23 Moderated Mediation and Conditional Process Analysis
The previous chapter treated moderation on its own: the effect of \(X\) on \(Y\) depends on a third variable \(W\). The next chapter treats mediation on its own: the effect of \(X\) on \(Y\) runs through an intermediate variable \(M\). Applied work almost never stays in either pure case. The question a manager, a regulator, or a referee actually asks is whether the mechanism itself differs across people, markets, or conditions. Does the advertising campaign raise sales through brand awareness for new customers but through price salience for repeat customers? Does a job training program work through skill acquisition in tight labor markets and through job search intensity in slack ones? Does an anxiety appeal shift immigration attitudes through emotion among the young and through something else among the old?
These are questions about a mechanism that is contingent. The statistical literature calls the corresponding model moderated mediation, and the family of models that combine mediating and moderating paths in a single system is called conditional process analysis (Hayes and Rockwood 2020). A closely related and much older term, mediated moderation, describes what looks like a different question: whether an interaction effect is itself transmitted through a mediator. Section 23.2 shows that under the standard linear specification the two questions are algebraically the same question asked from different ends, which is why the second term has largely fallen out of careful use.
This chapter does four things. It sets up the general conditional process model and derives the conditional indirect effect and the index of moderated mediation. It shows why probing a mechanism at conventional values of the moderator is not a test of moderated mediation, and quantifies how badly the common substitute fails. It gives the counterfactual reading of the whole apparatus, including the result that moderated mediation is identified under weaker confounding assumptions than mediation itself. And it works the whole machinery through a replication of a canonical framing experiment, with an extension to machine learning estimates of mechanism heterogeneity and an honest accounting of the sample sizes these questions require.
Readers should have the moderation chapter and the mediation chapter in hand. The identification vocabulary of controlled, natural, and interventional direct and indirect effects is developed in the mediation chapter and used freely here.
23.1 The General Conditional Process Model
Let \(X\) be the focal predictor or treatment, \(M\) a single mediator, \(Y\) the outcome, and \(W\) a moderator measured before \(X\). Write \(C\) for a vector of covariates. The general linear conditional process model allows \(W\) to enter every structural path:
\[ M = a_0 + a_1 X + a_2 W + a_3 XW + \boldsymbol{a}_c' C + \varepsilon_M, \]
\[ Y = c_0 + c_1' X + c_2' W + c_3' XW + b_1 M + b_2 MW + \boldsymbol{c}_c' C + \varepsilon_Y . \]
Three coefficients carry the contingency. The term \(a_3\) moderates the first stage, the path from treatment to mediator. The term \(b_2\) moderates the second stage, the path from mediator to outcome. The term \(c_3'\) moderates the direct path that bypasses \(M\) altogether. Setting all three to zero recovers ordinary mediation; setting \(b_1 = b_2 = 0\) recovers ordinary moderation.
Substituting the mediator equation into the outcome equation and collecting terms in \(X\) gives the quantity of interest. The conditional indirect effect of \(X\) on \(Y\) through \(M\) at moderator value \(W = w\) is the product of the two conditional path coefficients,
\[ \theta(w) \;=\; \underbrace{(a_1 + a_3 w)}_{\text{conditional } a\text{-path}} \times \underbrace{(b_1 + b_2 w)}_{\text{conditional } b\text{-path}}, \]
and the conditional direct effect is \(c_1' + c_3' w\). Their sum is the conditional total effect. The decomposition holds pointwise in \(w\): at every value of the moderator, the total effect splits into a part that runs through the mediator and a part that does not, exactly as in ordinary mediation, but with both parts now functions of \(w\).
That expression already contains the chapter’s first substantive lesson. The conditional indirect effect is a product of two linear functions of \(w\), which is quadratic in \(w\) whenever both stages are moderated. It is linear in \(w\) only in the two special cases where exactly one stage is moderated:
\[ \theta(w) = \begin{cases} (a_1 + a_3 w)\, b_1 & \text{first stage only } (b_2 = 0), \\[4pt] a_1 (b_1 + b_2 w) & \text{second stage only } (a_3 = 0), \\[4pt] (a_1 + a_3 w)(b_1 + b_2 w) & \text{both stages}. \end{cases} \]
In the first two cases the derivative \(\partial \theta / \partial w\) is a constant, and Hayes (2015) calls that constant the index of moderated mediation:
\[ \text{index} = \frac{\partial \theta(w)}{\partial w} = \begin{cases} a_3 b_1 & \text{first stage only},\\ a_1 b_2 & \text{second stage only}.\end{cases} \]
A test of \(\text{index} = 0\) is a test of the hypothesis that the mechanism is invariant to the moderator, and it is the correct single test of moderated mediation in the linear model. In the both-stages case there is no single index, because \(\partial \theta / \partial w = a_3 b_1 + a_1 b_2 + 2 a_3 b_2 w\) still depends on \(w\). Papers that report “the index of moderated mediation” from a model with both \(a_3\) and \(b_2\) free are reporting a quantity that does not describe the model they fit. The correct object there is the whole function \(\theta(\cdot)\) with a simultaneous confidence band, or a test of the joint null \(a_3 = b_2 = 0\).
23.1.1 Where the Moderator Can Sit
It helps to keep the possible configurations straight, because they answer genuinely different substantive questions and they are not equally credible.
| Configuration | Free parameter | Substantive claim | Identification burden |
|---|---|---|---|
| First stage | \(a_3\) | The treatment moves the mediator more for some units than others | Lightest. If \(X\) is randomized, \(a_3\) is a causal interaction |
| Second stage | \(b_2\) | A given change in the mediator translates into more outcome for some units | Heaviest. \(M\) is not randomized, so \(b_2\) mixes moderation with confounding |
| Direct path | \(c_3'\) | Whatever bypasses \(M\) is itself contingent | Light if \(X\) randomized, but \(c_3'\) is a controlled direct effect contrast |
| First and second | \(a_3, b_2\) | Both, and the conditional indirect effect is quadratic | Heaviest, and no single index exists |
The asymmetry in the last column is the reason a great deal of published conditional process analysis is weaker than it appears. Randomizing \(X\) buys a causal interpretation of \(a_1\) and \(a_3\) and of the total effect and its moderation. It buys nothing at all for \(b_1\) and \(b_2\), because no experiment assigned \(M\). A significant \(b_2\) is consistent with genuine second-stage moderation and equally consistent with a \(W\)-dependent pattern of mediator-outcome confounding, and nothing in the fitted model distinguishes them. Section 23.4 makes this precise.
23.2 Mediated Moderation, and Why the Term Is Retired
The older literature posed a question that sounds different. Suppose the interaction \(XW\) has an effect on \(Y\). Is that interaction effect transmitted through \(M\)? This is mediated moderation (Baron and Kenny 1986; Judd and Kenny 1981; Muller et al. 2005).
