Where this sits: Lesson 09 gave you the bivariate case — one r, two variables, and the two reasons an association can't establish cause (directionality and third variables). This lesson is the multivariate sequel: designs with three or more measured variables, aimed squarely at those two problems. You've had statistics, so we'll treat regression as an old acquaintance — the goal here is what the numbers mean, and what they're routinely oversold as meaning.
The big ideaGetting closer to cause without an experiment
Everything in this lesson exists because sometimes you can't run the experiment. You can't randomly assign people to smoke for thirty years, to grow up poor, to be high in trait self-compassion, or to spend a decade eating meat at every meal. When manipulation is impossible or unethical, researchers who still want causal traction reach for tools that chip away at the two hardest causal criteria (Shadish, Cook, & Campbell, 2002): temporal precedence — which longitudinal designs can genuinely buy you — and internal validity — which statistical control buys you only partially, and only for the rivals you thought to measure.
Keep one framing in mind for the whole lesson: adding variables is a strategy for ruling out alternative explanations. A bivariate correlation is compatible with dozens of causal stories. Each well-chosen additional variable — a second measurement occasion, a plausible confound, a candidate mechanism — kills off some of those stories. The stories that survive every attempt to kill them get to be taken seriously. That's not a consolation prize for people who couldn't run experiments; it's how epidemiology convicted cigarettes, and it's how much of psychology works on questions that will never fit inside a lab.
Longitudinal logicMeasure the same people twice (at least)
Here's a real problem from the self-compassion literature. Cross-sectionally, self-compassion and depressive symptoms are strongly negatively correlated — people who treat themselves kindly under failure report less depression. But which way does the arrow run? Maybe low self-compassion is a vulnerability that breeds depression. Maybe depression erodes self-compassion — a scar the disorder leaves on how you relate to yourself. Maybe both. A single-occasion correlation cannot distinguish these stories, no matter how large the sample.
Krieger, Berger, and grosse Holtforth (2016) attacked the question with a longitudinal design: 125 formerly depressed outpatients, measured three times — at the end of cognitive-behavioral therapy, then six and twelve months later — on both self-compassion and depressive symptoms. Measuring the same people on the same variables at multiple time points produces three distinct kinds of correlation, and the entire causal argument hinges on telling them apart:
| Correlation type | What it links | What it buys you |
|---|---|---|
| Cross-sectional | Two variables at the same time point | Covariance only — the arrows point both ways |
| Autocorrelation | One variable with itself across time | Stability — how trait-like is this construct? |
| Cross-lagged | Earlier measure of X with a later measure of Y | Temporal precedence — which came first |
The payoff lives in the cross-lags, and specifically in their asymmetry. Two paths get tested against each other: does earlier self-compassion predict later depressive symptoms, and does earlier depression predict later self-compassion? In Krieger et al., only the first was significant. Lower self-compassion forecast higher depressive symptoms six months later — even after controlling for how depressed people already were — while depressive symptoms did not forecast later self-compassion (the path was near zero). The same asymmetric pattern held when depression was measured not by questionnaire but by a diagnostic interview for a major depressive episode. That asymmetry is the tell: it fits the vulnerability story and embarrasses the scar story.
Cross-sectional correlations are causally mute because everything is measured in the same breath. The cross-lagged path is different in kind: because it connects an earlier X to a later Y while holding earlier Y constant, a significant path means X carried information about change in Y over time. When one direction is significant and the other isn't, you have genuine evidence about temporal order. But notice what Krieger et al. themselves wrote in their limitations: causality still cannot be inferred. Self-compassion and depression could both be downstream of an unmeasured third variable — neuroticism, early adversity, rumination style — that produces exactly this pattern. Longitudinal designs solve the directionality problem. They do nothing, by themselves, about the third-variable problem. Keep the two problems separate in your head; the tools that address them are different.
For decades the cross-lagged panel model (CLPM) was the gold standard for exactly this kind of question. Then Hamaker, Kuiper, and Grasman (2015) showed that its lagged paths quietly blend two very different things: stable between-person differences (some people are simply, chronically higher in self-compassion than others — a trait) and within-person change (whether my dip in self-compassion this year predicts my rise in symptoms next year — the actual causal question). When constructs are trait-like — and in Krieger et al. the stability coefficients ran around .80, about as trait-like as it gets — the standard CLPM's cross-lagged estimates can be biased in size and even in sign. The fix, the random-intercept CLPM (RI-CLPM), gives each person their own baseline and estimates the lagged paths on deviations from it. The lesson for you as a consumer: a cross-lagged arrow is a model-dependent claim, and "X predicted later Y" from a traditional CLPM deserves one notch less confidence than it usually gets.
