Statistics Guide for Research Grant Applicants

B. Clinical Trials

  • B-1 Describing the patient group / eligibility criteria
  • B-2 Describing the intervention (s) / treatment (s)
  • B-3 Choice of control treatment / need for control group
  • B-4 Blindness
  • B-4.1 Double blind and single blind designs
  • B-4.2 Placebos
  • B-5 Randomisation
  • B-5.1 What is randomisation?
  • B-5.2 When might we use randomisation?
  • B-5.3 Why randomise?
  • B-5.4 What is not randomisation?
  • B-5.5 How do we randomise?
  • B-5.6 Randomisation in blocks
  • B-5.7 Randomisation in strata
  • B-5.8 Minimisation
  • B-5.9 Clusters
  • B-5.10 Trial designs
  • B-5.10a Parallel groups
  • B-5.10b Crossover design
  • B-5.10c Within group comparisons
  • B-5.10d Sequential design
  • B-5.10e Factorial design
  • B-6 Outcome variables
  • B-7 Data monitoring
  • B-7.1 Data monitoring committee
  • B-7.2 When should a trial be stopped early?
  • B-8 Informed consent
  • B-8.1 Consent
  • B-8.2 Emergencies
  • B-8.3 Children
  • B-8.4 Mentally incompetent subjects
  • B-8.5 Cluster randomised designs
  • B-8.6 Randomised consent designs
  • B-9 Protocol violation and non-compliance
  • B-10 Achieving the sample size
  • B-11 After the trial is over
  • Worth reading several times is the CONSORT statement, a set of recommendations for improving the quality of reports of parallel group randomized trials.

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    B-1 Describing the patient group and eligibility criteria

    The proposal should contain a clear statement as to what patient group is to be treated in the trial. For example, in a hypertension trial we should specify the range within which patients' blood pressures should lie. This can take the form of a list of inclusion and exclusion criteria. For example, in a trial of a low sodium, high potassium, high magnesium salt in older subjects with mild to moderate hypertension, subjects were recruited from a population based cohort of non-hospitalised older inhabitants of a suburb of Rotterdam (Geleijnse et al. 1994). All subjects had their blood pressure measured between 1990 and 1992. Men and women aged 55-75 with a blood pressure above 140 mm Hg systolic or 85 mm Hg diastolic without antihypertensive treatment (n=419) were invited by letter and telephone for re-measurement of blood pressure. To be eligible for the trial subjects' systolic blood pressure had to be between 140 and 200 mm Hg or diastolic pressure between 85 and 110 mm Hg at two measurements one week apart. In addition, systolic blood pressure had to be not below 130 mm Hg and diastolic pressure not below 70 mm Hg.

    Thus the inclusion criteria were:

    * Member of the Rotterdam cohort
    * Aged 55-75
    * Untreated BP above 140 mm Hg systolic or 85 mm Hg diastolic
    * Current BP between 140 and 200 mm Hg systolic or between 85 and 110 mm Hg diastolic at two measurements one week apart.
    * Systolic pressure not below 130 mm Hg and diastolic pressure not below 70 mm Hg.

    The exclusion criteria were:

    * History of myocardial infarction
    * Angina pectoris
    * Diabetes mellitus
    * Impaired renal function (serum creatinine concentration >200 mumol/l)
    * Eating a salt restricted diet on medical advice

    Ethics committees often want to know about what provision will be made for non-English-speakers. Simply excluding them, while it makes things easy for the researcher, may not be considered acceptable. If we can treat people, we can recruit them to clinical trials of those treatments.

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    B-2 Describing the intervention(s) and treatments

    It may appear self-evident, but it is important to describe the treatment to be tested clearly. Remember that not all those reading your proposal will be clinically qualified, including statisticians. The treatment description must be comprehensible by all. The nature of the treatment may have implications for the trial design, for example for blinding (see B-4), which may not be obvious to those outside your field. You are very close to the subject. You should get someone completely outside the area to read your proposal for you.

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    B-3 Choice of control treatment and need for a control group

    The essence of a trial or experiment is that we carry out a treatment and observe the result. If we are not applying some form of intervention, it is not a trial but an observational study. (see A-1.1) In a clinical trial we are concerned with a treatment to modify a disease process in some way. This can be a medical or surgical treatment, or it might be a less direct intervention, such as supplying treatment guidelines to GPs or carrying out a health education programme.

    To see whether a treatment has an effect, we usually need a control group. (This is not always the case. No control group was used for the first administration of penicillin. The effect was unlike anything ever seen before. Control was provided by general experience of past cases. Controlled trials were carried out later when penicillin was applied to more minor conditions, where the consequences of the infection were not so severe (Pocock 1983). However, such revolutions are very rare and most advances are small. We cannot tell whether a new treatment is effective from a single patient and the difference the treatment makes may not be large.) We need to compare patients given the new treatment with a group of patients who do not receive the new treatment. The latter are known as a control group.

    We need to have a control group which is comparable in all respects to the group of subjects receiving the new treatment: in the same place at the same time with the same distribution of disease severity and prognosis, and receiving the same care apart from the treatment of interest. The most reliable way to do this is by random allocation (see B-5.1, B-5.5) or minimisation (see B-5.8). Other methods, such as alternate allocation, should be avoided (see B-5.4) and would need a strong justification in the proposal, as would methods which do not meet all these criteria, such as patients seen at a different time or in a different place (see B-5.4).

