Crossover Designs

A crossover trial gives every subject every treatment, one after another, and compares the treatments within each person. Because the comparison is within-subject, the stable differences between people — the dominant source of variability in most biological measurements — cancel out, so a crossover can reach the same power as a parallel-group trial with far fewer participants. The price is a set of order effects you must design against: the treatment given first can leave a residue that colours the second period.

Figure 1. The 2x2 crossover schematic. Sequence AB receives treatment A in period 1 and B in period 2; sequence BA receives them in the opposite order, with a washout between periods. Each subject contributes a within-person A-versus-B contrast, and comparing the two sequences separates the treatment effect from a period effect.

The 2×2 crossover#

In the simplest design, subjects are randomized to one of two sequences: AB (treatment A then B) or BA. Each subject is measured at the end of each period, with a washout in between long enough for the first treatment to clear. Three effects compete to explain the two measurements:

the treatment effect $\tau$ (A versus B) — the quantity of interest;
a period effect $\pi$ (period 2 differs from period 1 for everyone, e.g. disease progression or familiarity);
a carryover effect $\lambda$ (the previous treatment still acting in the next period).

Model the response for subject $i$ in period $p$ as

$y_{ip} = \mu + s_i + \pi_p + \tau_{d(i,p)} + \varepsilon_{ip}, \qquad s_i \sim \mathcal{N}(0, \sigma_s^2),$

where $d(i,p)$ is the treatment subject $i$ receives in period $p$ and $s_i$ is the subject’s level.

Separating treatment from period#

Differencing the two periods within a subject removes $s_i$ entirely — that is the whole point of the crossover. Comparing those within-subject differences between the two sequences then separates treatment from period, because the sequences see the same period effect but opposite treatment orders:

$\hat{\tau} = \tfrac{1}{2}\big[\,\overline{(y_1 - y_2)}_{\text{AB}} - \overline{(y_1 - y_2)}_{\text{BA}}\,\big].$

The period effect comes from the sum of the same within-subject differences.

Warning

In the 2×2 design, carryover is aliased with the sequence (between-subject) contrast, so it can only be estimated from the least precise comparison in the study — and testing for it then adjusting is unreliable. The robust fix is design, not analysis: make the washout long enough that $\lambda \approx 0$ . Higher-order designs (more periods or sequences, e.g. ABB/BAA) de-alias carryover and let it be estimated within subjects.

A worked example#

Twenty-four subjects are split between the AB and BA sequences; treatment B lowers the response by $\tau = 3$ relative to A, and period 2 sits $\pi = 1$ above period 1 for everyone. The between-subject spread ( $\sigma_s = 5$ ) dwarfs the within-subject noise ( $\sigma = 1$ ). A within-subject analysis estimates the treatment and period effects with tight intervals, while the carryover contrast — forced through the between-subject comparison — comes out with an interval several times wider, showing exactly why the 2×2 design leans on washout rather than on estimating $\lambda$ (Figure 2).

Figure 2. Estimated crossover effects with 95% intervals. Treatment and period, estimated within subjects, have narrow intervals; the carryover effect, aliased with the between-subject sequence contrast, has a wide interval and cannot be pinned down — the argument for controlling it by washout.

In code#

R#

library(lme4)
# treatment and period are within-subject; (1 | subject) removes subject level
fit <- lmer(y ~ treatment + period + (1 | subject), data = d)
# Classic hand analysis: within-subject period differences, compared by sequence
# tau_hat = 0.5 * (mean(d | AB) - mean(d | BA)),  d = y_period1 - y_period2

Python#

Python

import numpy as np
import pandas as pd
import statsmodels.formula.api as smf

rng = np.random.default_rng(11)
seqs = {"AB": ("A", "B"), "BA": ("B", "A")}
eff = {"A": 0.0, "B": -3.0}                        # treatment B lowers response by 3
rows = []
sid = 0
for seq, (t1, t2) in seqs.items():
    for _ in range(12):                            # 12 subjects per sequence
        s = rng.normal(0, 5.0)                     # big subject level
        for period, t in [(1, t1), (2, t2)]:
            y = 20 + s + 1.0 * (period - 1) + eff[t] + rng.normal(0, 1.0)
            rows.append((sid, seq, period, t, y))
        sid += 1
d = pd.DataFrame(rows, columns=["subject", "seq", "period", "treatment", "y"])
m = smf.mixedlm("y ~ treatment + C(period)", d, groups=d["subject"]).fit()
print("treatment B:", round(m.params["treatment[T.B]"], 2),
      "period 2:", round(m.params["C(period)[T.2]"], 2))

treatment B: -3.4 period 2: 1.0

Julia#

Julia

using MixedModels, DataFrames
# within-subject treatment and period effects; subject as random intercept
m = fit(MixedModel, @formula(y ~ treatment + period + (1 | subject)), d)

Why it matters for statistics#

Crossover trials are a mainstay of studies on chronic, stable conditions — analgesics, antihypertensives, asthma controllers, bioequivalence — where each patient can serve as their own control and the treatment washes out between periods. They are a repeated-measures design with treatments as the repeated conditions, so they inherit both its power and its correlation structure, plus the special hazard of carryover. The lesson generalizes: when a design confounds an effect with your least precise contrast, the answer is usually to design that effect away rather than to trust a weak test of it.