Design paperThe utility of partial cross-over designs in early phase randomized prevention trials
Introduction
In double-blind randomized clinical trials, there are two popular and straightforward designs that have been a mainstay of clinical researchers for many years:
- 1.
The parallel groups design.
- 2.
The cross-over design.
In this note, we explore the design issues centered around phase II type investigations, having limited resources, where the goal is to determine whether or not to proceed to a phase III trial, e.g. a phase II federally funded prevention trial may have funding capped by an the RO3 mechanism. In this setting, resources are often scarce, sample sizes are often limited and information about the treatment is limited, especially in terms of the optical dose response and the duration of the effect.
Usually, in phase II type investigations, the design choice comes down to the classic parallel versus cross-over design (a small function of designs tend to be factorial in nature) and depends upon an endless list of factors such as:
- 1.
Patient safety (increased chance of toxicities).
- 2.
Disease type (chronic or acute).
- 3.
Resources (small grants, competition for subjects).
- 4.
Outcome of interest (censoring or not).
- 5.
Patient recruitment (attractiveness of one or the other design).
- 6.
Equivalence versus superiority.
- 7.
Logistical considerations.
- 8.
Washout period and carryover issues.
- 9.
Anticipated differential dropout rates.
In general, the choice of a 2×2 cross-over design relative to a two-arm parallel groups design in superiority trials comes down to the perception by clinicians of greater efficiency, i.e. it is assumed that fewer subjects are needed to carry out a test of treatment mean differences or other measures of centrality for the cross-over design relative to the parallel groups design. It is basically true that under ideal conditions that at least twice as many subjects are needed for the simple parallel design versus a cross-over design. Say for example we are interested in testing two treatments for differences in mean outcome and we wish to choose between the two-arm parallel groups design with a final outcome versus a 2×2 cross-over design.
In the simplest case assume no carryover effect, no period effect and a straightforward randomization scheme (equally balanced sample size). Also denote the treatment 1 outcome as T1 and the treatment as 2 outcome T2, respectively. Assume that for both designs that E(T1)=μ1, E(T2)=μ2, Var(T1)=Var(T2)=σ2 and that for the cross-over design Cov(T1, T2)=σ2ρ between treatment periods. If T1 and T2 are normally distributed, univariate for the parallel design and bivariate for the cross-over design, then E(T¯1−T¯2)=μ1−μ2 for either design. The relative efficiency of the test statistics T¯1−T¯2 for the parallel design relative to the cross-over design is simply (1−ρ)/2. As ρ edges closer to 0, the efficiency is closer to 1/2. In this case, the perceived gain in efficiency does not necessarily translate into a greater savings if expensive blood chemistries, diagnostic tests, etc. make up the bulk of the cost of the trial. In this instance, the overall cost of a simple parallel design with one measure per subject will basically be similar to the cross-over design with two measures per subject. In some instances, once potential dropouts are considered, the parallel design with twice as many subjects may actually prove more cost effective. Note also that the very nature of the cross-over trial increases the likelihood of a differential drop-out as compared to a parallel design, i.e. the missing at random (MAR) assumption may no longer be valid. This increases the likelihood of a biased estimate of treatment effect. Thus, any gains in efficiency for the cross-over design are potentially wiped out by an increased likelihood of a biased estimate of treatment effect.
A second key factor that speaks more to the 2×2 cross-over design is that all subjects have the opportunity to receive the active drug. This may offer added inducement to participate because randomization to placebo is temporary. This factor may actually be more important in choosing a design than the statistical properties. Note, however, there are many biological factors to consider that weigh against carrying out a cross-over designs, such as a potential curative treatment [3].
In phase II type prevention trials, oftentimes, researchers are interested in the cumulative effect of a given vitamin, supplement or drug over time at some fixed daily dose in high risk subjects, e.g. mg/day, versus a placebo control. This is in contrast to a typical dose ranging phase II therapeutic trial of a pharmaceutical agent in subjects with disease designed to find the optimal dose per day which may effect a cure or stabilizes a given condition. Oftentimes, the primary outcome of interest in a phase II prevention study, due to the length of disease onset, is to first examine a premalignant lesion or set of biomarkers of disease. Oftentimes, these biomarkers have a great deal of within and across subject variability. In addition, these studies usually involve subjects at a high risk for a disease. Therefore, efficiency in terms of smaller sample sizes is at a premium. In general, these types of studies do not necessarily fall into a design category of cross-over versus placebo and may be suited for a design, which combines the best features of both. Hence, we coin these designs partial cross-over designs. The partial cross-over design is a specific repeated measures design where not all subjects receive all treatments.
Section snippets
Design lay-out
Let Yij(k) denote the outcome of interest for subject i and j over the course of time period k, where i=1,2,…,n and subjects are randomized to one of two sequences, either A: j(k)=0(1), 1(2), 2(3), …, t(p) or B: j(k)=1(1), 2(2), 3(3), …, t+1(p), in a balanced fashion, and p denotes the total number of periods. The value of j=0(1) corresponds to receiving placebo over period k=1. The value of j=1 corresponds to the active cumulative dose administered over the course of the first time period for k
Model formulation
For our model, let us start with general notation assuming a continuous outcome variable. Letwhere the terms in the model are: μ: overall mean; si: the random effect of subject i, i=1,2,…,n, where E(si)=0 and Var(si)=σs2; τj(k): the effect of treatment j at period k, where subjects are randomly assigned to sequence A: j(k)=0(1), 1(2), 2(3), …, t(p) or B: j(k)=1(1), 2(2), 3(3), …, t+1(p); εi(k): random error for subject i in period k, where E(εi(k))=0 and Var(εi(k))=σ2; s
Prevention trial
Recently, we designed a study to determine if selenium supplementation will alter the grade of histologic abnormalities detected in the lung tissue of high-risk patients screened at Roswell Park Cancer Institute (RPCI), Buffalo, NY. The proposal was designed as a randomized comparison of former and current smokers on selenium supplementation versus a placebo control. Subject inclusion criteria consisted of moderate to high levels of smoking exposure, be residents of the Buffalo, NY metropolitan
Acknowledgements
Dr. Hutson's work is partially suppored by a NYSTAR Faculty Development grant. Dr. Reid's work is partially supported by NCI grant CA49764-15. We would like to thank the reviewers for their helpful comments.
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Design and Analysis of Cross-Over Trials
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