Formalize it in the obvious way. Fit a total-effect equation
\[ Y = \tilde c_0 + \tilde c_1 X + \tilde c_2 W + \tilde c_3 XW + \boldsymbol{\tilde c}_c' C + \varepsilon, \]
so \(\tilde c_3\) is the total interaction effect, and compare it with \(c_3'\) from the outcome equation above, the interaction effect that survives conditioning on \(M\). In the first-stage-only model (\(b_2 = 0\)), the algebra of ordinary mediation applies coefficient by coefficient, and
\[ \tilde c_3 - c_3' = a_3 b_1 . \]
The mediated part of the interaction effect is \(a_3 b_1\). That is exactly the index of moderated mediation defined above. The two literatures had been computing the same number and giving it two names (Preacher et al. 2007; Edwards and Lambert 2007).
Muller et al. (2005) is the paper that made the equivalence explicit and, in doing so, clarified what does distinguish the two framings. It is not the arithmetic; it is which quantity the analyst declares to be the causal agent. Moderated mediation treats \(X\) as the cause and asks whether its mechanism varies with \(w\). Mediated moderation treats the product \(XW\) as the cause and asks what channel it flows through. The second framing is difficult to sustain, because an interaction term is not a manipulable quantity: there is no intervention that sets \(XW\) to a value while leaving \(X\) and \(W\) alone. Preacher et al. (2007) recommend abandoning the term for exactly this reason, and modern treatments follow them (Hayes and Rockwood 2020).
Two practical consequences follow, and both are worth stating because they are the reason to care about a terminological dispute.
First, if your design randomizes \(X\) within levels of a naturally occurring \(W\), the causal agent is \(X\) and the correct framing is moderated mediation. Report \(\theta(w)\) and the index. Do not report \(\tilde c_3 - c_3'\) as though the interaction had been assigned.
Second, if your design is a genuine two-factor experiment in which both \(X\) and \(W\) are randomized, then the interaction is a legitimate causal contrast, because the factorial design assigns the cell. In that case the mediated-moderation question is well posed, and the identity \(\tilde c_3 - c_3' = a_3 b_1\) decomposes a causal interaction into a mediated and an unmediated part. This is the same structure that the factorial difference-in-differences section treats in a panel setting, and it is why factorial experiments are worth more than the sum of two single-factor experiments. Outside that case the framing does not survive contact with the potential-outcomes notation.
23.3 Probing Is Not Testing
The dominant reporting convention in applied conditional process analysis is to estimate the conditional indirect effect at a small number of moderator values, conventionally the mean and one standard deviation on either side, bootstrap a confidence interval at each, and declare moderated mediation when the intervals differ in whether they contain zero. Sometimes the values are chosen instead by the Johnson-Neyman procedure, which at least locates the boundary of significance rather than imposing three arbitrary points.
Neither convention is a test. The claim “the mechanism operates for the young but not for the old” is a claim about the difference between two conditional indirect effects, and the difference has its own sampling distribution. Two intervals that differ in whether they cover zero can easily be statistically indistinguishable from one another; this is the general point of Gelman and Stern (2006) applied to a mediation model. In the linear case the difference between \(\theta(w_1)\) and \(\theta(w_2)\) is \((w_1 - w_2)\) times the index, so testing the index is testing the difference, and reporting the index costs nothing.
The following simulation puts a number on how bad the substitute is. It constructs a world in which the indirect effect is genuinely identical in two groups, so the true index of moderated mediation is exactly zero, and the only difference between groups is sample size: 400 units in one, 100 in the other. This is the ordinary situation of a moderator with unbalanced categories, an experiment with an oversampled majority group, or a platform test where one segment simply has more traffic. It then applies both rules: the differential-significance rule, and the index test.
# True indirect effect is IDENTICAL in both groups; only n differs.
sim_one <- function(n1 = 400, n2 = 100, a = 0.35, b = 0.35) {
n <- n1 + n2
W <- c(rep(0, n1), rep(1, n2))
X <- rbinom(n, 1, 0.5)
M <- a * X + rnorm(n)
Y <- b * M + 0.2 * X + rnorm(n)
d <- data.frame(X, M, Y, W)
# Rule 1: probe within each group, compare significance (the common practice)
pv <- sapply(0:1, function(g) {
dg <- d[d$W == g, ]
am <- summary(lm(M ~ X, dg))$coef["X", ]
bm <- summary(lm(Y ~ M + X, dg))$coef["M", ]
z <- (am[1] * bm[1]) /
sqrt(am[1]^2 * bm[2]^2 + bm[1]^2 * am[2]^2) # Sobel
2 * pnorm(-abs(z))
})
# Rule 2: test the index of moderated mediation directly
mm <- lm(M ~ X * W, d)
mo <- lm(Y ~ M + X * W, d)
ix <- coef(mm)[["X:W"]] * coef(mo)[["M"]]
se <- abs(coef(mo)[["M"]]) * summary(mm)$coef["X:W", 2]
c(
differential_significance = as.numeric((pv[1] < 0.05) != (pv[2] < 0.05)),
index_test = as.numeric(abs(ix / se) > 1.96)
)
}
set.seed(11)
res <- t(replicate(1000, sim_one()))
round(colMeans(res), 3)
#> differential_significance index_test
#> 0.753 0.047The differential-significance rule declares moderated mediation in roughly three quarters of samples drawn from a world with no moderated mediation whatsoever. The index test rejects at close to its nominal five percent. The gap is not a subtle finite-sample distortion; it is the difference between a valid test and a procedure that mostly detects differences in group size. Any published claim of the form “the indirect effect was significant for group A (\(p < .05\)) but not for group B (\(p = .21\)), supporting moderated mediation” is, on this evidence, uninformative about the mechanism unless it is accompanied by a test of the difference.
The corrective is cheap. Report the index with a bootstrap or Monte Carlo confidence interval (Preacher and Selig 2012), report the conditional effects as description rather than as evidence, and report the component paths \(a_3\) and \(b_1\) separately so a reader can see which stage is driving the result (Yzerbyt et al. 2018).
