The Problem of Scaling in Exponential Random Graph Models

Abstract

This study shows that residual variation can cause problems related to scaling in exponential random graph models (ERGM). Residual variation is likely to exist when there are unmeasured variables in a model—even those uncorrelated with other predictors—or when the logistic form of the model is inappropriate. As a consequence, coefficients cannot be interpreted as effect sizes or compared between models and homophily coefficients, as well as other interaction coefficients, cannot be interpreted as substantive effects in most ERGM applications. We conduct a series of simulations considering the substantive impact of these issues, revealing that realistic levels of residual variation can have large consequences for ERGM inference. A flexible methodological framework is introduced to overcome these problems. Formal tests of mediation and moderation are also proposed. These methods are applied to revisit the relationship between selective mixing and triadic closure in a large AddHealth school friendship network. Extensions to other classes of statistical work models are discussed.

Keywords

social network analysis exponential random graph models scaling mediation moderation

Over the past decade, social scientists have increasingly looked to statistical network methods to address important substantive questions. These methods improve upon classical approaches of statistical inference for network data by relaxing independence assumptions and providing a means to formally represent interdependent social phenomena. Among the models available, exponential random graph models (ERGM) have established themselves as an especially popular tool for this type of inference given their flexibility and ability to represent nodal, dyadic, and network covariates. Indeed, the diffusion of ERGM across the social, political, behavioral, and health sciences has led to an explosion of research examining the generative properties of social networks (Adams and Schaefer 2016; Cranmer et al. 2017; Kreager et al. 2017; Lewis 2013; Papachristos, Hureau, and Braga 2013; Young 2011).

However, there is a problem in ERGM applications that has gone largely unnoticed: ERGM coefficients are confounded with residual variation–unexplained variation in tie probabilities—that rescales model coefficients. This has several important consequences. First, coefficients and exponentiated coefficients cannot be interpreted as effect sizes. Second, scaling can produce differences in coefficient size across models that are unrelated to either mediation or confounding. Third, scaling can bias interaction coefficients—including homophily coefficients—yielding incorrect assessments of direction, interaction effect size, and significance.

While recent studies have sought to address several sources of residual variation, including unobserved heterogeneity (unmeasured nodal covariates; Box-Steffensmeier, Christenson, and Morgan 2018; Thiemichen et al. 2016; van Duijn, Snijders, and Zijlstra 2004), nesting structure (Schweinberger 2020; Schweinberger and Handcock 2015; Stewart et al. 2019), and measurement error (Kim, Leonardo, and Kirkland 2016), the consequences of scaling for statistical inference using ERGM have been largely overlooked. In addition to these sources, we show that scaling can affect ERGM results even when omitted variables are uncorrelated with other predictors. We further illustrate that residual variation can impact ERGM coefficients when the logistic formulation of the model is inappropriate for the data, which is common in both sparse and especially dense networks and is related to the known problem of degeneracy (e.g., Handcock et al. 2003; Mele 2017).

Because we rarely have measures of all variables relevant to network formation,¹ problems linked to residual variation and scaling are likely prevalent in ERGM applications, and their consequences for scientific inquiry using statistical network methods are potentially large. Indeed, a survey of sociological literature applying ERGM shows that it is common for researchers to interpret coefficients as effect sizes, to compare coefficients between models, and to rely on interaction coefficients to interpret interactions (e.g., Kreager et al. 2017:707; Lewis 2013:18,816; Papachristos and Bastomski 2018:545; Papachristos et al. 2013:434; Stewart et al. 2019:108; Wimmer and Lewis 2010:618). Current introductory texts on ERGM also make no mention of scaling and instead recommend interpreting interaction coefficients as interaction effects (Lusher, Koskinen, and Robins 2013:54) or comparing coefficients between models to assess confounding (Cranmer et al. 2017:242; Goodreau, Kitts, and Morris 2009:115).

Although similar issues have been documented in generalized linear models (see Mood 2010), they have gone unaddressed in statistical network analysis.² The goal of this article is to introduce the problem of scaling in ERGM, to outline its sources, and to propose methods for overcoming the issue in ERGM. The first section provides a brief overview of ERGM. The second section introduces the problem of scaling and how it affects parameter interpretation by deriving a latent variable formulation of ERGM. The third section evaluates the impact of scaling for assessing effect size, differences in coefficients between models, and interaction coefficients with a series of simulations. The fourth section proposes methods for overcoming each of these issues. These methods are extended to develop formal tests for mediation and moderation analysis, which have yet to be introduced for statistical network models. It concludes with a replication study using the largest AddHealth in-school friendship network examined by Goodreau et al. (2009). The empirical application shows that correcting for scaling can change substantive conclusions in ERGM applications. Extensions to other statistical network models are also discussed.

Overview of ERGM

ERGMs are a class of statistical network model that represent graph probabilities using an exponential-family distribution. Common ERGM formulations are Erdos-Renyi models (Erdos and Renyi 1959), dyad independence ( $p 1$ ) models (Holland and Leinhardt 1981), Markov graphs (Frank and Strauss 1986), and curved ERGMs (Hunter 2007; Snijders et al. 2006). In most applications, ERGMs are used to represent some kind of dyadic dependence structure (e.g., Markov graphs or curved ERGMs) in binary cross-sectional networks though extensions to dynamic and weighted networks exist (Desmarais and Cranmer 2012; Hanneke, Fu, and Xing, 2010; Krivitsky 2012).

Given a network Y with $y_{i j}$ ties connecting actors i and j, ERGM estimates the probability of observing Y as a function of exogenous actor level characteristics and sufficient graph statistics. ERGM has the following probability mass function:

P r (Y = y | z (y, x)) = \frac{exp (θ^{T} z (y, x))}{κ (θ)},

where $θ$ is the parameter vector, $z (y, x)$ is a p vector of exogenous characteristics x and endogenous graph statistics computed on Y, and $κ (θ) = \sum exp (θ^{T} z (y, x))^{'}$ is a normalizing constant ensuring that the sum of equation (1) over all possible networks equals 1. Due to the intractability of $κ (θ)$ in most networks of interest, the denominator is typically approximated using Markov chain Monte Carlo (MCMC) sampling (Geyer and Thompson 1992; Snijders 2002). A large distribution of possible networks are simulated and randomly sampled to approximate the maximum likelihood.³

Because the measured network is only a single representation of the underlying generative process, the graph statistics of the measured network are the expectation of those statistics across all possible networks. It is assumed that the measured network is a reasonable representation of the underlying stochastic distribution, that the likelihood principle is true, and that the likelihood formulation of the problem is reasonable.

Equation (1) provides the joint form of the model representing the probability of observing a network as a function of its sufficient statistics. This equation can be rewritten in its conditional form to provide a tie-level interpretation. Consider the tie variable $y_{i j}$ , where $y_{i j} = 1$ if i and j are connected and $y_{i j} = 0$ otherwise. The conditional form of ERGM is

\frac{p_{i j}}{1 - p_{i j}} = \frac{P r (Y_{i j} = 1 | X = x, Y_{- i j} = y_{i j})}{P r (Y_{i j} = 0 | X = x, Y_{- i j} = y_{- i j})} = exp (θ_{e n d o g e n o u s}^{T} δ_{i j}^{+} (y) + θ_{e x o g e n o u s}^{T} x_{i j}),

with cumulative distribution function:

p_{i j} = \frac{exp (θ_{e n d o g e n o u s}^{T} δ_{i j}^{+} (y) + θ_{e x o g e n o u s}^{T} x_{i j})}{1 + exp (θ_{e n d o g e n o u s}^{T} δ_{i j}^{+} (y) + θ_{e x o g e n o u s}^{T} x_{i j})},

where $δ_{i j}^{+}$ is the change in parameterized graph statistic when a focal tie $y_{i j}$ is toggled from 0 to 1. Readers will recognize the functional form from logistic regression. Indeed, ERGM is a logit model—an auto-logistic regression (Frank and Strauss 1986; Wasserman and Patterson 1996)—but is distinct from logistic regression in that tie variables are treated as conditional on the entire graph structure and are not assumed to be independent (except in special cases; Besag 1972:72; Besag 1974:201). Parameters can thus be interpreted as the increase/decrease in log-odds of an ij tie given a one unit change in a focal covariate effect, conditional on other covariates in the model.

Scaling in ERGM

The Problem of Scaling: A Latent Variable Formulation

Problems related to scaling and rescaling emerge in ERGM because the error distribution is invariant across models. Although all stochastic models (which ERGM and generalized linear models are cases) assume some random error, this error is not reflected in either equations (1) or (2). Researchers are consequently forced to (implicitly) assume a distribution for the error. The distribution of this error is invariant regardless of model specification.

The simplest way to show how error invariance arises is to formulate ERGM as a latent variable model. This formulation is common in the literature on logistic regression (Cramer 2007; Hosmer and Lemeshow 2000; Karlson, Holm, and Breen 2012; Long 1997; Mood 2010) but has not been derived for ERGM. Online Appendix A (which can be found at http://smr.sagepub.com/supplemental/) shows that the latent ERGM representation presented below is equivalent to the traditional ERGM representation.

To begin, we can regard $Y_{i j}$ as a binary indicator of the latent variable $Y_{i j}^{*}$ that takes a value of 1 of when $Y_{i j}^{*}$ is greater than 0⁴ and takes a value of 0 otherwise:

Y_{i j} = \{\begin{matrix} 1 & if Y_{i j}^{*} > 0 \\ 0 & otherwise . \end{matrix}

We can then write the latent model for $Y_{i j}^{*}$ as a function of latent endogenous and exogenous parameters:

Y_{i j}^{*} = α_{e n d o g e n o u s}^{T} δ_{i j}^{+} (y) + α_{e x o g e n o u s}^{T} x_{i j} + ∊_{i j} .

