Quick overview

Generally speaking, why might baseline measurements have any impact at all? The curse of any clinical trial is variability – the more noise (variability) there is in the outcome, the more difficult it is to identify the signal (effect). For example, if we are interested in measuring the impact of an intervention on the quality of life (QOL) across a diverse range of patients, the measurement (which typically ranges from 0 to 1) might vary considerably from person to person, regardless of the intervention. If the intervention has a real but moderate effect of, say, 0.1 points, it could easily get lost if the standard deviation is considerably larger, say 0.25.

It turns out that if we collect baseline QOL scores and can “control” for those measurements in some way (by conducting a repeated measures analysis, using ANCOVA, or assessing the difference itself as an outcome), we might be able to reduce the variability across study subjects sufficiently to give us a better chance at picking up the signal. Previously, I’ve written about baseline covariate adjustment in the context of clinical trials where randomization is at the individual subject level; now we will turn to the case where randomization is at the cluster or site level.

This post focuses on work already done to derive design effects for parallel cluster randomized trials (CRTs) that collect baseline measurements; we will get to stepped wedge designs in future posts. I described the design effect pretty generally in an earlier post, but the paper by Teerenstra et al, titled “A simple sample size formula for analysis of covariance in cluster randomized trials” provides a great foundation to understand how baseline measurements can impact sample sizes in clustered designs.

Here’s a brief outline of what follows: after showing an example based on a simple 2-arm randomized control trial with 350 subjects that has 80% power to detect a standardized effect size of 0.3, I describe and simulate a series of designs with cluster sizes of 30 subjects that require progressively fewer clusters but also provide 80% power under the same effect size and total variance assumptions: a simple CRT that needs 64 sites, a cross-sectional pre-post design that needs 52, a repeated measures design needs that 38, and a repeated measures design that models follow-up outcomes only (i.e. uses an ANCOVA model) that requires only 32.

Simple RCT

We start with a simple RCT (without any clustering) that randomizes individuals to treatment or control.

\[ Y_{i} = \alpha + \delta Z_{i} + s_{i} \] where \(Y_{i}\) is a continuous outcome measure for individual \(i\), and \(Z_{i}\) is the treatment status of individual \(i\). \(\delta\) is the treatment effect. \(s_{i} \sim N(0, \sigma_s^2)\) are the individual random effects or noise.

Now that we are about to start coding, here are the necessary packages:

RNGkind("L'Ecuyer-CMRG")
set.seed(19287)

library(simstudy)
library(ggplot2)
library(lmerTest)
library(parallel)
library(data.table)
library(pwr)
library(gtsummary)
library(paletteer)
library(magrittr)

In the examples that follow, overall variance \(\sigma^2 = 64\). In this first example, then, \(\sigma_s^2 = 64\) since that is the only source of variation. The overall effect size \(\delta\), which is the difference in average scores across treatment groups, is assumed to be 2.4, a standardized effect size \(2.4/8 = 0.3.\) We will need to generate 350 individual subjects (175 in each arm) to achieve power of 80%.

pwr.t.test(d = 0.3, power = 0.80)
## 
##      Two-sample t test power calculation 
## 
##               n = 175
##               d = 0.3
##       sig.level = 0.05
##           power = 0.8
##     alternative = two.sided
## 
## NOTE: n is number in *each* group

simple_rct <- function(N) {
  
  # data definition for outcome
  
  defS <- defData(varname = "rx", formula = "1;1", dist = "trtAssign")
  defS <- defData(defS, varname = "y", formula = "2.4*rx", variance = 64, dist = "normal")

  dd <- genData(N, defS)
  
  dd[]
}

dd <- simple_rct(350)

fit1 <- lm(y ~  rx, data = dd)
tbl_regression(fit1) %>% 
  modify_footnote(ci ~ NA, abbreviation = TRUE)

replicate <- function() {
  dd <- simple_rct(350)
  fit1 <- lm(y ~  rx, data = dd)
  
  coef(summary(fit1))["rx", "Pr(>|t|)"]
}

p_values <- mclapply(1:1000, function(x) replicate(), mc.cores = 4)

mean(unlist(p_values) < 0.05)
## [1] 0.79

Parallel cluster randomized trial

If we need to randomize at the site level (i.e., conduct a CRT), we can describe the data generation process as

\[Y_{ij} = \alpha + \delta Z_{j} + c_j + s_i\]

where \(Y_{ij}\) is a continuous outcome for subject \(i\) in site \(j\). \(Z_{j}\) is the treatment indicator for site \(j\). Again, \(\delta\) is the treatment effect. \(c_j \sim N(0,\sigma_c^2)\) is a site level effect, and \(s_i \sim N(0, \sigma_s^2)\) is the subject level effect. The correlation of any two subjects in a cluster is \(\rho\) (the ICC):

\[\rho = \frac{\sigma_c^2}{\sigma_c^2 + \sigma_s^2}\]

