those with as those without CT experiences. When GxE holds, however, this conception is clearly incorrect. By permitting genetic effects to vary across CT categories, the counterfactual framework more accurately captures the empirical pattern. In technical terms, it allows two possible decompositions of a total effect (of the PRS, in this case)—either into (a) the pure natural direct effect (PNDE) and the total natural indirect effect (TNIE) or into (b) the total natural direct effect (TNDE) and the pure natural indirect effect (PNIE: VanderWeele, 2016). Both indirect paths are provided in the results (Table 3), with full results reported in the e-supplement (Table S2). For this study, however, the TNIE was more useful as it combined the indirect path through the gene-CT interaction with the one through the “main effect” of CT. Thus, it yielded a comprehensive mediation estimate.

An additional issue was selection bias—whether through overtime attrition or module nonparticipation (Elwert & Winship, 2014; Munafò, Tilling, Taylor, Evans, & Smith, 2018). Accordingly, logistic regression was first used to fit predictive models for between-wave attrition. These models were lag-specific—that is, for attrition from 2006 to 2010 (14.82%), 2010 to 2012 (9.12%), and 2012 to 2014 (10.97%). Covariates included participants’ demographic and health attributes—age, ethnicity, gender, years of education, self-rated physical health, and number of health conditions diagnosed over the lifetime. Based on predicted probabilities from these analyses, lag-specific and stabilized inverse-probability-of-attrition weights (IPAWs) were created (Weuve et al., 2012). The same strategy was used to create inverse-probability weights (IPWs) for missingness in the genetic sample (27%). To avoid extreme values, all weights were capped at the 1st and 99th percentile. Finally, growth models were weighted by the cumulative product of the lag-specific IPAWs, the genetic IPWs, and HRS-provided cross-sectional weights designed specifically for the 2006 EFTF psychosocial module (Smith, Ryan, Sonnega, & Weir, 2017). The first two components ensured that participants with characteristics associated with a lower probability of post-2006 continuation (IPAWs), and/or of providing genetic data (IPWs), were assigned larger weights, “compensating” for their underrepresentation in the final longitudinal sample. In turn, the cross-sectional weights ensured baseline generalizability to all U.S. households containing at least one person in the age-eligible range, and incorporated a module-specific nonresponse adjustment based on age, gender, race/ethnicity, and geography.

Standard errors were adjusted for sample stratification (sampling strata independently) and clustering (sampling participants within primary sampling units). To minimize data loss from measure-specific missingness, estimation was through full information maximum likelihood (FIML).

Results

Genetic Effects on CT: Logit and Multinomial Logit Models

Among women, consistent with rGE, the depressive symptoms PRS was positively associated with stable reports of childhood physical abuse (Table 1)—that is, affirmative responses in both 2006 and 2010 (coefficient = 0.31, p < .05). However, the same genetic linkage appeared with unstable responses—that is, reports of physical abuse in one wave but not the other (coefficient = 0.29, p < .05). Thus, the estimate for the dichotomous “any report” item could have reflected either or both components (coefficient = 0.32, p < .01). Moreover, PRS-effects on parental substance abuse were found for the same unstable category (coefficient = 0.23, p < .01)—and may have driven the association with the dichotomous “any report” item (coefficient = 0.13, p < .05).

Among men, genetic associations with stable trauma responses did not reach significance—possibly due to cell size issues (Table S1, e-supplement). Instead, the PRS was linked positively to affirmative reports in only one wave, with observations missing in the other—for childhood physical abuse (coefficient = 0.18, p < .05) as well as parental substance abuse (coefficient = 0.17, p < .05). For physical abuse, the estimate for the dichotomous “any report” item was also significant (coefficient = 0.32, p < .01).

Additive Growth Analysis

In the next stage, linear growth models examined additive associations of the PRS and of stable CT reports with a respondent’s depressive symptoms. For each gender, Model 1 (Table 2) presents results for physical abuse and Model 2 for parental substance abuse. Among women, Model 1 only yielded positive genetic effects on between-person depression variation (coefficient = 0.15, p < .01). The corresponding effect of physical abuse, in contrast, was not significant—and neither factor had any linkage with the slope growth factor. Consistent with rGE findings in the multinomial logit analysis above, women’s genetic score was also associated with their stable physical abuse reports (coefficient = 0.35, p < .05). Analysis of indirect paths, however, indicated no mediation of genetic effects by this early experience.