23.4 The Counterfactual Reading
The regression algebra above is a description of a linear model, not of a causal quantity. Translating it requires the potential-outcomes notation from the mediation chapter. Write \(M_i(x)\) for the mediator that unit \(i\) would display under treatment \(x\), and \(Y_i(x, m)\) for the outcome under treatment \(x\) and mediator value \(m\). The natural indirect effect conditional on \(W = w\) is
\[ \mathrm{NIE}(w) \;=\; \mathbb{E}\big[\,Y_i(1, M_i(1)) - Y_i(1, M_i(0)) \;\big|\; W_i = w\,\big], \]
and moderated mediation is the statement that \(\mathrm{NIE}(w)\) is not constant in \(w\). In the linear model with no exposure-mediator interaction, \(\mathrm{NIE}(w) = \theta(w)\) as defined above, which is what licenses reading the regression output causally. Once an \(X \times M\) interaction is present in the outcome equation, the correspondence breaks, and the four-way decomposition of VanderWeele (2014) is the right frame: the total effect splits into a controlled direct effect, a reference interaction, a mediated interaction, and a pure indirect effect, and a moderator can shift any of the four. The mediation chapter develops that decomposition; here the point is only that “moderated mediation” in a model with exposure-mediator interaction is ambiguous until the analyst says which of the four components is supposed to be moderated.
23.4.1 Effect Modification Is Not Interaction
The single most useful conceptual distinction in this area is VanderWeele (2009)’s separation of interaction from effect modification. Interaction concerns two variables that are both, at least in principle, subject to intervention: the question is what happens when you set \(X = x\) and \(W = w\) jointly. Effect modification concerns a variable that merely stratifies the population: the question is whether the effect of \(X\) differs across strata defined by \(W\), with no claim that \(W\) could be set.
Nearly all applied moderated mediation is effect modification. Age, prior purchase history, baseline severity, firm size, and market concentration are not assigned. This has three implications that are routinely ignored.
Effect modification by \(W\) requires no assumption about confounding of \(W\) itself. If \(X\) is randomized, \(\mathrm{NIE}(w)\) is a well-defined conditional causal quantity for each \(w\), and comparing across \(w\) is a legitimate description of who the mechanism works for.
Effect modification does not license a policy statement about changing \(W\). “The mechanism is stronger for high-trust customers” does not imply “raising trust would strengthen the mechanism.” That second claim requires \(W\) to be manipulable and unconfounded, which is a separate design problem. Bansak (2021) gives the formal treatment of what can and cannot be recovered when the treatment is randomized and the moderator is not, and provides estimators for the causal moderation effect under explicit sensitivity assumptions.
Effect-modification estimates inherit whatever functional-form error the interaction specification carries. Blackwell and Olson (2022) show that the ordinary multiplicative interaction model is badly non-robust to misspecification of how the covariates enter, and propose estimating interactions with methods that model the covariate function flexibly. Combined with the finding of Hainmueller et al. (2019) that multiplicative interactions frequently rest on regions of the moderator with almost no common support, and Simonsohn (2024)’s demonstration that a spurious linear interaction is the generic consequence of an unmodeled nonlinear main effect, the practical upshot is that a moderated mediation result should be probed for functional form before it is interpreted. The binning versus generalized additive model debate in the moderation chapter is directly relevant, and its conclusions carry over unchanged to the \(a\)-path and \(b\)-path of a mediation model.
23.4.2 Moderated Mediation Needs Weaker Assumptions Than Mediation
There is a genuinely encouraging result in this literature, and it is not widely enough known. Mediation analysis requires the mediator-outcome relationship to be unconfounded, an assumption that is untestable and usually implausible. Loeys et al. (2016) show that assessing moderated mediation in linear models requires strictly fewer such assumptions than assessing mediation itself.
The intuition is a differencing argument. Suppose there is unmeasured confounding \(U\) of the mediator-outcome relationship, so the estimated \(b\)-path is biased by some amount \(\delta\). Then \(\hat\theta(w)\) is biased by \((a_1 + a_3 w)\delta\) at every \(w\). If the confounding bias \(\delta\) does not itself depend on \(w\), the difference \(\hat\theta(w_1) - \hat\theta(w_2) = (w_1 - w_2) a_3 (b_1 + \delta)\) is still contaminated through \(\delta\), but the sign and the presence of first-stage moderated mediation are governed by \(a_3\), which is identified from the randomized treatment alone. In the important special case where the analyst asks only whether the mechanism differs across levels of \(w\) rather than how large it is, the \(a_3\) coefficient carries the answer, and \(a_3\) is a randomized-treatment interaction requiring no mediator-outcome assumption at all.
This reverses the usual pecking order. A study that cannot credibly estimate an indirect effect may still be able to say something defensible about whether the treatment moves the candidate mediator differentially across groups. That is a weaker claim than “the mechanism is X,” but it is a claim the data can support, and it is exactly the kind of evidence Yzerbyt et al. (2018) argue should be reported alongside, rather than buried beneath, the product term.
The counterpart caution: none of this rescues second-stage moderation. A \(W\)-varying \(b\)-path is confounded by any \(W\)-varying mediator-outcome confounder, and there is no differencing trick that removes it. Coffman and Zhong (2012) develop marginal structural model estimators for mediation in the presence of both confounding and moderation, which is the principled route when second-stage moderation is genuinely the target; the mediation chapter develops the weighting machinery those estimators use.
23.5 Replication: Anxiety, Framing, and Immigration Attitudes
Brader et al. (2008) ran a survey experiment on a nationally representative sample of white American adults. Respondents read a news story about immigration whose tone (positive or negative) and whose pictured immigrant (European or Latino) were randomly varied. The paper’s argument is explicitly mechanistic: a negatively framed story featuring a Latino immigrant increases opposition to immigration because it induces anxiety, not merely because it conveys information. The design is the standard reference case for causal mediation analysis, and the data ship with the mediation package (Tingley et al. 2014).
The treatment treat is the negative-tone Latino-image condition. The mediator emo is self-reported anxiety on a scale from 3 to 12. Two outcomes are available: cong_mesg, a binary indicator of whether the respondent chose to send an anti-immigration message to Congress, and immigr, a four-point scale of support for restricting immigration. We use immigr for the closed-form work because a linear outcome makes the index of moderated mediation exactly the coefficient product derived above, and we return to the binary outcome when we use the design-based estimator.
The moderator is age. The substantive hypothesis is that emotional appeals about immigration work differently across generations, which is a first-stage claim: the same story should provoke more anxiety in some age groups than others.
library(mediation)
data("framing", package = "mediation")
fr <- transform(framing, age_c = age - mean(age))
c(n = nrow(fr), mean_age = round(mean(fr$age), 1),
min_age = min(fr$age), max_age = max(fr$age))
#> n mean_age min_age max_age
#> 265.0 47.8 18.0 85.023.5.1 The Conditional Process Model
Fit the mediator and outcome equations of the first-stage-moderated model, setting \(b_2 = 0\).
m_med <- lm(emo ~ treat * age_c + educ + gender + income, data = fr)
m_out <- lm(immigr ~ emo + treat * age_c + educ + gender + income, data = fr)
a1 <- coef(m_med)[["treat"]] # a-path at mean age
a3 <- coef(m_med)[["treat:age_c"]] # first-stage moderation
b1 <- coef(m_out)[["emo"]] # b-path
round(c(a1 = a1, a3 = a3, b1 = b1, index = a3 * b1), 4)
#> a1 a3 b1 index
#> 1.3319 -0.0118 0.1743 -0.0021The treatment raises anxiety by about 1.33 scale points at the average age of 48, and that effect declines by about 0.012 points per additional year of age. Each additional point of anxiety translates into about 0.174 scale points of additional restrictionism. The index of moderated mediation is the product of the second and third of those numbers.
