Family Formation and Religious Service Attendance

Abstract

The positive relationship between family formation and regular weekly religious service attendance is well established, but cross-sectional data make it difficult to be confident that this relationship is causal. Moreover, if the relationship is causal, cross-sectional data make it difficult to disentangle the effects of three distinct family-formation events: marrying, having a child, and having a child who reaches school age. We use three waves of the new General Social Survey panel data to disentangle these separate potential effects. Using random-, fixed-, and hybrid-effect models, we show that, although in cross-section marriage and children predict attendance across individuals, neither leads to increased attendance when looking at individuals who change over time. Having a child who becomes school aged is the only family-formation event that remains associated with increased attendance among individuals who change over time. This suggests that the relationships between marriage and attending and between having a first child (or, for that matter, having several children) and attending are spurious, causal in the other direction, or indirect (since marrying and having a first child make it more likely that one will eventually have a school-age child). Adding a school-age child in the household is the only family-formation event that directly leads to increased attendance.

Keywords

GSS panel religious participation family processes panel models causal models

Religious socialization and family formation are the two most important determinants of participation in religious organizations (Myers 1996:858-60; Petts 2009:553; Smith and Denton 2005). While religious socialization mainly works intergenerationally (King, Elder, and Whitbeck 1997; Sherkat 1998), family formation is associated with increased participation for people within each generation, following declines during young adulthood (Benson and King 2006; Stolzenberg, Blair-Loy, and Waite 1995; Uecker, Regnerus, and Vaaler 2007). The literature on family formation and religious participation is vast, but it can be summarized with three main points. First, it is firmly established that living in a “traditional family”—meaning two parents plus school-age children—is strongly correlated with participation in organized religion (Chaves 2011:52). Recognizing this, many congregations design their programs to cater to families rather than single adults (Wilcox, Chaves, and Franz 2004).

Second, evidence of various sorts leads many scholars to conclude that family formation indeed causes increased religious service attendance. As young adults get married and start families they may become involved in religious communities to interact with other married couples (Stolzenberg, Blair-Loy, and Waite 1995), to provide a structured environment for their children (Ingersoll-Dayton, Krause, and Morgan 2002), and to settle into a conventional social and cultural system that for many people includes religious involvement (Wilcox 2006; Wuthnow 2007).

But a third feature of this literature provides the key motivation for our article: Family formation is a multistep process, and the relative causal importance for religious service attendance of each step in the family-formation process—marrying, having children, having children reach school age—remains unclear. Each of these events is plausibly a direct cause of increased attendance, and researchers have tended to emphasize the causal importance of one or another of them.

Some researchers, for example, have concluded that marrying exerts its own direct causal influence, independent of its association with childbearing. Scholars suggest that married individuals become more involved in organized religion as a way to interact with other couples and integrate into their community (Stolzenberg, Blair-Loy, and Waite 1995). Others emphasize single individuals’ greater geographic mobility, making them less likely to develop strong connections to a religious community (Thornton, Axinn, and Hill 1992). Some literature focuses on gender differences in religiosity and concludes that marriage’s direct causal effect is greater for men than women (Becker and Hofmeister 2001; Sandomirsky and Wilson 1990). And one scholar has observed that marriage’s causal effect seems stronger than the effect of having children and that recent declines in religious participation are explained almost entirely by young people choosing to marry later or not at all (Wuthnow 2007:73).

Others have emphasized the causal effect of parenthood on religious service attendance (Ploch and Hastings 1998; Sandomirsky and Wilson 1990). The mechanisms here include parents viewing religious communities as social institutions that help to establish core values for their children (Ingersoll-Dayton, Krause, and Morgan 2002), wanting to pass their faith on to their children (Wilcox 2006; Wuthnow 2007), and seeing congregations as sources of good parenting strategies (Alwin 1986; Wilcox 1998). As with marriage, some have found that parenthood’s positive effect on attendance is stronger for men than for women (Sandomirsky and Wilson 1990; Wilson and Sherkat 1994). And even atheist parents attend religious services more frequently than atheist nonparents (Ecklund and Lee 2011:734-35).

Still other scholars have pointed out that parenthood’s causal effect on religious participation depends on timing. Some conclude that the effect of parenthood is stronger when a couple has children during their mid-20s than when they have their first child later (Stolzenberg, Blair-Loy, and Waite 1995). But another timing hypothesis is most pertinent for our article: Rather than parenthood itself causing increased attendance, some have found that the causal effect occurs only when children reach school age (Argue, Johnson, and White 1999; Becker and Hofmeister 2001; Uecker, Regnerus, and Vaaler 2007).

There is much interesting detail in this vast literature, but the key point is that researchers have not yet fully disentangled the relative causal importance of marrying, becoming a parent, and having school-age children on religious participation. Disentangling these effects is further complicated by the likely possibility that causation also works in the other direction. Religiously active individuals are more likely to get married during their young adulthood than those who are less religious (Uecker, Regnerus, and Vaaler 2007), and they also have more children (McQuillan 2004).

There is an obvious reason that the true causal effects remain unclear: Most previous work relies on cross-sectional and repeated cross-sectional data, comparing individuals who are married to those who are not, or individuals who have children to those who do not. Much has been learned from this work, but cross-sectional data do not allow analysts to follow individuals over time to isolate which family-formation events are associated with increased religious service attendance for the same individuals. From a counterfactual perspective (Morgan and Winship 2007), the key issue is that causal inference relies on an implicit comparison between individuals experiencing the presumed causal event and those same individuals had they not experienced the causal event. The problem is that we can never observe what the behavior of a person who experiences the causal event would have been had they not experienced that event. Nor can we ever observe what the behavior of a person who did not experience an event would have been had they experienced the event. In the case at hand, when we observe a married person regularly attending religious services, we can never observe what that person’s religious behavior would have been had he or she not married. Similarly, we can never observe what an unmarried person’s religious behavior would have been had they married before the moment of observation. The unobserved possibilities remain forever counterfactual.