Findings were somewhat similar for parental substance abuse (Model 2). This “environmental” factor was positively linked to women’s between-person depression variation (coefficient = 0.42, p < .01). The same was true of the genetic score (coefficient = 0.16, p < .01). As in the multinomial logit analysis, no rGE pattern was found for stable substance abuse reports. Correspondingly, the latter did not mediate genetic effects on women’s intercept growth factor.

Intriguingly, men’s results suggested only environmental and not genetic influences. Specifically, both physical abuse (coefficient = 1.17, p < .01; Model 1) and parental substance abuse (coefficient = 0.60, p < .01; Model 2) were positively linked to their between-person but not within-person depression variation. No other estimates reached significance.

Multiplicative Growth Analysis

For each gender, the next set of growth analyses multiplicatively included the genetic score—with physical abuse in Model 1 and parental substance abuse in Model 2 (Table 3). As above, neither the genetic nor environmental covariates had any influences on within-person depression change (slope growth factors) for either women or men. Among the former, in Model 1, a positive “main genetic effect” was again found on between-person depression variation (coefficient = 0.13, p < .05). In addition, however, the interaction with physical abuse also reached significance (coefficient = 0.39, p < .05). As above, an apparent rGE pattern was found, with the genetic score influencing women’s stable physical abuse reports (coefficient = 0.35, p < .05). However, counterfactually defined indirect effects did not suggest any mediation of the PRS–depression linkage by this early factor—even in combination with the positive interaction term.

Parental substance abuse, in contrast, had no interaction with women’s genetic score (Model 2). Only the main effects of this childhood experience (coefficient = 0.41, p < .01) and of the PRS (coefficient = 0.17, p < .01) reached significance. Neither an rGE pattern nor any indirect effects were found. Results were even sparser among men. As in Table 2, only main effects of trauma were found—for physical abuse (coefficient = 1.26, p < .01; Model 1) as well as parental substance abuse (coefficient = 0.58, p < .01; Model 2).

Discussion

This study began by noting that new findings on rGE render suspect the independent psychosocial influence of CT. Such effects may either be confounded by genes, such that previous estimates are partly spurious, or may just mediate the genetic impact. Accordingly, this study leveraged the recent availability of PRSs and CT reports in the nationally representative HRS to address three questions: (a) Is CT predicted by one’s depressive symptoms PRS? (b) Does CT predict late life depressive symptoms, net of this PRS? and (c) Are genetic effects on these outcomes mediated by CT?

The answer to the first question was ambiguous. With stable CT reports, rGE was found only for physical abuse, and only among women (Table 1). Whether this finding reflected passive gene-environment correlation, or harsher parental discipline evoked by a participant’s gene-linked maladaptive behaviors (Avinun & Knafo, 2014; Krapohl et al., 2017), was beyond the scope of this study. Null genetic linkages with other stable reports may well have been due to cell size issues rather than absent empirical linkages. But each of the four multinomial logit models in Table 1 also suggested an apparent “rGE” pattern driven by CT responses that were either contradictory or of uncertain stability. As in any survey-based study, the correspondence between such responses and actual trauma experiences could not be directly explored. However, this ambiguity does call for caution in interpreting at least cross-sectional self-reports of past abuse, as well as rGE findings for such measures. As noted, genetic liabilities could easily influence such responses through current affect rather than “true” rGE. This is worrying, given that the vast majority of CT studies—and of rGE results for childhood “environmental” exposures—are based on retrospective self-reports. Previous findings may be less robust than assumed. Research is needed on whether patterns above also apply to measures that tap objective events, rather than subjective perceptions of abuse or trauma. For instance, the widely used Conflict Tactics Scale queries unambiguous experiences such as being “spanked on the bottom with a bare hand” and “slapped on the face, head or ears” by a parent (Straus, Hamby, Finkelhor, Moore, & Runyan, 1998). Such measures, even if retrospective, may possibly be less vulnerable to bias than simple dichotomous self-assessments. The CT categories above may also have tapped experiences of varying severity—with inconsistent reports indicating less traumatizing events (or those more ambiguous). Given data limitations, such patterns could not be examined.

For the second study question, the answer was less ambiguously “yes”—at least for between-person depression variation. With the sole exception of women’s physical abuse, net of the genetic score, stable trauma reports were uniformly linked to this outcome (Table 2). However, in keeping with arguments above, some evidence of genetic confounding was also found: in supplementary analysis run on identical subsamples but leaving out only the depressive symptoms PRS, the physical abuse effect also reached significance for women (e-supplement, Table S3). The actual change in p value was from .06 to .04, and of magnitude was from .42 to .48, indicating mild confounding. Change in other CT estimates was negligible. Moreover, for both the genetic score and CT, effects on within-person change over the study duration were uniformly null (Table 2). Mortality selection arguably did not drive this pattern, given that IPAWs were used to take such attrition into account. It is also unlikely that older adults do not experience more or worsening stressors, the depressive effects of which could be exacerbated by preexisting genetic or trauma-induced sensitization. Findings, then, may instead indicate that such sensitization fades before late life. An “age as maturity” perspective in gerontology also suggests elevations in multiple stress-buffering psychological attributes at this stage. These include self-integration, insight, skill, and self-esteem (Mirowsky & Ross, 1992). Data were not sufficient to adjudicate between these mechanisms.

Finally, CT did not mediate genetic effects on between-person depression variation. Counterfactual analysis of such indirect paths was as thorough as possible—examining those passing solely through main effects of trauma as well as those also incorporating the interaction term (Table 3; see also Figure S1 in the e-supplement). At least among women, consistent with “stress diathesis” arguments above, physical abuse apparently amplified genetic risk (Assary et al., 2018; Shanahan & Hofer, 2005). Despite incorporating this GxE interaction, however, the “total natural indirect effect” did not reach significance.

Overall, then, early trauma does seem to have a genetically exogenous influence on lifetime depressive outcomes. However, caution is warranted in this interpretation. Polygenic scores are limited to the additive effects of common variants on a particular trait that the discovery GWAS was powered to detect. Empirical genetic influences, however, may also involve interactions between SNPs—both within (dominance) and across loci (epistasis; Lin & Wu, 2006). These interactions may be a major reason “SNP heritability” is uniformly and substantially lower than “twin heritability” (Cheesman et al., 2017). GWAS-based scores also do not incorporate rare genetic variants with potentially large influences. Moreover, the extent to which CT exposure reflects nontransmitted parental alleles—over and above transmitted ones that could influence rGE with the offspring’s own polygenic risk—remains unknown (Kong et al., 2018). Establishing such linkages would require parental polygenic scores, currently unavailable in any population-representative data set.

This study had several other limitations. Controls were limited to factors known not to be “post treatment” (Pearl, 2009)—that is, not influenced either by the depressive symptoms PRS or by CT. As HRS data did not include other plausible “pre-treatment” controls, omitted variable bias remained a concern. Next, null results for slope growth factors could have been driven by the short analytic duration (2010-2014). Models also had to be restricted to White participants as the corresponding black subsample was too small for rigorous analysis. Nor was genetic information available for any other ethnic group. In addition, while IPWs were used to address selection issues within the White sample, predictive models for these weights may well have excluded factors crucial to these processes. The approach also does not adjust for “missingness not at random” (MNAR; Perkins et al., 2018). Most importantly, this was a one-sample analysis. A previous generation of “candidate gene” studies lost credibility due to nonreplication of findings (Conley, 2016). Although polygenic scores are promoted partly as a solution to this issue, cross-sample consistency in their effects remains poorly explored. Pending replication in independent samples, then, inferences above remain tentative.

Conclusion

Findings from a national probability sample of older White adults suggested that apparent gene–CT correlations may partly reflect genetic effects on unstable trauma reports—possibly through current emotions. Extent of bias in current rGE literature remains unknown. Stable trauma measures, in contrast, appear to have an autonomous influence on lifetime depressive symptoms. With the sole exception of women’s physical abuse, their effects are neither confounded by nor mediate genetic ones. Indeed, men’s depressive symptoms seem influenced only by these early experiences and not by genetic risk. However, long-term sensitizing effects of CT seem expended by late life, such that they do not induce further change in depression at this stage. Deeper investigation is needed to parse true from artifactual genetic correlations with other childhood environments and to establish psychosocial implications.

Supplemental Material

e-supplement – Supplemental material for Genes, Childhood Trauma, and Late Life Depressive Symptoms

Supplemental material, e-supplement for Genes, Childhood Trauma, and Late Life Depressive Symptoms by Aniruddha Das in Journal of Aging and Health

Footnotes

Declaration of Conflicting Interests

The author declared no potential conflicts of interest with respect to the research, authorship, and/or publication of this article.

Funding

The author received no financial support for the research, authorship, and/or publication of this article.

ORCID iD

Aniruddha Das

Supplemental Material

Supplemental material for this article is available online.

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