Lecture 12
So often our examples were motivated by a lurking causal question that we couldn’t really answer because our data were purely observation:
We can deal with confounders before or after we collect the data.
Design
Modeling / Analysis
Confounding variables make it hard to conclude that \(A\) causes \(B\);
But if we can remove or account for the effects of confounding — either by design or by modeling — we can conclude causality.
A study in which the researcher assigns units (people, schools, hospitals, …) to treatment or control;
Assignment uses a random mechanism — like a coin flip — not the unit’s own choice or the researcher’s judgment;
This is in contrast to an observational study, where we observe but do not intervene;
Examples: clinical drug trials, A/B tests, policy evaluations.
\(Z \in \{0, 1\}\): treatment indicator — 1 if a unit receives treatment, 0 if control;
\(X\): covariates — pre-treatment background variables (age, sex, baseline health, …);
\(Y\): outcome — the quantity we want to understand causally (recovery, test score, revenue, …);
Treatment group: units assigned \(Z = 1\);
Control group: units assigned \(Z = 0\).
Placebo: a “fake” treatment (eg. a sugar pill) given to the control group; indistinguishable from the real treatment;
Single-blind: participants do not know their treatment assignment;
Double-blind: neither participants nor the researchers administering treatment know the assignment — guards against bias on both sides.
https://pubmed.ncbi.nlm.nih.gov/30389226/
Using the paper (https://pubmed.ncbi.nlm.nih.gov/30389226/), identify the following:
Nowak-Węgrzyn et al., Journal of Allergy and Clinical Immunology (2019) — https://pubmed.ncbi.nlm.nih.gov/30389226/
Cohort: 46 children and young adults (ages 4–22) with confirmed wheat allergy;
Design: Multicenter, randomized, double-blind, placebo-controlled Phase 2 trial;
Treatment (\(Z=1\)): Vital wheat gluten (VWG) oral immunotherapy — biweekly escalation to 1,480 mg wheat protein/day over 1 year;
Control (\(Z=0\)): Matched placebo — participants and researchers blinded to assignment;
Outcome (\(Y\)): Passing a 1,480 mg double-blind placebo-controlled food challenge (DBPCFC) at year 1;
Covariates (\(X\)): Age, sex, baseline wheat IgE, threshold dose at baseline.
Randomization is incredibly powerful:
Treatment \(Z\) is assigned independently of everything (\(Z \perp X\));
This includes measured confounders and unmeasured confounders;
Even if confounders exist, they are (on average) distributed evenly across both groups — so they don’t bias our estimate;
Any average difference in \(Y\) between groups must be due to \(Z\), not a confounder;
This is why RCTs are considered the gold standard for causal inference.
Randomization creates two comparable groups — the only systematic difference should be the treatment itself;
We verify this empirically with a balance table (called “Table 1” in medical research);
Compare means and proportions of key pre-treatment covariates across the two groups;
Good balance → confident that differences in \(Y\) are attributable to \(Z\).
| Characteristic | Placebo (n = 23) | VWG OIT (n = 23) |
|---|---|---|
| Age (years), mean (SD) | 8.1 (3.9) | 7.8 (4.1) |
| Female, \(n\) (%) | 9 (39%) | 10 (43%) |
| Wheat IgE (kU/L), median | 31.4 | 29.8 |
| Threshold dose at baseline (mg), median | 200 | 200 |
If groups differ on \(X\) before treatment, we can’t be sure whether differences in \(Y\) are due to \(Z\) or \(X\);
Example: if the treatment group happens to be younger on average, better outcomes might reflect age — not the treatment;
Solution 1: include the imbalanced covariate(s) in your regression model;
Solution 2: rerandomize — if the initial draw produces an imbalanced allocation, redraw until balance is achieved (can be built into the design ahead of time).
Now our question is: does the change in our treatment affect our outcome \(Y\)?
I.e., does switching from the control group to our treatment group produce a meaningful change in \(Y\) on average?