    If we want to do a trial, we usually have a clear idea of what the treatment is which we wish to test. The proposal must explain what this is and why we think it might work, but there is rarely much problem in deciding what the treatment is to be. What treatment the control group will receive may be more debatable. Should the control group receive a treatment at all? If there is no current treatment available, then this question is easily answered: the control group will be untreated, although we may need to apply a dummy treatment to maintain the blindness (see B-4.2). Sometimes a new treatment is given in addition to an existing treatment, the control group may then receive the existing treatment, with a suitable dummy for the new treatment where appropriate. If there is an available treatment, the current Declaration of Helsinki (Clause 32) says that:

    The benefits, risks, burdens and effectiveness of a new intervention must be tested against those of the best current proven intervention, except in the following circumstances:

    The exceptions were added following protests from researchers who want to do trials where the best existing therapy is too expensive, specifically in HIV research in Africa (Ferriman 2001) and from pharmaceutical researchers and drug regulators (Tollman et al. 2001). This did not appear satisfactory to some critics (Bland 2002a, 2002b). Any such trial will need a strong justification in the proposal.

    Sometimes there is more than one possible control treatment. If we want to test a new hypertension treatment, for example, should we compare this to an ACE-inhibitor, a beta-blocker, a diuretic, a salt restriction diet, exercise, or a combination of two or more of these? And which ACE-inhibitor, beta-blocker, etc., should we use and at what dose? We must beware of running a trial which is open to the criticism that the control treatment is not appropriate or is not the best of its type. When there is a choice of control treatment the protocol should contain a justification for the control treatment which has been chosen.

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    B-4 Blindness

    B-4.1 Double blind and single blind designs

    Bias in response can occur through subconscious effects. A patient's response may be affected by knowing which treatment he is receiving, either through a belief that a particular treatment is or is not beneficial or through a desire to please the clinician. Further, an observer's evaluation may be affected by knowing which treatment a patient is receiving, particularly in a trial comparing an active and an inert drug. For these reasons it is preferable that neither the patient nor the assessor knows which treatment the patient is receiving. This is known as double blind assessment. Sometimes it is only possible for one party to be unaware of the treatment, in which case the trial is single blind. This most often occurs when only the patient is blind because it is often impossible for the clinician to be unaware of the treatment. For example if the intervention is a form of surgery. Sometimes, the assessment can be done blind even when the patient and clinician cannot be blinded. For example if the assessment is an x-ray which can be scored by an independent observer who does not know which treatment the subject has received. It is always best if the maximum degree of blindness is achieved and applicants should describe exactly how this will be done.

    It is also desirable that the person entering patients into the trial does not know which treatment the next patient will receive. Ways of achieving this are described in section B-5. Double blind trials clearly require that the treatments are indistinguishable to the patient and to the assessor.

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    B-4.2 Placebos

    If we wish to conduct a double blind trial to compare a new treatment with no treatment we need to give the control group a dummy pill or placebo. This makes the two treatments indistinguishable and prevents psychological effects whereby a patient's condition may improve simply due to the knowledge that he is receiving a particular treatment. This psychological response to treatment is known as the placebo effect. Placebo tablets should be identical in appearance and taste to the active treatment, but be pharmacologically inactive. The use of placebos enables us to assess any benefit or side effects of the new treatment. The placebo effect can be very strong. For example in a trial of analgesics three active drugs were compared with a placebo, but in addition each drug was manufactured in four colours. It turned out that overall, the active treatments did better than the placebos but strangely, red placebos were as effective as the active drugs (Huskisson 1974).

    Placebos can be used in non-drug trials but their use may not be ethical. For example in a vaccination trial a saline injection could be used but may not be ethically acceptable. Sometimes we may wish to compare two drugs which cannot be made to look alike. In this case to maintain blindness we can use a double dummy - i.e. we give each patient two drugs, the allocated active one and a placebo resembling the alternative one. An example would be if we were to compare a tablet with a cream. Then each patient would get either an active tablet plus a placebo cream or a placebo tablet plus active cream.

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    B-5. Randomisation

    B-5.1 What is randomisation?

    Randomisation or random allocation is a method of dividing subjects into groups in such a way that the characteristics of the subject do not affect the group to which they are allocated. To achieve this, we allow chance to decide which group each subject is allocated to. Thus each subject is equally likely to be allocated to any of the available groups and any differences between these groups happen by chance. In a clinical trial, randomisation can be used to decide which treatment each subject should receive. For example in a trial of a new treatment versus an existing treatment, randomisation can be used to ensure that each subject has the same chance of receiving either the new or the existing treatment.

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    B-5.2 When might we use randomisation?

    We can use randomisation in any experimental study where we wish to compare groups receiving different interventions. These can be studies of humans, animals, or some other biological or organisational unit. A typical example where randomisation is used is for a clinical trial comparing individuals receiving one of two treatments. We can also use randomisation when we wish to assign individuals to more than two groups or when we are assigning whole groups of individuals to different intervention groups. An example of this would be assigning whole general practices to receive one of two different interventions. This is known as cluster randomisation (see B-5.9)

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    B-5.3 Why randomise?

    There are three reasons why randomisation is preferred in clinical trials. Firstly, we want to be able to assess the difference between the treatments in an unbiased way. We want to be able to conclude that any differences that we observe between the treatment groups are due to differences in the treatments alone. We do not want differences between the subjects themselves to confound the treatment differences. Without randomisation, treatment comparisons may be prejudiced, whether consciously or not, by selection of participants of a particular kind to receive a particular treatment (CONSORT statement). Random allocation does not guarantee that the groups will be identical apart from the treatment given but it does ensure that any differences between them are due to chance alone.

    Secondly, randomisation facilitates the concealment of the type of treatment from the researchers and subjects to further reduce bias in treatment comparison. (see B-4). Thirdly, randomisation leads to treatment groups which are random samples of the population sampled and thus makes valid the use of standard statistical tests based on probability theory.

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    B-5.4 What is not randomisation?

    Some trials have compared current patients receiving a new treatment with former patients treated with an existing treatment. These patients are not randomly allocated. Historical controls may differ from current patients in many ways and do not provide an unbiased comparison to current patients given a new treatment (see B-3).

    Another common approach is to use a method of systematic allocation. Examples include alternate allocation (A B A B etc) and using date of birth or date of enrolment to study (e.g. even date = A and odd date = B). We have seen grant applications and even papers in journals which clearly state that the allocation was performed at random but where the authors have then later indicated that subjects were allocated alternately to treatments. While such schemes are in principle unbiased, problems arise from their openness since it is well known that people with access to the procedure sometimes change the allocation, albeit for altruistic purposes. For these reasons systematic allocation is not recommended unless there is really no alternative.

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    B-5.5 How do we randomise?

    The obvious and most simple way to randomise is to use a physical method. Physical randomisation methods have been in use since the first Stone Age man cast a couple of knucklebones. For example, we could toss a coin when a patient is recruited into the trial. Randomisation is usually described in this way on patient information sheets. We do not usually do this in practice, however. The main reason is the lack of an audit trail. We cannot check back to ensure that the random allocation was done correctly. An external observer could not be satisfied that the researchers had not tossed the coin again if they did not like the result, for example. For these reasons` the random allocation should be determined in advance. We could toss the coin in advance and produce a list of allocations before any patients are recruited to the trial. This would be done by someone who will not see any of the trial subjects and the allocation concealed from those recruiting patients into the trial. In a large trial this would be extremely tedious.

    Instead we use pseudorandom numbers generated by a mathematical process. There are tables of random numbers, usually generated by a computer program, which can be used to generate the random sequence. For example, given such a table we could choose a random starting point in it by throwing dice or some other similar method. We then produce a list of allocations by odd number = new treatment, even number = old treatment. (Bland 2000 gives examples.) However, now that computers are so easily available, we usually cut this stage out and use the computer directly. It is not difficult to write a computer program to carry out random allocation. Our web directory of randomisation software and services lists some, including our own completely free DOS program Clinstat. Such a program can print out a randomisation list in advance. We think it is very important that the method of randomisation be described in the application.

    After the randomisation list has been prepared by someone who will not be involved in recruitment to the trial, it must be made available to researchers. This can either be at long range, by telephone from the clinic, or the randomisation can be physically present at the recruitment point. One way to do this is to put the allocation into envelopes. It is important that these envelopes be opaque, as there are well-attested cases of researchers holding envelopes to a lamp in order to read what is written inside. For the same reason these envelopes should be numbered so that the recruiter has to take the next envelope. Shuffling envelope placed in a box is not a good idea. This is a physical method which leaves no audit trail.

    The researchers should not be given an open randomisation list, so that they know the treatment to which the next potential recruit to the trial will be allocated. This is a really bad idea. It has been shown that the differences in outcome between treatment groups are considerably larger in trials where allocation is open in this way. It produces a clear bias.

    Long range allocation by telephone is suited to large trials and multi-centre trials in particular. It requires that there be someone in the office to take the call. This may be throughout normal office hours or twenty-four hours a day, depending on the disease being studied. This is difficult for researchers to organise for their own trial, so we usually use a commercial trials office for this. These provide a twenty-four hour phone line, often computer operated, which gives the randomisation. Our web directory of randomisation software and services lists some service providers and their contact details.

    It is a good idea to keep track of randomisation. From time to time check that the distribution of variables such as age, sex, important prognostic variables is similar in each treatment group. This is particularly important when a third party is providing randomisation by telephone.

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    B-5.6 Randomisation in blocks

    If we wish to keep the numbers of subjects in each group very similar at all times, then we use block randomisation. For example, suppose we have two treatments A and B and we consider subjects in blocks of four at a time. There are six ways of allocating treatments to give two A's and two B's:

    1. AABB  2. BBAA  3. ABAB  4. BABA  5. ABBA  6. BAAB

    If we use combinations of these six ways of allocating treatments then the numbers in the groups can never differ by more than two at any point in the trial recruitment. We can choose blocks at random to create the allocation sequence using random numbers (1 gives AABB, 2 gives BBAA etc and we ignore random numbers other than 1-6). Block allocation can also be done using a computer. Our web directory of randomisation software and services lists some suitable programs.

    In clinical trials it is best if those giving the treatments do not know how the randomisation sequence was constructed to avoid their deducing in advance which treatment some patients are to be allocated. For this reason larger block sizes of say 20 are sometimes used in large trials. Such block sequences are virtually impossible to guess. A computer is needed to generate such sequences.

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    B-5.7 Randomisation in strata

    The aim of randomisation is that the groups of patients receiving different treatments are as similar as possible with respect to features which may affect their prognosis. For example we usually want our groups to have a similar age distribution since prognosis is often related to age. There is however no guarantee that randomisation will give balanced groups, particularly in a small trial. Although any differences will have arisen by chance, they may be inconvenient and lead to doubts being cast as to the reliability of the results. One solution to this problem is to use stratified randomisation at the outset for any variables which are strongly prognostic. Another possible approach is to use minimisation (see B-5.8)

    In stratified randomisation we produce a separate randomisation list for each subgroup (stratum) so that we get very similar numbers of patients receiving each treatment within each stratum. For example if we were doing a trial of two alternative treatments for breast cancer then we might want to take menopausal status into account. We would then take two separate lists of random numbers and prepare two separate piles of sealed envelopes for premenopausal and postmenopausal women. We may additionally use blocks (see B-5.6) to ensure that there is a balance of treatments within each stratum. Stratified randomisation can be extended to two or more stratifying variables. However, we can only have a few strata, otherwise the subgroups produced will be too small.

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    B-5.8 Minimisation

    In small studies with several important prognostic variables, random allocation may not provide adequate balance in the groups. In addition, stratified allocation (see B-5.7) may not be feasible due to there being too few subjects to stratify by all important variables. In such studies it is still possible to achieve balance by using a technique called minimisation. This is based on the idea that the next patient to enter the trial is given whichever treatment would minimise the overall imbalance between the groups at that stage of the trial. In the protocol, it is important to specify exactly which prognostic variables are to be used and to say how they are to be grouped. For example just to say that "age" will be used in not sufficient. The actual age groups need to be stated, for example <50 and 50+.

    Briefly, minimisation works like this. The first patient is randomised to either A or B. When subsequent patients are recruited and their prognostic characteristics noted, their allocation is decided such that the overall balance in the groups at that point is optimised. It is easiest to illustrate this with an example, for which we thank Sally Kerry. This was a study in which 16 general practices were allocated to intervention and control groups.

    There were three variables on which the groups should be balanced:

    1. number of doctors in the practice,
    2. number of patients in the practice,
    3. number of long-term mentally ill patients.

    These were grouped as follows:

    1. number of doctors in the practice: 3 or 4 vs. 5 or 6,
    2. number of patients in the practice: <8,600 vs. ³8.600,
    3. number of long-term mentally ill patients: <25 vs. ³25.

    The first practice had:

    1. number of doctors: 4,
    2. number of patients: 8,500,
    3. number of long-term mentally ill: 23.

    The two treatment groups were perfectly balanced at the outset, being empty, so there was no reason to choose either group for the first practice. This practice was therefore allocated randomly. It was allocated to Intervention. This gives the following table for the minimisation variables:

                      Intervention  Control
    3 or 4 doctors        1            0
    5 or 6 doctors        0            0
    <8,600 patients       1            0
    ³8.600 patients       0            0
    <25 mentally ill      1            0
    ³25 mentally ill      0            0

    The second practice had:

    1. number of doctors: 4,
    2. number of patients: 7,800,
    3. number of long-term mentally ill: 17.

    From the table, we can see which allocation would reduce the imbalance. The second practice would affect the highlighted rows:

                       Intervention  Control
    3 or 4 doctors         1            0
    5 or 6 doctors         0            0
    <8,600 patients        1            0
    ³8.600 patients        0            0
    <25 mentally ill       1            0
    ³25 mentally ill       0            0
    Imbalance              3            0

    The imbalance is the sum of the totals in the highlighted rows. Clearly, putting practice 2 in the Intervention group would make the imbalances 6 and 0, whereas assigning it to control would make them 3 and 3. The second practice was allocated to Control.

    The groups were now perfectly balanced, so the third practice was allocated randomly. This had characteristics

    1. number of doctors: 5,
    2. number of patients: 10,000,
    3. number of long-term mentally ill: 24.

    This practice was allocated to Intervention and the allocation was then:

                      Intervention  Control
    3 or 4 doctors        1            1
    5 or 6 doctors        1            0
    <8,600 patients       1            1
    ³8.600 patients       1            0
    <25 mentally ill      2            1
    ³25 mentally ill      0            0

    The fourth practice had:

    1. number of doctors: 3,
    2. number of patients: 3,400,
    3. number of long-term mentally ill: 12.

    This would affect the imbalance in the highlighted rows:

                      Intervention  Control
    3 or 4 doctors        1            1
    5 or 6 doctors        1            0
    <8,600 patients       1            1
    ³8,600 patients       1            0
    <25 mentally ill      2            1
    ³25 mentally ill      0            0
    Imbalance             4            3

    The fourth practice was assigned to Control to make the imbalance totals 4 and 6, rather than to Intervention, which would make them 7 and 3. This procedure continued until all the 16 practices had been allocated. If the imbalance would be the same whichever group the next practice went into, we would allocate randomly.

