Alfred DeMaris - Regression with Social Data, Modeling Continuous and Limited Response Variables

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and female partner’s schooling (years of schooling completed), church attendance

(interval-level predictor ranging from 1 ⫽ “never” to 9 ⫽ “more than once a week”)

and income (in thousands of dollars). Recall the discussion of the authenticity of a

SLR of modernism in Chapter 2. There I suggested that the eﬀect of male’s school-

ing might be only an artifact of its association with female’s schooling. In that case,

male’s schooling might not have any independent eﬀect on modernism, and the rela-

tionship between these two variables would be spurious. In model 1 in Table 3.2 we

see that controlling for female’s schooling, male’s schooling still has a signiﬁcant

eﬀect on modernism, albeit substantially reduced compared to its eﬀect in the SLR

(see Table 2.3). However, we might now ask whether male’s schooling and female’s

schooling have equal eﬀects on couple modernism. In fact, we might wonder whether

there is any diﬀerence in the impact of males’ versus females’ schooling, church atten-

dance, or income on couple modernism.

The eﬀects in model 1 seem to suggest that there is. The eﬀect for female’s school-

ing is close to twice as large as the eﬀect for male’s schooling. Church attendance has

opposite eﬀects for males and females, although only male’s church attendance is sig-

niﬁcant. Similarly, male and female incomes have opposite eﬀects, with only female’s

income signiﬁcant. Nevertheless, sample coeﬃcients can be diﬀerent from each

other due entirely to sampling error, even were there no diﬀerence between males’ and

females’ eﬀects in the population. We can use a nested F test to test whether the impact

of males’ and females’ characteristics is the same. The parent model is model 1, which

can be represented in the population as

E(Y) ⫽ β

⫹ δ

⫹ γ

⫹ λ

, (3.3)

where Y is couple modernism, X

is male’s schooling, X

is female’s schooling, X

male’s church attendance, X

is female’s church attendance, X

is male’s income, and

is female’s income. The null hypothesis that we want to test is that the parameters

for males’ and females’ characteristics are equal. That is, we test H

: δ

⫽ δ

⫽ δ,

⫽ γ

⫽ γ, λ

⫽ λ

⫽ λ against H

: at least one pair of parameters is not equal. Under

the null hypotheses, the model becomes

E(Y) ⫽ β

⫹ δX

⫹ γX

⫹ λX

⫽ β

⫹ δ(X

⫹ X

) ⫹ γ(X

⫹ X

) ⫹ λ(X

⫹ X

). (3.4)

Notice that equation (3.4) is now nested inside equation (3.3) because of the

constraints in H

. There are three constraints being imposed here. The nature of each

constraint is that a given parameter is being set equal in value to another parameter.

Therefore, H

is tested by performing a nested F test to compare these two models.

Notice also that model (3.4) can be estimated by summing male and female scores

on each of the variables representing schooling, church attendance, and income, and

entering these three sums as the regressors in the model. These results are shown in

model 2 in Table 3.2. The coeﬃcient for the sum of male and female schooling,

.160, is shown as the common coeﬃcient for male and female schooling in the

EMPLOYING MULTIPLE PREDICTORS 95

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model. The other coeﬃcients are similarly portrayed. The test statistic for H

is then

F ⫽⫽8.153.

Under the null hypothesis, this statistic has the F distribution with 3 and 409 degrees

of freedom and a signiﬁcance level of p ⬍ .001. Apparently, we should reject H

and

conclude that at least one pair of coeﬃcients is not equal.

Testing Coefficient Differences. Diﬀerences between particular pairs of coeﬃcients

can be tested with individual t tests. The estimated diﬀerence between the jth and kth

coeﬃcients is b

⫺ b

. To ﬁnd the standard error of this diﬀerence, we ﬁrst ﬁnd its

variance. Using covariance algebra, we have

V(b

⫺ b

) ⫽ Cov(b

⫺ b

, b

⫺ b

)

⫽ Cov(b

) ⫺ Cov(b

) ⫹ Cov(b

)

⫽ V(b

) ⫹ V(b

) ⫺ 2Cov(b

). (3.5)

This variance can be estimated by requesting the variance–covariance matrix of param-

eter estimates as part of one’s regression output. The entries in this matrix make sense

if one considers the possibility of repeatedly taking random samples of the same size

(i.e., 416) from the population of intimate couples, running model 1 each time, and

recording the estimates from each run. The diagonal entries of the matrix represent the

estimated variances of the coeﬃcients across all of the samples, and the oﬀ-diagonal

entries represent the estimated covariances between each pair of coeﬃcients. The rele-

vant terms from this matrix can then be substituted into (3.5).