We can estimate this directly as the difference in group means:
\[\tau = \bar{Y}_{\text{treated}} - \bar{Y}_{\text{control}}\]
\[ \hat{Y}_i = b_0 + b_1 Z_i \]
\(b_0\): predicted outcome in the control group (\(Z = 0\));
\(b_1\): estimated average treatment effect — the average change in \(Y\) when going from control to treatment;
In fact, \(b_1 = \bar{Y}_{\text{treated}} - \bar{Y}_{\text{control}}\) exactly.
glimpse(wheat_trial)Rows: 46
Columns: 5
$ id <int> 1, 2, 3, 4, 5, 6, 7, 8, 9, 10, 11, 12, 13, 14, 15, …
$ age <dbl> 20.5, 20.9, 9.2, 18.9, 15.6, 13.3, 17.3, 6.4, 15.8,…
$ baseline_wheat_ige <dbl> 13.3, 7.1, 30.8, 32.4, 38.6, 17.1, 90.6, 14.9, 10.6…
$ vwg_oit <dbl> 1, 1, 1, 1, 1, 1, 1, 1, 1, 1, 1, 1, 1, 1, 1, 1, 1, …
$ max_dose_mg <dbl> 1331, 1391, 1126, 960, 1197, 1175, 1052, 1184, 1384…This dataset is artificially generated to represent the structure of the real study. In practice, clinical trial data like this is Protected Health Information (PHI) — individually identifiable health data (e.g. diagnoses, lab values, treatment records) protected under HIPAA — and cannot be shared publicly.
Is VWG oral immunotherapy effective at increasing wheat tolerance?
. . .
More precisely: is there a significant relationship between VWG OIT treatment and maximum tolerated wheat protein dose?
. . .
\[H_0: \beta_1 = 0 \qquad H_A: \beta_1 \neq 0\]
wheat_fit <- linear_reg() |>
fit(max_dose_mg ~ vwg_oit, data = wheat_trial)
tidy(wheat_fit)# A tibble: 2 × 5
term estimate std.error statistic p.value
<chr> <dbl> <dbl> <dbl> <dbl>
1 (Intercept) 234. 31.3 7.48 2.29e- 9
2 vwg_oit 967. 44.2 21.9 2.79e-25\[\widehat{\text{max dose}} = b_0 + b_1 \times \text{VWG OIT}\]
Intercept: The estimated max tolerated dose for participants in the placebo group is \(b_0\) mg, on average.
vwg_oit: Receiving VWG OIT causes an estimated increase of \(b_1\) mg in max tolerated dose compared to placebo, on average.
In every previous lecture, we bent over backwards to say: “A one-unit increase in \(Z\) predicts an average change in \(Y\) of \(b_1\);”
Now, we say “A one-unit increase in Z causes Y to change by \(b_1\), on average.”
We’ve eliminated the effect of confounding via randomization, so any changes in \(Y\) can be plausibly attributed to the change in \(Z\) alone.
If covariate balance is not satisfied, we can include those covariates in the model to adjust for them:
wheat_fit_adj <- linear_reg() |>
fit(max_dose_mg ~ vwg_oit + baseline_wheat_ige, data = wheat_trial)
tidy(wheat_fit_adj)# A tibble: 3 × 5
term estimate std.error statistic p.value
<chr> <dbl> <dbl> <dbl> <dbl>
1 (Intercept) 312. 27.8 11.2 2.22e-14
2 vwg_oit 947. 34.2 27.7 4.57e-29
3 baseline_wheat_ige -1.84 0.328 -5.62 1.31e- 6Without covariate adjustment:
linear_reg() |>
fit(max_dose_mg ~ vwg_oit, wheat_trial) |>
tidy() |>
select(term, estimate, std.error)# A tibble: 2 × 3
term estimate std.error
<chr> <dbl> <dbl>
1 (Intercept) 234. 31.3
2 vwg_oit 967. 44.2With covariate adjustment:
linear_reg() |>
fit(max_dose_mg ~ vwg_oit + baseline_wheat_ige, wheat_trial) |>
tidy() |>
select(term, estimate, std.error)# A tibble: 3 × 3
term estimate std.error
<chr> <dbl> <dbl>
1 (Intercept) 312. 27.8
2 vwg_oit 947. 34.2
3 baseline_wheat_ige -1.84 0.328. . .
The point estimate of the treatment effect is similar, but estimation uncertainty is reduced. More on this in a few weeks.
Generalizability: The wheat OIT trial enrolled 46 children and young adults at a small number of academic medical centers. Results may not generalize to all ages, allergy severities, or healthcare settings;
Feasibility and cost: RCTs require careful coordination, long follow-up periods, and significant funding. Not every research question can be studied this way;
Ethical constraints: We can only randomize participants to treatments we believe are plausibly safe. We cannot randomly assign people to harmful exposures: