hip protectors. We provided three hip protectors per resident … .
Clearly if an extreme intervention has little or no demonstrable effect, then a less extreme intervention is also likely to be ineffective. Nevertheless, one has to be cautious in pushing the extent of the intervention too far as it may be that less intervention also has the desired effect. Thus, one might be concerned, for example, that one of the components (structured education of staff or provision of three hip protectors per resident) of the intervention for elderly residents may not be essential to achieve the reduction in the hip fracture rates. As an extreme example, if cure can be achieved with dose d/2, then it would be foolish to give patients dose d. These issues have to be debated thoroughly by the trial design team.
2.6 Choice of design
The final choice of the design for the trial will depend crucially on the questions posed, and these will be a key determinant of the interventions that are to be compared. Clearly if there are only two interventions involved, then one option for the design is the two‐group parallel trial illustrated in Figure 2.1. We discuss other options including cross‐over and split‐mouth (Chapter 13), repeated measures (Chapter 14), non‐inferiority (Chapter 15), cluster (Chapter 16) and stepped wedge (Chapter 17) designs.
However, even within the structure of the simplest of all comparative trial designs, there are options that have to be considered. Although randomisation is mandatory for such a design, the choice of the allocation ratio of standard to test has to be agreed. Statistical considerations of efficiency usually favour a 1 : 1 allocation but other issues may predominate such as, for example, the availability of the test compound in a drug trial. The final choice of allocation ratio will influence the number of participants required to some extent and may complicate the informed consent process if (say) an option other than equal allocation is chosen and which may then be more difficult to explain or justify in lay terms.
Further, as is suggested by the hierarchy of Figure 1.2, the options for presenting the interventions in a blinded or masked manner need to be discussed. In many circumstances, no blinding is possible so that an ‘open’ trial is conducted. In such cases, it is very important that the endpoint assessments are determined in as objective and reproducible manner as is possible.
If more than two interventions are to be compared, then the number of design options increases and which to choose may crucially depend on the presence or absence of structure of the options under test. For example, if one is comparing three (or more) entirely different drugs none of which can be considered as standard, the chosen design may be quite obviously a parallel three‐group design with randomisation of equal patient numbers assigned to each, although how to determine the appropriate trial size is less clear. Alternatively, if one of the drugs can be considered a standard then strategies for sample size calculation tend to be more clear‐cut, as would be the case if the three drugs were in fact three different doses of the same drug. These issues are discussed in Chapter 12.
In certain situations, it may be possible to ask two (therapeutic) questions within the same trial design rather than to conduct two separate two‐group trials. For example, in the trial conducted by Yeow, Lee, Cheng, et al. (2007), and which we describe in greater detail in Chapter 12, infants are randomised to one of two types of surgery and also to whether the operation should be undertaken at 6 months or 1 year of age. Thus, the two questions posed concern (i) the choice of surgery and (ii) when the surgery should be performed. The infants recruited to this so‐called 2 × 2 or 22, factorial design, are then randomised to one of the four options in equal proportions.
When the endpoint of concern is also a measure that can be assessed at baseline, that is immediately prior to randomisation then, whatever the design structure, such information may be used to improve the statistical efficiency of the corresponding analysis. Thus, in the trial of Meggitt, Gray and Reynolds (2006) of Example 1.7, the disease activity of a patient’s eczema was determined using the SASSAD score. This was assessed at −2 weeks and at baseline (0) immediately prior to randomisation, and then postrandomisation at 4, 8 and 12 weeks during the course of treatment. In brief, the analysis consisted of calculating the slopes of the individual patient regression lines using their post‐treatment values. From these, the change from the date of randomisation was determined giving the values shown earlier in Figure 1.1. The increase in sensitivity accords with what clinicians would expect, because the measure evaluates within‐patient change over the whole trial period. Albeit using a statistical analysis that does not explicitly use baseline scores. Such repeated measures designs are discussed in Chapter 14, where it is shown that increasing the number of pre‐ and postrandomisation measurements impacts on reducing the final numbers of subjects that need to be recruited. A reduction may be achieved even in the simplest situation of a single (baseline) measure together with one postrandomisation assessment on every recruited individual.
However, obtaining the necessary regulatory approval of the trial may inhibit the choice of design that one may wish to conduct. For example, the committee may find unacceptable on ethical grounds the double‐placebo arm in a proposed 2 × 2 factorial design or may suggest that this makes obtaining consent difficult and could therefore compromise the ability to recruit the required numbers of patients. Thus, in some cases, the best experimental design may not be a practical option for the investigation and a balance has to be struck between what is statistically optimal and what is feasible.
We discuss details of how the size of a trial is determined in Chapter 9.
2.7 Assigning the interventions
A crucial role of randomisation is to ensure that there are no systematic differences between the patient groups assigned to the different interventions. To preserve this situation, we need to, at all cost, avoid losing patients subsequent to randomisation, and we want to maximise the probability that the allocated treatment is indeed applied. Hence, it is extremely important to minimise the delays between consent, randomisation and the commencement of therapy.
In an ideal setting, once a patient has consented to take part in a clinical trial, randomisation should take place immediately. Once the treatment allocation is known, therapy should begin immediately following that. This minimises delay and avoids the patient having the opportunity to change his or her mind before therapy begins. This helps to prevent the dilution that can occur if a patient refuses the allocated treatment or switches to the comparator option in the period between randomisation and starting treatment. As we will discuss later, for purposes of analysis, such patients are retained in the treatment group to which they were allocated. Consequently, for example, a patient who switches from intervention A to B will still be retained in A for analysis, and this will make the effect of B appear more similar to that of A than might truly be the case. Thus, the prospect of dilution should be anticipated at the design stage and all steps taken to reduce this possibility to a minimum.