The bottom panel of Table 3.2 shows the relevant part of that matrix for testing

whether male and female schooling have equal eﬀects on couple modernism, based on

estimating model 1. The variance of the diﬀerence in coeﬃcients for male versus female

schooling is

v(d

⫺ d

) ⫽ .00199 ⫹ .00234 ⫺ 2(⫺.00104) ⫽ .006338.

The standard error is the square root of this quantity, .0796. The test statistic for the

equality of these coeﬃcients is then

t ⫽

ᎏ

.11

⫺

.211

ᎏ

⫽⫺1.269.

Under the null hypothesis that the coeﬃcients for schooling are equal, this statistic

has the t distribution with 409 degrees of freedom. With p ⬎ .1, we would fail to

reject the null hypothesis. Apparently, there is not enough evidence to conclude that

female schooling has a diﬀerent eﬀect on modernism than male schooling in the pop-

ulation of intimate couples. The other pairs of coeﬃcients in model 1 could be tested

in a similar fashion were we so inclined.

(473.121 ⫺ 348.285)/3

ᎏᎏᎏ

5.104

96 INTRODUCTION TO MULTIPLE REGRESSION

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Testing Coefficient Changes. Researchers are frequently interested in whether the

eﬀect of a given variable changes after other variables are held constant. For example,

let us return to the analyses in Table 3.1. We might hypothesize that in the population,

part of the impact of math diagnostic score on exam score is accounted for by the asso-

ciation of college GPA with both of these variables. We notice that the eﬀect of math

diagnostic score is indeed reduced when college GPA is added to the model for exam

score, which appears to support the hypothesis. But the observed coeﬃcient change in

the math diagnostic eﬀect across models might be due only to chance. The question is:

Is there a signiﬁcant reduction in the coeﬃcient for math diagnostic score when col-

lege GPA is added to the model? What is needed is a test for the diﬀerence in the eﬀect

of math diagnostic score between models 1 and 2. The testing approach is complicated

by the fact that the coeﬃcients in the initial model (model 1) are not independent of

the same coeﬃcients after variables have been added (Clogg et al., 1995).

The test proposed by Clogg et al. (1995), which accounts for the dependence

of the coeﬃcients, is as follows. We suppose that the baseline model with p param-

eters is

Y ⫽ α ⫹

冱

⫹ ε, (3.6)

whereas the full model with q added parameters is

Y ⫽ α ⫹

冱

⫹

冱

⫹ υ. (3.7)

Now, let δ

⫽ β

⫺ β

be the diﬀerence in the kth parameter after the additional

variables—the Z’s—have been added. The sample estimate of δ

is d

⫽ b

⫺ b

, the

diﬀerence between the corresponding sample coeﬃcients. We test H

: δ

⫽ 0 against

: δ

⫽ 0 using the test statistic

t ⫽

ᎏ

which is distributed as a t random variable with n ⫺ ( p ⫹ q) ⫺ 1 degrees of freedom

under H

. The estimated variance of d

⫽ s

⫺ s

ᎏ

␷

ᎏ

where s

is the sample variance of b

in model (3.7), s

is the sample variance of

in model (3.6), and the MSE’s from the models are used to estimate their respec-

tive error variances. The sample variance of the coeﬃcient for diagnostic score in

model 1 is .097455, while the sample variance for the same coeﬃcient in model 2 is

.081867. In the current case, then, we have σ

for math diagnostic score as

⫽ .081867 ⫺ .097455

冢

ᎏ

冣

⫽ .004.

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The standard error of the coeﬃcient diﬀerence is therefore .0632, and the test statistic is

t ⫽

ᎏ

2.74

⫺

.275

ᎏ

⫽ 7.5.