Controlling forWhat multiple regression actually does
Now the third-variable problem. A bivariate correlation can't rule out a single confound; multiple regression can rule out the confounds you measured. Suppose — a deliberately hypothetical example — a large survey finds that red-meat consumption correlates with cardiovascular problems. The obvious objection: meat-heavy eaters in Western samples also smoke more, exercise less, and drink more. So the researchers measure smoking, exercise, and alcohol too, and regression answers a sharper question: does meat consumption still predict heart trouble among people who are equivalent on those three variables?
The most honest intuition for "controlling for smoking" is subgroups. Imagine splitting the sample into non-smokers, light smokers, and heavy smokers, and checking whether the meat–heart slope is still positive within each band. If it is, the relationship holds "controlling for smoking." If the slope flattens to zero inside every band, then smoking was doing the work all along — the meat–heart association was spurious. Regression does this smoothly and simultaneously for every predictor in the model, but the subgroup picture is what the math is accomplishing: comparing people who differ on your predictor while being statistically matched on the others.
Vocabulary you already own from statistics, refreshed: the outcome being predicted is the criterion (the DV); everything else in the model is a predictor. Each predictor gets a coefficient — b in raw units, beta (β) standardized — representing its unique association with the criterion holding the other predictors constant.
Find the criterion in the table title or note. Every row is a predictor. Read the β column: sign gives direction, and because betas are standardized you may compare their magnitudes within the table — the biggest |β| is the strongest unique predictor. Check the stars: a significant β means that predictor relates to the criterion even with everything else in the model held constant. Then ask the three questions the table can't answer for itself: What isn't in the model? How well was each control variable actually measured? And why did the authors pick these controls and not others? If the paper can't tell you the third one, the model was assembled by vibes.
Two technical footnotes worth keeping. First, never compare two b values to decide which predictor matters more — they live in raw units, so a variable measured in cigarettes-per-day and one measured in servings-per-week aren't on speaking terms. Second, a predictor's β can shrink, vanish, or flip when other predictors enter the model. That's not the statistics misbehaving; that's the whole point. What survives adjustment is the interesting part.
The seductionWhy regression tempts you into causal language
Here is where this lesson earns its keep. Regression output feels causal. "Meat consumption predicted cardiovascular problems, controlling for smoking, exercise, and alcohol" slides effortlessly into "meat contributes to heart disease" — and reviewers, journalists, and the researchers themselves make that slide constantly. Rohrer (2018) is the clearest modern statement of why that's a mistake, and her argument has two prongs.
Prong one: you cannot control for what you didn't measure. The regression adjusts for exactly the variables in the model — nothing else. Every unmeasured confound (genetics, income, a health-conscious personality) sits untouched, fully capable of generating the association. Random assignment equates groups on every variable at once, measured, unmeasured, and unimagined; regression equates people only on the columns in your spreadsheet. That asymmetry is why a single decent experiment can outweigh a dozen regressions.
Prong two — the one students rarely hear: controlling for more is not automatically better. Rohrer's central tool is the causal diagram (DAG): a sketch of your assumptions about what causes what, which tells you which variables to adjust for and which to leave alone. Adjust for a variable that lies on the causal path (a mediator) and you erase the very effect you're studying. Adjust for a collider — a variable caused by both X and Y — and you manufacture a spurious association that wasn't there before. "We controlled for everything we could think of" is not rigor; it's a coin flip about whether each control helped or actively poisoned the estimate. Choosing control variables is a causal-theory decision, not a statistical reflex.
Not even the measured confounds are fully ruled out. Westfall and Yarkoni (2016) showed that statistical control works only as well as the measurement of the control variable: when your covariate is a noisy proxy for the construct you care about (and in psychology, reliability around .70–.80 is normal), regression removes only the portion it captured. The leftover — residual confounding — routinely produces "X predicts Y above and beyond Z" findings that are pure measurement error, with false-positive rates that approach 100% in large samples. Read that again: bigger samples make this problem worse, because they give you the power to detect the artifact reliably. So a claim of incremental validity requires good answers to two questions: was the confound measured at all, and was it measured well?