If we have a pre-specified number (\(n\)) of subjects at each site, we can estimate the sample size required in the CRT might applying a design effect \(1+(n-1)\rho\) to the sample size of an RCT that has the same overall variance. So, if \(\sigma_c^2 + \sigma_s^2 = 64\), we can augment the sample size we used in the initial example. If \(\sigma_c^2 = 9.6\) + \(\sigma_s^2 = 54.4\), \(\rho = 0.15\). We anticipate having 30 subjects at each site so the design effect is

\[1 + (30 - 1) \times 0.15 = 5.35\]

This means we will need \(5.35 \times 350 = 1872\) total subjects based on the same effect size and power assumptions. Since we anticipate 30 subjects per site, we need \(1872 / 30 = 62.4\) sites - we will round up to the nearest even number and use 64 sites.

simple_crt <- function(nsites, n) {
  
  defC <- defData(varname = "rx", formula = "1;1", dist = "trtAssign")
  defC <- defData(defC, varname = "c", formula = "0", variance = 9.6, dist = "normal")  
  
  defS <- defDataAdd(varname="y", formula="c + 2.4*rx", variance = 54.4, dist="normal")

# site/cluster level data
  
  dc <- genData(nsites, defC, id = "site")

# individual level data
  
  dd <- genCluster(dc, "site", n, "id")
  dd <- addColumns(defS, dd)
  
  dd[]
}

dd <- simple_crt(20, 50)

dd <- simple_crt(200,100)

fit2 <- lmer(y ~  rx + (1|site), data = dd)
tbl_regression(fit2, tidy_fun = broom.mixed::tidy)  %>% 
  modify_footnote(ci ~ NA, abbreviation = TRUE)

replicate <- function() {
  dd <- simple_crt(64, 30)
  fit2 <- lmer(y ~  rx + (1|site), data = dd)
  
  coef(summary(fit2))["rx", "Pr(>|t|)"]
}

p_values <- mclapply(1:1000, function(x) replicate(), mc.cores = 4)

mean(unlist(p_values) < 0.05)
## [1] 0.8

CRT with baseline measurement

We paid quite a hefty price moving from an RCT to a CRT in terms of the number of subjects we need to collect data on. If these data are coming from administrative systems, that added burden might not be an issue, but if we need to consent all the subjects and survey them individually, this could be quite burdensome.

We may be able to decrease the required number of clusters (i.e. reduce the design effect) if we can collect baseline measurements of the outcome. The baseline and follow-up measurements can be collected from the same subjects or different subjects, though the impact on the design effect depends on what approach is taken.

\[ Y_{ijk} = \alpha_0 + \alpha_1 k + \delta_{0} Z_j + \delta_{1}k Z_{j} + c_j + cp_{jk} + s_{ij} + sp_{ijk} \]

where \(Y_{ijk}\) is a continuous outcome measure for individual \(i\) in site \(j\) and measurement \(k \in \{0,1\}\). \(k=0\) for baseline measurement, and \(k=1\) for the follow-up. \(Z_{j}\) is the treatment status of cluster \(j\), \(Z_{j} \in \{0,1\}.\) \(\alpha_0\) is the mean outcome at baseline for subjects in the control clusters, \(\alpha_1\) is the change from baseline to follow-up in the control arm, \(\delta_{0}\) is the difference at baseline between control and treatment arms (we would expect this to be \(0\) in a randomized trial), and \(\delta_{1}\) is the difference in the change from baseline to follow-up between the two arms. (In a randomized trial, since \(\delta_0\) should be close to \(0\), \(\delta_1\) is the treatment effect.)

The model has cluster-specific and subject-specific random effects. For both, there can be time-invariant effects and time-varying effects. \(c_j \sim N(0,\sigma_c^2)\) are time invariant site-specific effects, and \(cp_{jk}\) are the site-specific period (time varying) effects, where \(c_{jk} \sim N(0, \sigma_{cp}^2)\). At the subject level there can be \(s_{ij} \sim N(0, \sigma_s^2)\) and \(sp_{ijk} \sim N(0, \sigma_{sp}^2)\).