All analyses that aspire to causal inference somehow simulate these comparisons between observed reality and an unobserved counterfactual, but analytical strategies differ in how that comparison is specified. In cross-sectional data, we can use only between-person comparisons, so we simulate the counterfactual state by comparing people who experience the purported causal event to other people who did not experience the event but are otherwise similar on variables we observe. Panel data, by contrast, offer the possibility of comparing people experiencing the causal event to themselves before they experienced that event. Here, the unobserved counterfactual state is inferred from the individual’s state before he or she had the causal experience rather than from the state of other people who are like him or her in all observed ways except for the causal experience. The great advantage of within-person comparisons is that unobservable as well as observable time-invariant differences between the factual and counterfactual states are taken into account.

Panel data occasionally have been used to study the relationship between family formation and religiosity, but the panel-based articles we know about are limited in important ways. Stolzenberg, Blair-Loy, and Waite (1995) used a life-course approach that does not take advantage of models that distinguish within- and between-individual variation. Uecker, Regnerus, and Vaaler’s (2007) data included only two time points, which led them to use an adjusted cross-sectional modeling strategy. And Argue, Johnson, and White (1999) used a panel that included only married people, making it impossible to distinguish marriage from parenthood effects.

We use three waves of the new General Social Survey (GSS) panel data to disentangle the effects of marriage, parenthood, and child age on church attendance by estimating fixed-, random-, and hybrid-effect models (Allison 2005, 2009). We isolate individual change over time to increase confidence in causal interpretations of the observed relationships between different family-formation events and religious service attendance. The results are clear and robust to alternative specifications. Neither marrying nor having a first child directly increases church attendance when married individuals and parents are compared to themselves before they married or had a child. Neither does having additional children increase attendance when people are compared to themselves before and after having additional children. Having a child reach school age is the only family-formation event that remains associated with religious service attendance when people are compared to themselves before and after the event.

Method

GSS Panel Data

We use three waves of panel data collected by the GSS in 2006, 2008, and 2010. The GSS is a nationally representative face-to-face survey of the noninstitutionalized adult population of the United States. Of the 4,510 respondents surveyed in 2006, the GSS randomly selected 2,000 to reinterview in 2008 and 2010. The panel response rate in 2008 was 77 percent (N = 1,536), and in 2010 it was 83 percent (N = 1,276). Overall, 64 percent of the respondents impaneled in 2006 were reinterviewed in 2010. In a formal test of survey item reliability across this panel, Hout and Hastings (2012) found that objective religious characteristics had a reliability coefficient of .94 and religious beliefs and values had coefficients above .75. We limited our analysis to individuals who responded to all three waves of the survey.

Missing Data Imputation

We performed multiple imputations for all cases with missing data in order to retain as much information as possible. This approach has distinct advantages over listwise deletion, dummy variable adjustment, or mean imputation (Allison 2002). We implemented multivariate imputation using chained equations to create five data sets that replaced missing information with values based on regression models.¹ Imputation chained equations iteratively imputed the missing data for each variable sequentially, using different models for different types of variables (StataCorp 2011; White, Royston, and Wood 2011).² We used all model variables except the one being imputed in its prediction equation.³ Following Von Hippel (2007), we included our dependent variable (attendance) when imputing missing values, but when we estimated our final models we excluded cases with missing data on the religious service attendance measure. The regression estimates, standard errors, and significance levels that we report are the combined results of the models for each of five imputed data sets.

Income is the only variable we use for which there is a nontrivial amount of missing data. There are 394 person/years (11 percent of our observations) for which income data are missing. We imputed missing values to retain as much information as possible, but models that simply drop cases with missing values and exclude income produce the same results produced by the models using imputation. The models using listwise deletion but including income similarly produce coefficients that mimic those in our imputed models, though the reduced statistical power in these models led to some loss of statistical significance. We report the results from models that retain income as a control variable and use imputed values for all missing data. In the end, our data included 1,270 individuals and 3,810 individual-year combinations.

Dependent Variable

During each of the three interviews, respondents were asked: “How often do you attend religious services?” Responses were coded into these categories: “never” (0), “less than once a year” (1), “once a year” (2), “several times a year” (3), “once a month” (4), “two or three times a month” (5), “nearly every week” (6), “once a week” (7), and “more than once a week” (8). We treat this variable as continuous, and we retain these codes. Slightly more than half (55 percent) of individuals changed their reported attendance between the first and second GSS waves, and essentially the same proportion (56 percent) changed between the second and third waves, with 33 percent increasing attendance and 39 percent decreasing attendance at least once between waves.

Key Independent Variables

Marrying

We constructed a binary measure of whether or not respondents are currently married. The GSS asks each respondent: “Are you currently married, widowed, divorced, separated, or have you never been married?” We collapsed this into a dummy variable, where married is coded 1 and everything else is coded 0. The sample has slightly more married (50.6 percent) than unmarried individuals. Across the survey years, 6 percent of the unmarried become married and 9 percent of the married individuals leave that category.