The trio you'll confuseMediator vs. moderator (vs. confound)
Once researchers have three or more variables in play, two words start doing heavy lifting: mediation and moderation. The vocabulary comes from one of the most-cited papers in all of psychology — Baron and Kenny (1986), which has accumulated over a hundred thousand citations precisely because researchers kept using the two terms interchangeably and needed an authority to point to. They do completely different jobs.
Mediator — the why
A mechanism on the causal path: X → M → Y. Raes (2010) found that the link between low self-compassion and depressive symptoms ran substantially through rumination — harsh self-relating feeds repetitive negative thought, and the repetitive thought feeds the symptoms. The mediator explains how the effect travels. The statistical signature: the X→Y association shrinks when M enters the model. It's internal to the process and usually the researcher's main theoretical interest.
Moderator — the when / for whom
An "it depends" — the strength (or even direction) of X→Y changes across levels of the moderator, shown statistically by an interaction term. Marshall et al. (2015) tracked over two thousand adolescents and found that low self-esteem predicted poor mental health a year later — but almost entirely among teens low in self-compassion. For highly self-compassionate teens, low self-esteem barely mattered. Self-compassion didn't explain the link; it marked out where the link lives.
A confound is a third variable external to the X–Y relationship and unwanted: it causes both, making them look related when they're only both tethered to it. Contrast the geometry. A mediator sits on the causal path (X → M → Y) and you want to spotlight it; a confound sits off to the side (X ← C → Y) and you want it gone. Here's the uncomfortable part: the same statistical operation — the X→Y coefficient shrinking when the third variable enters — flags both. The data alone cannot tell you whether the shrinkage means "we found the mechanism" or "the association was spurious." Only your causal theory, ideally drawn as a DAG before you touch the data (Rohrer, 2018), says which story you're in. This is the single most-missed distinction on every exam I have ever graded, so consider yourself armed.
Two modern upgrades to the classic story, since you've had the statistics to appreciate them. First, nobody serious still runs Baron and Kenny's original four-step procedure; the field moved to estimating the indirect effect (the a×b product) directly and testing it with bootstrapped confidence intervals, the approach built into Hayes's (2018) PROCESS framework you may meet in a later stats course. Second — and this one is a genuine trap — mediation claims from cross-sectional data are shaky by construction. Mediation is a process that unfolds in time: X changes M, and M then changes Y. Maxwell and Cole (2007) showed that estimating this from a single-occasion snapshot yields substantially biased estimates of the true longitudinal process, even under ideal conditions — cross-sectional data can indicate strong mediation where essentially none exists over time, and vice versa. Raes (2010) was cross-sectional; treat its mediation story as a plausible hypothesis that later longitudinal work has to earn, not a demonstrated mechanism. When you read "M mediated the X–Y link" in a one-shot survey study, the correct mental annotation is: consistent with mediation, not evidence of it.
ConvergencePattern and parsimony — the honest endgame
So no single correlational study proves cause. How, then, do we know smoking causes lung cancer? Nobody ever randomly assigned humans to a thirty-year pack-a-day condition. The answer is the most important idea in this lesson: a web of correlational findings, each individually vulnerable, can converge on one causal explanation that accounts for the whole pattern with the fewest contortions. Abelson (1995) called the principle pattern and parsimony; epidemiology's version is Hill's (1965) famous considerations — strength, consistency, dose–response, temporality, plausibility, and colleagues. One simple mechanism (carcinogens contacting lung tissue) predicted that longer smoking means more cancer, quitting means less, filtered cigarettes mean somewhat less, secondhand exposure means somewhat more, and the cancers cluster where the smoke touches. Every prediction held. Explaining that entire pattern without causation requires a conspiracy of coincidences; explaining it with causation requires one sentence. Parsimony wins.
The same logic, at smaller scale, is how a psychological literature builds a causal case. Take the running example: cross-sectional correlations show self-compassion and depression covary; cross-lagged panels show self-compassion precedes symptom change and not the reverse (Krieger et al., 2016); mediation studies propose a mechanism through rumination (Raes, 2010); moderation studies map the boundary conditions (Marshall et al., 2015); and — closing the loop — randomized experiments show that training self-compassion reduces depressive symptoms. No single study carries the weight. The converging pattern does. That's the difference between "correlation isn't causation" as a thought-terminating cliché and as the opening move of a research program: the cliché stops at the gap; the program spends a decade narrowing it from every side and says exactly how much daylight remains.
Mediator, moderator, or confound? Tap each scenario to reveal the answer and the tell.
SourcesCited in APA 7
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