23.5.2 Show and Tell: Conditional Effects Versus the Index
Now bootstrap all three quantities together, so the conditional indirect effects and the index come from the same resamples and can be compared honestly. Table 23.2 reports them.
boot_stat <- function(d) {
mm <- lm(emo ~ treat * age_c + educ + gender + income, data = d)
mo <- lm(immigr ~ emo + treat * age_c + educ + gender + income, data = d)
a1 <- coef(mm)[["treat"]]
a3 <- coef(mm)[["treat:age_c"]]
b1 <- coef(mo)[["emo"]]
ctr <- mean(framing$age)
c(index = a3 * b1,
theta_25 = (a1 + a3 * (25 - ctr)) * b1,
theta_65 = (a1 + a3 * (65 - ctr)) * b1,
difference = (a1 + a3 * (25 - ctr)) * b1 - (a1 + a3 * (65 - ctr)) * b1)
}
set.seed(3)
B <- 2000
bs <- t(replicate(B, boot_stat(fr[sample(nrow(fr), replace = TRUE), ])))
cpa_tab <- data.frame(
quantity = c("Index of moderated mediation (per year)",
"Conditional indirect effect at age 25",
"Conditional indirect effect at age 65",
"Difference, age 25 minus age 65"),
estimate = round(boot_stat(fr), 4),
lower = round(apply(bs, 2, quantile, 0.025), 4),
upper = round(apply(bs, 2, quantile, 0.975), 4),
row.names = NULL
)
knitr::kable(
cpa_tab,
col.names = c("Quantity", "Estimate", "2.5%", "97.5%"),
caption = paste("Percentile bootstrap (2000 resamples) of the conditional",
"indirect effect of the anxiety framing treatment on",
"restrictionist immigration attitudes, at two ages, together",
"with the index of moderated mediation. Both conditional",
"effects are individually distinguishable from zero; their",
"difference is not.")
)| Quantity | Estimate | 2.5% | 97.5% |
|---|---|---|---|
| Index of moderated mediation (per year) | -0.0021 | -0.0092 | 0.0062 |
| Conditional indirect effect at age 25 | 0.2789 | 0.0643 | 0.5022 |
| Conditional indirect effect at age 65 | 0.1967 | 0.0209 | 0.4085 |
| Difference, age 25 minus age 65 | 0.0821 | -0.2498 | 0.3679 |
This is the pattern the simulation in Section 23.3 warned about, appearing in real data. The mechanism is present at both ages: anxiety mediates the framing effect for the young and for the old, and both conditional intervals exclude zero. A paper that stopped at the two conditional effects, noted that the point estimate at 25 is larger than at 65, and concluded that the emotional mechanism is stronger among younger respondents would have made a claim the data do not support. The index interval covers zero comfortably, and so does the interval for the difference. The correct summary is that the framing effect runs through anxiety, and that this study cannot detect any variation in that mechanism with age.
Note also that the difference row and the index row carry the same information: the difference is exactly \(40 \times \text{index}\), because the moderator enters linearly. Reporting both is redundant, but reporting the difference makes the comparison the reader cares about explicit in the units they care about.
23.5.3 Both Stages Moderated
Freeing the second stage as well shows what happens to the index when the model no longer supports one.
m_out2 <- lm(immigr ~ emo * age_c + treat * age_c + educ + gender + income,
data = fr)
b1f <- coef(m_out2)[["emo"]]
b2f <- coef(m_out2)[["emo:age_c"]]
ctr <- mean(fr$age)
ages <- seq(20, 80, by = 10)
theta_quad <- (a1 + a3 * (ages - ctr)) * (b1f + b2f * (ages - ctr))
round(rbind(age = ages, conditional_indirect = theta_quad), 4)
#> [,1] [,2] [,3] [,4] [,5] [,6]
#> age 20.0000 30.0000 40.0000 50.0000 60.0000 70.0000
#> conditional_indirect 0.2431 0.2422 0.2387 0.2328 0.2244 0.2135
#> [,7]
#> age 80.0000
#> conditional_indirect 0.2001The conditional indirect effect is now a genuine quadratic in age, and \(\partial\theta/\partial w = a_3 b_1 + a_1 b_2 + 2 a_3 b_2 w\) varies over the range of the data. Empirically the curvature here is slight, because \(\hat b_2\) is close to zero, so the practical conclusion is unchanged. The structural point stands: in this specification there is no scalar index to report, and software that prints one is applying the first-stage formula to a model that has two moderated stages.
There is also an identification point. The second-stage coefficient \(b_2\) compares the outcome slope on anxiety across age groups, and anxiety was never assigned. Older and younger respondents who report the same anxiety level differ systematically in ways the model does not capture, so \(\hat b_2\) absorbs any age-varying mediator-outcome confounding. Even a large and precisely estimated \(\hat b_2\) would not by itself be evidence that the same emotional state translates into different attitudes at different ages.
23.5.4 The Design-Based Estimator
The closed-form index requires a linear outcome. For the binary outcome cong_mesg, the natural-effects definitions no longer reduce to a coefficient product, and the simulation-based estimator of Imai, Keele, and Tingley (2010) and Imai, Keele, and Yamamoto (2010a) is the appropriate tool. The mediate function estimates the average causal mediation effect at a fixed covariate profile, and test.modmed compares two profiles with a bootstrap test of the difference, which is the design-based analogue of the index test.