Here is the generic code that will facilitate data generation in this model:

crt_base <- function(effect, nsites, n, s_c, s_cp, s_s, s_sp) {

  defC <- defData(varname = "c", formula = 0, variance = "..s_c")
  defC <- defData(defC, varname = "rx", formula = "1;1", dist = "trtAssign")
  
  defCP <- defDataAdd(varname = "c.p", formula = 0, variance = "..s_cp")
  
  defS <- defDataAdd(varname = "s", formula = 0, variance = "..s_s")
  
  defSP <- defDataAdd(varname = "y",
    formula = "..effect * rx * period + c + c.p + s", 
    variance ="..s_sp")
  
  dc <- genData(nsites, defC, id = "site")

  dcp <- addPeriods(dc, 2, "site")
  dcp <- addColumns(defCP, dcp)
  dcp <- dcp[, .(site, period, c.p, timeID)]
  
  ds <- genCluster(dc, "site", n, "id")
  ds <- addColumns(defS, ds)
  
  dsp <- addPeriods(ds, 2)
  setnames(dsp, "timeID", "obsID")
  
  setkey(dsp, site, period)
  setkey(dcp, site, period)
  
  dd <- merge(dsp, dcp)
  dd <- addColumns(defSP, dd)
  setkey(dd, site, id, period)
  
  dd[]
}

Design effect

In their paper, Teerenstra et al develop a design effect that takes into account the baseline measurement. Here are a few key quantities that are needed for the calculation:

The correlation of two subject measurements in the same cluster and same time period is the ICC or \(\rho\), and is:

\[\rho = \frac{\sigma_c^2 + \sigma_{cp}^2}{\sigma_c^2 + \sigma_{cp}^2 + \sigma_s^2 + \sigma_{sp}^2} \]

In order to estimate design effect, we need two more correlations. The correlation between baseline and follow-up random effects at the cluster level is

\[\rho_c = \frac{\sigma_c^2}{\sigma_c^2 + \sigma_{cp}^2}\]

and the correlation between baseline and follow-up random effects at the subject level is

\[\rho_s = \frac{\sigma_s^2}{\sigma_s^2 + \sigma_{sp}^2}\]

A value \(r\) is used to estimate the design effect, and is defined as

\[ r = \frac{n\rho\rho_c + (1-\rho)\rho_s}{1 + (n-1)\rho}\]

If we are able to collect baseline measurements and our focus is on estimating \(\delta_1\) from the model, the design effect is slightly modified from before:

\[ (1 + (n-1)\rho)(2(1-r)) \]

Cross-sectional cohorts

We may not be able to collect two measurements for each subject at a site, but if we can collect measurements on two different cohorts, one at baseline before the intervention is implemented, and one cohort in a second period (either after the intervention has been implemented or not, depending on the randomization assignment of the cluster), we might be able to reduce the number of clusters.

In this case, \(\sigma_s^2 = 0\) and \(\rho_s = 0\), so the general model reduces to

\[ Y_{ijk} = \alpha_0 + \alpha_1 k + \delta_{0} Z_j + \delta_{1} k Z_{j} + c_j + cp_{jk} + sp_{ijk} \]

dd <- crt_base(effect = 2.4, nsites = 20, n = 30, s_c=6.8, s_cp=2.8, s_s=0, s_sp=54.4)

dd <- crt_base(effect = 2.4, nsites = 200, n = 100, s_c=6.8, s_cp=2.8, s_s=0, s_sp=54.4)

fit3 <- lmer(y ~ period*rx+ (1|timeID:site) + (1 | site), data = dd)
tbl_regression(fit3, tidy_fun = broom.mixed::tidy)  %>% 
  modify_footnote(ci ~ NA, abbreviation = TRUE)

s_c <- 6.8
s_cp <- 2.8
s_s <- 0
s_sp <- 54.4

rho <- (s_c + s_cp)/(s_c + s_cp + s_s + s_sp)
rho_c <- s_c/(s_c + s_cp)
rho_s <- s_s/(s_s + s_sp)

n <- 30

r <- (n * rho * rho_c + (1-rho) * rho_s) / (1 + (n-1) * rho)