Having a first child

The total number of children the respondent ever has had is measured by the GSS as a count variable that runs from zero to eight or more. The mean number of children is 2, with 26 percent of individuals reporting two children in at least one survey wave and 23 percent reporting no children throughout the panel period. We used this item to construct four dummy variables: having one child, two children, three children, and four or more children, with the comparison group having no children. The first of these dummy variables provides our indicator of having a first child, an event experienced by 7 percent of individuals between 2006 and 2010. Religious people have more children than others do, and we conceptualize the other dummy variables as control measures of the respondent’s total number of children.

Having a child who reaches school age

The GSS also collects information about the age of children in the household. Respondents were asked the number of household members under 6 years of age (BABIES), 6 to 12 years of age (PRETEENS), and 13 to 17 years of age (TEENS). Each is a count variable that runs from zero to eight or more. We collapsed each of these variables into a dummy variable indicating the presence, or not, of children of that age. Twenty-one percent of individuals moved in or out of the “babies” category. This means that they either had a baby or ceased to have at least one child under the age of 6 in their household. For both the “preteen” and “teenager” categories, 22 percent of individuals moved in or out between 2006 and 2010.

The dichotomized preteen item provides our indicator of having a child who reaches school age. Note that, because the observation period spans only four years, and a respondent will be coded as having a preteen only if there is a child at least six years old, our measure of having a child who reaches school age is not at all confounded with simply having a first child. Relatedly, this timing means that we do not need to be concerned about reverse causation involving this key variable. A respondent’s religiosity level in 2006 could not cause them to have a school-age child in 2008 or 2010 because a school-age child in 2010 must have been born before the first-panel observation in 2006.

Control Variables

We used a set of control variables that is standard in studies of religious participation: income, age, education, gender, race, region, religious affiliation, and whether the respondent lives in a city. We used the natural log of family income in 2010 dollars. We used a continuous measure of age to control for variation in attendance across the life course (Dillon and Wink 2007). Gender was measured with a dummy variable in which 1 = female. Race was measured with two dummy variables indicating black and “other,” with white as the reference category. Education was measured with a set of dummy variables indicating those who have a high school diploma, junior college degree, bachelor’s degree, or advanced degree, with those without a high school diploma as the reference category. A dummy variable indicating whether the respondent lives in a city measured urban/rural differences. Region was measured with dummy variables for Northeast, Midwest, and West (with South as the reference category).

To adjust for denominational variation in regular attendance, we used a slightly modified version of the scheme proposed by Steensland et al. (2000) to represent six religious affiliation categories with five binary measures. The reference category is evangelical Protestants; the five dummy variables indicate mainline Protestants, Catholics, black Protestants, those affiliated with other traditions, and those with no religious affiliation.⁴ The GSS also includes a measure of self-reported religiosity. We transformed this into a dummy variable, with those who report being “very religious” coded 1 and everyone else coded 0.

We treat gender, race, region, year, and city as time-invariant measures. We treat year as time invariant because we include age in our fixed-effects models and this covaries with our control for survey year. In principle, region and city could be treated as time varying, but there is very little within-individual variation on these measures in our data. Across the panel, only 2.6 percent of individuals moved to a different region of the country, and only 9.7 percent moved across the city versus noncity categories.

Table 1 presents the descriptive statistics for variables used in our analyses. These statistics were calculated after applying the GSS panel weight variable, WTPANNR123.

Table 1.

Summary Statistics From the 2006–2010 General Social Survey (GSS) Panel.

	Original Data set					Imputed Data
	N × Y	M	SD	Minimum	Maximum	M	SD
Outcome variable
Religious service attendance	3,810	3.773	2.807	0	8	3.773	2.807
Independent variables
Married	3,808	.5645	.4959	0	1	.5648	.4959
Total number of children
One child	3,803	.1635	.3700	0	1	.1631	.3695
Two children	3,803	.2625	.4401	0	1	.2619	.4397
Three children	3,803	.1610	.3676	0	1	.1610	.3675
Four or more children	3,803	.1442	.3514	0	1	.1435	.3507
Age of children in household
Have Baby (0–5 Years old)	3,766	.1599	.3666	0	1	.1610	.3676
Have Preteen (6–12 Years old)	3,765	.1843	.3878	0	1	.1857	.3889
Have Teen (13–17 Years old)	3,766	.1719	.3773	0	1	.1735	.3787
Religious controls
Religious affiliation
Mainline	3,775	.1406	.3477	0	1	.1422	.3493
Catholic	3,775	.2696	.4438	0	1	.2674	.4426
No affiliation	3,775	.1464	.3535	0	1	.1467	.3538
Other tradition	3,775	.0764	.2657	0	1	.0783	.2687
Black Protestant	3,775	.0750	.2635	0	1	.0748	.2631
Very religious	3,780	.1906	.3928	0	1	.1914	.3935
Time-variant controls
Household income (logged)	3,421	10.81	1.014	6.25	12.3	10.78	1.031
Age	3,768	47.15	16.49	18	89	47.21	16.45
Highest degree earned
High school	3,809	.4935	.5000	0	1	.4936	.5000
Junior college	3,809	.0770	.2667	0	1	.0772	.2669
Bachelor’s degree	3,809	.2067	.4050	0	1	.2067	.4050
Advanced degree	3,809	.1113	.3145	0	1	.1113	.3145
Time-invariant controls
Female	3,810	.5648	.4958	0	1
Race
Black	3,810	.1178	.3225	0	1	.5648	.4958
Other race	3,810	.1156	.3197	0	1	.1178	.3225
Region
Northeast	3,810	.1781	.3827	0	1	.1156	.3197
Midwest	3,810	.2129	.4094	0	1	.1781	.3827
West	3,810	.2417	.4281	0	1	.2129	.4094
City	3,810	.3214	.4671	0	1	.2417	.4281

Analytical Strategy

The GSS panel data provide the opportunity to develop better models of religious behavior because, in addition to the variation between individuals available in cross-sectional data, we observe within-person variation as people change over time. We exploit both forms of variation by estimating random- and fixed-effects models.⁵ Both types of models provide useful information. Random-effects models estimate coefficients using both within-individual and between-individual variance. These estimates are more efficient than those generated by fixed-effects models because they use all the available variance in the dependent variable (Argue, Johnson, and White 1999). However, random-effects models assume that unobserved variables are uncorrelated with the error term (Allison 2005, 2009). This can lead to omitted variable bias and model misspecification, making it risky to infer causation from a statistically significant regression coefficient, even when other variables are controlled.

Alternatively, fixed-effects models discard between-person variation and focus exclusively on within-person variation. Discarding the between-person variation has the hugely attractive feature of allowing each individual to act as a statistical control for himself or herself, thereby effectively controlling for all time-invariant correlates, including those that are unobserved (Allison 2009; Morgan and Winship 2007). In the case at hand, for example, if a between-individual regression equation predicting weekly religious service attendance produced a positive coefficient attached to being married, we can never be sure that coefficient is not spuriously produced by some unmeasured but causally important difference between individuals—such as holding traditional values that lead both to marrying and to religious practice, or being embedded in a subculture in which both marriage and religious practice are highly valued. But if a within-individual regression—one that included only individuals who changed their religious practice—produced that same marriage coefficient, we can with more confidence interpret that coefficient causally because no variation in the dependent variable is associated with differences between people in underlying values, embeddedness in a certain subculture, or any other ways, measured or not, in which people might differ from each other. This is why fixed-effect models that exclude between-person variation in favor of focusing exclusively on within-person change can increase our confidence in a causal interpretation of the results. They effectively increase our confidence that there is no unmeasured prior variable leading both to marrying and to religiosity, and they also increase our confidence that the result is not observed because religious individuals are more likely to get married.

If, on the other hand, the marriage coefficient dropped to zero in the fixed-effect model, this would suggest that the significant marriage coefficient in a random-effects model should not be interpreted causally. This would not mean that results from the random-effects model are less informative. The significant marriage coefficient still would mean that, cross-sectionally, married people are more likely than unmarried people to be religiously active, and that is important to know. However, it would also mean that the coefficient should not be interpreted as evidence that marrying directly increases attendance.

The main cost of using a fixed-effects model is that statistical power is reduced because the between-individual variation on the dependent variable is not used in the analysis. This loss of statistical power requires the analyst to pause before deciding, as in the example mentioned previously, that a coefficient that is significant in a random-effects model but insignificant in a fixed-effects model provides evidence against a causal interpretation. This loss of a coefficient’s significance might simply be produced by a loss in statistical power, so the analyst must look closely at differences between the two models in the coefficient’s magnitude and standard error before deciding that the fixed-effect model implies that the random-effects coefficient is not directly causal. Sticking with the marriage example, we would be on firmest ground in interpreting a lost significant marriage coefficient as evidence of spuriousness (or reverse causation or, at best, indirect causation) rather than reduced statistical power if the coefficient’s magnitude decreased in the fixed-effect model and its standard error decreased or remained the same.

But it is not necessary to rely only on comparing random- and fixed-effect models. We also estimate Allison’s (2005, 2009) hybrid fixed- and random-effects model. This strategy takes advantage of both fixed- and random-effect approaches by modeling individual means (between-individual variance) and deviation from those means (within-individual variance) in a single equation. These hybrid models “decompose each time-varying predictor into a within-person component and a between-person component, and then [fit] a random effects model with both components. The between-person component is just the person-specific mean of each variable … [while] the within-person component is the deviation for that person-specific mean” (Allison 2009:39). This allows us to maintain statistical power by not discarding information while still using the within-person variation to increase confidence in our causal interpretations. These models also allow us to perform tests comparing the fixed and random effects to establish whether the fixed-effect model’s sacrifice of efficiency is justified.

As a further check on our results’ robustness, we assessed whether there is a difference in the predicted attendance trajectory for those individuals who experienced a family-formation event and those who did not. From a counterfactual perspective, it is important to assess whether individuals who experience the alleged cause (in this case a family-formation event) were on a different starting trajectory on the dependent variable than those individuals who did not have that experience. If these groups were on different trajectories to start with, then the effects we observe may be produced by some unobserved prior difference not captured in the data rather than by the family-formation events.

We assessed this possibility using the strategy recommended in chapter 9 of Morgan and Winship (2007). We generated an additional set of family-formation variables indicating whether individuals ever have experienced the family-formation event. For example, this version of our marriage variable is coded 1 for individuals who were married before the 2006 GSS survey and for those who were married between the 2006 and 2010 surveys. This allows us to compare the attendance trajectories of those who ever experienced the family-formation events with those who did not experience these events before or during the observation period. We then examined interactions between GSS year and these new family-formation variables. Significant interactions would imply that people in the two groups (e.g., people with and without school-age children) are following different religious attendance trajectories over time and that the within-individual differences we observe might be attributable to these different historical trajectories rather than to the experience whose causal force we are trying to assess. The absence of interactions between time and these new family-formation variables would suggest that people in the different family structure categories are not following different trajectories on attendance, and this would increase our confidence that within-individual differences in attendance are in fact produced by the family-formation experience.

A final modeling note regards weighting. We followed Winship and Radbill (1994) by estimating our models without applying the GSS weight variable. Instead, for each model, we performed the diagnostic test they recommend by interacting the GSS weight variable, WTPANNR123, with each independent variable. None of these interactions were significant, so we conclude that it is unnecessary to include any of them in our final models and that using unweighted data is appropriate for our regression models.

Results

Random- and Fixed-Effect Models

Table 2 presents a series of random- and fixed-effects regressions of religious service attendance on our key family-formation variables. The first model of each type includes only the married indicator, the second includes only the number-of-children and child-age indicators, and the third includes both sets of variables. Later tables present models with more controls and models using the more complex hybrid strategy, but our central results are apparent in Table 2, so it is helpful to focus first on this simple table.

Table 2.

Random- and Fixed-Effects Ordinary Least Squares (OLS) Models: Family Formation Effects on Religious Service Attendance.^a

	Random-Effects Models			Fixed-Effects Models
	Married	Children	Both	Married	Children	Both
Married	0.386*** (0.10)		0.318** (0.10)	0.003 (0.13)		−0.016 (0.13)
Total number of children^b
One child		0.356* (0.15)	0.296* (0.15)		0.209 (0.19)	0.211 (0.19)
Two children		0.567*** (0.16)	0.482** (0.16)		0.229 (0.24)	0.231 (0.24)
Three children		0.723*** (0.18)	0.655*** (0.18)		−0.047 (0.28)	−0.045 (0.28)
Four or more children		0.918*** (0.18)	0.860*** (0.18)		0.289 (0.29)	0.289 (0.29)
Age of children in household
Have Baby (0–5 Years old)		−0.102 (0.11)	−0.124 (0.11)		0.019 (0.12)	0.020 (0.12)
Have Preteen (6–12 Years old)		0.217* (0.10)	0.204* (0.10)		0.276** (0.11)	0.276** (0.11)
Have Teen (13–17 Years old)		0.021 (0.10)	0.019 (0.10)		0.027 (0.10)	0.027 (0.10)
N	3,810	3,810	3,810	3,810	3,810	3,810

Note: ^aStandard errors in parentheses. ^bNever had children is the comparison group.

^†p < .10. *p < .05. **p < .01. ***p < .001.

The random-effects models—which, recall, include the between-person as well as the within-person variation—show all the expected correlations between family structure and weekly attendance at religious services. Married people attend religious services significantly more frequently than unmarried people, and those with more children attend more frequently than those with fewer children. Each additional child is associated with a bit more attendance, and people with four or more children report attending almost a full category more than those with no children. This pattern of coefficients—more strongly positive with the addition of each child—supports the established knowledge that people with more children are more religiously active.

After taking marriage and number of children into account, having a preteen in the household also is associated with more religious service attendance. Overall, then, the random-effects models, which use both between- and within-individual variation in attendance, lead to the conclusion that all three family-formation steps—marrying, having children, and having a preteen—are associated with increased religious service attendance.

Crucially, the fixed-effect models in Table 2 tell a very different story. Recall that fixed-effects models look only at within-person variation, so these models ignore all the between-person comparisons in favor of comparing individuals only with themselves before they experienced these events. Since the fixed-effect models isolate within-individual change, the coefficients in these models can be interpreted as the difference in an individual’s attendance if he or she changes on the family-formation measures. The key result is that people whose households add a school-age child—essentially, people who have a child turn six—significantly increase their attendance, and this is the only significant family-formation coefficient in the fixed-effect models. The positive marital status and number-of-children relationships evident in the random-effects models disappear in the fixed-effects models. This means that, although in cross-section married people and people with more children are more religiously active than others, it is not the case that, when people who marry, have a first child, or have more children, they attend more than they themselves did before they experienced these events. This pattern suggests that none of these events directly causes increased attendance, at least for the people who married during the observation period covered by the GSS panel data.⁶

Inspection of standard errors and coefficient magnitudes increases our confidence that the disappearance of the marriage and number-of-children relationships in the fixed-effect models is not an artifact of reduced statistical power. The standard errors associated with each of these indicators in the fixed-effect models are slightly larger than in the random-effects models, but for each of these indicators the random-effect coefficient is substantially reduced in magnitude in the fixed-effect model. The effects disappear because the coefficients are smaller, not because we lost statistical power.

All in all, these results suggest that between-individual variation is driving the marriage and number-of-children relationships evident in the random-effects models. Moreover, these results suggest that these cross-sectional relationships are produced by some combination of unobserved prior variables, reverse causation, and/or indirect causation via the path of eventually having a school-age child. When controlling in the fixed-effect framework for all time-invariant characteristics, including unobserved characteristics, these relationships disappear. Only the effect of having a school-age child passes this more rigorous test—a test in which the counterfactual comparison is oneself before experiencing the event rather than other people who are similar to you on measured variables. Of course, marrying and having a first child make it much more likely that you eventually will have a school-age child, so these results do not imply that marrying and having a child have no causal connection with religious service attendance. They do imply, however, that the causal impact of marrying and having a child are indirect rather than direct, kicking in only when a child reaches school age.

Table 3 presents random- and fixed-effects models that contain our full set of control variables. The first model of each type includes only our family-formation variables, the second model adds demographic and religious affiliation controls, and the third adds self-reported religiousness. The central results evident in Table 2 are fully confirmed here, so we will not rehearse them again. The only important new finding in Table 3 is that the relationship between number of children and attendance evident in Table 2’s random-effects model is completely explained in Table 3 by demographic differences. The control variables show all the usual relationships with religious participation. Religious participation is higher among older people, more highly educated people, women, African Americans, Southerners, evangelical Protestants, and those who describe themselves as very religious.

Table 3.

