Introduction to Graphical Causal Inference

Getting Started

Moritz Ketzer

moritz.ketzer@hu-berlin.de

Humboldt-Universität zu Berlin

March 9, 2026

Welcome

• welcome everyone
• thank them for being there

• one sentence on who you are
  • studied psychology
  • last year phd in psych methods

• one or two sentences on the goal of the workshop
  • accessible introduction to (graphical) causal inference
• set tone:
  • lets be interactive
  • no pressure
  • we go slow
  • you have time
  • ask all kinds of questions
  • everybody benefits from every question
  • this is difficult material
    • dont expect to understand everything
    • give yourself time
    • if you are confused, it means you are paying attention
• you get all of the material
• you get further reading material

• name, role, context (research / practice)
• what outcome/topic they care about
• what they hope to take away

Walk through the website together: Zoom info, presentations, RStudio server setup, resources.

Workshop Website and RStudio Server Setup

moritzketzer.github.io/iqb-workshop

• open the workshop website — type the URL or click the link
• under “RStudio Server”: first claim a login, then open RStudio
• you get a username from a famous statistician or causal inference researcher
• password is changeme
• hello-world.R is in your home directory — run it to check everything works
• we will use this for the R exercises later

Why bother with Causal Inference?

Messerli (2012)

Descriptive

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Predictive

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Explanatory

“Spurious Correlations” (n.d.)

“Spurious Scholar” (n.d.)

Shmueli (2010)

Editorial (2021)

Kidney Stones

Two treatments

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Which one is better?

Charig et al. (1986)

Transition from spurious correlations → what about non-obvious cases? Real data. Open surgery (A) vs less invasive (B). 700 patients.

Stone size	Treatment A	Treatment B
Small	81 / 87 (93%)	234 / 270 (87%)
Large	192 / 263 (73%)	55 / 80 (69%)
Total	273 / 350 (78%)	289 / 350 (83%)

Table has the full story already. Don’t spoil — let them read. A wins both subgroups, B wins overall. Paradox.

Treatment A (open surgery): 78%. Treatment B (less invasive): 83%. B looks better. Should we recommend B?

By stone size: - Small: A 93% vs B 87% - Large: A 73% vs B 69% A wins BOTH. Overall was misleading → Simpson’s paradox.

Panel sizes = allocation. A got mostly large (hard), B got mostly small (easy). Severity drove assignment AND outcome → confounding. Stratify → A genuinely better. But how do we know when to stratify?

Pearl (2013); Kievit et al. (2013)

Why?

Stone size influences both which treatment you get and how well you recover.

✓ Stratify!

Blood pressure (measured after)	Drug	No drug
Low BP	81 / 87 (93%)	234 / 270 (87%)
High BP	192 / 263 (73%)	55 / 80 (69%)
Total	273 / 350 (78%)	289 / 350 (83%)

Identical numbers — just relabeled. BP measured AFTER treatment → consequence of drug, not prior cause. Drug wins both BP subgroups. No drug wins overall. Same paradox, opposite correct answer.

✗ Don’t stratify!

BP on causal path, not common cause. Chain, not fork. Stratify by BP → filter out mechanism → drug looks useless. Aggregate correct here: drug helps THROUGH lowering BP.

Same data. Opposite answers.

The statistics are identical.

Only the causal story changed.

Key slide. Kidney: common cause → stratify. BP: consequence → don’t stratify. Same table, opposite correct answers. Statistics alone can’t resolve this. Need causal structure → transition to “what IS causal inference?”

Pearl (2009); Pearl and Mackenzie (2018)

Largely because of this guy — Judea Pearl. “Causality” (2009, technical) and “The Book of Why” (2018, accessible). Pearl formalized the graphical approach: encode causal assumptions in a graph, then read off what’s identifiable.

Pearl and Mackenzie (2018, fig. 1.2)

Three rungs: seeing, doing, imagining. Can’t climb with data alone. Dog: “Owners are happier” → “Would getting one make ME happier?” → “Would I still be happy WITHOUT it?” Today: rung 1 → 2. But first, rung 3 — why it’s hard.

Rung 3: Imagining

You got a dog. You’re happy.

Y_i(\text{dog}) = 1 \quad \checkmark

Would you have been happy without the dog?

Y_i(\text{no dog}) = \; ?