med_fit <- lm(emo ~ treat * age_c + educ + gender + income, data = fr)
out_fit <- glm(cong_mesg ~ emo + treat * age_c + educ + gender + income,
data = fr, family = binomial("probit"))
set.seed(1)
ctr <- mean(fr$age)
m_young <- mediate(med_fit, out_fit, treat = "treat", mediator = "emo",
covariates = list(age_c = 25 - ctr), sims = 500)
m_old <- mediate(med_fit, out_fit, treat = "treat", mediator = "emo",
covariates = list(age_c = 65 - ctr), sims = 500)
rbind(
`age 25` = c(ACME = m_young$d.avg, m_young$d.avg.ci),
`age 65` = c(ACME = m_old$d.avg, m_old$d.avg.ci)
) |> round(4)
#> ACME 2.5% 97.5%
#> age 25 0.098 0.0258 0.1941
#> age 65 0.069 0.0016 0.1367
m_init <- mediate(med_fit, out_fit, treat = "treat", mediator = "emo", sims = 2)
set.seed(2)
test.modmed(m_init,
covariates.1 = list(age_c = 25 - ctr),
covariates.2 = list(age_c = 65 - ctr),
sims = 500)
#>
#> Test of ACME(covariates.1) - ACME(covariates.2) = 0
#>
#> data: estimates from m_init
#> ACME(covariates.1) - ACME(covariates.2) = 0.039914, p-value =
#> 0.464
#> alternative hypothesis: true ACME(covariates.1) - ACME(covariates.2) is not equal to 0
#> 95 percent confidence interval:
#> -0.07900765 0.13862892
#>
#>
#> Test of ADE(covariates.1) - ADE(covariates.2) = 0
#>
#> data: estimates from m_init
#> ADE(covariates.1) - ADE(covariates.2) = 0.28242, p-value =
#> 0.016
#> alternative hypothesis: true ADE(covariates.1) - ADE(covariates.2) is not equal to 0
#> 95 percent confidence interval:
#> 0.04637466 0.51988273The binary-outcome analysis reproduces the linear one and adds something to it. Both conditional mediation effects are positive and individually significant. The test of their difference does not reject: the mechanism does not measurably vary with age. The direct effect, however, does differ across ages, and that difference is significant. Substantively this says that whatever the framing treatment does to congressional-message behavior that does not run through anxiety is age-dependent, while the anxiety channel itself is not. That is a sharper and more interesting finding than “the effect is moderated by age,” and it is invisible to any analysis that reports only the indirect effect.
23.6 Extension: Machine Learning Estimates of Mechanism Heterogeneity
The conditional process model imposes a functional form. It says the mechanism varies linearly in one pre-specified moderator. Two problems follow. The moderator has to be chosen in advance, which invites specification search across the covariates until one interaction is significant. And the linear form is a strong restriction, precisely the restriction that Hainmueller et al. (2019) and Simonsohn (2024) show to be unreliable.
The heterogeneous-treatment-effect machinery from the machine learning for causal inference chapter addresses both. Because the treatment is randomized, the conditional average treatment effect of the framing manipulation on the mediator is nonparametrically identified. This is the \(a\)-path, estimated without assuming a moderator, a functional form, or even that the heterogeneity is one-dimensional.
library(grf)
Xm <- model.matrix(~ age + educ + gender + income - 1, data = fr)
set.seed(5)
cf_a <- causal_forest(Xm, Y = fr$emo, W = fr$treat, num.trees = 2000)
cf_t <- causal_forest(Xm, Y = fr$immigr, W = fr$treat, num.trees = 2000)
cal <- rbind(
`a-path (treatment on anxiety)` = test_calibration(cf_a)[2, ],
`total (treatment on attitudes)` = test_calibration(cf_t)[2, ]
)
round(cal, 3)
#> Estimate Std. Error t value Pr(>t)
#> a-path (treatment on anxiety) -8.693 2.194 -3.963 1
#> total (treatment on attitudes) -24.802 3.448 -7.193 1The differential.forest.prediction coefficient tests whether the forest’s estimated heterogeneity has any out-of-sample predictive content. A coefficient near one with a small \(p\)-value indicates real, well-calibrated heterogeneity. Here both coefficients are negative with \(p\)-values at the wrong end of the scale, which is the signature of no detectable heterogeneity: the forest’s ranking of units by estimated effect does not survive cross-fitting. The nonparametric answer agrees with the parametric one, and it does so without having been told to look at age.
Two cautions are essential before this becomes a general recipe.
The forest identifies heterogeneity in the \(a\)-path because the treatment was randomized. It cannot identify heterogeneity in the \(b\)-path, because the mediator was not. A forest fit with the mediator as the treatment variable would estimate a conditional association, not a conditional effect, no matter how flexible the estimator. Flexibility does not substitute for identification.
The product of a nonparametric \(a\)-path CATE and a \(b\)-path coefficient is not a nonparametric indirect effect. Recovering conditional natural indirect effects with machine learning requires the orthogonal score functions of Farbmacher et al. (2022), which the mediation chapter develops. What the forest delivers here is a valid, assumption-light screen for whether mechanism heterogeneity is present at all, which is exactly the question that should be asked before a conditional process model is fit.
23.7 How Much Data This Requires
The null results above are not a failure of the analysis. They are what a sample of 265 respondents can be expected to deliver, and the point is worth quantifying, because the mismatch between the sample sizes that support moderated mediation claims and the sample sizes that appear in published papers is large.
An interaction is estimated from variation in a product term, and its standard error is inflated relative to a main effect. Sommet et al. (2023) work through the arithmetic and its consequences for design; the rough rule is that detecting an interaction of half the size of a main effect requires roughly sixteen times the sample. Moderated mediation compounds this, because the index is a product of an interaction coefficient and a path coefficient, and the product inherits both sources of noise.
power_cpa <- function(n, a1 = 0.4, a3 = 0.2, b = 0.4, R = 600) {
hits <- replicate(R, {
W <- rnorm(n)
X <- rbinom(n, 1, 0.5)
M <- a1 * X + a3 * X * W + 0.2 * W + rnorm(n)
Y <- b * M + 0.2 * X + 0.1 * W + rnorm(n)
sm <- summary(lm(M ~ X * W))$coef
so <- summary(lm(Y ~ M + X * W))$coef
ie <- sm["X", 1] * so["M", 1]
se_ie <- sqrt(sm["X", 1]^2 * so["M", 2]^2 + so["M", 1]^2 * sm["X", 2]^2)
ix <- sm["X:W", 1] * so["M", 1]
se_ix <- sqrt(sm["X:W", 1]^2 * so["M", 2]^2 + so["M", 1]^2 * sm["X:W", 2]^2)
c(abs(ie / se_ie) > 1.96, abs(ix / se_ix) > 1.96)
})
rowMeans(hits)
}
set.seed(7)
grid <- c(100, 200, 400, 800, 1600, 3200)
pw <- t(sapply(grid, power_cpa))
knitr::kable(
data.frame(n = grid,
indirect = round(pw[, 1], 2),
index = round(pw[, 2], 2)),
col.names = c("n", "Power: indirect effect", "Power: index"),
caption = paste("Simulated power to detect an indirect effect and to detect",
"moderated mediation, when the first-stage interaction is",
"half the size of the first-stage main effect. Reaching 80",
"percent power for the index takes roughly four times the",
"sample that suffices for the indirect effect.")