Random and Fixed Effects of Family Formation on Religious Service Attendance: With Controls.^a

	Random-Effects Models			Fixed-Effects Models
	Model #1	Model #2	Model #3	Model #1	Model #2	Model #3
Married	0.358*** (0.10)	0.369*** (0.10)	0.359*** (0.10)	−0.040 (0.13)	−0.041 (0.13)	−0.040 (0.13)
Total number of children^b
One child	0.140 (0.15)	0.115 (0.15)	0.067 (0.14)	0.263 (0.19)	0.263 (0.19)	0.244 (0.19)
Two children	0.180 (0.16)	0.090 (0.15)	0.041 (0.15)	0.284 (0.24)	0.235 (0.24)	0.220 (0.24)
Three children	0.357^† (0.18)	0.252 (0.18)	0.221 (0.17)	0.019 (0.28)	−0.058 (0.28)	−0.069 (0.28)
Four or more children	0.529** (0.19)	0.372* (0.19)	0.284 (0.18)	0.355 (0.29)	0.211 (0.29)	0.177 (0.29)
Age of children in household
Have Baby (0–5 Years old)	−0.043 (0.11)	−0.085 (0.11)	−0.060 (0.11)	0.017 (0.12)	−0.010 (0.12)	−0.003 (0.12)
Have Preteen (6–12 Years old)	0.242* (0.10)	0.233* (0.10)	0.238* (0.10)	0.279** (0.11)	0.264* (0.11)	0.259* (0.10)
Have Teen (13–17 Years old)	0.024 (0.10)	0.010 (0.10)	0.045 (0.10)	0.020 (0.10)	0.014 (0.10)	0.028 (0.10)
Religious affiliation^c
Mainline		−0.374** (0.14)	−0.351** (0.13)		−0.053 (0.17)	−0.054 (0.16)
Catholic		−0.248^† (0.14)	−0.159 (0.14)		−0.333 (0.22)	−0.339 (0.22)
No affiliation		−1.76*** (0.13)	−1.72*** (0.13)		−0.88*** (0.15)	−0.87*** (0.15)
Other tradition		−0.220 (0.18)	−0.247 (0.17)		0.181 (0.22)	0.173 (0.22)
Black Protestant		0.019 (0.22)	0.023 (0.22)		0.178 (0.24)	0.153 (0.24)
Very religious			1.259*** (0.10)			0.525*** (0.11)
Time-variant controls
Household income (logged)	0.097* (0.04)	0.086* (0.04)	0.095* (0.04)	0.089^† (0.05)	0.085^† (0.05)	0.090^† (0.05)
Age	0.017*** (0.00)	0.015*** (0.00)	0.012** (0.00)	−0.010 (0.01)	−0.008 (0.01)	−0.007 (0.01)
Degree^d
High school	0.239 (0.16)	0.135 (0.15)	0.130 (0.15)	0.018 (0.21)	−0.062 (0.21)	−0.088 (0.21)
Junior college	0.226 (0.20)	0.202 (0.20)	0.218 (0.19)	−0.200 (0.25)	−0.248 (0.25)	−0.269 (0.25)
Bachelor’s degree	0.190 (0.20)	0.188 (0.19)	0.224 (0.18)	−0.400 (0.27)	−0.469^† (0.27)	−0.464^† (0.27)
Advanced degree	0.438^† (0.22)	0.454* (0.22)	0.487* (0.21)	−0.016 (0.32)	−0.087 (0.32)	−0.082 (0.32)
Time-invariant controls
Female	0.825*** (0.13)	0.713*** (0.12)	0.606*** (0.11)
Race^e
Black	0.711*** (0.18)	0.663** (0.21)	0.649** (0.20)
Other race	0.082 (0.15)	0.095 (0.15)	0.136 (0.15)
Region^f
Northeast	−1.15*** (0.19)	−1.02*** (0.18)	−0.91*** (0.17)
Midwest	−0.242 (0.17)	−0.191 (0.16)	−0.140 (0.14)
West	−1.08*** (0.17)	−0.93*** (0.16)	−0.84*** (0.15)
City	0.091 (0.12)	0.092 (0.11)	0.068 (0.11)
N	3,810	3,810	3,810	3,810	3,810	3,810

Note: ^aStandard errors in parentheses. ^b Never had Children, ^cEvangelicals, ^dless than high school, ^ewhite, and ^fsouth are the comparison groups.

^†p < .10. *p < .05. **p < .01. ***p < .001.

Hybrid Model

We used Allison’s (2005, 2009) hybrid fixed- and random-effects strategy to model within- and between-individual variance simultaneously and to test directly the random-effects assumption that between-individual coefficients are equal to within-individual coefficients. Recall that the difference between coefficients in the random-effects models in Tables 2 and 3 and the between-individual coefficients in Table 4’s hybrid model is that the coefficients in the random-effects models reflect an amalgamation of both between- and within-individual variation, whereas the between-individual coefficients in the hybrid model in Table 4 reflect only the between-individual variation. The random-effect model’s amalgamation of between- and within-individual effects into a single set of coefficients is justified only if these effects are equivalent. The hybrid model allows us to test this assumption by assessing whether or not the differences we observe between our random-effect and fixed-effect coefficients are statistically significant.

Table 4.