Two scenarios: Y(no dog)=1 → dog didn’t matter. Y(no dog)=0 → dog caused it. Can’t rewind time. Every causal question has this structure.

The Individual Treatment Effect

Rubin (1974)

\tau_i = Y_i(1) - Y_i(0)

We can never observe both for the same person.

Holland (1986): fundamental problem of causal inference. Not statistics — metaphysics. Can’t be in two states at once.

The Fundamental Problem of Causal Inference

i	T	Y	Y(1)	Y(0)	\tau_i
1	0	0	?	0	?
2	1	1	1	?	?
3	1	0	0	?	?
4	0	0	?	0	?
5	0	1	?	1	?
6	1	1	1	?	?

Missing data problem — not measurement failure, but metaphysics. Half the table always missing. So what CAN we do?

Holland (1986)

From Individual to Average

We can’t know \tau_i for any single person.

But we can ask about the average across many people:

\begin{aligned} ATE &= \mathbb{E}[Y(1) - Y(0)] \\ &= \mathbb{E}[Y(1)] - \mathbb{E}[Y(0)] \end{aligned}

Rung 3 → Rung 2

Give up on individual → ask about the average. This is what RCTs target. Distribute expectation → two population means we can estimate separately. Key question: how do we estimate this from observational data?

Observational

\mathbb{E}[Y \mid X = x]

“What Y do we see when X = x?”

Interventional

\mathbb{E}[Y \mid \text{do}(X = x)]

“What Y do we get when we set X = x?”

When are these equal?

Left = rung 1, right = rung 2. Differ whenever there’s confounding. Dog: owners are happier ≠ getting a dog makes you happier. Maybe happy people get dogs. This question drives everything today.

Neal (n.d., fig. 4.2)

Conditioning = filter operation. Pick the subgroup where T=1 — self-selected, may differ systematically. Intervening = force everyone into treatment. No self-selection. Conditioning ≠ intervening when there’s confounding.

Structural Causal Models

Pearl et al. (2016)

\mathcal{M} = \langle U, V, F, P(U) \rangle

V	endogenous variables (what we model)
U	exogenous variables (background factors, error terms)
F	structural functions (how each V is determined by its parents + U)
P(U)	probability distribution over the exogenous variables

“The causal story has a formal name” (Pearl, Glymour & Jewell 2016). All four parts in kidney stones:

— V: treatment, stone size, recovery. — U: patient genetics, lifestyle, surgeon skill — everything else. — F: how stone size determines treatment assignment, how both determine recovery. — P(U): distribution over background factors — makes the model probabilistic.

Every SCM implies a DAG -> tells us what to adjust for.

For SEM users: SEM is an SCM with linear F and normal U. Same object, specific assumptions.

An SCM Example

Structural Equations

\begin{aligned} Z &\leftarrow f_Z(U_Z) \\ X &\leftarrow f_X(Z, U_X) \\ Y &\leftarrow f_Y(Z, X, U_Y) \end{aligned}

Distributional Assumptions

U_Z, U_X, U_Y \overset{\text{ind.}}{\sim} P(U)

Concrete example: Z confounder, X treatment, Y outcome. Each has its own U. U’s usually omitted from DAGs — shown here to connect to formal definition.

Graph Surgery

Structural Equations

\begin{aligned} Z &\leftarrow f_Z(U_Z) \\ X &\leftarrow \color{#107895}{x} \\ Y &\leftarrow f_Y(Z, \textcolor{#107895}{x}, U_Y) \end{aligned}

Distributional Assumptions

U_Z, \textcolor{lightgray}{U_X}, U_Y \overset{\text{ind.}}{\sim} P(U)

do-operator = graph surgery. Replace X’s equation with a constant, cut incoming arrows. Downstream (Y) keeps its equation. Upstream (Z) unaffected. U_X irrelevant. Key: this is NOT conditioning — conditioning doesn’t remove arrows. ATE: E[Y|do(X=1)] - E[Y|do(X=0)] = “what happens when we surgically set X to 1 vs 0?”

A Linear SCM

Structural Equations

\begin{aligned} Z &= U_Z \\ X &= \beta^{XZ} Z + U_X \\ Y &= \beta^{YX} X + \beta^{YZ} Z + U_Y \end{aligned}

Distributional Assumptions

\begin{pmatrix} U_Z \\ U_X \\ U_Y \end{pmatrix} \sim \mathcal{N}\left(\begin{pmatrix} 0 \\ 0 \\ 0 \end{pmatrix}, \begin{pmatrix} \sigma^2_Z & 0 & 0 \\ 0 & \sigma^2_X & 0 \\ 0 & 0 & \sigma^2_Y \end{pmatrix}\right)

Special case SEM users know. β’s ARE the causal effects. Diagonal covariance = independent errors = no unmeasured common causes beyond what’s modeled.