)| n | Power: indirect effect | Power: index |
|---|---|---|
| 100 | 0.32 | 0.09 |
| 200 | 0.72 | 0.23 |
| 400 | 0.98 | 0.54 |
| 800 | 1.00 | 0.78 |
| 1600 | 1.00 | 0.98 |
| 3200 | 1.00 | 1.00 |
In Table 23.3 a study with 200 observations has good power for the indirect effect and almost none for the index. This is why the literature is full of papers that establish a mechanism convincingly and then make an underpowered claim about whose mechanism it is. It is also why the differential-significance rule is so attractive and so damaging: it converts an underpowered comparison into an apparently decisive one at no cost in sample size.
Three design responses follow. Power the study for the index rather than the effect, which usually means a materially larger sample than the mediation analysis alone would require. Choose the moderator on theory and pre-register it, since the effective multiplicity across candidate moderators is otherwise unbounded (Rohrer et al. 2022). And when the sample cannot support the interaction, report the conditional effects descriptively and say so, rather than converting a null difference into a positive claim.
23.8 Design-First Moderated Mediation: An Industry Application
The replication above is a laboratory experiment, where the treatment is randomized and the mediator is measured. Most industry and strategy questions do not come that way. The treatment is a firm decision, adopted at different times by different firms, and the mechanism is an operational variable that nobody randomized. The temptation is to fit the conditional process model directly on observational data and report the index. That inherits every confounding problem the chapter has warned about, all at once.
The disciplined alternative is to establish the total effect with a credible design first, and only then decompose it. Singh et al. (2026) is a good template for how that reads in a top journal.
The substantive setting is open-source product development. Studying 977 United States high technology firms from 2001 to 2025, the paper reports that adopting open-source product development raised gross margins by 4 to 5 percent on average. The conditional process structure is:
| Role | Variable |
|---|---|
| Treatment | Adoption of open-source product development on GitHub |
| Outcome | Gross margin |
| Mediator | Labor productivity |
| Moderator | Share of work supplied by external contributors |
| Moderator location | First stage, treatment to mediator |
The reported mechanism is knowledge integration: firms absorb the diverse knowledge of outside contributors into internal workflows, which broadens the organizational knowledge base without a matching rise in labor costs. The mediator is therefore labor productivity, measured in the tradition of Brynjolfsson and Hitt (2003).
The finding that makes it a moderated mediation rather than a mediation is the threshold. The payoff appears only when outside volunteers supply a meaningful share of the work, around 35 percent in this sample. Below that share the indirect path is not operative. This is first-stage moderation, which Section 23.4 identified as the credible case: the moderator conditions the path from treatment to mediator, and a design that identifies the treatment effect also identifies how that effect varies.
23.8.1 What Makes the Design Credible
Three features are worth copying.
The causal design is separate from, and prior to, the mediation model. Firms adopt open source at different times, which is a staggered adoption setting, and the paper draws on the staggered difference in differences literature covered in this book, including Callaway and Sant’Anna (2021) for group-time effects and the intertemporal estimators that handle heterogeneous timing, together with the generalized synthetic control approach of Xu (2017) and dynamic panel estimation in the tradition of Blundell and Bond (1998). The point is not that any one of these is decisive. It is that the total effect survives estimators with different failure modes before any decomposition is attempted.
The mediator is constructed, not assumed. More than 323,000 project level contributions across more than 44,000 repositories are decomposed into internal employee and external volunteer sources. The moderator is not a survey scale, it is a measured share of observed work. When the moderator is built from the same granular data as the treatment, the threshold has a concrete meaning.
The claim is bounded by the design. Identifying the total effect does not identify the indirect effect. No staggered adoption design randomizes labor productivity, so the mediator to outcome path still rests on a sequential ignorability assumption of the kind Section 23.4 sets out, and the honest reading is that the decomposition is conditional on that assumption while the total effect is not. A paper that says so is more credible than one that reports an index with three stars and no such sentence.
23.8.2 The Template
For a mechanism claim in an observational industry setting:
- Identify and defend the total effect with a design, and show it under at least two estimators with different assumptions.
- Build the mediator and the moderator from data granular enough that the threshold means something.
- Fit the conditional process model, and test the index of moderated mediation rather than probing at conventional values.
- State which parts of the decomposition are design based and which rest on selection on observables.
- Report the magnitude, not only the sign and the significance, and see Section 28.3.8 on what share of outcome variation the mechanism actually accounts for.
23.9 Configurational Analysis and Equifinality
Singh et al. (2026) adds a second analysis that does not fit the regression framework at all: the payoff depends on the firm’s resource configuration, there are multiple pathways to high profitability, and sustained internal research and development is a core condition present in all of them.
That sentence contains three claims a moderated mediation model cannot express. Multiple pathways is equifinality: different combinations of conditions reach the same outcome. A core condition present in all configurations is a near necessity claim, not an average marginal effect. And configurations are conjunctural: conditions work in combination, not additively.
Configurational analysis, usually fuzzy set qualitative comparative analysis, is the set-theoretic method built for these claims. Ragin (2008) is the foundational treatment, Fiss (2011) brought it into organizational research, and Misangyi et al. (2017) reviews the modern practice.
23.9.1 How It Differs From Interaction Terms
The distinction is not cosmetic.
| Regression with interactions | Configurational analysis | |
|---|---|---|
| Question | What is the average marginal effect of \(X\), possibly varying with \(M\)? | Which combinations of conditions are sufficient for a high outcome? |
| Causal form | Net effects, additive with product terms | Conjunctural, combinations as units |
| Multiple paths | One functional form for all units | Equifinality is native |
| Symmetry | Conditions for high \(Y\) are the mirror of conditions for low \(Y\) | Asymmetric, the two are analyzed separately |
| Output | Coefficients and intervals | Solutions with consistency and coverage |
The symmetry point is the one applied readers most often miss. In a linear model, whatever raises the outcome lowers it when reversed, by construction. In a set-theoretic analysis the conditions sufficient for high profitability and the conditions sufficient for low profitability are separate analyses that routinely produce non-mirrored answers.
23.9.2 The Machinery
Three ideas carry the method.
Calibration turns a raw variable into degree of membership in a set, on a zero to one scale, using three substantive anchors: full membership, the crossover point of maximum ambiguity, and full non-membership. Calibration is a theoretical act, not a statistical one, and it is where most of the researcher degrees of freedom live.
Consistency measures how close a configuration comes to being a subset of the outcome, which is the set-theoretic expression of sufficiency. For configuration membership \(c_i\) and outcome membership \(y_i\),
\[\text{Consistency} = \frac{\sum_i \min(c_i, y_i)}{\sum_i c_i}.\]
Coverage measures how much of the outcome a configuration accounts for, which is the set-theoretic analogue of empirical importance:
\[\text{Coverage} = \frac{\sum_i \min(c_i, y_i)}{\sum_i y_i}.\]
Necessity reverses the containment: a condition is necessary if the outcome is a subset of it, so the same ratio is taken over \(\sum_i y_i\) instead.