Hybrid Model of Family Formation on Religious Service Attendance.^a

	Between	Within
Married	0.571*** (0.14)	−0.044 (0.13)
Total number of children^b
One child	−0.158 (0.21)	0.242 (0.19)
Two children	−0.183 (0.19)	0.192 (0.24)
Three children	0.183 (0.22)	−0.099 (0.28)
Four or more children	0.133 (0.24)	0.158 (0.29)
Age of children in household
Have Baby (0–5 Years old)	−0.087 (0.24)	0.001 (0.12)
Have Preteen (6–12 Years old)	0.362 (0.22)	0.258* (0.11)
Have Teen (13–17 Years old)	−0.070 (0.21)	0.037 (0.10)
Religious affiliation^c
Mainline	−0.628** (0.20)	−0.067 (0.16)
Catholic	−0.123 (0.17)	−0.340 (0.22)
No affiliation	−3.191*** (0.21)	−0.880*** (0.15)
Other tradition	−0.527* (0.25)	0.156 (0.22)
Black Protestant	0.297 (0.33)	0.081 (0.25)
Very religious	2.833*** (0.18)	0.511*** (0.11)
N	3,810

Note: ^aStandard errors in parentheses. All coefficients were produced simultaneously in the same model. This model controls for between-individual variation in income, age, education by degree, gender, race, region, and city. In addition, the model controls for within-individual variation in income, age, and education by degree, which are omitted for space. ^bNever had children and ^cEvangelicals are the comparison groups.

^†p < .10. *p < .05. **p < .01. ***p < .001.

Table 4 presents results from our hybrid model. The model includes the family measures and our full set of demographic and religious controls, but to save space the demographic control coefficients are not presented. The coefficients from the single hybrid model are presented in adjacent columns to facilitate comparing the between- and within-individual effects associated with each independent variable.

The key results evident in Tables 2 and 3 are confirmed in this hybrid model. Having a preteen in the household is the only family variable that is significantly associated with attendance when within-individual change is considered. Being married is related to between-individual variation in attendance even in the presence of religious and demographic controls, but being married is not related to within-individual variation in attendance. And, as in Table 3, the between-individual relationship between number of children and attendance does not persist in the face of demographic and religious controls.

Table 5 presents the results of directly testing the assumption behind our random-effects models that coefficients using only between-person variation are equal to coefficients using only within-person variation. We directly tested this assumption in four hybrid models. These models correspond to the three models in Table 2 plus the full model in Table 3: a model including only the married indicator, a model including only the variables indicating number and ages of children, a model including both the marriage and children variables, and a model that includes the marriage and children variables plus our full set of controls. The most important test, the results of which are in the table’s bottom line, assesses the null hypothesis that, for the set of family measures included in the model, the within-person coefficients are equal to the between-person coefficients. In all of these hybrid models, we reject this null hypothesis. As the F tests for individual coefficients make clear, this is mainly because of the very substantial between- versus within-person differences for the married coefficient and the coefficients associated with having three or more children. As we have seen in previous models, both these coefficients shift from being strongly positive in the random-effects context to being statistically indistinguishable from zero in the fixed-effect context. The F tests show that these shifts are statistically significant.

Table 5.

Tests of Equality for Within and Between Coefficients in the Hybrid Model.

	F Tests
	Marriage	Children	Both	Full
Married	23.094***		17.664***	10.444**
Total number of children
One child		0.296	0.002	1.985
Two children		2.330	0.302	1.500
Three children		14.387***	10.116**	0.628
Four or more children		6.198**	3.400^†	0.004
Age of children in household
Have Baby (0–5 Years old)		2.447	3.676^†	0.106
Have Preteen (6–12 Years old)		1.050	1.503	0.178
Have Teen (13–17 Years old)		0.0004	0.115	0.203
All family-formation measures	23.094***	3.012**	4.804***	2.225*

^†p < .10. *p < .05. **p < .01. ***p < .001.

In none of the hybrid models is there a significant difference between the between- and within-person preteen coefficients. This is because the preteen coefficient is not hugely different when considering between-person variation as when considering within-person variation. The key point here is that, unlike the marriage and number-of-children relationships, the preteen relationship has a substantial within-person component. All in all, the results in Tables 4 and 5 support the conclusion we reached from our other analyses. The within-individual coefficients associated with several of the family-formation variables are indeed statistically different from the between-individual coefficients, and, in both the fixed-effects model and the hybrid model, only having a school-age (but not teen) child in the household has a significant within-individual connection with religious service attendance.

Trajectory Model

As a further check on our results’ robustness, we used the strategy recommended in chapter 9 of Morgan and Winship (2007) to examine interactions between GSS year and a set of family-formation variables indicating whether or not people ever had the experience. As we noted earlier, significant interactions would imply that the within-individual differences we observe might be attributable to people with school-age children following a different religious trajectory than people without school-age children rather than to the experience of having children who reached school age. The absence of interactions between time and these ever-experienced family-formation variables would suggest that people in the different family structure categories are following similar historical trajectories on attendance, increasing our confidence that an individual’s attendance level before their children reached school age is a reasonable estimation of the counterfactual situation of what their later attendance would be had they not had school-age children. Null interactions would increase our confidence because they would rule out one more potential threat to a causal interpretation of our fixed-effect results.

Table 6 presents this model. The model includes family measures that vary across time within individuals and the time-constant, ever-experienced versions of the family measures. The within-individual coefficients, as with the hybrid- and fixed-effect models, capture the effect of individual change on the family-formation measures. The ever-experienced variables capture differences between those who ever have experienced the family-formation event and those who have not. The ever-by-year interactions capture differences in the historical trajectories followed by the two groups (i.e., those who ever and never experience the event). This model includes our full set of demographic and religious controls, but to save space these coefficients are not presented. The within-individual, ever-experienced, and associated time interactions are presented in adjacent columns to facilitate comparing the within-individual and ever-experienced coefficients and examining the interactions.

Table 6.