Graph Surgery: Linear Case

Structural Equations

\begin{aligned} Z &= U_Z \\ X &= \color{#107895}{x} \\ Y &= \beta^{YX} \textcolor{#107895}{x} + \beta^{YZ} Z + U_Y \end{aligned}

Distributional Assumptions

\begin{pmatrix} U_Z \\ \textcolor{lightgray}{U_X} \\ U_Y \end{pmatrix} \sim \mathcal{N}\left(\begin{pmatrix} 0 \\ \textcolor{lightgray}{0} \\ 0 \end{pmatrix}, \begin{pmatrix} \sigma^2_Z & 0 & 0 \\ 0 & \textcolor{lightgray}{\sigma^2_X} & 0 \\ 0 & 0 & \sigma^2_Y \end{pmatrix}\right)

ATE in linear SCM = β^{YX}. The path coefficient IS the causal effect. SEM users have been estimating causal effects all along — just needed the graph to justify it.

Estimand in do notation

ATE = \mathbb{E}[Y \mid do(X=1)] - \mathbb{E}[Y \mid do(X=0)]

do(X=1) = “set X to 1”, not “observe X = 1”. Same target as E[Y(1)-Y(0)], different notation. Pearl connects to graphs, Rubin to experiments.

Binary case — textbook RCT. ATE = difference in group means under intervention.

Estimand in do notation

ATE = \mathbb{E}[Y \mid do(X=x')] - \mathbb{E}[Y \mid do(X=x)]

Generalized: any two values x’ vs x, not just 0/1.

Continuous X, linear effect. Slope = β from the linear SCM. One number everywhere.

Nonlinear: effect depends on where you are. No single number. do-operator still well-defined — just varies by location.

Linear projection = weighted average of local effects. Hides heterogeneity. We work linear today — framework is more general than models we fit.

Two Frameworks, One Estimand

Potential Outcomes (Rubin)

ATE = \mathbb{E}[Y_i(1) - Y_i(0)]

Structural Causal Model (Pearl)

ATE = \mathbb{E}[Y \mid do(X=1)] - \mathbb{E}[Y \mid do(X=0)]

Two traditions, same target.

One Estimand, three expressions

\begin{aligned} ATE &= \mathbb{E}[Y_i(1) - Y_i(0)] \\ &= \mathbb{E}[f_Y(1, \mathbf{U}_i) - f_Y(0, \mathbf{U}_i)] \\ &= \mathbb{E}[Y \mid do(X=1)] - \mathbb{E}[Y \mid do(X=0)] \end{aligned}

Potential outcomes = structural equations evaluated in the mutilated model. Y_i(x) = f_Y(x, U_i) — that’s the middle line. Linear case: everything cancels, ATE = β^{YX}.

Directed Acyclic Graphs (DAGs)

Nodes = variables. Arrows = direct causal effects. Acyclic = no loops. Encodes assumptions — including what’s NOT connected. Absence of arrow = no direct effect.

Wright (1920, fig. 1)

Sewall Wright, 1920 — the first path diagram. Guinea pig coat color. If you’ve drawn a path diagram, you’ve already drawn a DAG.

Wright (1934)

Wright formalized path coefficients in 1934. Direct ancestor of SEM. Pearl added the formal rules for what you can and can’t conclude. Now: three building blocks.

The Three Elemental Structures

Fork (Common Cause)

Title slide — name the structure, then advance to the interactive demo. Fork: Z causes both X and Y. Spurious association disappears when you condition on Z.

Interactive fork demo. Default: run → d-connected (ball passes through unobserved Z). Condition on Z → d-separated (ball blocked by observed non-collider). Key: this is why we “control for confounders.”

Simulated data from a fork SCM. Looks like one homogeneous cloud. Ask: “What’s the relationship between X and Y?” Let them say “negative.” Then advance.

Same data — split Z at the median into two groups. Within each group: positive slope. Aggregate: still negative. Simpson’s paradox appears. But two bins is coarse.

