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C r o s s - o v e r t r i a l s i n p r a c t i c e : C r o s s - o v e r t r i a l s i n p r a c t i c e : t a l e s o f t h e u n e x p e c t e dt a l e s o f t h e u n e x p e c t e d

Previously we compared the cross-over trial1 to the subtle knife used by one of the characters in Philip Pullman’s trilogy His Dark Materials2,3 and showed what a sharp tool it can be. The trial used as an illustration was one for two treat-ments that had two sequences AB and BA and lasted for two periods. This 2×2 trial, as it is often referred to, is a handy and useful knife to have in the toolkit of the practicing statisti-cian, but is nevertheless limited in what it can achieve. Unlike the fi ctional subtle knife, which can cut through any material and so is the only tool needed, the 2×2 trial is only useful when certain conditions apply. The most limiting of these is the need to assume that there is no carry-over effect of one treatment to another. Also, of course, there is a need for cross-over trials that compare more than two treatments. In this article we describe and illustrate cross-over designs for two treatments that have three periods. Cross-over designs for three and four treatments will follow in a future piece.

Returning to Philip Pullman’s trilogy, one of the central characters, Lyra, comes into pos-

session of the golden compass which she can use to tell the future. This allows her and her companions to know what the future holds and to plan accordingly. Unfortunately, in the real world we do not have such aids and must rely on experience and skill to plan ahead. In the phar-maceutical industry, for example, the trials that are run are often non-standard and the required designs cannot be found in standard texts. In addition the results are sometimes not what are expected. The statistician must therefore be in-novative in the choice of design—and this is the theme of this article. Unlike the fi ctional Lyra, we cannot know the future with certainty. However, as statisticians we can use past data to help determine what trends we might see in future data. This, in conjunction with the cur-rent state of knowledge, helps us determine which designs out of many might be the most suitable for the current task.

Here, we hope to give at least a fl avour of the variety of designs that are needed in practice. We begin by adding a third period to a cross-over design for two treatments.

Two-treatment designs with three periods

In the previous article1 it was pointed out that the presence of carry-over effects in the 2×2 trial meant that this design could not be used unless the carry-over effects could be “washed-out” by interposing a suitably long enough period of time between the two active treatment periods. This

extends the time the trial will take to complete and is often an unattractive option. Given certain assumptions about the nature of the carry-over effects, they can be estimated and eliminated from the comparison of the treatments by add-ing a third period to the design. An example of such a design is given in Table 1. Here, we see that this is the original 2×2 design with an extra period. In this additional period the treatment in the second period is repeated.

Now that we have a third period we can con-ceive of the possibility that, if there are carry-over effects, the carry-over effect of a treatment given in the fi rst period could still be present at the start of the third period. However, it is usu-ally the case that such “second-order” carry-over effects are extremely unlikely. We therefore only allow for the possibility that a carry-over effect can persist into the period immediately following (so-called “fi rst-order” carry-over effects). Given some assumptions on the nature of the carry-over effect, a statistical model can be fi tted to the data from such a trial that will not only allow the treatment difference to be estimated, completely free of the carry-over effects, but this estimate is independent of (orthogonal to) the estimate of the difference in the carry-over effects. It

In a previous Toolkit article, Byron Jones compared the cross-over trial to the fi ctional “subtle knife”, which can

cut any substance. Here, he and Scott Haughie explain that using cross-over trials in real-life requires skill and

innovation.

Table 1. 2x3 cross-over design

Group Period 1 Period 2 Period 3

1 A B B2 B A A

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also goes without saying that the difference in carry-over effects can also be estimated using within-patient information. One of the key as-sumptions to make all this possible is that the carry-over effects of A and B are constants that do not depend on which treatment is allocated in the following period.

The design in Table 1 is an example of what we might call a “standard design”. Many others, for three and four periods and with two, four or six sequence groups (including perhaps, all the useful ones) are described by Jones and Ken-ward4. These designs have a certain symmetry and structure that gives them appealing math-ematical and statistical properties. However, in real life some of the symmetry and structure has to be given up in order to meet the scientifi c and practical needs of a clinical trial. The following is an example of where this was the case.

Example 1: exploratory trial

This trial compared an active treatment (B) to a placebo treatment (A) in patients suffering from a particular disorder. In addition to assessing the drug effect, it was also of interest to assess the within-patient variability of the study endpoint between identical doses of the same study drug (B). The design used is given in Table 2, where each active period was separated by a wash-out period of at least 1 week. Eight patients were assigned to each treatment sequence. It can be seen that a key property of this design is that each patient receives treatment B on two oc-casions. This is necessary if the within-patient variability of B is to be estimated. It was not of interest to give repeated administrations of the placebo (A).