While it may seem strange to write the latent variable model as conditional on the measured graph statistics, recognizing that the measured network is a direct mapping of the latent variable clarifies that this notation is merely a convenience. We could equivalently write the latent variable model as conditional on all values of $Y_{i j}^{*} > 0$ without losing generality.

The benefit of equation (5) is that we are able to account for the error ( $∊$ ) because $Y^{*}$ is continuous, while Y is not. As in any stochastic model, we require an assumption on the mean of the error to formulate the model, which is ubiquitously assumed to be 0 conditional on other covariates. However, because $∊$ is unmeasurable, we also require an assumption on the variance to scale the inequality in equation (4). As in other logit models, we assume that $∊$ is a logistic random variable with mean 0 and variance $\frac{π^{2}}{3} \approx 3.29$ (see, for instance, Winship and Mare 1983:61-63; Allison 1999:189; Mood 2010:68-69).

The problem of scaling emerges because the variance of $∊$ is fixed regardless of model specification. When the true mean of the error is not 0, we encounter the well-known problem of omitted confounding variable bias. However, when the true error variance is not 3.29, coefficients are also biased by scaling. This is clearest to see by incorporating the scale $τ$ into the latent variable model:

Y_{i j}^{*} = α_{e n d o g e n o u s}^{T} δ_{i j}^{+} (y) + α_{e x o g e n o u s}^{T} x_{i j} + τ ∊_{i j} .

$τ$ relates the assumed logistic distribution of $∊$ to the true error distribution. It is the ratio of the true standard deviation of the latent error to the assumed standard deviation of the latent error.

It can be shown (Online Appendix A, which can be found at http://smr.sagepub.com/supplemental/) that $τ$ links the latent model to the estimated model via:

θ_{e n d o g e n o u s}^{T} δ_{i j}^{+} (y) + θ_{e x o g e n o u s}^{T} x_{i j} = \frac{α_{e n d o g e n o u s}^{T} δ_{i j}^{+} (y) + α_{e x o g e n o u s}^{T} x_{i j}}{τ},

and the latent parameters to the estimated parameters as: $θ = α / τ$ . Consequently, only in the special case where the true error variance is 3.29 ( $τ = 1$ ) can we conclude that $θ = α$ . As discussed below, this conclusion is rarely supported in practice. In the majority of cases, residual variation is absorbed into $τ$ , and, consequently, the estimated coefficients do not equal the true (latent) coefficients.

While scaling does not affect predicted probabilities or change the sign of non-interaction coefficients or their z statistics (because standard errors scale along with coefficients),⁵ it does bias coefficient size. Further, because $τ$ usually varies between groups and between models, scaling can bias interaction coefficient size, sign, and significance, and prevent comparisons of coefficients between models (discussed below). Simulations in Online Appendix B (which can be found at http://smr.sagepub.com/supplemental/) also indicate that the MCMC methods that address many estimation problems in ERGM do little to reduce the bias created by scaling.

Sources of Scaling

It should be clear from the above discussion that ERGM coefficients are only identified to a scale when residual variation is present. Several causes of residual variation have been discussed elsewhere. For instance, Box-Steffensmeier et al. (2018) discuss how unmeasured nodal covariates can contribute to omitted variable bias and model degeneracy. Schweinberger and colleagues (Schweinberger 2020; Schweinberger and Handcock 2015; Stewart et al. 2019) develop a similar argument for the broader case of nesting structure, where accounting for nesting structure improves estimation of decay parameters and out-of-sample statistics for triad and degree distributions in curved ERGMs (see Stewart et al. 2019). Kim et al. (2016) document that measurement error during network data collection can generate inaccurate sufficient statistics that bias ERGM coefficients.

Each of these studies provides problem-specific solutions such as including nodal random effects (Box-Steffensmeier et al. 2018; Thiemichen et al. 2016; van Duijn et al. 2004), explicitly modeling nesting structure (Stewart et al. 2019), and using pseudolikelihood estimation to reduce attenuation bias in the presence of measurement error (Kim et al. 2016). However, residual variation can produce problems of scaling in more difficult to detect circumstances and is likely to persist even in research that utilizes these corrections.

The first source of residual variation is when the logistic formulation of the cumulative distribution function is inappropriate. This is a common concern in rare event models for independent binary data, such as rare event logistic regression, where the concentration of event probabilities is too extreme to be appropriately represented by the logistic sigmoid function (see Cramer 2007). In the case of ERGM, dense concentrations of tie probabilities close to 0 or close to 1 can disturb the logistic functional form of the model, which is likely to occur in either very dense or very sparse networks. In these circumstances, it is unreasonable to assume a logistic functional form for the model and, as a consequence, the true error is unlikely to be a logistic random variable. This issue is related to the well-known problem of fitting ERGMs to either very dense networks or very sparse networks (Handcock et al. 2003; Mele 2017). However, instead of pertaining to MCMC-MLE convergence, the problems outlined here can emerge even in converged models.

The second and perhaps more concerning cause of scaling is omitted variables, even those that are uncorrelated with other predictors. When an omitted variable is a determinant of tie probabilities, its residual variation is absorbed into $τ$ , causing coefficients to rescale. Because this scaling is caused by the unmeasured effect of an omitted variable, ERGM coefficients are biased even when omitted variables are uncorrelated with other predictors. This is an important result. Recent methodological extensions to ERGM have focused on developing corrections for unmeasured nodal covariates and unmeasured confounding variables (Box-Steffensmeier et al. 2018; Thiemichen et al. 2016). However, omitted variables do not need to confound any observed relationship to rescale ERGM coefficients. Nor is unmeasured heterogeneity among nodes the sole-source of residual variation. Residual variation may exist due to unmeasured dyadic- and network-level covariates or because of unmeasured interactions between or within any of these levels. As a consequence, these corrections do not resolve problems of scaling in many ERGM applications. Because the assumption of no omitted variables is untestable, we can rarely rule out the possibility that ERGM results are affected in practice.

Consequences of Scaling for ERGM Inference

Because we cannot test for residual variation, we can rarely rule out the possibility of scaling in applied research. As Box-Steffensmeier et al. (2018:4) observe, many variables relevant to an empirical model go unmeasured during data collection. The more realistic and more conservative assumption is that some residual variation exists in most models and that coefficients are only identified to a scale in most ERGM applications. This has several important consequences for ERGM inference.

First, coefficients and exponentiated coefficients cannot be interpreted as effect sizes. While rescaling does not alter conclusions about the direction and significance of noninteraction coefficients, it does affect coefficient magnitude. For example, assume that we have a latent model $Y^{*} = α_{1} X_{1} + α_{2} X_{2} + τ∊$ and that X₁ and X₂ are exogenous and uncorrelated node-level variables. If we do not include X₂ into our ERGM, it can be shown (see Online Appendix C, which can be found at http://smr.sagepub.com/supplemental/) that $θ_{1}$ will rescale to

θ_{1} \approx α_{1} \frac{\sqrt{3.29}}{\sqrt{3.29 + α_{2}^{2} V a r (X_{2})}} .

If X₁ and X₂ are correlated, we obtain:

θ_{1} \approx (α_{1} + α_{2} γ_{1}) \frac{\sqrt{3.29}}{\sqrt{3.29 + α_{2}^{2} V a r (v)}},

where $γ_{1}$ is the effect of X₁ on X₂ and v is the variation in X₂ unexplained by X₁. Consequently, if the effect size of $α_{2}$ or the variance of X₂ is large, the rescaling can be substantial.

Second, coefficients cannot be compared between models unless we assume that $τ$ is invariant. In fact, we cannot meet this assumption in any scenario where we include or exclude a variable that we expect to hold some explanatory power (i.e., that explains residual variation). Because we are typically interested in assessing differences between coefficients when we expect some amount of confounding, we must instead assume:

τ^{M o d e l 1} \neq τ^{M o d e l 2},

and thus,

θ^{M o d e l 1} - θ^{M o d e l 2} = \frac{α^{M o d e l 1}}{τ^{M o d e l 1}} - \frac{α^{M o d e l 2}}{τ^{M o d e l 2}} \neq α^{M o d e l 1} - α^{M o d e l 2} .

Differences in coefficients are therefore an uninterpretable blend of the change in $τ$ and actual confounding. This issue proves to be somewhat more dramatic for between model comparisons than for interpretations of effect size. Because $τ$ can either increase or decrease in size between models, it is possible that $θ^{M o d e l 1} - θ^{M o d e l 2}$ can provide the opposite sign to $α^{M o d e l 1} - α^{M o d e l 2}$ . It is also possible that rescaling can suppress the difference in coefficients, such that we would conclude no change between models even though there actually is confounding or exaggerate the difference, such that we conclude confounding when two variables are uncorrelated.

Third, interaction coefficients, including homophily and heterophily coefficients, cannot be used to assess significance or interpret the effect of interactions unless we assume that the each group-specific coefficient is identified to the same scale. This is easiest to see by writing separate models for each group. Consider the simplest case of two groups with latent models representing the group-specific tie propensity:

G r o u p 0 : Y_{i j}^{* 0} = α_{e n d o g e n o u s}^{0 T} δ_{i j}^{+} {(y)}^{0} + α_{e x o g e n o u s}^{0 T} x_{i j}^{0} + τ^{0} ∊_{i j}^{0}

G r o u p 1 : Y_{i j}^{* 1} = α_{e n d o g e n o u s}^{1 T} δ_{i j}^{+} {(y)}^{1} + α_{e x o g e n o u s}^{1 T} x_{i j}^{1} + τ^{1} ∊_{i j}^{1} .