With 211 degrees of freedom, this result is highly signiﬁcant at p ⬍ .00001. We con-

clude that college GPA accounts for some of the eﬀect of math diagnostic score on

exam score. One ﬁnal comment about tests involving nested models is in order:

Models are nested only if the sample size remains the same in each model. If the n’s

change as variables are added or constraints are imposed, nesting no longer holds.

Omitted-Variable Bias

Earlier I alluded to the problem of omitted-variable bias. In this section I elaborate

on the problem. The estimate of a given coeﬃcient is biased whenever a regressor is

omitted from the model that is a determinant of Y and is also correlated with the pre-

dictor(s) of interest. The nature of the bias depends on both the correlation between

the included and omitted regressors and the eﬀect of the omitted regressor on the

response. Figure 3.6 presents models exhibiting three diﬀerent types of omitted-

variable bias, which I refer to as confounding, spuriousness, and mediation. Without

loss of generality, I assume that all variables have means of zero, obviating the need

for an equation intercept in any model. In each case the focus variable is X, the omit-

ted variable is Z, and the response is Y. Also, in each case the parameter that we are

trying to estimate without bias is β. I employ simple models involving only three

variables to avoid excessively tedious mathematics. In Chapter 6 I revisit this issue

with a more complex model. As scalar algebra becomes unwieldy with more than

three variables in the model, I employ matrix algebra for that explication.

Panel (a) of Figure 3.6 illustrates the confounding scenario, in which the eﬀect of

X on Y is confounded with Z. That is, part of X’s eﬀect on Y is realized via X’s con-

nection (correlation) with Z. In this case, we are unwilling to specify the nature of

the causal relationship between Z and X. Or, perhaps Z and X are not causally related

but simply correlated for reasons that remain unanalyzed. Hence, Z is depicted as

falling into the same causal sequence as X by my showing Z even with X in the

ﬁgure. The correlation between Z and X is symbolized by ρ, where

ρ ⫽

ᎏ

(

,Z)

ᎏ

which implies that Cov(X,Z) ⫽ ρσ

. The model depicted is the true model for X,

Y, and Z. Mathematically, it is Y ⫽ βX ⫹ γZ ⫹ ε, with Cov(X,ε) ⫽ Cov(Z,ε) ⫽ 0.

Instead, suppose that we estimate the model Y ⫽ βX ⫹ ε⬘, where ε⬘⫽γZ ⫹ ε is now

no longer uncorrelated with X, since X and Z are correlated. Thus, the orthogonality

condition no longer holds. What are the consequences? Recall from Chapter 2 that

the OLS estimate of b in this SLR can be written

b ⫽

ᎏ

cov(

,Y)

ᎏ

98 INTRODUCTION TO MULTIPLE REGRESSION

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Now we ask: What parameter is b consistent for? To answer this, we ﬁnd plim b:

plim b ⫽ plim

冢

ᎏ

cov(

,Y)

ᎏ

冣

⫽

ᎏ

plim

,Y))

ᎏ

(by the Slutsky theorem)

⫽

ᎏ

Cov

,Y)

ᎏ

EMPLOYING MULTIPLE PREDICTORS 99

(a) Confounding

(b) Spuriousness

Figure 3.6 Three-variable models exhibiting varieties of omitted-variable bias.

c03.qxd 8/27/2004 2:48 PM Page 99

(because the sample variance and covariance are consistent estimators of their respec-

tive population parameters)

⫽⫽

ᎏ

βσ

⫹ γ

ov(X,Z )

ᎏ

⫽ β ⫹

ᎏ

γρ

ᎏ

⫽ β ⫹ γρ

ᎏ

. (3.8)

This result shows that b is consistent for β ⫹ γρ(σ

/σ

) rather than β. The bias in the

estimation of β is the term γρ(σ

/σ

). The nature of the bias depends on β, the true

eﬀect of X on Y, γ, the nature of the impact of Z on Y, and ρ, the nature of the correla-

tion between X and Z. (Since σ

/σ

is always positive, it has no eﬀect on the direction

of the bias.) If the sign of the product γρ is the same as the sign of β, we will overes-

timate the magnitude of X’s impact on Y when Z is excluded from the model. But if γρ

is opposite in sign to β, the eﬀect of X is suppressed, or underestimated, when Z is

excluded. If γρ is opposite in sign to β and its magnitude is greater than β’s, the eﬀect

of X is reversed when Z is excluded. This last phenomenon is also known as Simpson’s

paradox (Agresti, 2002).