The conclusions from this trial were rather unexpected (which, given the theme of this article, should not be a surprise). Before esti-mating the within-patient variance between the two repeats of B (let us call them B1 and B2, where B1 is the fi rst administration of B and B2 is the second) it was considered prudent to check that B1 and B2 were not different. Before we say what the results of doing this were, it is useful to consider the available degrees of freedom for this design. What are degrees of freedom? (Well it’s not what you’re allowed to do and get away with, if that’s what you thought!) It is a number that tells you how many independent parameters you can estimate from a given model and design.

This trial will provide a mean response for each cell in Table 2. These nine cells therefore have nine degrees of freedom. It is usual to measure parameters relative to the overall mean response and so one degree of freedom is taken up with estimating this mean, leaving eight. These eight are divided as follows: two for the differences between the groups (sequence effects), two for the differences between the periods (period ef-fects) and two for the differences between the three treatments (A, B1 and B2), leaving an-other two. These two are somewhat mysterious because they have two identities. One identity is when they refer to the treatment-by-period interaction. The other is when they refer to the differences in carry-over effects. Of course, liking the air of mystery they possess, they do not let on which identity they have at any one time. Statisticians refer to this phenomenon as alias-ing, and it can cause much confusion.

The only good thing about these aliased ef-fects is that only one, unique, statistical test is needed to determine if they are zero or not. If they are zero, then the problem of aliasing is solved. Unfortunately, in our case the test for the effects related to these last two degrees of freedom were highly signifi cantly different from

zero. As it was thought unlikely that carry-over effects could be present in this trial, the alias-ing was solved by assuming that the degrees of freedom referred to the treatment-by-period in-teraction identity. Of course, the knowledgeable reader will realise that the carry-over effects are a particular form of treatment-by-period interac-tion. However, this particular form is so special a case that it is better to consider it in its own right, as we have done here.

After some consideration it was clear that any differences between B1 and B2 were mixed up with the interaction effects. Plotting the means for each treatment in each period, (see Figure 1) is a good way to try and make sense of the interaction effects. Looking at Figure 1, we can see that the means in the second group (B1, B2, A) are almost constant. We can only speculate on why this was the case.

As a design for three treatments, this is a poor design. Of course, at the planning stage it was not thought likely that the interaction effects would be present. The reason why the design is not so good is because, of the two administrations of B, B1 appears in period 1 but B2 does not (by defi nition), and B2 appears in

period 3 but B1 does not (again by defi nition). So there is a high degree of correlation between the estimated period and treatment effects. One way round this, which was done as one of the analyses of this trial, is to consider the peri-ods as a random effect. This then breaks their strong link to the treatments. This is not a bad assumption because the actual periods were not the same for each patient, as the patients were sequentially recruited over time. It was chance that determined when a patient came into the trial. The more usual assumption of three fi xed period effects can be considered as a simplifi -cation that accounts for the average effects of the periods, which more correctly we should refer to as the fi rst period the patient receives a treatment, the second period a patient receives a treatment, etc., rather that thinking of them as three periods fi xed in chronological time (see Jones and Kenward4, for defi nitions of fi xed and random effects). We also looked at including the pre-period baseline values as a covariate to help explain the within-patient changes but this did not result in any modifi cations to our conclu-sions. Finally, you can imagine that the results of this trial meant that the trials originally planned to follow on from this one would need re-assess-ment in the light of the unexpected results. Such is life in pharmaceutical research!

References1 Jones, B. (2008) The cross-over trial: a subtle

knife. Signifi cance, 5, 135–137.2 Pullman, P. (2007a) The Subtle Knife.

Scholastic: London.3 Pullman, P. (2007b) Northern Lights.

Scholastic: London.4 Jones, B. and Kenward, M. G. (2003) Design

and Analysis of Cross-over Trials, 2nd edn. Boca Raton, FL: Chapman and Hall/CRC.

Both authors are statisticians employed by Pfi zer Global Research and Development at Sandwich, Kent, UK. Byron Jones is a Senior Director in the Statistical Research and Consulting Centre, and Scott Haughie is a Director in the Urology and Sexual Health Therapy Area. Byron Jones holds honorary professorships at University College London and the London School of Hygiene and Tropical Medicine.

Symmetry is appealing, but some symmetry has to

be given up to meet practical needs.

period

mea

n re

spon

se

1 2 3

010

2030

40

AB1

B2B1 B2 A

B1

A

B2

Figure 1. Groups-by-periods plot for Example 1.

Table 2. Non-standard cross-over design for two treatments

Group Period 1 Period 2 Period 3

1 A B B2 B B A3 B A B