Since $∊^{0} = ∊^{1}$ , $θ^{0}$ and $θ^{1}$ will only be properly scaled when $τ^{0} = τ^{1}$ . If $τ^{0} \neq τ^{1}$ , interaction coefficients used to represent differences between Groups 0 and 1 will be biased.⁶ Moreover, because we anticipate heterogeneity in effects when we model interactions, it is typically implausible to assume that $τ$ is invariant between groups. In fact, because interaction coefficients measure the equality of coefficients between groups, interaction coefficients can provide the incorrect sign and incorrect z statistic when the amount of residual variation differs between groups.

Despite that scaling and rescaling present important problems for statistical inference using ERGM, these issues have not been addressed in statistical network analysis. As illustrated above, scaling can emerge when there are omitted variables in a model, even when those omitted variables are uncorrelated with all other covariates in a model. Scaling is thus likely prevalent in applications as the assumption of no omitted variables is difficult to meet and impossible to verify. The following section evaluates the substantive impact of these issues for ERGM inference with a series of simulations.

The Substantive Impact of Scaling

Given that most ERGM coefficients are likely only identified to a scale, a pressing question is how much impact we should expect scaling and rescaling to have in applied research. To address this question, we carry out a series of simulation studies that evaluate the impact of scaling on coefficient size, differences in coefficients, and interaction coefficients. All simulations are based on empirical data so that conclusions are realistic.⁷ In the simulations to follow, residual variation is introduced by omitting uncorrelated variables from ERGM. The change in parameters of interest therefore arise because the model is only identified to a scale rather than because of an omitted confounding variable.

Simulation of Coefficient Size

To assess the substantive impact of scaling on coefficient size in ERGM, a simulation was conducted using the Faux Dixon High network as a reference network. Faux Dixon High is a directed network of 1,305 friendship ties between 248 high school students. The network is simulated from one large high school in the National Longitudinal Study of Adolescent Health.⁸ We first fit an ERGM of the form: $log (\frac{\hat{p}}{1 - \hat{p}}) = θ_{1} δ^{+} (G W E S P) + θ_{2} Re c e i v e r G r a d e$ , where $G W E S P$ indicates a geometrically weighted edgewise shared partnership term (fixed decay parameter of 0.1), $θ_{1}$ is approximately 1 ( $p < .001$ ), and $θ_{2}$ is approximately −0.5 ( $p < .001$ ). We used an MCMC sampler (Metropolis–Hastings algorithm) to simulate 1,000 network data sets using the empirical ERGM parameters, where $θ_{1}$ equaled 1 and $θ_{2}$ could equal −0.4, −0.45, or −0.5. We chose these values to remain within the scope of effect sizes that are realistic given the empirical network data. With 1,000 replications for each condition, the sample space of the experiment contains results from ERGMs fit to 3,000 network data sets.

The goal was to simulate networks from the model and then attempt to recapture the true value of $θ_{1}$ when the amount of residual variation increased. To introduce residual variation, we fit an ERGM to each of the simulated data sets with ReceiverGrade omitted from the model. Because ReceiverGrade is uncorrelated with $G W E S P$ ( $r = - .03$ ),⁹ the only source of bias in the simulated values of $θ_{1}$ is scaling, where larger absolute values of $θ_{2}$ correspond to more residual variation and thus greater scaling. We also fit an ERGM to each network that included ReceiverGrade to provide a control condition for the experiment. Because these latter ERGMs were fit with prespecified knowledge of the generative model, there is little-to-no residual variation in the control condition.

Results are straightforward to summarize (Figure 1). While the mean $G W E S P$ coefficient approximates its true value of 1 across conditions, the estimated $G W E S P$ coefficient rarely replicates its true value when residual variation is present. As the amount of residual variation increases, the estimated coefficient increases. When the coefficient for ReceiverGrade is fixed to −0.4, the amount of bias is manageable, where the mean coefficient for $G W E S P$ is 1.35. However, even modest increases in residual variation have sizable effects. The mean coefficient for $G W E S P$ is 1.4 when the ReceiverGrade coefficient is equal to −0.45 and increases to 1.57 when the ReceiverGrade coefficient is −0.5. If we were to interpret the results from an ERGM in this latter case, we would conclude that $G W E S P$ has an effect size 57 percent larger than its actual effect size despite there being no omitted confounding variables. These differences are exaggerated if we use exponentiated coefficients to interpret effect sizes. For instance, the true odds ratio is 2.72 (exp(1) = 2.72), but the estimated odds ratio increases to 3.86 (exp(1.35) = 3.86), 4.06 (exp(1.4) = 4.06), and finally to 4.81 (exp(1.57) = 4.81) at each successive increase in the amount residual variation.

Figure 1.

Effect of scaling on $θ_{1}$ . Note: $N = 6, 000$ . Dashed vertical line marks its true value of 1.

Also of note are the confidence intervals in each simulation. Every confidence interval is narrow, and none of the confidence intervals in any of the treatment conditions contained the true GWESP (geometrically weighted edgewise shared partnerships) coefficient of 1. This result illustrates that scaling can pose problems for ERGM inference even when resampling is possible because confidence intervals rescale alongside ERGM coefficients. These results illustrate that the consequences of scaling for conclusions about effect size can be substantial. Even though even though ReceiverGrade and GWESP are uncorrelated, the bias in the bias in estimated coefficients is sizable in every treatment condition. We therefore caution researchers against relying on coefficients and exponentiated coefficients to interpret effect size in ERGM applications.

Simulation of Differences in Coefficients

We now consider the effect of scaling on the difference in coefficients using a simulation based on the Faux Mesa High network data. The Faux Mesa Network is an undirected network of 205 students and 203 ties. We first estimated an ERGM predicting ties as a function of students’ sex and GWESP (fixed decay term equal to 0.3). Next, we simulated a confounding or mediating edge covariate M to be correlated with $G W E S P$ , but uncorrelated with $G r a d e$ , using a linear model of the form: $M = 1 + .5 δ^{+} (G W E S P) + e$ , where e is a randomly distributed error with a mean of 0 and a standard deviation of 2. We used the following ERGM equation to simulate network data sets:

log (\frac{p}{1 - p}) = θ_{E d g e s} + θ_{G W E S P} δ^{+} (G W E S P) + θ_{M} M + θ_{G r a d e} G r a d e,

where the coefficients for $E d g e s$ and $G W E S P$ were set to their empirical values ( $θ_{E d g e s} = - 5.4$ and $θ_{G W E S P} = 1.85$ ) and $θ_{M}$ was set to equal 1. To introduce residual variation, we varied the value of $θ_{G r a d e}$ to equal either −0.1, −0.15, or −0.2, where higher absolute values increase the amount of residual variation and the degree of scaling. With 1,000 simulated data sets for each condition, the sample space of the experiment includes the differences in coefficients for 3,000 simulated networks.

At each replication, we fit two ERGMs to the simulated network data to calculate the naive difference in coefficients. The first ERGM predicted ties as a function of the number of edges and GWESP; the second ERGM included M. Because $G r a d e$ is uncorrelated with either $G W E S P$ ( $r = - .02$ ) or M ( $r = 0$ ), omitting it from both models introduces residual variation without introducing omitted confounding variable bias. The naive difference in coefficients is the difference in $θ_{G W E S P}$ between models. We calculated the true difference in coefficients using the product of true coefficients, which is equivalent to the true difference in coefficients when using the latent parameter for M ( $α_{M}$ ) (see Breen, Karlson, and Holm 2013; Mackinnon et al. 2007). The true difference in coefficients is $β_{1} α_{M}$ ,¹⁰ where $β_{1}$ is obtained from fitting the linear regression $M = β_{0} + β_{1} δ^{+} (G W E S P) + e$ and $α_{M} = 1$ is the true coefficient used to simulate the network. We used a linear regression to estimate $β_{1}$ instead of the predetermined value of 0.5 because the $G W E S P$ statistic, and thus, the value of $β_{1}$ varies endogenously for each simulated network.¹¹

Figure 2 summarizes simulation results. When there are low amounts of residual variation, the naive difference in coefficients is small in value and close to 0. Here, the mean naive difference in coefficients is 0.03 despite the mean true difference being substantial in size at 0.17. In other words, the estimated difference in coefficients is 17 percent of the size of the true difference in coefficients. The naive difference in coefficients also provides the incorrect sign in 26 percent of cases. Increasing residual variation increases the discrepancy between the true and naive difference in coefficients. For instance, when $θ_{G r a d e}$ is fixed to equal −0.2, the naive difference in coefficients yields the incorrect sign in 34 percent of cases. The mean naive difference in coefficients is 0.05, while the mean true difference in coefficients is 0.22. A researcher encountering these results would conclude that either there is no difference in coefficients between models or that M suppresses, rather than explains, the effect of $G W E S P$ . Thus, we caution researchers against comparing coefficients between models in ERGM applications.

Figure 2.

Effect of scaling on difference in coefficients. Note: $N = 6, 000$ . Dashed line marks zero.