Pattern solidifies — all three upward. Aggregate is the outlier.

Same story, finer bins. Building toward the limit.

Five bins, all positive. Finer conditioning, same result.

Dense fan of positive slopes. Aggregate still negative — that’s the confounding.

Z <- runif(n, 0, 10)
X <- 0.6 * Z + rnorm(n, mean = 0, sd = 2)
Y <- 1.0 * X - 2.0 * Z
    + rnorm(n, mean = 0, sd = 1.5)

Conditioning taken to the limit. At any fixed Z, X-Y positive. Aggregate trend = confounding. “Controlling for confounder” = comparing within Z-slices.

Chain (Mediator)

Title slide — name the structure, then advance to the interactive demo. Chain: X causes Z causes Y. Conditioning on Z blocks the causal path.

Interactive chain demo. Default: run → d-connected (causal path is open). Condition on Z → d-separated (blocking the mediator). Key: controlling for a mediator removes the causal effect — don’t do it.

tutoring <- rnorm(n, mean = 5, sd = 2)
homework <- rbinom(n, 1,
    plogis(tutoring - 5))
scores <- 20 * homework
        + rnorm(n, mean = 50, sd = 8)

Tutoring → Homework → Scores. Aggregate: positive slope. Ask: “Homework correlates with both. Should we control for it?” They’ll say yes — it’s a trap.

tutoring <- rnorm(n, mean = 5, sd = 2)
homework <- rbinom(n, 1,
    plogis(tutoring - 5))
scores <- 20 * homework
        + rnorm(n, mean = 50, sd = 8)

Controlling for homework: within each group, flat. Tutoring works THROUGH homework. Dashed = total effect. Controlling killed it. This is overcontrol bias.

Collider

Elwert and Winship (2014)

Title slide — name the structure, then advance to the interactive demo. Collider: both X and Y cause Z. Conditioning OPENS a spurious path.

Interactive collider demo. Default: run → d-separated (no path between independent causes). Condition on Z → d-connected (collider bias — conditioning opens the path). The counterintuitive case. Let audience verify it themselves.

talent   <- rnorm(n, mean = 0, sd = 1)
beauty   <- rnorm(n, mean = 0, sd = 1)
celebrity <- talent + beauty

Talent and beauty independent in population. Flat line. Ask: “What if we only look at celebrities?”

talent   <- rnorm(n, mean = 0, sd = 1)
beauty   <- rnorm(n, mean = 0, sd = 1)
celebrity <- talent + beauty
# Top 15% become famous
celeb <- celebrity > P85

Among celebrities: strong negative slope. “Famous but can’t act — must be the looks.” Explaining away. Phantom association — doesn’t exist in the population.

talent   <- rnorm(n, mean = 0, sd = 1)
beauty   <- rnorm(n, mean = 0, sd = 1)
celebrity <- talent + beauty

Not a threshold artifact — structural. At every level of fame, negative association.

Collider (Descendant)

Same collider, but now: what about something DOWNSTREAM of the collider? You know not to condition on Celebrity. But what about Instagram followers?

Condition on W (not Z!) → still d-connected. W = Followers, a consequence of Celebrity. Conditioning still partially opens the path.

talent   <- rnorm(n, mean = 0, sd = 1)
beauty   <- rnorm(n, mean = 0, sd = 1)
celebrity <- talent + beauty
followers <- 0.8 * celebrity
            + rnorm(n, mean = 0, sd = 1.2)

“You just study actors with >100k followers.” Noisy proxy for Celebrity. Negative slope weaker but still there. Bias attenuated, not eliminated.

Putting It Together

Title slide — transition from elemental structures to a realistic graph where multiple structures overlap and interact.

Multiple paths from X to Y. Let them explore: which nodes to condition on? This is where intuition needs algorithms.

D-Separation

Pearl (2009)

“You just did this intuitively. Now let’s name the rule.” Synthesis moment, not new content.

Directed Separation

A path between X and Y is blocked given a conditioning set Z if it contains:

	a non-collider (fork or chain) that is in Z
	a collider that is not in Z (and has no descendant in Z)

X and Y are d-separated given Z if every path between them is blocked.

Two rules, that’s it. They already used them on the widget. Descendant clause: conditioning on a child of collider partially opens path too.

