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5 Design of Medical Experiments There are two broad types of study in medical research: observational and experimental. In this chapter we will look at the design of experimental studies. These experiments may be performed in the laboratory, on animals or on humans; trials of treatments on human subjects are called clinical trials. 5.1 Medical Ethics Ethics is the study of moral principles, thus medical ethics is the study of moral principles which apply in the field of medicine. The medical statistician is part of the medical process and thus needs to have an understanding of the ethical framework within which medicine is practised. This section will outline the basic moral principles which are taken to apply in conducting scientific (medical) research on humans. Thus when we design a study of humans we should expect that these experiments meet all the requirements of these moral principles. We take morality to refer to those social conventions about right and wrong human conduct that are so widely accepted by any group (usually country) that they form an enduring consensus. It is not necessary that everyone believes in the absolute rightness of these conventions, but it is expected that everyone abides by them. There are three main moral principles: Autonomy The principle of autonomy requires that every person can only agree to take part in a medical study provided they have had all the ramifications of taking part explained to them and that they understand these ramifications. This is known as informed consent. This principle also requires that they will suffer no adverse consequences if they refuse. This is known as no duress. Also, once having agreed to participate, a person is free to withdraw at any time and suffers no adverse consequences other than those which directly result from the decision to withdraw. Non-maleficence The principle of non-maleficence requires that harm is not deliberately done, whether by acts of commission or omission. Thus in a medical study we are not allowed to harm a patient just because we believe that we would learn something from such an action. Beneficence The principle of beneficence requires that we contribute to the welfare of people. Firstly, if we are offering a patient an experimental treatment we must have good reason to believe that it is at least as good as the conventional treatment. Also we must design our studies in such a way that that we gain the maximum information from them, thus providing the maximum benefit to our subjects and the rest of society. 5.1.1 Medical ethics committees While we have an absolute duty to abide by these principles, adherence to them is seen to be so important that all research proposals are scrutinised by an ethics committee. The proposed research is described in a document, called the research protocol, in sufficient detail to demonstrate how it meets the principles; in particular it explains how the research will be conducted and analysed. The proposed analysis is contained in an analytical protocol. Part of the construction of a research protocol and its scrutiny by an ethics committee requires considerable technical expertise, especially in the areas of epidemiological method and statistics. Thus both consultant epidemiologists and statisticians should play a key part in these processes. In addition, the research protocol forms a handbook to guide those conducting the study. The protocol usually has the following sections: 26 1. Rationale: the background to the study. 2. Aim of study: exactly what are the experimenters trying to find out. 3. Design of the study: the epidemiological method used and the methods used to avoid bias. Sample size calculations. 4. Study population and selection of patients, including exclusion criteria. 5. The intervention, specified in sufficient detail to allow another clinician to repeat it. 6. Methods of assessment of the success or otherwise of the intervention. Outcomes should be divided into the primary outcome measure, which is the main way the intervention will be judged, and secondary outcome measures which add further data on the performance of the intervention. 7. Documentation: Patient information sheets and consent forms, data sheets etc. 8. The procedure to be adopted, including all decisions to be taken. 9. Withdraws: while patients may elect to leave the study at any time the experimenters must know the circumstances when a subjects best interest are served by withdrawing them from the experiment. 10. Adverse events: their description and consequent decision making. 11. The process of consenting patients. 12. Ethics: The name of the ethics committee(s) consulted. 13. Analytical protocol. 14. Confidentiality: how the data will be managed to ensure patient confidentiality. 15. A statement of conflicts of interest and declaration that the protocol will be followed. In large multi-centred studies a data monitoring committee is set up to oversee the data, and to ensure that no unexpected problems are arising with any of the treatments. The experimenters cannot do this as partial knowledge of the results can subconsciously influence the decisions they take. The role of the statistician is pivotal here to determine if the interim results of a study are fully informative, especially where repeat statistical testing takes place. Once the research is completed the results should be placed in the public domain; the experiment is written up as a paper and submitted to a medical journal. The paper is sent by the journal to several independent reviewers who check on the validity of the experimental process and the legitimacy of the conclusions. This process is called peer review. Most journals have statistical advisors to help the editor deal with some of the more complex or less common statistical issues that arise. The publication of the results of a study should not be taken as confirming that the results represent the ‘true state of nature’. Rather the publication confirms that the study has been conducted and written up to an appropriate standard. 5.1.2 Statutory procedures in new drug testing in the UK The testing of new drugs is very tightly regulated; a number of criteria need to be met before a drug is licensed for routine use. There are four stages or phases of drug testing on humans. This testing on humans follows both in vitro (laboratory testing, often on tissue) and animal experimentation (which provokes further ethical deliberation). The four phases, which reflect the different stages of human experimentation, are: 27 Phase 1 trials Testing of drug safety and basic dose response (pharmaco-kinetics). Usually done on a small number of healthy volunteers using sub-therapeutic doses. Phase 2 trials The first experiments on patients, that is people with the condition that the drug is intended to treat. These studies try to identify the optimum therapeutic dose, balancing benefit against side effects. Careful monitoring of the subjects is required, often involving a wide range of measurements. The number of subjects involved is small, but usually more than phase 1 studies. Phase 3 trials These are the large scale comparative clinical investigations which take place within ordinary medical practice. This is the most formal of the phases and can involve thousands of patients. Once phase 3 data are available the drug can be reviewed by the regulatory bodies who can issue a product licence so that the drug can be marketed. This phase is often referred to as clinical trials. Phase 4 trials This is the post-marketing surveillance and is concerned with the long term safety and efficacy of the drug. For consistency of terminology these studies are called trials but strictly they are surveys rather than experiments. 5.2 Randomised controlled trials Randomised controlled trials, or RCTs, are the gold standard for the assessment of medical interventions. While they have their critics and have a number of known disbenefits they give results which are far easier to draw safe inferences from than any other type of experimental design. All of the key design features of RCTs are intended to remove bias; that is, systematic differences between the two groups to be compared. Blind recruitment The eligibility of a patient is assessed without knowing to which of the treatments under study he/she will be allocated. The patient is then admitted to the trial only if there is no preference between treatments A and B for this particular patient. Random allocation to treatment Where the comparison groups are not selected at random, one group may be intrinsically favoured to do well, irrespective of the treatment they receive. If we randomly allocate patients we are seeking to avoid any overall bias in favour of one treatment (we are not trying to make the two groups equal, just avoid bias). Groups are comparable in that differences between groups are no greater than would be observed through chance. Patients blinded to treatment For reasons that are not always clear patients can tend to improve more on one type of treatment compared to another, even when it is known that the treatments are identical. This applies to both subjective symptoms such as degree of pain, and even apparently purely physiological measures such as blood pressure. It is a matter of vigorous ethical debate as to the steps which can be taken to preserve this blindness. Experimenters blinded to treatment Despite strong protestations to the contrary by researchers, knowledge of the treatment that the patient is receiving can influence decisions taken. Similar circumstances apply during the assessment of subjects, such as a clinician’s subjective opinion on a patient’s progress. With drug treatments it is usual for only the pharmacist to know which treatment each patient is taking. Analysis blind to treatment If the task of managing the data is done by a different person to the one who will analyse it there is no reason why the analysis and statistical interpretation cannot be done blind to the treatments. Care needs to be taken when attempting this as often a treatment group can be identified by the characteristics of the data e.g. the pattern of adverse events. 