Simulation of Interaction Coefficients

We now return to the Faux Dixon network data to examine the impact of scaling on interaction coefficients. We first fit an ERGM to the Faux Dixon High network with the form:

log (\frac{p}{1 - p}) = θ_{S a m e S e x} S a m e S e x + θ_{S e n d e r S e x} F e m a l e + θ_{R e c e i v e r S e x} F e m a l e + θ_{S e n d e r G r a d e} G r a d e + θ_{R e c e i v e r G r a d e} G r a d e + θ_{M u t u a l} δ^{+} (M u t u a l i t y),

where the $S a m e S e x$ interaction coefficient is the coefficient of interest (model results in Table 1). We then used a Metropolis–Hastings algorithm to simulate 1,000 networks from the empirical ERGM. We fit an ERGM to each of the simulated networks, where the regressors were $S e n d e r S e x$ , $R e c e i v e r S e x$ , $M u t u a l$ , and $S a m e S e x$ . Residual variation was introduced by omitting $S e n d e r G r a d e$ in one condition and then increased in a second condition by omitting both $S e n d e r G r a d e$ and $R e c e i v e r G r a d e$ . Because same sex friendships are uncorrelated with either $R e c e i v e r G r a d e$ ( $r = .003$ ) or $S e n d e r G r a d e$ ( $r = - .01$ ), the only source of bias in the interaction coefficient is from scaling.¹² We also fit an ERGM to each network where both grade covariates were included to provide a control condition for the experiment.

Table 1.

ERGM of Friendships in Faux Dixon High.

Parameters	Model 1
Sex (male is referent)
Sender	0.02 (.06)
Receiver	−0.04 (.06)
Same sex	0.11* (.05)
Grade
Sender	−0.25*** (.02)
Receiver	−0.22*** (.02)
Mutual	3.46*** (.10)
AIC	11,063
BIC	11,117

$^{*} p < .05.$ $^{* *} p < .01.$ $^{* * *} p < .001.$

Figure 3 summarizes the simulation results. In the control condition, the simulated values of $θ_{S a m e S e x}$ reproduce the true value of 0.11 without trouble. The mean value of $θ_{S a m e S e x}$ is 0.12 with a mean z statistic of 2.4 (true value 2.33). When there are low amounts of residual variation and only $R e c e i v e r G r a d e$ is omitted from the model; however, the average coefficient for $S a m e S e x$ is 0.05 with a mean z statistic of 1.06. Only in 15 percent of cases did the estimated value of $θ_{S a m e S e x}$ approximate its true value of 0.11 with a z statistic greater than 1.96. In an additional 12 percent of cases, $θ_{S a m e S e x}$ yielded a negative sign. If we were to interpret these results under conditions of little scaling, we would conclude that sex homophily has little-to-no substantive effect on friendship formation. Results are even more striking when we increase the amount of residual variation. When both $R e c e i v e r G r a d e$ and $S e n d e r G r a d e$ are omitted from the simulated ERGMs, the mean coefficient for $S a m e S e x$ is −3.29—a substantial increase in size and a reversal of sign when compared to the true value of $θ_{S a m e S e x}$ . At no point did the simulated coefficients approximate the true coefficient. Moreover, each simulated ERGM returned this value at a high level of confidence, where the mean z statistic for $θ_{S a m e S e x}$ was −82.78. A researcher examining this model would be led to conclude that sex homophily is inversely related to friendship formation. We therefore caution researchers against interpreting interaction coefficients and their z statistics as evidence of an interaction effect.

Figure 3.

Effect of scaling on $S a m e S e x$ coefficient. Note: $N = 3, 000$ . Dashed line marks the true value of $θ_{S a m e S e x}$ (0.11) and its z statistic (2.3).

Summary of Simulation Results

Simulation results illustrate that residual variation and scaling have important consequences for interpreting effect sizes, assessing differences in effects between models, and interpreting and testing interactions. When residual variation is present, ERGM coefficients are a biased measure of effect size, and this bias can be substantial under realistic circumstances. Coefficients also frequently rescale between models, suppressing differences in effects and potentially altering conclusions about confounding and mediation. Interaction coefficients and their z statistics are also often biased in the simulations, frequently yielding the incorrect sign. Collectively, these results illustrate that realistic amounts of residual variation can have large consequences for ERGM inference. We now introduce methods for addressing scaling in ERGM.

Methods for Handling Scaling

Simulation results reveal that realistic amounts of scaling can have large consequences for ERGM inference. Because we rarely have observational measures of all relevant variables, it is likely that these problems are common in practice. How should this issue be overcome in applied research? While a number of studies have proposed solutions for addressing scaling and rescaling in GLM (generalized linear models), their extension to statistical network models is problematic. Most solutions that circulate the literature on GLM assume independent and identically distributed observations—an assumption violated by network data. For instance, one popular method for comparing coefficients between models is to first regress the confounding variable of interest on the remaining predictor variables and then standardize the focal variable using the residual from this regression (Breen et al. 2013; Karlson et al. 2012; Mackinnon et al. 2007). Since residuals are biased by nonindependence and endogeneity, this method cannot be used in dyadic dependence ERGMs. Likewise, a common strategy for testing interactions is to estimate separate regressions for each group and use likelihood ratio tests to assess the equivalence of coefficients between groups (Allison 1999). However, because network data are interdependent, splitting the data into separate models will fundamentally damage the representation of network structure with potentially impactful consequences.

We propose using a marginal effects framework to overcome problems related to scaling in ERGM. While ERGM coefficients can only be identified to a scale, scaling has no effect on predicted tie probabilities (see Online Appendix A, which can be found at http://smr.sagepub.com/supplemental/). Moreover, because marginal effects are obtained in postestimation, the only necessary independence assumption is that the ERGM is estimated at the correct level of independence, which is an assumption implicit in all ERGMs (Koskinen and Daraganova 2013). The framework integrates methods that have been recently proposed for GLM (Long and Mustillo 2018; Mize, Doan, and Long, 2019; Mood 2010) but can be extended to ERGM due to their relaxed independence assumptions. The framework is flexible and can be easily applied across ERGM specifications and applications. We focus here on the average marginal effect (AME), though all methods can be applied to any marginal effect variant, including partial effects (see Wooldridge, 2002), marginal effects at means (Agresti 2002; Long 1997), or marginal effects at representative values (Long and Mustillo 2018; Mize et al. 2019).¹³

Interpreting Effect Sizes

Marginal effects are based on the derivative of the slope at a particular point in the cumulative distribution function (equation 3). The marginal effect for a variable is the expected increase in tie probability when the variable increases by 1. For a continuous variable, we define the marginal effect with respect to a variable X as its partial derivative,

M E_{θ_{x}}^{i j} = θ_{x} \frac{δ {\hat{p}}_{i j}}{δ X_{i j}} .

For binary variables, the partial derivative is equivalent to the difference in tie probabilities when X changes from 0 to 1. The superscript $i j$ indexes that all dyads in the ERGM sample space have a marginal effect. Because marginal effects summarize changes in tie probability, they are unaffected by scaling (Cramer 2007; Long 1997). Equation (14) also makes clear that the marginal effect preserves ERGM independence assumptions; that is, marginal effects are assumed to be independent conditional on the parameterized sufficient statistics.

The AME of a variable is its mean marginal effect. Formally, we calculate the AME as:

A M E_{θ_{x}} = θ_{x} \frac{1}{n} Σ_{i j = 1} \frac{δ {\hat{p}}_{i j}}{δ X_{i j}} = \frac{Σ_{i j = 1} M E_{θ_{x}}^{i j}}{n},

where n is the number of dyads in the ERGM sample space. The AME expresses the average change in expectation given a one-unit increase in X. It can be calculated on either the scale of the ERGM linear component or the scale of tie probabilities. Standard errors are obtained with the Delta method (see Agresti 2002).¹⁴ The Delta method standard error provides a z statistic equal to the coefficient z statistic for noninteraction coefficients. AMEs therefore do not affect conclusions regarding the significance, direction, or relative size of effects within a model for non-interaction terms.¹⁵

An appealing property of the AME is that it has an intuitive interpretation. Suppose that we are examining the effect of age on friendship networks and we obtain an AME of 0.005 (calculated on the scale of tie probabilities) and a coefficient of 2. A one-unit increase in the coefficient for age would correspond to an exp(2) = 7.38 increase in the estimated odds of a friendship. However, because of scaling, we cannot be sure that the estimated odds ratio is the true odds ratio. Moreover, because odds ratios are ratios, the substantive change in tie probability varies multiplicatively for each unit increase in age. Alternatively, we can interpret the AME equivalently regardless of the value of age or amount of scaling: A one-year increase in age correlates with an average 0.005 increase in tie probability. This interpretation is more intuitive and often more immediately relevant to research interests than odds ratios. Moreover, because AMEs do not rescale between models or groups, they provide a basis for drawing cross-model comparisons and for evaluating interaction effects. We now introduce these methods for ERGM.

Testing Differences between Models

As described above, we cannot attribute the difference in coefficients to confounding or mediation. Comparisons of coefficient significance are also problematic as the difference between significant and insignificant is not, in itself, statistically significant (Bollen and Stine 1990; Gelman and Stern 2006). To assess the change in effect size, we calculate the difference in the AME between models:

A M E_{θ_{x}}^{M o d e l 1} - A M E_{θ_{x}}^{M o d e l 2} .

Because AMEs are robust to scaling but are still affected by omitted correlates, AMEs only change in size when a confounding variable is excluded or included. Differences in AMEs can therefore be attributed to substantively relevant differences in effects.

To determine whether the change in AME is statistically significant, we use a Wald test with test statistic:

z = \frac{A M E_{θ_{x}}^{M o d e l 1} - A M E_{θ_{x}}^{M o d e l 2}}{\sqrt{V a r (A M E_{θ_{x}}^{M o d e l 1}) + V a r (A M E_{θ_{x}}^{M o d e l 2}) - 2 C o v (A M E_{θ_{x}}^{M o d e l 1}, A M E_{θ_{x}}^{M o d e l 2})}},

where the denominator is the standard error for the difference in AMEs. Rejecting the null hypothesis means that there is a statistically significant difference in AME between models.