From Surgery to Statistics

Graph surgery — physically cut arrows into X

Backdoor adjustment — statistically neutralize them

P(Y \mid do(X = x)) = \sum_z P(Y \mid X = x, Z = z) \; P(Z = z)

Left side: causal (rung 2). Right side: observable (rung 1).

Surgery = thought experiment. Backdoor adjustment = the computable version. Condition on Z → X “as if randomized” within each stratum. That’s the fork plots. “Controlling for Z” simulates an intervention. Works when Z satisfies backdoor criterion, fails otherwise (collider, mediator).

Exercise: The Causal Quartet

D’Agostino McGowan et al. (2024)

Same association, different causal structures → different answers. Don’t spoil — let them discover it.

moritzketzer.github.io/iqb-workshop

Open causal-quartet.R

Breakout rooms in pairs (~30 min), then 5 min break before debrief.

Script guides: (1) explore + discover equivalence, (2) predict from DAGs, (3) verify with adjusted lm, (4) reflect. DAG PNGs in their home directory. Walk around, help with R issues, don’t give away the punchline. If stuck on (4) M-bias: “Trace the paths. What happens when you condition on Z?”

Debrief. Let THEM explain what they see — they know this from the code now. “All four datasets, same slope, same scatter. So same answer for all four?”

“But the underlying structures are different. You looked at these DAGs — four different roles for Z.” Walk through briefly: collider, confounder, mediator, M-bias. “Who predicted all four correctly?” Hands up.

Dashed = unadjusted (all ~1). Teal = adjusted for Z. (1) Collider: 1.0 → 0.55 — adjusting introduced bias. (2) Confounder: 1.0 → 0.5 — only case where controlling helps. (3) Mediator: 1.0 → 0.0 — blocked the mechanism. (4) M-bias: 1.0 → 0.88 — Z is a collider on a backdoor path, conditioning opens it. “Who was surprised by at least one?”

Adapted from Bareinboim et al. (2022, fig. 27.4)

Two-DAG identification diagram. Relevant for identification theory. Could follow the backdoor criterion section if there’s time.

Can you prove mediation?

Kline (2015)

Let the question sit 30 seconds. Open the floor. Mediator dataset (3) statistically indistinguishable from confounder (2). Same slopes, same correlations. Baron & Kenny tests patterns consistent with mediation — also consistent with confounding. Kline (2015) “The Mediation Myth” — the Baron & Kenny procedure doesn’t test mediation, it tests a pattern equally consistent with confounding. No statistical test can distinguish a chain from a fork. “Mediation is a causal claim. You can estimate it under assumptions. You cannot test it.” For those interested: see the Mediation Analysis section in the further reading list — Imai et al. (2010) show what nonparametric identification of mediation actually requires, and it’s a lot.

Today

Quick recap of what we covered:

• Simpson’s paradox and the kidney stone example — correlation flips depending on how you slice the data
• Structural Causal Models — equations + graph = a model of the data-generating process
• Three elementary structures: fork, chain, collider — and why they matter for conditioning
• d-separation — reading off conditional independencies from the graph
• The do-operator and graph surgery — turning observation into intervention
• The Causal Quartet — same ATE, radically different data stories
• dagitty exercise — building a DAG for Open Science, finding adjustment sets, seeing what goes wrong when you control for everything

Open floor:

• Questions about anything from today?
• Anything unclear or surprising?
• Feedback — pace, level of detail, exercises?

Tomorrow

Preview of Day 2 — we go deeper:

• What happens when the causal effect isn’t the same for everyone? Heterogeneous treatment effects, CATE
• How functional form connects to DAGs — linear SCMs, interactions, what the graph can and can’t tell you
• Multilevel models as causal models — varying intercepts and slopes, the BFLPE as a running example
• Directed Acyclic Mixed Graphs (DAMGs) — how to draw multilevel DAGs properly
• Group-mean centering and the Mundlak device — why centering is a causal operation
• Confounding in multilevel settings — between-cluster vs within-cluster confounding
• If time: dynamic SCMs and longitudinal panel models (CLPM)

Open floor:

• Wishes for tomorrow? Topics you’d like more depth on?
• Anything from your own research you’d like to map onto a DAG?
• Interests we can try to weave in — no promises, but good to know

Optional: DAG your Research

References

Bareinboim, Elias, Juan D. Correa, Duligur Ibeling, and Thomas Icard. 2022. “On Pearl’s Hierarchy and the Foundations of Causal Inference.” In Probabilistic and Causal Inference, 1st ed., edited by Hector Geffner, Rina Dechter, and Joseph Y. Halpern. ACM. https://doi.org/10.1145/3501714.3501743.