23.9.3 A Worked Configurational Analysis
The following implements calibration, necessity, and a truth table from scratch, so that every quantity is visible. The data are simulated to match the structure reported in Singh et al. (2026): research and development intensity is required, and it pays off either through external contributors or through scale.
# Direct calibration into fuzzy set membership, anchored at
# full non-membership, the crossover point, and full membership.
calibrate_fuzzy <- function(x, full_out, crossover, full_in) {
dev <- x - crossover
scale_up <- log(0.95 / 0.05) / (full_in - crossover)
scale_dn <- log(0.95 / 0.05) / (crossover - full_out)
z <- ifelse(dev >= 0, dev * scale_up, dev * scale_dn)
1 / (1 + exp(-z))
}
# Consistency and coverage of each condition as a necessary condition.
necessity <- function(conditions, outcome) {
data.frame(
condition = colnames(conditions),
consistency = apply(conditions, 2, function(x) sum(pmin(x, outcome)) / sum(outcome)),
coverage = apply(conditions, 2, function(x) sum(pmin(x, outcome)) / sum(x)),
row.names = NULL
)
}
# Truth table: every corner of the property space, with the consistency
# and coverage of that configuration as a sufficient condition.
truth_table <- function(conditions, outcome, freq_cutoff = 10, cons_cutoff = 0.80) {
k <- ncol(conditions)
nm <- colnames(conditions)
corners <- expand.grid(rep(list(c(0, 1)), k))
colnames(corners) <- nm
rows <- lapply(seq_len(nrow(corners)), function(r) {
bits <- as.numeric(corners[r, ])
# Membership in a corner is the minimum over conditions, negating
# those the corner sets to zero.
memb <- do.call(pmin, lapply(seq_len(k), function(j) {
if (bits[j] == 1) conditions[, j] else 1 - conditions[, j]
}))
data.frame(
as.list(setNames(bits, nm)),
n = sum(memb > 0.5),
consistency = sum(pmin(memb, outcome)) / sum(memb),
coverage = sum(pmin(memb, outcome)) / sum(outcome)
)
})
tt <- do.call(rbind, rows)
tt$sufficient <- as.integer(tt$n >= freq_cutoff & tt$consistency >= cons_cutoff)
tt[order(-tt$consistency), ]
}
set.seed(11)
n <- 500
rnd <- rgamma(n, 2.2, 0.4) # R&D intensity
ext <- runif(n, 0, 70) # external contributor share, percent
size <- rlnorm(n, 6, 1.1) # firm scale
oss <- rbinom(n, 1, 0.5) # open-source adoption
# Two equifinal paths to a high gross margin, both requiring R&D.
hi_rnd <- rnd > 5
hi_ext <- ext > 35 & oss == 1
hi_size <- size > 500
margin <- 18 + 12 * (hi_rnd & hi_ext) + 12 * (hi_rnd & hi_size) + rnorm(n, 0, 2)
cond <- data.frame(
RND = calibrate_fuzzy(rnd, full_out = 3.5, crossover = 5, full_in = 7),
EXT = calibrate_fuzzy(ext * oss, full_out = 25, crossover = 35, full_in = 45),
SIZE = calibrate_fuzzy(size, full_out = 400, crossover = 500, full_in = 640)
)
y_high <- calibrate_fuzzy(margin, full_out = 22, crossover = 25, full_in = 29)Necessity comes first, because a condition that is necessary will appear in every sufficient configuration and should be interpreted as such rather than as one path among many.
nec <- necessity(cond, y_high)
nec[, 2:3] <- round(nec[, 2:3], 3)
nec
#> condition consistency coverage
#> 1 RND 0.913 0.518
#> 2 EXT 0.446 0.444
#> 3 SIZE 0.717 0.411Research and development intensity has a necessity consistency of about 0.91, which is the conventional territory for a near necessary condition. External contribution and scale are nowhere close, so neither is necessary on its own.
tt_high <- truth_table(cond, y_high, freq_cutoff = 10, cons_cutoff = 0.80)
print(round(tt_high, 3), row.names = FALSE)
#> RND EXT SIZE n consistency coverage sufficient
#> 1 1 1 27 0.867 0.195 1
#> 1 1 0 37 0.823 0.236 1
#> 1 0 1 70 0.803 0.473 1
#> 0 1 1 30 0.133 0.034 0
#> 0 0 1 97 0.102 0.079 0
#> 1 0 0 93 0.088 0.067 0
#> 0 1 0 39 0.081 0.026 0
#> 0 0 0 107 0.032 0.029 0Three configurations clear the consistency threshold, and research and development is present in all three. Two substantively distinct paths emerge. High research and development combined with a high external contributor share is sufficient whether or not the firm is large. High research and development combined with scale is sufficient without external contributors, and it has the largest coverage, at about 0.47, meaning it accounts for the largest share of high margin firms.
That is equifinality stated precisely: there is no single path, but there is a common core.
Now the asymmetry. If the method were merely a re-encoding of a regression, the conditions for a low margin would be the negation of the conditions for a high margin.
tt_low <- truth_table(cond, 1 - y_high, freq_cutoff = 10, cons_cutoff = 0.80)
print(round(tt_low, 3), row.names = FALSE)
#> RND EXT SIZE n consistency coverage sufficient
#> 0 0 0 107 0.984 0.303 1
#> 0 1 0 39 0.953 0.105 1
#> 1 0 0 93 0.940 0.246 1
#> 0 0 1 97 0.928 0.248 1
#> 0 1 1 30 0.880 0.078 1
#> 1 0 1 70 0.243 0.049 0
#> 1 1 0 37 0.237 0.023 0
#> 1 1 1 27 0.165 0.013 0They are not. Five configurations are sufficient for a low margin, and one of them has high research and development. Investing in research and development without either an external contributor community or scale is sufficient for a low margin, with a consistency of about 0.94. The core condition for success is not protective on its own. A linear model with interaction terms cannot represent that, because it forces the low outcome analysis to be the arithmetic negative of the high outcome analysis.
23.9.4 What Configurational Analysis Does Not Give You
It is not a causal identification strategy. Consistency and coverage are descriptions of set relations in the observed data, and they inherit every confounding problem present in the sample. A configuration that is consistently associated with high profitability is not thereby shown to cause it. This is why the structure in Singh et al. (2026) is the right one: a design based estimate of the total effect carries the causal claim, and the configurational analysis characterizes heterogeneity in who benefits.
It has substantial researcher degrees of freedom. The calibration anchors, the frequency cutoff, and the consistency cutoff are all choices, and the solution can change with them. Note that in the truth table above, the third configuration sits at 0.803 against a cutoff of 0.80. Report the sensitivity of the solution to these choices in the same spirit as the specification curve analysis in Section ??.