To calculate the standard error for the difference in AMEs, we require the variance estimates for both AMEs and the cross-model covariance between AMEs. We obtain the cross-model covariance using seemingly unrelated estimation (Mize et al. 2019; Weesie 1999). Suppose $θ_{1}$ and $θ_{2}$ are the parameter vectors from two separate ERGMs fit to the same network. The cross-model covariance vector is calculated as:

C o v (θ_{1}, θ_{2}) = D_{1}^{- 1} Σ_{i} w_{i} u_{1 i} u_{2 i}^{T} D_{2}^{- 1},

where $D$ is the negative Hessian matrix of the ERGM log-likelihood ( $D^{- 1}$ is the covariance matrix of the ERGM estimator), $u$ is the gradient of the log-likelihood, and w is a vector of weights equal to zero if the $i th$ parameter does not appear in both models and equal to 1 if it does. The cross-model covariance matrix for the marginal effects can be estimated using the Delta method and the cross-model covariance matrix.

A desirable property of equation (17) is that it reduces to a Sobel test (see Sobel 1986) in large-sample linear models (see Online Appendix D, which can be found at http://smr.sagepub.com/supplemental/).¹⁶ Under standard assumptions for mediation analysis (see Mackinnon 2008:53-55), we can use this method as a formal test of mediation. If we are conducting mediation analysis, the difference in AMEs is the indirect effect, or the average change in tie probability indirectly attributable to X through a mediating pathway. We can interpret $A M E_{θ_{x}}^{M o d e l 2}$ as the partial or direct effect. Another desirable trait of this method is that $A M E_{θ_{x}}^{M o d e l 1}$ is equal to the sum of the indirect and partial effects, which is not usually true in mediation analysis in nonlinear probability models (Mackinnon 2008). The total effect is equal to $A M E_{θ_{x}}^{M o d e l 1}$ .

We can assess the extent of mediation by calculating how much of the total effect is explained by controlling for the mediator. The percent mediated is

100 (1 - \frac{A M E_{θ_{x}}^{M o d e l 2}}{A M E_{θ_{x}}^{M o d e l 1}}) .

The percent mediated is a useful quantity when the goal is to summarize the degree of confounding by including a correlated variable. However, the quantity may be misleadingly large if the total effect is small. Researchers will often wish to interpret the percent mediated with respect to the total and indirect effects.

Simulation

Because there is no baseline method for comparing coefficients between models in ERGM, it is useful to demonstrate the validity of the proposed test under conditions of residual variation. The following simulation uses the Faux Desert High network, which is a simulated friendship network based on one rural Southwest high school in the AddHealth data collection. The network is undirected¹⁷ with 107 students and 439 friendship ties. We first estimated an ERGM to the network of the form $log (\frac{{\hat{p}}_{i j}}{1 - {\hat{p}}_{i j}}) = θ_{0} E d g e s + θ_{1} G r a d e + θ_{2} A b s D i f f (G r a d e)$ , where $G r a d e$ is a nodal covariate and $A b s D i f f (G r a d e)$ is the absolute difference in two students’ grades. We stored the estimated coefficients to use for simulation, where $θ_{0} \approx 1.65$ , $θ_{1} \approx - 0.2$ , and $θ_{2} \approx - 1.45$ .

To conduct the simulation, we simulated random networks using the above model, but we included a random nodal-level covariate with a mean of 0 and a standard deviation 1 to manipulate residual variation. The random variable was uncorrelated with any other predictor. Its coefficient could obtain three possible values of 0.5, 1, and 1.5. We fit four ERGMs to each network and assessed the difference in AMEs for each matched pair. The first pair of ERGMs was estimated with and without $A b s D i f f (G r a d e)$ , and the difference in $A M E_{θ_{1}}$ was recorded. These models included the random variable, so that residual variation was minimized. This provided a control condition and an estimate of the true difference in AMEs between models. The same comparisons were performed in the second set of ERGMs, but the random nodal variable was excluded from ERGM estimations. By increasing the coefficient for the random nodal variable, we are thus able to increase residual variation and evaluate its impact on the difference in AMEs. For each condition, we simulated 1,000 networks. With three levels of residual variation and four ERGMs fit to each network, the simulation considers the differences in AMEs in 12,000 ERGMs between 6,000 matched pairs in 3,000 network data sets.

Figure 4 plots the differences between the true and estimated values of $A M E_{θ_{1}}^{M o d e l 1} - A M E_{θ_{1}}^{M o d e l 2}$ , the difference in z statistics, and the difference in the upper and lower bounds for 95 percent confidence intervals. Across measures and levels of residual variation, there is little difference between the true and estimated statistics. The largest discrepancy is for the z statistic, where in one case the estimated z static was 0.58 below the true z statistic. However, given that the true z statistic was 8.38, the relative discrepancy was negligible (the estimated z statistic was 7.79). In the overwhelming majority of cases, there was little-to-no discrepancy between the estimated and true values: The mean difference in z statistics is −0.04, the mean difference in $A M E_{θ_{1}}^{M o d e l 1} - A M E_{θ_{1}}^{M o d e l 2}$ is $4.6 \times 10^{- 6}$ , the mean difference in 95 percent confidence interval lower bounds is $1.2 \times 10^{- 5}$ , and the mean difference in 95 percent confidence interval upper bounds is $- 2.9 \times 10^{- 6}$ . Consistent with theoretical results, these simulation findings illustrate that the test of differences in AMEs is robust to scaling and can be used to compare effects across models in the presence of residual variation.

Figure 4.

Difference in true and estimated $A M E_{θ_{1}}^{M o d e l 1} - A M E_{θ_{1}}^{M o d e l 2}$ when residual variation is introduced. Note: $N = 3, 000$ . Dashed line marks 0 representing no difference in estimates.

Testing Interaction Effects

As demonstrated in simulation analyses, excluding as few as two uncorrelated explanatory variables can reverse the sign of ERGM interaction coefficients. We now show how marginal effects can be used to interpret and test interaction effects in ERGM. Moderation exists when the effect of a variable varies when a second variable changes in value. We measure the interaction effect using the second difference in AMEs (Long and Mustillo 2018). We define the AME for a level of an interaction as $A M E_{θ_{x}}^{g = k}$ , where $θ_{x}$ is the effect of interest and g is the moderator with k values. The second difference is:

Δ A M E_{θ_{x}}^{g} = A M E_{θ_{x}}^{g = k_{1}} - A M E_{θ_{x}}^{g = k_{2}} .

If g is binary, the only second difference for the interaction is when g changes from 0 to 1. If g is continuous, we can specify the values of g to be any values in the data set. We can also set g to representative values or summary statistics, such as the mean plus or minus one standard deviation.

We interpret the second difference as the increase/decrease in AME when g changes in value. Say that we are interested in assessing the effect of sex homophily in a friendship network. The AME of interest is a binary indicator variable for female students. Let the AME for male alters be 0.001 and the AME for female alters be 0.004. The second difference would be 0.003, indicating that the effect of being female on tie probabilities increases by 0.003 when an alter is female instead of male, reflecting a preference for same sex friendships. We assess significance using a Wald test with the following test statistic:

z = \frac{A M E_{θ_{x}}^{g = k_{1}} - A M E_{θ_{x}}^{g = k_{2}}}{\sqrt{V a r (A M E_{θ_{x}}^{g = k_{1}}) + V a r (A M E_{θ_{x}}^{g = k_{2}}) - 2 C o v (A M E_{θ_{x}}^{g = k_{1}}, A M E_{θ_{x}}^{g = k_{2}})}},

where the denominator is the standard error for the second difference. As before, we can use the Delta method to estimate the AME covariance matrix.

When g has a large number of unique values, it may be difficult to succinctly summarize the impact of an interaction using second differences. One way to do so is to compute the second difference when g changes from its smallest value to its maximum, which will provide insight to the overall change in the interaction effect. In other cases, researchers may simply want to report the average interaction effect or the average second difference. We first calculate the second differences for all k in increasing order and then take the mean second difference:

\bar{Δ} A M E_{θ_{x}}^{g} = \frac{\sum A M E_{θ_{x}}^{g = k} - A M E_{θ_{x}}^{g = k - 1}}{N_{k} - 1},

where N_k is the number of unique values in g. We can interpret $\bar{Δ} A M E_{θ_{x}}^{g}$ as the average change in effect when g increases in value. We can also calculate the average absolute second difference if the interaction is curvilinear. If we are examining the average second difference, we test the significance of the interaction with the average Wald statistic for the second differences. If we are examining the average absolute second difference, we test significance with the average absolute Wald statistic. In either scenario, the null hypothesis is that the average second difference or the average absolute second difference is zero.¹⁸

Because marginal effects are robust to scaling, we can also compare second differences between models. For instance, if we are studying a school friendship network, we may be interested in evaluating whether triadic closure explains the effect of sex homophily. We estimate two ERGMs, one that includes sex homophily, and one that includes both sex homophily and triangles. We would then compute the second difference for sex homophily in each model and use equation (17) to test their equivalence, replacing the AMEs with second differences.

Summary

The marginal effects framework outlined above provides a strategy to overcome problems of scaling in ERGM. Because it is typically impossible to determine that there are no omitted variables in a model, we recommend that researchers use these methods to interpret effect size, test for and interpret interaction effects, and to compare effects between models. These methods are available for use via the opensource software package ergMargins for R (Duxbury 2019), available through the Comprehensive R Archive Network repository and as a part of the xergm suite of packages. We now apply these methods in an empirical application reexamining the role of selective mixing and triadic closure in a large AddHealth school friendship network.

Empirical Application: Revisiting Birds of a Feather or Friend of a Friend?

To demonstrate how these methods can be used to correct for scaling, we examine the relationship between selective mixing and triad counts in one large AddHealth friendship network. An empirical regularity in social networks is high levels of clustering (Newman 2010; Watts and Strogatz 1998). Observed levels of clustering in social networks are typically attributed to two underlying processes: selective mixing (preferential attachment to similar alters) and triadic closure. Goodreau et al. (2009) sought to disentangle these two processes using ERGM on a pooled sample of 59 school networks from the AddHealth data set. Based on comparisons of homophily coefficients between models, they found that (1) triadic closure explains much of the effect of selective mixing, (2) that selective mixing promotes triadic closure, and (3) that there is little relationship between students’ nodal attributes and triad closure, with the exception of female students’ tendency to be embedded in triangles.

However, because coefficients are only identified to a scale in most ERGM applications, we are unable to compare homophily coefficients between models or interpret them as evidence of a homophily effect. We now revisit this research question in a replication analysis of the largest AddHealth in-school network in Goodreau et al.’s (2009) sample. The network contains friendship nominations between 2,209 7th and 12th graders (school ID: 44 in the supplementary tables to Goodreau et al. 2009). While the in-school network is directed, we follow Goodreau et al.’s (2009) inclusion criteria and only examine the 1,893 mutual ties between students. Our model specification is, for the most part, identical to the original study. The only difference is that we include Native American students in the “other” racial category, instead of as an independent group. Nodal covariates or “sociality” terms include students’ race (whites are referent), sex (males are referent), and grade (7th grade is referent). Each sociality term is treated as a categorical variable, with missing values controlled for as a discrete category. Selective mixing is measured by including homophily (matched attribute) interactions for each nodal covariate. Triadic closure is measured with a GWESP term using a fixed decay parameter of 0.25. Consistent with Goodreau et al. (2009), we estimated three models. The first is a dyad independence model including only exogenous attributes. The second is a curved ERGM including only the GWESP parameter. The third is a fully specified model including all variables.

Table 2 presents results (Panel A). While we were unable to perfectly replicate Goodreau et al.’s (2009) models, the substantive results are mostly consistent in terms of direction, relative coefficient size, and differences in coefficients between models.¹⁹ In model 1, female students have higher tie probabilities as compared to male students. Black and Asian students have higher tie probabilities than whites, while Latino students have lower tie probabilities. Naive interpretations of selective mixing coefficients also suggest that there is a preference for sex, race, and grade homophily across categories. Model 2 includes only GWESP and an edges term. The positive coefficient indicates that triadic closure increases the probability of friendship formation. Model 3 presents full model results. The percent change in coefficients indicates that most coefficients decline in size in the full model, with the exception of the black sociality coefficient. Consistent with Goodreau et al. (2009), the change in coefficient size is also quite large, with most coefficients declining by more than 20 percent. If scaling were not a problem, these results would indeed imply confounding. We now turn to AMEs to interpret effect size, interaction effects, and differences in effects between models.

Table 2.

ERGM of Friendships in Large AddHealth School Network.

Panel A. Model results presented as coefficients and standard errors.
	Model 1	Model 2	Model 3	Percent Change
	$θ$ (SE)	$θ$ (SE)	$θ$ (SE)	Percent Change
Edges	−19.83*** (.41)	−7.78*** (.03)	−17.70*** (.51)
Sociality
Female	0.32*** (.03)		0.18*** (.05)	−34
Black	0.25*** (.06)		0.30* (.12)	20
Latino	−0.41*** (.03)		−0.16*** (.04)	−39
Asian	0.43*** (.09)		0.35* (.15)	−19
Other race	−0.29 (.21)		0.03 (.33)	−90
8th Grade	0.03 (.06)		−0.14 (.11)	−467
9th Grade	−0.56*** (.05)		−0.32*** (.09)	−43
10th Grade	−0.60*** (.05)		−0.33*** (.09)	−45
11th Grade	−0.43*** (.05)		−0.19* (.09)	−56
12th Grade	−0.27*** (.06)		−0.16 (.10)	−41
Selective mixing
Female	0.72*** (.05)		0.61*** (.06)	−15
White	1.05*** (.08)		0.74*** (.10)	−30
Black	1.52*** (.12)		1.18*** (.16)	−22
Latino	1.01*** (.08)		0.87*** (.09)	−14
Asian	1.53*** (.16)		1.01*** (.21)	−34
Other race	−0.14 (.23)		−0.07 (.34)	−50
7th Grade	2.89*** (.20)		2.42*** (.21)	−16
8th Grade	2.66*** (.19)		2.00*** (.21)	−25
9th Grade	1.79*** (.09)		1.49*** (.11)	−17
10th Grade	0.98*** (.08)		0.79*** (.11)	−20
11th Grade	0.78*** (.08)		0.66*** (.10)	−15
12th Grade	1.26*** (.09)		0.91*** (.12)	−28
Triadic closure
GWESP		2.57*** (.05)	1.92*** (.07)	−25
Panel B. Model results presented as AMEs and second differences
	AME × 10 (SE)	AME × 10 (SE)	AME × 10 (SE)	Percent Change
Sociality
Female	0.003*** (.000)		0.001*** (.000)	−51**
Black	0.002*** (.000)		0.002* (.000)	−3
Latino	−0.003*** (.000)		−0.001*** (.000)	−65***
Asian	0.003*** (.000)		0.002* (.001)	−29
Other race	−0.001 (.002)		0.000 (.000)	9
8th Grade	0.000 (.000)		0.000 (.000)	−460
9th Grade	−0.004*** (.000)		−0.002*** (.000)	−48**
10th Grade	−0.005*** (.000)		−0.002*** (.000)	−52**
11th Grade	−0.003*** (.000)		−0.001* (.000)	−62**
12th Grade	−0.002*** (.000)		−0.001 (.000)	46
Selective mixing
Female	0.007*** (.000)		0.004*** (.000)	−29***
Black	0.006*** (.000)		0.005*** (.000)	−17
Latino	0.007*** (.000)		0.006*** (.000)	−15
Asian	0.004*** (.000)		0.004*** (.000)	−19
Other race	−0.001 (.000)		0.000 (.002)	−62
8th Grade	0.007*** (.000)		0.005*** (.000)	−31**
9th Grade	0.010*** (.000)		0.008*** (.000)	−22*
10th Grade	0.005*** (.000)		0.004*** (.000)	−12
11th Grade	0.004*** (.000)		0.004*** (.000)	−11
12th Grade	0.006*** (.000)		0.004*** (.000)	−26
Triadic closure
GWESP		.018*** (.000)	0.013*** (.000)	−27***
AIC	25,310	28,110	24,187
BIC	25,641	28,136	24,530

Note: Coefficients for “missing” categories not reported. AME standard errors are calculated with the Delta method. AMEs for selective mixing coefficients are second differences. All AMEs are calculated on the scale of tie probabilities. AMEs are multiplied by 10 to simplify presentation. The significance of the percent change in AMEs is determined using equation (15).

$^{*} p < .05.$ $^{* *} p < .01.$ $^{* * *} p < .001.$

Panel B in Table 2 presents results as AMEs and second differences. A focus on AMEs reveals that the sociality effect sizes are relatively small. For instance, the AME for female students is 0.0003 in model 1, indicating that female students are only, on average, 0.03 percent more likely to be part of a mutual friendship than male students. Based on these averages, we would expect that an Asian female student in seventh grade would only be 0.11 percent more likely—one tenth of one percent—to form a mutual friendship than a white male student in 10th grade (0.0003 + 0.0003 − (−0.0005) = 0.0011). By comparison, the AME for GWESP is 0.002 in model 2, indicating that a one-unit increase raises the tie probability by 0.0018 (0.18 percent increase), with diminishing returns. In other words, closing a single triangle yields a greater difference in tie probabilities than the absolute difference in tie probabilities between the demographic most likely to forge a tie (seventh grade Asian female students) compared to the least likely demographic (10th grade White male students). This stands in contrast to the substantive impact implied by the sociality coefficients, which appear, at least intuitively, to have noteworthy effect sizes.

We now assess the interaction effect for homophily terms in model 3. Results for the direction and significance of second differences are consistent with those for interaction coefficients, indicating that scaling is not problematizing conclusions about the positive influence of homophily. However, it is also clear that interaction coefficients imply misleading conclusions about interaction effect size. If we were to interpret homophily coefficients as odds ratios, for instance, we would conclude that eighth grade homophily increases the odds of friendship seven times over (exp(2.00) = 7.39). Likewise, we would conclude that same sex friendships increase the odds of friendship by 84 percent (exp(0.61) = 1.84). Figure 5 makes clear that the differences in interaction effect sizes are not that large. Instead, the interaction effect for eighth grade friendships is approximately equal to the interaction effect for female friendships. In fact, the largest second difference is for same grade friendships among ninth graders, which has a smaller coefficient than 8th grade homophily. We arrive at a similar result for racial homophily. Although the homophily coefficient is largest for black students, the homophily interaction effect is greatest for Latinos. These results illustrate that even in cases where scaling does not problematize conclusions about the significance and direction of interaction coefficients, it can still alter conclusions about the relative and overall importance of interaction effects.

Figure 5.

Average marginal effects for homophily terms. Note: X axis is students’ attributes. Bands are 95 percent confidence intervals. Second differences are printed at the top of the plot.