Charig, C. R., D. R. Webb, S. R. Payne, and J. E. Wickham. 1986. “Comparison of Treatment of Renal Calculi by Open Surgery, Percutaneous Nephrolithotomy, and Extracorporeal Shockwave Lithotripsy.” Br Med J (Clin Res Ed) 292 (6524): 879–82. https://doi.org/10.1136/bmj.292.6524.879.

D’Agostino McGowan, Lucy, Travis Gerke, and Malcolm Barrett. 2024. “Causal Inference Is Not Just a Statistics Problem.” Journal of Statistics and Data Science Education 32 (2): 150–55. https://doi.org/10.1080/26939169.2023.2276446.

Editorial. 2021. “Description, Prediction, Explanation.” Nature Human Behaviour 5 (10): 1261–61. https://doi.org/10.1038/s41562-021-01230-5.

Elwert, Felix, and Christopher Winship. 2014. “Endogenous Selection Bias: The Problem of Conditioning on a Collider Variable.” Annual Review of Sociology 40 (July): 31–53. https://doi.org/10.1146/annurev-soc-071913-043455.

Holland, Paul W. 1986. “Statistics and Causal Inference.” Journal of the American Statistical Association 81 (396): 945–60. https://doi.org/10.1080/01621459.1986.10478354.

Kievit, Rogier A., Willem E. Frankenhuis, Lourens J. Waldorp, and Denny Borsboom. 2013. “Simpson’s Paradox in Psychological Science: A Practical Guide.” Frontiers in Psychology 4: 513. https://www.frontiersin.org/articles/10.3389/fpsyg.2013.00513/full.

Kline, Rex B. 2015. “The Mediation Myth.” Basic and Applied Social Psychology 37 (4): 202–13. https://doi.org/10.1080/01973533.2015.1049349.

Messerli, Franz H. 2012. “Chocolate Consumption, Cognitive Function, and Nobel Laureates.” New England Journal of Medicine 367 (16): 1562–64. https://doi.org/10.1056/NEJMon1211064.

Neal, Brady. n.d. “Introduction to Causal Inference.” Accessed March 7, 2026. https://www.bradyneal.com/causal-inference-course.

Pearl, Judea. 2009. Causality: Models, Reasoning, and Inference. Second edition, reprinted with corrections. Cambridge University Press.

Pearl, Judea. 2013. “Understanding Simpson’s Paradox.” SSRN Electronic Journal, ahead of print. https://doi.org/10.2139/ssrn.2343788.

Pearl, Judea, Madelyn Glymour, and Nicholas P. Jewell. 2016. Causal Inference in Statistics: A Primer. 1. edition. Wiley.

Pearl, Judea, and Dana Mackenzie. 2018. The Book of Why: The New Science of Cause and Effect. First edition. Basic Books.

Rubin, Donald B. 1974. “Estimating Causal Effects of Treatments in Randomized and Nonrandomized Studies.” Journal of Educational Psychology 66 (5): 688. https://psycnet.apa.org/record/1975-06502-001.

Shmueli, Galit. 2010. “To Explain or to Predict?” Statistical Science 25 (3): 289–310. https://www.jstor.org/stable/41058949.

“Spurious Correlations.” n.d. Accessed February 27, 2026. https://tylervigen.com/spurious-correlations.

“Spurious Scholar.” n.d. Accessed February 27, 2026. https://tylervigen.com/spurious-scholar.

Wright, Sewall. 1920. “The Relative Importance of Heredity and Environment in Determining the Piebald Pattern of Guinea-Pigs.” Proceedings of the National Academy of Sciences 6 (6): 320–32. https://doi.org/10.1073/pnas.6.6.320.

Wright, Sewall. 1934. “The Method of Path Coefficients.” The Annals of Mathematical Statistics 5 (3): 161–215. https://www.jstor.org/stable/2957502?casa_token=W2Rnt77K4xEAAAAA:OIfplx9Qlg2_3chSeXIWMD6DNY6o0MpQ52AEhlHD-q_gRNSON3XE4zckyozxyl9IbLP-PyOOdYTcvpKNzCFr7xYWRyL5pdWwZ53q_uktbvmSb5oiWAg.