Panel (b) illustrates spuriousness, in which the eﬀect of X on Y is partially (or com-

pletely) spurious, due to Z. That is, part or all of X’s “eﬀect” on Y is due to the fact that

Z causes both X and Y. In that Z is causally prior to both X and Y, Z is pictured as the

leftmost variable in the diagram. Once again, the true model for Y is Y ⫽ βX ⫹ γZ ⫹ ε,

with Cov(X,ε)⫽ Cov(Z,ε) ⫽ Cov(Z,υ) ⫽ Cov(υ,ε) ⫽ 0. The model for X is X ⫽ λZ ⫹ υ.

As before, if we estimate the model Y ⫽ βX ⫹ ε⬘, where ε⬘⫽γZ ⫹ ε, we ﬁnd that ε⬘ is

no longer orthogonal to X, since X is correlated with Z by virtue of Z’s eﬀect on X.

Moreover, for the OLS estimate of β we have

b ⫽

ᎏ

cov(

,Y)

ᎏ

and by virtue of the same mathematics, plim b is, again,

β ⫹ γρ

ᎏ

and the remarks about the nature of the bias are the same as before. In this case, plim b

can be rewritten by taking advantage of a reexpression of ρ. Recall that in SLR, the

correlation coeﬃcient is the standardized slope, which equals the unstandardized

slope times the ratio of the standard deviation of X to the standard deviation of Y. In

panel (b), Z plays the role of X, while X plays the role of Y in this calculation. With λ

as the unstandardized slope, we have

ρ ⫽ λ

ᎏ

Cov(X,βX ⫹ γZ ⫹ ε)

ᎏᎏᎏ

100 INTRODUCTION TO MULTIPLE REGRESSION

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and therefore,

β ⫹ γρ

ᎏ

⫽ β ⫹ γ

冢

ᎏ

冣

ᎏ

⫽ β ⫹ γλ

ᎏ

Here it is evident that the bias in b as an estimate of β is a function of the eﬀect of

Z on X and the eﬀect of Z on Y.

Panel (c) illustrates mediation. We say that the impact of X on Y is mediated by Z if

Z is partly or completely the mechanism by which X’s eﬀect on Y is realized. In this

case, X causes Z, and Z, in turn, causes Y. Hence, Z is pictured as lying between X and

Y in the ﬁgure. As before, the true model for Y is Y ⫽ βX ⫹ γZ ⫹ ε, with Cov(X,ε) ⫽

Cov(Z,ε) ⫽ Cov(X,ω) ⫽ Cov(ω,ε) ⫽ 0. The model for Z is now Z ⫽ δX ⫹ ω. Suppose,

once again, that we estimate the model Y ⫽ βX ⫹ ε⬘, where ε⬘⫽γZ ⫹ ε. We ﬁnd that

ε⬘ is no longer orthogonal to X, since X is correlated with Z by virtue of X’s eﬀect on

Z. By virtue of the, by now, very familiar mathematics of consistency, plim b is, again,

β ⫹ γρ

ᎏ

Once again, plim b can be rewritten by taking advantage of a reexpression of ρ. In that

ρ ⫽ δ

ᎏ

we have that

β ⫹ γρ

ᎏ

⫽ β ⫹ γ

冢

ᎏ

冣

ᎏ

⫽ β ⫹ γδ.

This last expression suggests that the bias in b as an estimate of β is due to the prod-

uct of X’s eﬀect on Z with Z’s eﬀect on Y. In path analysis, this is called the indirect

eﬀect of X on Y via Z, while β itself is called the direct eﬀect of X on Y. The total

eﬀect of X on Y is the sum of direct and indirect eﬀects, or β⫹ γδ [see, e.g., Bollen

(1989) for a thorough discussion of path analysis]. From this perspective, mediation

is arguably not a form of bias, simply a conﬂation of the indirect and direct eﬀects

of one variable on another into one omnibus eﬀect.