Our final goal is to examine differences in effects between models. Although the percent change in AMEs is similar to the percent change in coefficients for some covariates, it is quite different for others. For instance, while the coefficient for black students increases by 20 percent, the AME does not change, indicating that the increase in coefficient size is entirely a result of scaling rather than a suppressing effect. This is particularly relevant for 12th graders. Even though the coefficient for 12th graders changes from significant to insignificant, a test of the difference in AMEs reveals that this change in significance is not itself statistically significant.

Moreover, even though most AMEs change by more than 10 percent between models, the difference in effects is only significant for 9 of the 21 model terms. Consequently, despite the relative change in coefficient size being fairly large in many cases, the conclusion of confounding is not supported for most covariates. In fact, while each second difference changes by more than 15 percent between models, the difference in second difference is only significant for 3 of the 10 interactions. Notably, there is no significant change in any of the racial homophily second differences. This contrasts with the differences in racial homophily coefficients, which decline by 15 percent to 35 percent between models. These results suggest that there is little systematic relationship between selective mixing and triadic closure in the school 44 network.

An interesting and unique result that arises from comparisons of AMEs is that the differences in AMEs are greater for nodal covariates than for homophily covariates (Table 3). Five of the 10 differences in sociality AMEs are statistically significant. For instance, the AME for female students declines by 51 percent between models. The direct and indirect effects for sex are both 0.0001. This means that, compared to male students, female students have a 0.0001 higher probability of forming friendship ties because of their gender (direct effect). The indirect effect reflects that being female is also $i n d i r e c t l y$ to forming friendship ties because female students tend to be embedded in a greater number of triangles. Put differently, being female instead of male indirectly increases the probability of forming a friendship tie by 0.0001 by contributing to triadic closure. Through both indirect and direct pathways, the probability that female students will form reciprocal friendships is 0.0003 higher than it is for male students (total effect).

Table 3.

Mediation Analysis for Sociality AMEs with GWESP as the Mediator.

	Total AME	Direct AME	Indirect AME	Percent Change
Female	.003*** (.000)	.001*** (.000)	.001** (.000)	−51
Black	.002*** (.000)	.002* (.001)	.000 (.000)	−3
Latino	−.003*** (.000)	−.001*** (.000)	−.002*** (.000)	−65
Asian	.003*** (.000)	.002* (.000)	.001 (.001)	−29
Other race	−.002 (.002)	.000 (.002)	−.002 (.003)	−9
8th Grade	.000 (.000)	.000 (.000)	.001 (.001)	−460
9th Grade	−.004*** (.000)	−.002*** (.001)	−.002** (.001)	−48
10th Grade	−.005*** (.000)	−.002*** (.000)	−.002** (.000)	−52
11th Grade	−.003*** (.000)	−.001* (.001)	−.002** (.000)	−62
12th Grade	−.002*** (.000)	−.001 (.001)	−.001 (.001)	46

Note: Delta Standard Errors in Parentheses. AMEs are Multiplied by 10. All AMEs are Calculated on the Scale of Tie Probabilities. Indirect AME is the Difference in AME between Models.

$^{*} p < .05.$ $^{* *} p < .01.$ $^{* * *} p < .001.$

Similarly, accounting for triadic closure explains a substantial portion of the effects of being in 9th, 10th, and 11th grade. The percent mediated for each of these variables ranges from 45 percent to 60 percent. This result suggests that part of the reason that students’ grade is predictive of tie probabilities is because it affects triangle counts; that is, students in 9th, 10th, and 11th grade tend to be embedded in a greater number of triangles as compared to students in 7th grade. The AME for Latinos also declines by 65 percent after controlling for GWESP. Because the percent mediated for sociality AMEs are on average larger than for selective mixing terms, these results suggest that triangle counts explain a greater share of the effect of sociality than they do of selective mixing.

A replication of Goodreau et al. (2009) reveals how scaling can alter conclusions in ERGM applications. While findings regarding the direction and significance of sociality, triad closure, and selective mixing effects were supported, conclusions regarding the substantive impact of these covariates and those related to indirect effects were problematized. Particularly, sociality terms appear to have small effect sizes when we correct for scaling. We further found that scaling affected the relative size of homophily coefficients, altering conclusions regarding the relative impact of some types of selective mixing. Scaling also led to increases in homophily coefficient size that were not reflected in the homophily effects, causing homophily coefficients to overstate the substantive importance of some types of selective mixing, like eighth grade homophily. Finally, a reanalysis of the differences in effects between models shows how scaling can alter conclusions about confounding and indirect pathways. Selective mixing only appears to affect triangle counts in the minority of cases. Further, sociality terms have greater impact on triadic closure than selective mixing, which is not reflected in comparisons of naive coefficients.

Discussion

Residual variation can have large consequences for ERGM inference. The equality of coefficients cannot be compared between models or groups in any scenario where coefficients are scaled nor can coefficients be interpreted as effect sizes. Because the assumption of no omitted variables is difficult to verify, we can rarely outrule the possibility of residual variation and scaling in practice. This study outlined these issues and proposed resolutions using marginal effects. The methods are robust to scaling and can be flexibly applied across ERGM specifications. These methods were further extended to develop formal tests of mediation and moderation, which have yet to be introduced for statistical network analysis. Collectively, the methods provide a flexible framework for interpreting effect sizes and conducting process analysis in research using statistical network methods.

While the methodological discussion here focused on ERGM, the same issues can also affect inference in other statistical network models that can be represented as logit models. Stochastic actor-oriented models, for instance, use a multinomial logistic regression to model network and behavioral change (Snijders 2001). Generalizations of ERGM map weighted edge data to a binary ERGM reference distribution (Desmarais and Cranmer 2012; Krivitsky 2012), and temporal ERGM reduces to an ERGM with block structure (Hanneke et al. 2010). Likewise, relational event models are often estimated as a logistic regression (Butts 2008). Because the proposed methods rely on postestimation, they can be used to overcome scaling in any of these models. The methods can therefore be flexibly applied in a variety of social network research to assess interaction effects and indirect pathways. They can also be applied in research using frailty ERGM (see Box-Steffensmeier et al. 2018) to address omitted confounding variables and rescaling simultaneously.

A further implication of our results is that meta-regressions of statistical network model output may be affected by scaling. Researchers often use meta-regression to combine output from multiple ERGMs, where the meta-coefficient is a weighted or unweighted average of the lower-level coefficients. The averages of these coefficients can be confounded with residual variation. Because each lower-level ERGM is identified to a unique scale ( $τ$ varies between models), it is likely that scaling could alter the size and potentially the direction of coefficients in ERGM meta-regression. Further research should explore the possibility that scaling affects results in ERGM meta-analyses.

In sum, ERGM results can be affected by scaling, which often arises when there is residual variation in an empirical model. Because we cannot test for all possible sources of residual variation (i.e., omitted variables), it is extremely difficult to rule out the possibility of scaling in practice. A methodological framework was introduced to overcome problems of scaling in ERGM. Formal tests were also developed to test the equivalence of marginal effects between models and groups. These methods can be applied to conduct mediation and moderation analysis in ERGM and related statistical network models. As such, they introduce a new methodological toolkit that can be used to assess the significance and effect of interactions and indirect pathways in statistical network analysis.

Supplemental Material

Supplemental Material, sj-docx-1-smr-10.1177_0049124120986178 - The Problem of Scaling in Exponential Random Graph Models

Supplemental Material, sj-docx-1-smr-10.1177_0049124120986178 for The Problem of Scaling in Exponential Random Graph Models by Scott W. Duxbury in Sociological Methods & Research

Footnotes

Acknowledgments

I thank David Melamed, Jacob Young, David Schaefer, Skyler Cranmer, and Carter Butts for helpful comments and conversations at various stages of this project.

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.

ORCID iD

Scott W. Duxbury

Supplemental Material

The supplemental material for this article is available online.

Notes

References

adams

jimi

Schaefer

David R.

. 2016. “How Initial Prevalence Moderates Network-based Smoking Change: Estimating Contextual Effects with Stochastic Actor-based Models.” Journal of Health and Social Behavior 57:22–38.

Agresti

Alan

. 2002. Categorical Data Analysis. New York: Wiley.

Chunrong

Norton

Edward C.

. 2003. “Interaction Terms in Logit and Probit Models.” Economics Letters 80:123–29.

Allison

Paul D.

1999. “Comparing Logit and Probit Coefficients across Groups.” Sociological Methods and Research 28:186–208.

Besag

Julian E.

1972. “Nearest-neighbour Systems and the Auto-logistic Model for Binary Data.” Journal of the Royal Statistical Society Series B 34:75–83.

Besag

Julian E.

1974. “Spatial Interaction and the Statistical Analysis of Lattice Systems.” Journal of the Royal Statistical Society Series B 36:192–236.

Bollen

Kenneth A.

Stine

Robert

. 1990. “Direct and Indirect Effects: Classical and Bootstrap Estimates of Variability.” Sociological Methodology 20:115–40.

Box-Steffensmeier

Janet M.

Christenson

Dino P.

Morgan

Jason W.

. 2018. “Modeling Unobserved Heterogeneity in Social Networks with the Frailty Exponential Random Graph Model.” Political Analysis 26:3–19.

Breen

Richard

Karlson

Kristian Bernt

Holm

Anders

. 2013. “Total, Direct, and Indirect Effects in Logit and Probit Models.” Sociological Methods and Research 42:164–91.

10.

Butts

Carter T.

2008. “A Relational Event Framework for Social Action.” Sociological Methodology 38:155–200.

11.

Cramer

Jan Salomon

. 2007. “Robustness of Logit Analysis: Analysis for Unobserved Heterogeneity and Mis-specified Disturbances.” Oxford Bulletin of Economics and Statistics 69:545–55.

12.