(des_effect <- (1 + (n - 1) * rho) * 2 * (1 - r))
## [1] 4.3
des_effect * 350 / n
## [1] 50

replicate <- function() {
  dd <- crt_base(2.4, 52, 30, s_c = 6.8, s_cp = 2.8, s_s = 0, s_sp = 54.4)
  fit3 <- lmer(y ~ period * rx+ (1|timeID:site) + (1 | site), data = dd)
  
  coef(summary(fit3))["period:rx", "Pr(>|t|)"]
}

p_values <- mclapply(1:1000, function(x) replicate(), mc.cores = 4)

mean(unlist(p_values) < 0.05)
## [1] 0.8

Repeated measurements

We can reduce the number of clusters further if instead of measuring one cohort prior to the intervention and another after the intervention, we measure a single cohort twice - once at baseline and once at follow-up. Now we use the full model that decomposes the subject level variance into a time invariant effect (\(c_j\)) and a time varying effect \(cp_{jk}\):

\[ Y_{ijk} = \alpha_0 + \alpha_1 k + \delta_{0} Z_j + \delta_{1} k Z_{j} + c_j + cp_{jk} + s_{ij} + sp_{ijk} \]

dd <- crt_base(effect=2.4, nsites=20, n=30, s_c=6.8, s_cp=2.8, s_s=38, s_sp=16.4)

dd <- crt_base(effect = 2.4, nsites = 200, n = 100, 
  s_c = 6.8, s_cp = 2.8, s_s = 38, s_sp = 16.4)

fit4 <- lmer(y ~ period*rx + (1 | id:site) + (1|timeID:site) + (1 | site), data = dd)
tbl_regression(fit4, tidy_fun = broom.mixed::tidy)  %>% 
  modify_footnote(ci ~ NA, abbreviation = TRUE)

s_c <- 6.8
s_cp <- 2.8
s_s <- 38
s_sp <- 16.4

rho <- (s_c + s_cp)/(s_c + s_cp + s_s + s_sp)
rho_c <- s_c/(s_c + s_cp)
rho_s <- s_s/(s_s + s_sp)

n <- 30

r <- (n * rho * rho_c + (1-rho) * rho_s) / (1 + (n-1) * rho)

(des_effect <- (1 + (n - 1) * rho) * 2 * (1 - r))
## [1] 3.1
des_effect * 350 / n
## [1] 37

replicate <- function() {
  dd <- crt_base(2.4, 38, 30, s_c = 6.8, s_cp = 2.8, s_s = 38, s_sp = 16.4)
  fit4 <-  lmer(y ~ period*rx + (1 | id:site) + (1|timeID:site) + (1 | site), data = dd)
  
  coef(summary(fit4))["period:rx", "Pr(>|t|)"]
}

p_values <- mclapply(1:1000, function(x) replicate(), mc.cores = 4)

mean(unlist(p_values) < 0.05)
## [1] 0.79

Repeated measurements - ANCOVA

We may be able to reduce the number of clusters even further by changing the model so that we are comparing follow-up outcomes of the two treatment arms (as opposed to measuring the differences in changes as we just did). This model is

\[ Y_{ij1} = \alpha_0 + \gamma Y_{ij0} + \delta Z_j + c_j + s_{ij} \]

where we have adjusted for baseline measurement \(Y_{ij0}.\) Even though the estimation model has changed, I am using the exact same data generation process as before, with the same effect size and variance assumptions:

dd <- crt_base(effect = 2.4, nsites = 200, n = 100, 
  s_c = 6.8, s_cp = 2.8, s_s = 38, s_sp = 16.4)

dobs <- dd[, .(site, rx, id, period, timeID, y)]
dobs <- dcast(dobs, site + rx + id ~ period, value.var = "y")

fit5 <- lmer(`1` ~ `0` + rx + (1 | site), data = dobs)
tbl_regression(fit5, tidy_fun = broom.mixed::tidy)  %>% 
  modify_footnote(ci ~ NA, abbreviation = TRUE)

(des_effect <- (1 + (n - 1) * rho) * (1 - r^2))
## [1] 2.7
des_effect * 350 / n
## [1] 31

replicate <- function() {
  
  dd <- crt_base(2.4, 32, 30, s_c = 6.8, s_cp = 2.8, s_s = 38, s_sp = 16.4)
  dobs <- dd[, .(site, rx, id, period, timeID, y)]
  dobs <- dcast(dobs, site + rx + id ~ period, value.var = "y")

  fit5 <- lmer(`1` ~ `0` + rx + (1 | site), data = dobs)
  coef(summary(fit5))["rx", "Pr(>|t|)"]
}

p_values <- mclapply(1:1000, function(x) replicate(), mc.cores = 4)

mean(unlist(p_values) < 0.05)
## [1] 0.78

Next steps

These simulations confirmed the design effects derived by Teerenstra et al. In the next post, we will turn to baseline measurements in the context of a stepped wedge design, to see if these results translate to a more complex setting. The design effects themselves have not yet been derived. In the meantime, to get yourself psyched up for what is coming, you can read more generally about stepped wedge designs here, here, here, here, here, and here.

Reference: