A Textbook of Clinical Pharmacology and Therapeutics

88 INTRODUCTION OF NEW DRUGS AND CLINICAL TRIALS

between diagnosis and treatment, individual differences in
determining entry criteria, facilities for treatment of complica-
tions, differing attitude to pain control, ease of transport, etc.

INCLUSION AND EXCLUSION CRITERIA

For any study, inclusion and exclusion criteria must be defined.
It is essential to maximize safety and minimize confounding
factors, whilst also ensuring that the criteria are not so strict
that the findings will be applicable only to an unrepresenta-
tive subset of the patient population encountered in usual
practice. The definition of a healthy elderly subject is problem-
atic. Over the age of 65 years, it is ‘normal’ (in the sense that it
is common) to have a reduced creatinine clearance, to be on
some concomitant medication and to have a history of allergy.
If these are exclusion criteria, a trial will address a ‘superfit’
elderly population and not a normal population.

DOUBLE-BLIND DESIGN

A ‘double-blind’ design is often desirable to eliminate psycho-
logical factors such as enthusiasm for the ‘new’ remedy. This
is not always possible. For example, if in the comparison of
treatment A and treatment B described above, treatment A
consists of regular intravenous infusions whilst treatment B
consists of oral medication, the ‘blind’ is broken. As ‘survival’
duration is ‘hard’ objective data, this should not be influenced
markedly, whereas softer end-points, such as the state of well-
being, are more easily confounded. In trials where these are
especially important, it may be appropriate to use more elabor-
ate strategies to permit blinding, such as the use of a ‘double
dummy’ where there is a placebo for both dosage forms. In
this case patients are randomized to active tablets plus placebo
infusion or to active infusion plus placebo tablets.

WITHDRAWALS

The number of patients who are withdrawn from each treat-
ment and the reason for withdrawal (subjective, objective or
logistic) must be taken into account. For example, if in an anti-
hypertensive study comparing two treatments administered
for three months only the data from those who completed three
months of therapy with treatment X or Y are analysed, this may
suggest that both treatments were equally effective. However,
if 50% of the patients on treatment X withdrew after one week
because of lack of efficacy, that conclusion is erroneous. Again,
if patients are withdrawn after randomization but before dos-
ing, this can lead to unrecognized bias if more patients in one
group die before treatment is started than in the other group,
leading to one group containing a higher proportion of fitter
‘survivors’. Conversely, if patients are withdrawn after ran-
domization but before dosing, adverse events cannot be attrib-
uted to the drug. Hence both an ‘intention-to-treat’ analysis
and a ‘treatment-received’ analysis should be presented.

PLACEBO

If a placebo control is ethical and practical, this simplifies

interpretation of trial data and enables efficacy to be deter-

mined more easily (and with much smaller numbers of sub-

jects) than if an effective active comparator is current standard

treatment (and hence ethically essential). It is well recognized

that placebo treatment can have marked effects (e.g. lowering

of blood pressure). This is partly due to patient familiarization

with study procedures, whose effect can be minimized by a

placebo ‘run-in’ phase.

TRIAL DESIGN

There is no one perfect design for comparing treatments.

Studies should be prospective, randomized, double-blind and

placebo-controlled whenever possible. Parallel-group studies

are those in which patients are randomized to receive different

treatments. Although tempting, the use of historical data as a

control is often misleading and should only be employed in

exceptional circumstances. Usually one of the treatments is

the standard, established treatment of choice, i.e. the control,

whilst the other is an alternative – often a new treatment which

is a potential advance. In chronic stable diseases, a crossover

design in which each subject acts as his or her own control can

be employed. Intra-individual variability in response is usu-

ally much less than inter-individual variability. The treatment

sequence must be evenly balanced to avoid order effects and

there must be adequate ‘washout’ to prevent a carry-over

effect from the first treatment. This design is theoretically

more ‘economical’ in subject numbers, but is often not appli-

cable in practice.

STATISTICS

It is important to discuss the design and sample size of any

clinical trial with a statistician at the planning phase.

Research papers often quote Pvalues as a measure of whether

or not an observed difference is ‘significant’. Conventionally,

the null hypothesis is often rejected if P 0.05 (i.e. a difference

of the magnitude observed would be expected to occur by

chance in less than one in 20 trials – so-called type I error, see

Figure 15.2). This is of limited value, as a clinically important

difference may be missed if the sample size is too small (type II

error, see Figure 15.2). To place reliance on a negative result,

the statistical power of the study should be at least 0.8 and

preferably 0.9 (i.e. a true difference of the magnitude pre-

specified would be missed in 20% or 10% of such trials,

respectively). It is possible to calculate the number of patients

required to establish a given difference between treatments at

a specified level of statistical confidence. For a continuous

variable, one needs an estimate of the mean and standard

deviation which one would expect in the control group. This is

usually available from historical data, but a pilot study may be

necessary. The degree of uncertainty surrounding observed