Cranmer

Skyler J.

Leifeld

Philip

McClurg

Scott D.

Rolfe

Meredith

. 2017. “Navigating the Range of Statistical Tools for Inferential Network Analysis.” American Journal of Political Science 61:237–51.

13.

Desmarais

Bruce A.

Cranmer

Skyler J.

. 2012. “Statistical Inference for Valued-edge Networks: The Generalized Exponential Random Graph Model.” PLoS One 7:e30136.

14.

Dumitrescu

Elena Ivona

Hurlin

Christophe

. 2012. “Testing for Granger Non-causality in Heterogenous Panels.” Economics Modeling 29:1450–60.

15.

Duxbury

Scott

. 2019. ergMargins: Process Analysis for Exponential Random Graph Models. Comprehensive R Archive Network.

16.

Erdos

Paul

Renyi

Alfred

. 1959. “On Random Graphs.” Publicationes Mathematicae 6:290–97.

17.

Frank

Ove

Strauss

David

. 1986. “Markov Graphs.” Journal of the American Statistical Association 81:832–42.

18.

Gelman

Andrew

Stern

Hal

. 2006. “The Difference between “Significant” and “Not Significant” Is Not Itself Statistically Significant.” The American Statistician 60:328–31.

19.

Geyer

Charles J.

Thompson

Elizabeth A.

. 1992. “Constrained Monte Carlo Maximum Likelihood for Dependent Data.” Journal of the Royal Statistical Society B 54:657–99.

20.

Goodreau

Steven M.

Kitts

James A.

Morris

Martina

. 2009. “Birds of a Feather, or Friend of a Friend? Using Exponential Random Graph Models to Investigate Adolescent Social Networks.” Demography 46:103–25.

21.

Handcock

Mark S.

Robins

Garry

Snijders

Tom A. B.

Moody

Jim

Besag

Julian

. 2003. “Assessing Degeneracy in Statistical Models of Social Networks.” Journal of the American Statistical Association 76:33–50.

22.

Hanneke

Steve

Wenjie

Xing

Eric P.

. 2010. “Discrete Temporal Models of Social Networks.” Electronic Journal of Statistics 4:585–605.

23.

Holland

Paul W.

Leinhardt

Samuel

. 1981. “An Exponential Family of Probability Distributions for Directed Graphs.” Journal of the American Statistical Association 76:33–50.

24.

Hosmer

David W.

Lemeshow

Stanley

. 2000. Applied Logistic Regression. Hoboken, NJ: Wiley-Interscience Publication.

25.

Hunter

David R.

2007. “Curved Exponential Family Models for Social Networks.” Social Networks 29:216–30.

26.

Karlson

Kristian Bernt

Holm

Anders

Breen

Richard

. 2012. “Comparing Regression Coefficients between Same-sample Nested Models Using Logit and Probit: A New Method.” Sociological Methodology 42:286–313.

27.

Kim

Yeaji

Leonardo

Antenangeli

Kirkland

Justin

. 2016. “Measurement Error and Attenuation Bias in Exponential Random Graph Models.” Statistics, Politics, and Policy 7:29–54.

28.

Koskinen

Johan

Daraganova

Galina

. 2013. “Dependence Graphs and Sufficient Statistics.” Pp. 77–90 in Exponential Random Graph Models for Social Networks, edited by Lusher

Dean

Koskinen

Johan

Robins

Garry

, chapter 7. Cambridge: Cambridge University Press.

29.

Kreager

Derek A.

Young

Jacob T. N.

Haynie

Dana L.

Bouchard

Martin

Schaefer

David R.

Zajac

Gary

. 2017. “Where “Old Heads” Prevail: Inmate Hierarchy in a Men’s Prison Unit.” American Sociological Review 82:685–718.

30.

Krivitsky

Pavel N.

2012. “Exponential-family Random Graph Models for Valued Networks.” Electronic Journal of Statistics 6:1100–1128.

31.

Lewis

Kevin

. 2013. “The Limits of Racial Prejudice.” Proceedings of the National Academy of Sciences 110:18814–819.

32.

Long

J. Scott

. 1997. Regression Models for Categorical and Limited Dependent Variables. Thousand Oaks, CA: Sage.

33.

Long

J. Scott

Mustillo

Sarah A.

. 2018. “Using Predictions and Marginal Effects to Compare Groups in Regression Models for Binary Outcomes.” Sociological Methods & Research. doi:10.1177/0049124118799374.

34.

Lusher

Dean

Koskinen

Johan

Robins

Garry

. 2013. Exponential Random Graph Models for Social Networks. Cambridge: Cambridge University Press.

35.

Mackinnon

David P.

2008. Introduction to Statistical Mediation Analysis. Abingdon, UK: Routledge.

36.

Mackinnon

David P.

Lockwood

Chondra M.

Brown

Hendricks

Wang

Wei

. 2007. “The Intermediate Endpoint Effect in Logistic and Probit Regression.” Clinical Trials 4:499–513.

37.

Mackinnon

David P.

Lockwood

Chondra M.

Williams

Jason

. 2004. “Confidence Limits for the Indirect Effects: Distribution of the Product and Resampling Methods.” Multivariate Behavioral Research 39:99–128.

38.

Mele

Angelo

. 2017. “A Structural Model of Dense Network Formation.” Econometrica 85:825–50.

39.

Mize

Trenton

Doan

Long

Scott Long

. 2019. “A General Framework for Comparing Predictions and Marginal Effects across Models.” Sociological Methodology 49(1):1–38.

40.

Mood

Carina

. 2010. “Logistic Regression: Why We Cannot Do What We Think We Can Do, and What We Can Do about It.” European Sociological Review 26:67–82.

41.

Newman

Mark E.J.

2010. Networks: An Introduction. Oxford, UK: Oxford University Press.

42.

Papachristos

Andrew V.

Bastomski

Sara

. 2018. “Connected in Crime: The Enduring Effect of Neighborhood Networks on the Spatial Patterning of Violence.” American Journal of Sociology 124:517–68.

43.

Papachristos

Andrew V.

Hureau

David M.

Braga

Anthony A.

. 2013. “The Corner and the Crew: The Influence of Geography and Social Networks on Gang Violence.” American Sociological Review 78:417–47.

44.

Schweinberger

Michael

. 2020. “Consistent Structure Estimation of Exponential Family Random Graph Models with Block Structure.” Bernoulli 26:1205–33.

45.

Schweinberger

Michael

Handcock

Mark S.

. 2015. “Local Dependence in Random Graph Models: Characterization, Properties, and Statistical Inference.” Journal of the Royal Statistical Society, Series B 77:647–76.

46.

Snijders

Tom A. B.

2001. “The Statistical Evaluation of Social Network Dynamics.” Sociological Methodology 31:361–95.

47.

Snijders

Tom A. B.

2002. “Markov Chain Monte Carlo Estimation of Exponential Random Graph Models.” Journal of Social Structure 3: 2–37.

48.

Snijders

Tom A.B.

Pattison

Phillipa E.

Robins

Garry L.

Handcock

Mark S.

. 2006. “New Specifications for Exponential Random Graph Models.” Sociological Methodology 36:99–150.

49.

Sobel

Michael E.

1986. “Direct and Indirect Effects in Linear Structural Equation Models.” Sociological Methods and Research 16:155–76.

50.

Stewart

Jonathan

Schweinberger

Michael

Bojanowski

Michal

Morris

Martina

. 2019. “Multilevel Network Data Facilitate Statistical Inference for Curved ERGMs with Geometrically Weighted Terms.” Social Networks 59:98–119.

51.

Thiemichen

Friel

Caimo

Kauermann

. 2016. “Bayesian Exponential Random Graph Models with Nodal Random Effects.” Social Networks 46:11–28.

52.

van Duijn

Marijtje A.

Snijders

Tom A. B.

Zijlstra

Bonne J. H.

. 2004. “p2: A Random Effects Model with Covariates for Directed Graphs.” Statistica Neerlandica 58:234–54.

53.

Wasserman

Stan

Patterson

Phillipa

. 1996. “Logit Models and Logistic Regressions for Social Networks I: An Introduction to Markov Graphs and p*.” Psychometrika 61:401–25.

54.

Watts

Duncan J.

Strogatz

Steven H.

. 1998. “Collective Dynamics of ‘Small-world’ Networks.” Nature 393:440–42.

55.

Weesie

Jeroen

. 1999. “Seemingly Unrelated Estimation and Cluster-adjusted Sandwich Estimator.” Stata Technical Bulletin 9:231–48.

56.

Wimmer

Andreas

Lewis

Kevin

. 2010. “Beyond and Below Racial Homophily: ERG Models of a Friendship Network Documented on Facebook.” American Journal of Sociology 2:583–642.

57.

Winship

Christopher

Mare

Robert D.

. 1983. “Structural Equations and Path Analysis for Discrete Data.” American Journal of Sociology 89:54–110.

58.

Wooldridge

Jeff

. 2002. Econometric Analysis of Cross Section and Panel Data. Cambridge, MA: MIT Press.

59.

Young

Jacob

. 2011. “How Do They ‘End Up Together’? A Social Network Analysis of Self-Control, Homophily, and Adolescent Relationships.” Journal of Quantitative Criminology 27:251–73.

Supplementary Material

Please find the following supplemental material available below.

For Open Access articles published under a Creative Commons License, all supplemental material carries the same license as the article it is associated with.

For non-Open Access articles published, all supplemental material carries a non-exclusive license, and permission requests for re-use of supplemental material or any part of supplemental material shall be sent directly to the copyright owner as specified in the copyright notice associated with the article.

0.00 MB

0.15 MB