                      Intervention  Control
    3 or 4 doctors          5             5
    5 or 6 doctors          3             3
    <8,600 patients         4             4
    ³8.600 patients         4             4
    <25 mentally ill        4             4
    ³25 mentally ill        4             4

    The two groups are balanced on all three variables.

    It may be objected that minimisation is not random. Also, it may be possible for the patient's characteristics to influence the investigator's decision about recruiting that patient to the trial, the investigator might know what treatment the patient would receive. We can introduce an element of randomisation into minimisation. We use the minimisation method to decide in which direction the subject should be allocated, but use unequal randomisation to choose the actual treatment. For example, we might allocate in favour of the allocation which would reduce imbalance with probability 2/3 or 3/4, and in the direction which would increase imbalance with probability 1/3 or 1/4. Further details with another worked example can be found in Pocock (1983).

    Minimisation is most useful when a small and variable group must be randomised. Large samples will be balanced after ordinary randomisation or can be stratified. In any case, variables which are used in minimisation or stratification should be taken into account in the analysis if possible, for example by multiple regression, as this will reduce the variability within the groups (see E-6.1).

    It is not necessary to minimise individuals in a trial by hand as there is a computer program, Minim, which will do minimisation for you. Minim is available via our web directory of randomisation software and services. Some clinical trials services will provide telephone minimisation. Some of these are also listed on our web directory.

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    B-5.9 Clusters

    Sometimes we cannot allocate individuals to treatments, but rather allocate a group of subjects together. For example, in a health promotion study carried out in general practices, we might need to apply the intervention to all the patients in the practice. Publicity may be displayed in the waiting room, for example. For another example, we may need to keep groups of patients separate to avoid contamination. If we were providing a special nurse to patients in a ward, it would be difficult for the nurse to visit some patients and not others. If we are providing training to the patients or their carers, we do not want the subjects receiving training to pass on what they have learned to controls. This might be desirable in general, but not in a trial. For a third case, we may provide an intervention to service providers, clinical guidelines for example. We evaluate the intervention by collecting data from their patients.

    A group of subjects allocated together to a treatment is called a cluster. Clusters must be taken into account in the design (Kerry & Bland 1998b, Kerry & Bland 1998dd, Kerry & Bland 1998e, Bland 2000) and analysis (Altman & Bland 1997, Bland & Kerry 1997, Kerry & Bland 1998, Kerry & Bland 1998c). The proposal should say how this is to be done (see sections D and E-11). For example, the use of clusters reduces the power of the trial and so requires an increase in sample size

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    B-5.10 Trial designs

    B-5.10a Parallel groups

    The simplest design for a clinical trial is the parallel group design where the two groups of patients are studied concurrently. This is the most common design.

    B-5.10b Crossover design

    A crossover trial is one in which the patient is his own control. In other words, each patient receives both (or all) treatments in sequence. The order in which the treatments is given is randomised (see B-5.5). The main advantage of this design is that comparisons can be made within subjects rather than between subjects as we have done before. This is particularly useful for outcomes which are very variable between subjects. Crossover trials clearly cannot be used for conditions which can be cured and are most suitable when the effect of the treatment can be assessed quickly. There may be a carry-over of treatment effect from one period to the next and so it may be necessary to have a 'wash-out' period between the two treatments. If a cross-over design is proposed then the issue of a wash-out period needs to be discussed and the length of time used specified and justified if appropriate.

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    B-5.10c Within group comparisons

    Cross-over trials are within-patient designs. Another type of within-patient design is when the two treatments are investigated concurrently in the same patients. It can be used for treatments that can be given independently to matching parts of the body, such as eyes, ears, limbs etc. This is a very powerful design but has obvious limited use.

    A similar design is the matched pairs design, where pairs of subjects are matched for say, age, sex etc. and the two treatments are allocated within pairs at random. Where there are known important prognostic variables this design removes much of the between subjects variation and ensures that the subjects receiving each treatment have similar characteristics.

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    B-5.10d Sequential design

    In sequential trials, parallel groups are studied and the trial continues until either there is a clear benefit of one treatment or it is clear that no difference is likely to emerge. The data are analysed after each patient's results are available and so the method is only appropriate if the outcome is known fairly quickly. If there is a large difference between the treatments then a sequential trial will be shorter than its equivalent parallel trial. The main ethical advantage is that as soon as one treatment is shown to be superior then the trial is stopped. Note that it is incorrect to analyse any parallel group design sequentially because this would involve unplanned multiple testing (see E-7) and might therefore lead to false significant results. The sequential nature of the analysis has to be built in at the design stage such that the sample size calculations allow for the fact that multiple testing will take place (see E-7.1, E-7.4f). Further details of sequential designs can be found in Whitehead (1997).

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    B-5.10e Factorial designs

    A factorial experiment is one where several factors are compared at the same time. To make it possible to do this, each subject receives a combination of all the factors such that all combinations are received by some subjects. An example is the EMLA trial of pain relief prior to venepuncture (Nott MR, Peacock JL 1990), where 4 treatments were used (EMLA at 5 and 60 mins before venepuncture, placebo and nothing). The other factors of interest were size of needle (three) and sex. The study was designed to be balanced i.e. with equal numbers of patients in each treatment/needle/sex combination. The design enabled the researchers to investigate the effects of treatments, needle size and sex on pain and also to look for interactions (see A-1.6a). Balanced designs are easier to analyse statistically but with powerful computer programs unbalanced designs are not usually a problem nowadays.

    A factorial design is particularly suited to the investigation of factor interactions. However it is sometimes proposed in an attempt to optimise statistical power when the number of patients available for study is limited and it is assumed that the factor effects are additive either on an arithmetic or logarithmic scale (i.e. no factor interactions). The assumption of no interactions is a strong one and unless it can be fully justified in the proposal, the reviewer would expect to see sample size calculations based on detecting interactions rather than main factor effects. It should be remembered that in a factorial experiment main factor effects are averaged over all combinations of levels of the other factors. If factor effects are not additive and interactions are not of interest these estimates may not be very useful.

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    B-6 Outcome variables

    It is essential to specify the main outcome variable which will be used to decide the result of the trial. This is usually called the primary outcome or primary endpoint. It is important that only one primary outcome is chosen, such that if that variable is statistically significant then it would be reasonable to conclude that the treatment under investigation had 'worked' or was superior to its comparator.

    Often trials will want to investigate a number of additional variables, perhaps related to potential side effects. These too should be specified in advance and are called secondary outcomes or secondary endpoints. Although statistical analysis is usually performed on secondary outcomes, the interpretation is different from the result of analysing the primary outcome. First, since there may be several secondary outcomes, it is essential to allow for multiple testing (see E-7) so that a lone significant result is not over-interpreted. Further, the trial would not usually conclude efficacy from statistical significance in a secondary outcome alone. Significant results in secondary outcomes must be interpreted as indicative of effects rather than providing conclusive evidence.

    The main analysis of a trial should first answer the original questions relating to the primary and secondary outcomes. Sometimes researchers wish to investigate other hypotheses. Such results should be presented cautiously and with much less emphasis than the main findings. This particularly applies to subgroup analyses where we might seek out a group of patients in which the treatment is especially effective. If this analysis was part of the original protocol then the interpretation of these analyses presents no problem. However it may appear that a treatment works well in a particular subgroup compared with other subgroups. In such a situation it is misleading to give undue emphasis to this finding and not to mention that other subgroups were also tested. If we really wish to identify a subgroup effect then we should do a multifactorial analysis (see E-1.1) and look at interactions (see A-1.6a).

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    B-7 Data monitoring

    B-7.1 Data monitoring committee

    Most trials have a data monitoring committee which comprises a group of independent specialists who meet at pre-specified intervals while the trial is in progress to check on the trial progress and conduct. The committee will usually compare the outcome in the different treatment groups to see if there is evidence for clear superiority of any one treatment over the other(s). Adverse events are also monitored to ensure that these are not excessive. It is best if the data monitoring committee is presented with the interim data analyses blind to the treatment so that any decision to stop the trial early will not be affected by the committee knowing which treatment appears to be superior.

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    B-7.2 When should a trial be stopped early?

    This should only happen if the evidence for superiority is overwhelming. Since data monitoring is conducted prior to the main trial analysis, and sometimes more than once, the possibility of statistical significance is increased beyond the usual significance level, 0.05. Effectively the data are subject to multiple testing and so the critical value for significance has to be modified to ensure that spurious significant differences are not found and the trial stopped prematurely in error. It is common therefore for a strict critical value of say, P<0.001 to be applied for data monitoring to ensure that the overall level of significance is preserved. Further details of setting critical values for P to take account of multiple testing can be found in Pocock (1983) and Whitehead (1997). Another reason why a trial should not be stopped early unless a large, highly significant difference is observed is that with less than the anticipated number of subjects the estimates will be less precise. Thus they need to be very extreme to provide adequate and convincing evidence for the scientific community. In the past, trials which have been stopped early have been criticised subsequently and their results ignored.

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    B-8 Informed consent

    B-8.1 Consent

    The ethical principles which should govern the conduct of medical research are set out in The Declaration of Helsinki, which has a lot to say about information and consent. We recommend that all clinical researchers read it from time to time. Any clinical trial which diverges from these principles must be justified very carefully (see F3.3).

    The proposal should say how subjects are to be recruited and how they are to give consent to the trial. When we recruit subjects into a clinical trial, we usually need to ask for their permission and co-operation. When we do this we must inform potential research subjects as to the purpose of the trial, what may happen to them, in particular what may happen which is different from treatment outside the trial, and potential risks and benefits to them. If subjects will be forgoing treatment which they might otherwise have had, this must be explained.

    The information may be given orally, in the form of a video, or in writing. In any case the information should be given additionally in writing, in clear, simple language, which is unambiguous and honest. Subjects should be given an information sheet or leaflet which can be kept. Writing such information sheets is not as easy as it looks. Research ethics committees spend a lot of their time reviewing them. This written version is very important, because people are often recruited into clinical trials under circumstances of great personal stress. They may have just been told that they have a life-threatening disease, for example. They may not recall any detail of what has been said to them, or even that they were asked to take part in a clinical trial at all. The Association of the British Pharmaceutical Industry gives some guidance.