28 Table 5: Results of the field trial of Salk polio vaccine for two different designs Number Treatment Group Randomised Control Trial Vaccinated 200745 Refused Vaccination 338778 Control 201229 Non-randomised Vaccinated 221998 Refused Vaccination 123605 Control 725173 5.2.1 Cases of Polio Rate per 100,000 33 121 115 16 36 57 38 43 330 17 35 46 Intention-to-treat analysis The procedures outlined above ensure that the groups who are allocated to receive the various treatments or placebo start off having no systematic bias. Not all patients will continue with the specified intervention or placebo until the endpoint of the study. There must be the option to adjust the patient’s treatment should clinical circumstances necessitate it, or patients may also decline to continue following the treatment they were randomised to. There are two strategies that can be used; the choice depends on the objectives of the study. Studies of therapeutic efficiency If we are interested in therapeutic efficiency (that is, does the treatment do what it is intended to do) then we only analyse the subjects who stayed on the treatment they were randomised to and we report the others as either protocol violators or patient withdraws. Thus the results will tell us the comparative advantage of one treatment over another for patients who complete the treatment. This is known as on treatment analysis. Studies of treatment policy In other cases, the ‘treatment’ may not be the medical intervention itself, but a policy of offering it to patients and treating those who accept; for example, vaccinations, health checkups. In this case we analyse the data according to the way we intended to treat subjects, rather than the way in which they actually were treated. This is known as analysis by intention to treat, and answers questions of policy effectiveness. 5.2.2 Cross-over designs Sometimes it is possible to use patients as their own controls so that each subject receives all treatments over different periods of time. Such designs are called cross-over designs and are advantageous since they remove variability between subjects. They also require fewer subjects than a two group trial. Treatment order should be assigned at random, and sufficient time allowed between treatments to allow any effect of the first treatment to dissipate. Cross-over designs are only suitable in clinical trials where the treatment will not affect the course of the disease and where the patient’s condition will not change appreciably over the course of the trial. They can also not be used to demonstrate long-term effects, or for treatments that have a long-term impact after discontinuation. 29 5.2.3 Deficiencies in the RCT The RCT can be criticised because of the highly stylised structure, and its inherent limited ability to test many scenarios or many different outcome measures at once. While these are legitimate criticisms there is no obvious alternative investigative model known. There are three cornerstones of the RCT design namely random allocation, patients blinded to treatment and assessors blinded to treatment. These features protect us from finding differences due to bias. They do not protect us from finding no difference due to bias. Thus any result from an RCT which finds ‘no difference’ could be due to bias unless very careful checks were made. 5.3 Non-randomised Designs Randomised controlled trials are not always possible or ethical. A cohort study can be used as a non-randomised design for experiments. A cohort is a well defined population, usually followed-up for a period of time. 5.3.1 Pre-test/Post-test Studies A pre-test/post-test study is a single cohort study in which a group of individuals are measured, then subjected to a treatment or intervention, and then measured again. The purpose of the study is to observe the size of the treatment effect. Deficiencies in before and after comparisons arise because serial changes in a single group of subjects are studied. Any changes seen over due to changes other than the treatment over the time period. Period effects There may be reason to expect systematic differences between the values recorded at two times that have nothing to do with the effect being studied. If the two times of assessment are separated by six months, and all patients enter the study in summer, the treatment effect will be confounded with a seasonal effect. If the study period is several years there may be an ageing effect. Placebo effects The fact that the patient is aware of having a potentially beneficial treatment administered or prescribed often has an effect. Placebo effects may also influence the observer, especially when the measurement being made is largely subjective. The Hawthorne Effect This is similar to the placebo effect except that the cause of the improvement is just taking part in a study. Regression towards the mean As in Section 2.2.4, this occurs when subjects are selected on the basis of having high levels of a relevant test measurement. 5.3.2 Comparative cohort In a comparative cohort design, we compare two groups as before, one group experiencing effect A, the other effect B. Our study is then a controlled trial. We can sometimes use historical controls. For example, when there is a national change in health care policy or available treatment, the new incidence of the condition of interest can be compared with the old incidence before the change. Again, this may introduce bias due to other differences before and after the change. 30