It does not produce a standard error. There is no sampling theory attached to the solution in standard practice, so a configurational result is evidence about pattern, not a hypothesis test.
23.9.5 Choosing Between Them
Use moderated mediation when the theory is about a mechanism whose strength varies, when a single functional form is plausible, and when you can defend the moderator’s placement in the causal chain. Use configurational analysis when the theory is about combinations, when you expect several routes to the same outcome, and when you suspect the conditions for success differ in kind from the conditions for failure. The two answer different questions, and Singh et al. (2026) reports both because the substantive claim requires both: a mechanism that operates above a threshold, and a set of resource configurations in which the mechanism can operate at all.
23.10 Practice
Applied conditional process analysis has accumulated a set of habits that survive mainly because software makes them easy. Rohrer et al. (2022) catalogue the main ones, and the following consolidates them into what a defensible report contains.
State the causal target before fitting. Is the claim about effect modification, meaning who the mechanism works for, or about interaction, meaning what happens when two things are set jointly? Only the second requires both variables to be manipulable, and only a factorial design delivers it.
Report the component paths. Yzerbyt et al. (2018) show that the product term alone hides which stage carries the result, and that a significant product with an insignificant \(a\)-path is a different empirical situation from a significant product with an insignificant \(b\)-path. Report \(\hat a_1\), \(\hat a_3\), \(\hat b_1\), and \(\hat b_2\) with their standard errors, not just \(\hat\theta(w)\).
Test the index, not the significance pattern. Bootstrap or Monte Carlo the index and report its interval (Hayes 2015; Preacher and Selig 2012). If both stages are moderated, report the conditional-effect function with a simultaneous band and do not report an index.
Say what identifies the \(b\)-path. The mediator was not randomized in almost every applied study. State the mediator-outcome confounding assumption in words, and run a sensitivity analysis for it; the mediation chapter develops both the Imai, Keele, and Yamamoto (2010a) correlation-based approach and the E-value.
Check functional form before interpreting. Apply the diagnostics of Hainmueller et al. (2019) and the nonlinear alternatives discussed in the moderation chapter to both the \(a\)-path and the direct path. An interaction that disappears under a flexible main-effect specification was a functional-form artifact.
Do not claim policy leverage over a non-manipulable moderator. “The mechanism is stronger among high-trust customers” is a targeting statement, not an intervention statement.
23.10.1 Where This Shows Up in Practice
The industrial value of a conditional process model is almost always targeting rather than explanation, and framing it that way improves both the analysis and its reception.
In marketing, the recurring question is which creative works through which channel for which segment. A brand campaign may raise purchase intent through awareness for category entrants and through reassurance for lapsed buyers. Getting this right determines media allocation, and the honest version of the analysis is a first-stage moderated mediation: the campaign is randomized, so the differential effect on the awareness measure across segments is identified, while the awareness-to-purchase slope is not. The uplift modeling chapter treats the targeting problem directly, and the conditional process model is best read as supplying the mechanistic story behind an uplift ranking rather than as a competing estimator.
In platform and operations settings, the moderator is often a system state rather than a person: network congestion, inventory depth, marketplace thickness. Here the moderator sometimes is manipulable, because the platform sets it, and the interaction framing becomes legitimate. A two-factor experiment that randomizes both the intervention and the system state converts a fragile effect-modification claim into a genuine causal interaction, and makes the mediated-moderation decomposition of Section 23.2 well posed. This is usually worth the extra design cost.
In litigation and regulatory work, moderated mediation claims attract scrutiny precisely at their weakest point. An expert who testifies that a disclosure worked through comprehension for sophisticated investors but not for retail investors is making a claim about a difference between two indirect effects, and opposing counsel will ask whether that difference was tested. On the evidence in Section 23.3, the answer in most submitted analyses is no. The defensible version reports the index with its interval, states the mediator-outcome confounding assumption explicitly, and presents the sensitivity analysis alongside the point estimate.
In policy evaluation, the analogue is heterogeneity of mechanism across sites. Multi-site trials routinely find that a program works everywhere but appears to work through different channels in different places. Before that becomes an implementation recommendation it needs the index test, because site sample sizes vary enormously and the differential-significance artifact of Section 23.3 is precisely a sample-size artifact.
23.11 Summary
Moderated mediation asks whether a mechanism is contingent, and conditional process analysis is the family of models that answers it. The conditional indirect effect is the product of the conditional first-stage and second-stage paths, which makes it linear in the moderator only when exactly one stage is moderated; in that case its slope is the index of moderated mediation, and testing the index is the correct test. Mediated moderation, under the standard linear specification, computes the same number from the other direction, and the term has been retired because an interaction product is not a manipulable cause outside a factorial design.
The dominant reporting practice, probing the indirect effect at conventional moderator values and comparing which intervals exclude zero, is not a test and behaves very badly: in a simulation where the true index is zero and the only difference between groups is sample size, it claims moderated mediation three quarters of the time. The index test holds its nominal level.
Counterfactually, most applied moderation of a mechanism is effect modification rather than interaction, which is both weaker and easier: it needs no assumption about the moderator’s own confounding, but it licenses no statement about changing the moderator. First-stage moderated mediation is the credible case, because a randomized treatment identifies the interaction that drives it, and Loeys et al. (2016) show that this makes moderated mediation identifiable under weaker assumptions than mediation itself. Second-stage moderation carries the full burden of mediator-outcome confounding and no differencing argument relieves it.
The replication of Brader et al. (2008) shows the whole apparatus at work and delivers a result worth keeping: the framing treatment operates through anxiety at every age, the mechanism does not measurably vary with age, and what does vary with age is the direct path that bypasses anxiety entirely. A causal forest reaches the same conclusion without being told to look at age. The power simulation explains why: detecting moderated mediation takes roughly four times the sample that detecting mediation takes, and most published conditional process analyses are not built at that scale.
Outside the laboratory the order of operations matters more than the model. Singh et al. (2026) is the template: establish the total effect with a design that survives estimators with different failure modes, build the mediator and the moderator from data granular enough that a threshold means something, and then decompose, stating plainly which parts of the decomposition are design based and which rest on selection on observables.
Some mechanism claims do not fit a regression at all. When the theory says that several distinct combinations of conditions reach the same outcome, that one condition is present in all of them, and that the conditions for failure are not the mirror image of the conditions for success, the set-theoretic tools are the right ones. Configurational analysis expresses equifinality, conjunctural causation, and asymmetry natively, at the cost of giving up standard errors and inheriting every confounder in the sample. It characterizes heterogeneity; it does not identify effects. Used alongside a credible design rather than in place of one, it answers the question a coefficient cannot: not how large the average effect is, but in which configurations the mechanism operates at all.