    If possible, subjects should have sufficient time between being informed about the trial and their decision as to whether to take part to discuss it with others, such as their family. They should be able to show their family members the information sheet and get their opinions.

    Wherever possible, people entering clinical trials should sign a consent form to confirm that they have been informed about the trial, agree to enter it, and understand that they can withdraw at any time. The consent form should be separate from the information sheet, so that the subject can retain the information when the form is returned. The subject should retain a copy of the signed consent form too, to remind them that they have agreed to the trial. It is not unknown for trial participants to deny having given consent, despite the existence of a signed consent form.

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    B-8.2 Emergencies

    Sometimes there is no time to allow potential subjects to discuss the pros and cons of the trial with others. For example, a trial of neuroprotection in stroke would require the treatment to be given as soon as possible after the stroke. Sometimes patients may be unconscious or extremely confused. In such cases, assent may and should be obtained from relatives accompanying the potential research subject, if any, but they cannot give consent on behalf of any person who is usually mentally competent. Randomisation may be carried out and emergency treatment begun and consent obtained later, if and when the subject is able to give it. If the subject then refuses, they should be deleted from the trial.

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    B-8.3 Children

    When the potential trial recruit is a child under the age of 16 years, consent must be obtained from the child's parents or other legal guardians. There should be an information sheet for parents and, where the child is old enough to read, one in language suitable for children of the likely age. Assent should be obtained from the subjects themselves if they are old enough to understand what is happening. Children may have to be treated against their will with parental consent, but they should not become research subjects against their will.

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    B-8.4 Mentally incompetent subjects

    When potential research subjects are mentally or physically unable to consent, for example through learning difficulties, mental illness, or paralysis, consent should be obtained from their legal guardians. As for children, assent should also be obtained from the subjects themselves wherever possible. Note that Clause 27 of the Declaration of Helsinki states that "These individuals must not be included in a research study that has no likelihood of benefit for them unless it is intended to promote the health of the population represented by the potential subject, the research cannot instead be performed with competent persons, and the research entails only minimal risk and minimal burden."

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    B-8.5 Cluster randomised designs

    Consent is more difficult in cluster randomised designs. Because people are randomised as a group, this is usually done without their consent. For example, in a general practice based trial, all patients of the chosen type in a practice may be randomised to the same treatment. In some such trials, it is impossible for patients to consent to treatment. For example, in a trial where GPs are randomised to receive guidelines for treatment of a disease, patients cannot agree to their GP being randomised or to receiving the guidelines. It has already happened. Patients can only consent to provide data for the trial. If the cluster has been randomised to receive an individual treatment, patients may still consent to or refuse treatment as they would do outside a trial. For example, if the treatment is to run special clinics, they can refuse to go to them when invited. For some treatments, such as health promotion interventions in general practice, workplace or school, subjects cannot even do that. All they can do is to refuse to listen. Some critics argue that cluster randomisation is never ethical for this reason. If the funding body to which you apply takes this view, then you will have to find another funder.

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    B-8.6 Randomised consent design

    In this design we have a new treatment to be compared to a standard treatment and we do not wish subjects in the control group to be informed about the new treatment. For example, in the Know Your Midwife trial the new treatment was to have the same midwife carry out all antenatal care, deliver the baby, and carry out all postnatal care. The control treatment was standard care, where mothers would be seen by whoever was duty at the time, and may never see the same midwife twice. The trial organiser thought that very few women would be happy with standard care if they knew that the Know Your Midwife clinic existed. To save them from disappointment, they were randomised to receive standard care, the control group, or to be offered Know Your Midwife, the treatment group. Those offered Know Your Midwife could then accept it or opt for standard care (which some did). All women were asked to consent to a study of maternity services, so that data could be collected.

    This is an example of a randomised consent design (Zelen 1979, 1990), where research subjects are randomised and consent is then obtained to treatment and data provision, but not to randomisation itself. Such a design would need a very strong argument if it were to be used in a trial. Some critics argue that randomised consent is never ethical.

    Randomised consent designs are analysed according to the principle of intention to treat (see E-9). This gives the best test of significance, but a rather biased treatment estimate. In addition, Zelen (1979) shows how better treatment estimates can be obtained, at the expense of wider confidence intervals.

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    B-9 Protocol violation and non-compliance

    Some patients may not have followed the protocol, either accidentally or deliberately (non-compliance) or their condition may have led to the clinician giving them an alternative treatment to the one they were originally allocated to (protocol violation). The only safe way to deal with these people is to keep all randomised patients in the trial i.e. to analyse according to the randomisation. This will maintain the balance between the groups that the original randomisation will have achieved and so ensure that the treatment groups are comparable apart from the treatment received. This is known as analysing according to the intention to treat (see E-9). An intention to treat analysis should be performed wherever possible but may not be possible if some patients have dropped out of the trial. In this case sensitivity analyses should be performed to assess the likely impact of the missing data.