Trajectory Model of Family Formation on Religious Service Attendance.^a

	Main Effects		Ever × Year
	Within	Ever	2008	2010
Married	−0.029 (0.13)	0.539*** (0.15)	0.021 (0.12)	0.217^† (0.12)
Total number of children^b
One child	0.205 (0.20)	−0.229 (0.17)	0.007 (0.15)	0.044 (0.15)
Two children	0.195 (0.26)	−0.134 (0.16)	0.043 (0.14)	0.058 (0.14)
Three children	−0.050 (0.30)	0.182 (0.18)	−0.167 (0.15)	−0.119 (0.16)
Four or more children	0.209 (0.31)	−0.104 (0.20)	0.162 (0.16)	0.254 (0.16)
Age of children in household
Have Baby (0–5 Years old)	−0.012 (0.12)	−0.146 (0.19)	−0.001 (0.15)	−0.018 (0.16)
Have Preteen (6–12 Years old)	0.244* (0.12)	0.262 (0.19)	0.194 (0.16)	−0.018 (0.17)
Have Teen (13–17 Years old)	0.040 (0.11)	−0.133 (0.17)	−0.091 (0.14)	0.0004 (0.15)
2008		0.082 (0.21)
2010		0.083 (0.22)
N	3,810		F Test^c	1.183

^aStandard errors in parentheses. All coefficients were produced simultaneously in the same model. This model also contains our full set of control variables and interactions between year and the “ever” versions of all time-varying control variables. ^bNever had children is the comparison group. ^cF test for whether including the full set of ever-by-year interactions improves model fit.

^†p < .10. *p < .05. **p < .01. ***p < .001.

The results in Table 6 confirm our key results. Adding a preteen to the household is the only within-individual family-formation change that is significantly associated with attendance. Furthermore, the insignificant interactions imply that the historical trajectory for those having preteen children at any point during the observation period is not different from the trajectory for those who do not have preteen children at any point during the observation period. Interestingly, there is a significant (at the .10 level) interaction between time and marriage, indicating that those who are ever married follow a more positive attendance trajectory than those who never marry during the observation period. But the F test indicates that adding the full set of ever-by-year interactions does not significantly improve model fit.

Conclusion

Our conclusion is straightforward. Having a child reach school age appears to directly increase parents’ religious service attendance. However, the commonly observed cross-sectional relationships between being married and regularly attending religious services and between having children and attendance do not seem to reflect a direct causal impact of these family-formation events on religious service attendance. These latter connections are strong when individuals are compared to others like them on observed control variables, but they disappear when individuals are compared to themselves before and after they experience these events. Having a child reach school age is the only family-formation event we examined in which comparing the same individuals before and after the event shows that attendance is higher after experiencing the event.

Our results suggest that the commonly observed cross-sectional relationships between attendance and marriage and between attendance and having children are produced by some combination of spurious connection to prior variables, causation in the other direction, and/or indirect causation that kicks in only when a child reaches school age. We suspect that all three of these connections operate to some degree. People share some characteristics that make them both more likely to marry and be parents and also more likely to attend religious services, religiosity makes people more likely to marry and have children, and marriage and parenthood do cause increased attendance, but indirectly, by making it more likely that people eventually experience the family-formation event that directly causes increased attendance: having a child who reaches school age. We are not in a position to sort out the extent to which the cross-sectional relationships between marriage and parenting and attendance are spurious or causal and, if causal, the extent to which the causation is indirect or operating in the other direction. We conclude only that these relationships are not directly causal.

We should also elaborate on a caveat we introduced in passing earlier when we said that neither marrying nor having a first child nor having more children directly leads to increased attendance at least for the people who experienced these events during the observation period covered by the GSS panel data. There of course is age patterning to family formation, with these events tending to happen relatively early in adulthood. When we limit our attention to within-individual change on these events within the 2006–2010 GSS panel, we are limiting our attention to people who experienced these events only during those years, and this means we mainly are studying people who are relatively young in those years. If no one in the GSS sample who was, say, 60 or older in 2006 married or had children or had children reach school age after 2006, then our conclusions directly apply only to people younger than 60. It remains possible that the causal connections between religiosity and the different family-formation events are different for people of earlier generations. Stated positively, our conclusions apply most directly to the set of people who formed families between 2006 and 2010. As we noted earlier, this four-year window presents some advantages for studying this subject, but it also presents some limits. It is not clear how future research might assess if our conclusions are true for earlier generations, but future research will be able to assess if they apply to the generations who will form families after 2010.

By conceptualizing religious service attendance as a continuous variable, our models assume that having a child reach school age will increase religious service attendance no matter how religiously active people are in the first place. But it is reasonable to wonder if family formation affects religiosity differently depending on how religious one is to begin with. It might be, for example, that those who never attend religious services are not likely to start attending when their children reach school age. Or it might be that the causal effect of having a child reach school age operates mainly by pushing some people who are somewhat regular, but not quite weekly, attenders to more regular weekly attendance. Future research might build on our results by assessing the possibility that family formation increases religious participation more or less for people with different starting levels of religiosity.

In addition to the substantive contribution of disentangling and clarifying the relationships between distinct family-formation events and religious service attendance, this analysis illustrates the tremendous potential of the new GSS panel data to increase our knowledge about causal processes. We encourage readers to examine the other articles in this special issue of Sociological Methods & Research to learn more about the methodological and substantive potential of the GSS panel data. The relationship between family structure and religious service attendance is one of the most well-established relationships within the sociology of religion, but data limitations have constrained our ability to discover as much as we would like to discover about how this relationship works. Our results will not be the last word on this subject, but we believe we have made progress and thereby illustrated how the new GSS panel data can be used to make even more progress in the sociology of religion and in other fields.

Footnotes

Declaration of Conflicting Interests

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

Funding

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

Notes

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