Example: Deciphering Omitted-Variable Bias. Recall the positive association

between frequenting bars and having sex that was documented in Chapter 2. In the

discussion of model authenticity in that chapter I also suggested that this association

might be spurious, due to the fact that younger people go to bars more frequently and

are also more sexually active. Let me now expand that argument. I propose that part

of the reason for the positive association between frequenting bars and having sex is

due to three background factors that aﬀect both phenomena: age, religiosity, and

EMPLOYING MULTIPLE PREDICTORS 101

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health. That is, I suggest that younger people, those who are less religious, and those

in better health are more likely both to frequent bars and to have sex. To the extent

that this is the case, the relationship between frequenting bars and having sex is spu-

rious. However, if frequenting bars also exerts a causal inﬂuence on sexual activity,

as was the argument in Chapter 2, it should still have a signiﬁcant eﬀect on sexual

activity even net of these three background factors. Moreover, I made the argument

in Chapter 2 that one means by which frequenting bars might enhance sexual activity

is by widening one’s pool of potential sex partners. If this is the case, the number of

sex partners should mediate the remaining impact of frequenting bars on sexual activ-

ity. Figure 3.7 presents the conceptual model representing these hypothesized rela-

tionships. Notice that all of the compound “paths” of the form γλ (for spuriousness)

or γδ (for mediation) linking frequenting bars with having sex via age, religiosity,

health, or number of sex partners are positive. This suggests that the eﬀect of fre-

quenting bars should diminish once these other variables are controlled.

Table 3.3 presents three regression models for having sex, which allow us to evalu-

ate the model in Figure 3.7. The ﬁrst model is the SLR for having sex as a function of

frequenting bars, and is similar to the results in Table 2.4 except that all analyses in

Table 3.3 are based on 2,320 respondents. We see that the eﬀect of frequenting bars is

signiﬁcant and positive, with a value of .224. Model 2 adds age (in years), religiosity

(continuous predictor that is the sum of ﬁve standardized measures; higher scores indi-

cate those who are more religious), and self-assessed health (ranging from 1 ⫽ “poor”

to 4 ⫽ “excellent”). The eﬀect of frequenting bars, although still signiﬁcant, has been

reduced by a proportion of (.224 ⫺ .058)/.224 ⫽ .74, or about 74%, once the back-

ground factors are held constant. This suggests that about 74% of the “eﬀect” of fre-

quenting bars on having sex is noncausal and due to the antecedents of both variables.

Nevertheless, frequenting bars still has a nonzero eﬀect on having sex (the sample

coeﬃcient is .058). Model 3 adds the respondent’s number of sex partners in the past

102 INTRODUCTION TO MULTIPLE REGRESSION

Frequenting Bars

Age

Religiosity

Health

Having Sex

No. of Sex

Partners

−

Figure 3.7 Model for frequency of having sex showing potential spurious, mediated, and direct eﬀects

for frequenting bars.

c03.qxd 8/27/2004 2:48 PM Page 102

ﬁve years (censored count variable ranging from 0 ⫽ “no partners” to 8 ⫽ “more than

100 partners”) as a potential mediator of the impact of frequenting bars on having sex.

We see now that the eﬀect of frequenting bars is diminished to approximately zero

in this last model (the coeﬃcient is .001). This suggests that the remaining eﬀect of

frequenting bars on having sex may be causal, since it appears to be mediated or

“explained” by one’s number of sex partners, which was hypothesized to be enhanced

by frequenting bars.

At this point a word of caution is in order in regard to the model’s authenticity.

Although the causal priority of age, religiosity,and health over frequenting bars is a

reasonable assumption, it is not so clear that frequenting bars is causally prior to

number of sex partners. The diﬃculty is the retrospective time frame associated with

each variable. Frequenting bars was measured with the question “How often do you

go to a bar or tavern,” while number of sex partners refers to the last ﬁve years.

Temporally speaking, therefore, it could be argued that number of sex partners is prior

to frequenting bars. On the other hand, it is theoretically reasonable that frequenting

bars enhances one’s number of sex partners. But it is not particularly reasonable that

one’s number of sex partners should determine how often one goes to bars. In fact, if

anything, those with more sex partners might go to bars less often, since they already

have what many bar patrons are looking for. This would imply a negative relationship

between frequenting bars and number of sex partners, which is contrary to the results.