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    B-10 Achieving the sample size

    The sample size required for a clinical trial is decided using standard methods of power calculations or confidence interval width, as would be used for any other statistical study (see Section D). However, a problem arises in clinical trials which is not so frequent in observational designs. The agreed sample size may be very hard to recruit. We have been involved with many clinical trials where recruitment has been much slower than anticipated. Indeed, we would say that this is the norm. One possible result of this is a request to the funders for an extension in time or for an extension in funding. Requests for time are likely to be agreed, but requests for money may well be turned down on the grounds that there is no point in throwing good money after bad. Another outcome may be the premature ending of the trial with only a small fraction of the planned recruitment, the analysis of a greatly under-powered trial and inconclusive findings.

    Why does this happen? It is the common experience that as soon as a clinical trial begins, potential patients melt away like snow in August. One reason for this might be that patients refuse to consent to the trial. There is evidence to suggest that patient compliance with clinical trials may be reducing as a result of adverse publicity about medicine in general and trials in particular. However, much more likely is the failure of recruiting staff to identify and approach potential research subjects. This may be because of a lack of commitment to the project, which might be caused by honest doubts about the safety or efficacy of the new treatment or by the view that the new treatment should be used. For example, in a sequential trial of sublingual nitrate in myocardial infarction, the statistician noticed that very few patients were dying, far fewer than the sample size calculations had assumed. It was explained by all the patients being entered into the trial having a good prognosis, based on the indicators used in the trial. High risk patients were not being entered into the trial, but were being prescribed nitrates by admitting physicians. Poor recruitment may also be because staff are too busy. If the clinical unit is under pressure from excessive patient numbers or understaffing, the research project will be the first thing to go. This is how it should be, of course, as the wellbeing of patients should be our first concern, but it is pretty frustrating for the experimenter. Another problem can be that other trials are already in progress in a unit. Staff may be unable to cope with or keep in mind the needs to recruit to yet another trial, or there may be competition between trials for the same patients. It is a good idea to check with potential collaborators what their other trial commitments are.

    Pilot studies (see A-1.9) are very helpful in sorting out some of these problems, as is having a research leader who can visit trial sites regularly and maintain good contact with staff actually concerned with recruitment. Funders may well be impressed by a proposal which shows that this issue has been considered by applicants and some positive plans exist for dealing with it. Also a good idea is to have recruitment targets (milestones) to enable the research team to monitor how well recruitment is going, so that problems can be detected as soon as possible.

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    B-11 After the trial is over

    The current Declaration of Helsinki states that:

    "At the conclusion of the study, patients entered into the study are entitled to be informed about the outcome of the study and to share any benefits that result from it, for example, access to interventions identified as beneficial in the study or to other appropriate care or benefits." (Clause 33)

    Of course this may not be possible or appropriate in many trials, such as treatments of acute conditions. However, the proposal should contain a statement about this if the trial is a direct patient treatment of a chronic condition. Is this going to take place and, if so, how will it be funded and administered?

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    References for this chapter

    Altman DG, Bland JM. (1997) Units of analysis. British Medical Journal 314 1874.

    Bland JM, Kerry SM. (1997) Trials randomised in clusters. British Medical Journal 315 600.

    Bland M. (2000) An Introduction to Medical Statistics, 3rd. ed. Oxford University Press, Oxford.

    Bland JM. (2002a) WMA should not retreat on use of placebos. British Medical Journal 324, 240.

    Bland JM. (2002b) Fifth revision of Declaration of Helsinki: Clause 29 forbids trials from using placebos when effective treatment exists. British Medical Journal 324 975.

    The CONSORT statement: revised recommendations for improving the quality of reports of parallel group randomized trials.

    Ferriman A. (2001) WMA agrees to refine changes to Declaration of Helsinki British Medical Journal 322, 1142.

    Gibbons, A. (2002) Performing and publishing a randomised controlled trial. British Medical Journal 324, S131.

    Huskisson, E.C. (1974) Simple analgesics for arthritis. British Medical Journal 4 196-200.

    Kerry SM, Bland JM. (1998) Analysis of a trial randomised in clusters. British Medical Journal 316 54.

    Kerry SM, Bland JM. (1998b) Sample size in cluster randomisation. British Medical Journal 316 549.

    Kerry SM, Bland JM. (1998c) Trials which randomise practices I: how should they be analysed? Family Practice 15 80-83

    Kerry SM, Bland JM. (1998d) Trials which randomise practices II: sample size. Family Practice 15 84-87

    Kerry SM, Bland JM. (1998e) The intra-cluster correlation coefficient in cluster randomisation. British Medical Journal 316 1455.

    Nott MR, Peacock JL (1990) Relief of injection pain in adults - EMLA cream for 5 minutes before venepuncture. Anaesthesia 45 772-774.

    Pocock SJ. (1983) Clinical Trials: A Practical Approach. John Wiley and Sons, Chichester.

    Tollman SM, Bastian H, Doll R, Hirsch LJ, Guess HA. (2001) What are the effects of the fifth revision of the Declaration of Helsinki? British Medical Journal 323, 1417-1423.

    Whitehead, J. (1997) The Design and Analysis of Sequential Clinical Trials, revised 2nd. ed. Chichester, Wiley.

    Zelen, M. (1979) A new design for clinical trials. New Eng J Med 300 1242-5.

    Zelen, M. (1990) Randomised consent designs for clinical trials: an update. Statistics in Medicine 9 645-6.

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