Since the positive eﬀect of frequenting bars is reduced when number of sex partners

is added, and since number of sex partners is positively related to having sex, the path

from frequenting bars to number of sex partners must be positive. At any rate, I argue,

based on these theoretical considerations, that frequenting bars is causally prior to

number of sex partners. Finally, to ascertain whether number of sex partners indeed

mediates the remaining eﬀect of frequenting bars on having sex, we must test whether

EMPLOYING MULTIPLE PREDICTORS 103

Table 3.3 Regression Models for Frequency of Having Sex for 2320 Respondents

from the General Social Survey

Model 1 Model 2 Model 3

Regressor bb

Intercept 2.270*** .000 3.984*** .000 3.225*** .000

Frequenting bars .224*** .157 .058* .042 .001 .001

Age ⫺.047*** ⫺.401 ⫺.038*** ⫺.326

Religiosity ⫺.009 ⫺.011 .008 .010

Self-assessed health .249*** .103 .265*** .110

No. partners in past .276*** .218

5 years

RSS 218.446 1815.340 2152.511

MSE 3.747 3.062 2.918

F 58.301*** 148.220*** 147.558***

.025 .204 .242

adj

.024 .203 .240

* p ⬍ .05. ** p ⬍ .01. *** p ⬍ .001.

c03.qxd 8/27/2004 2:48 PM Page 103

the reduction in the impact of frequenting bars from model 2 to model 3 is signiﬁcant.

Here, again, we draw on the test proposed by Clogg et al. (1995), which was intro-

duced earlier. As the result is highly signiﬁcant (t ⫽ 10.76; p ⬍ .00001), I conclude

that part of the impact of frequenting bars on having sex is due to the inﬂuence of fre-

quenting bars on one’s pool of potential sex partners.

Modeling Interaction Eﬀects

Recall, in the analyses in Figures 3.3 to 3.5, that the slope of the regression of Y on

X was approximately the same at each level of Z. Therefore, it made sense to report

the “average” of these three slopes as the eﬀect of X on Y when holding Z constant.

But what if the eﬀect of X depends on the level of Z? In this case, it no longer makes

sense to speak of the impact of X controlling for Z, since there may be many diﬀerent

impacts of X depending on which level of Z is being considered. When the slope of

the regression of Y on X changes signiﬁcantly across levels of Z, we say that X and

Z interact in their eﬀects on Y. Or, we say that the impact of X on Y is moderated by

or conditioned on the level of Z, and Z is referred to as a moderator variable. In this

section of the chapter I discuss the modeling of interaction eﬀects. I also discuss a

related notion, the idea that the model as a whole might diﬀer across groups of cases.

Interaction Model. When X and Z interact in their eﬀects on Y, this is captured by

including a cross-product term—representing the product of X with Z—as an addi-

tional regressor in the model. The model is

E(Y) ⫽ β

⫹ β

X ⫹ β

Z ⫹ γXZ.

Since the partial slope of the regression with respect to X is the parameter that multi-

plies X in the model, let’s factor this equation to isolate the common multipliers of X:

E(Y) ⫽ β

⫹ β

Z ⫹ (β

⫹ γZ )X. (3.9)

Equation (3.9) shows how the cross-product term captures the interaction eﬀect: The

impact of X—its partial slope—is now a function of the level of Z. In fact, the partial

slope of X, denoted ps

, is a simple linear regression model of the form ps

⫽ β

⫹ γZ.

That is, ps

increases (if γ is positive) or decreases (if γ is negative) linearly with

increases in Z. Interaction eﬀects are symmetric. We could also factor the equation so

as to isolate the common multipliers of Z. We would then ﬁnd that the partial slope

for Z is β

⫹ γX. In other words, the impact of Z is a simple linear function of X, too.

This type of interaction eﬀect, in which the eﬀect of X (Z ) varies in a simple linear

fashion with the level of Z (X), is the one most commonly modeled. However, non-

linear interaction eﬀects can also be modeled, as demonstrated in Chapter 5.

The interaction eﬀect modeled in equation (3.9) is called a ﬁrst-order interaction

eﬀect. This means that the eﬀect of X varies only according to the values of one other

variable. If the eﬀect of X varies according to the combination of values of two other

variables, we have a second-order interaction eﬀect, which is much more complicated.

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