Statistical Thinking for Non-Statisticians in Drug Regulation

Richard Kay

• Publisher: Wiley
• Year: 2014
• Print ISBN: 9781118470947
• eBook ISBN: 9781118470978
• Edition: 2
• Topic: Medicine
• Subtopic: Pharmacology

Statistical Thinking for Non-Statisticians in Drug Regulation, Second Edition, is a need-to-know guide to understanding statistical methodology, statistical data and results within drug development and clinical trials.

It provides non-statisticians working in the pharmaceutical and medical device industries with an accessible introduction to the knowledge they need when working with statistical information and communicating with statisticians. It covers the statistical aspects of design, conduct, analysis and presentation of data from clinical trials in drug regulation and improves the ability to read, understand and critically appraise statistical methodology in papers and reports. As such, it is directly concerned with the day-to-day practice and the regulatory requirements of drug development and clinical trials.

Fully conversant with current regulatory requirements, this second edition includes five new chapters covering Bayesian statistics, adaptive designs, observational studies, methods for safety analysis and monitoring and statistics for diagnosis.

Authored by a respected lecturer and consultant to the pharmaceutical industry, Statistical Thinking for Non-Statisticians in Drug Regulation is an ideal guide for physicians, clinical research scientists, managers and associates, data managers, medical writers, regulatory personnel and for all non-statisticians working and learning within the pharmaceutical industry.

Chapter 1
Basic ideas in clinical trial design

1.1 Historical perspective

As many of us who are involved in clinical trials will know, the randomised controlled trial is a relatively new invention. As pointed out by Pocock (1983) and others, very few clinical trials of the kind we now regularly see were conducted prior to 1950. It took a number of high-profile successes plus the failure of alternative methodologies to convince researchers of their value.

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Example 1.1 The Salk Polio Vaccine trial

One of the largest trials ever conducted took place in the USA in 1954 and concerned the evaluation of the Salk polio vaccine. The trial has been reported extensively by Meier (1978) and is used by Pocock (1983) in his discussion of the historical development of clinical trials.

Within the project, there were essentially two trials, and these clearly illustrated the effectiveness of the randomised controlled design.

Trial 1: Original design: Observed control

1.08 million children from selected schools were included in this first trial. The second graders in those schools were offered the vaccine, while the first and third graders would serve as the control group. Parents of the second graders were approached for their consent, and it was noted that the consenting parents tended to have higher incomes. Also, this design was not blinded so that both parents and investigators knew which children had received the vaccine and which had not.

Trial 2: Alternative design: Randomised control

A further 0.75 million children in other selected schools in grades one to three were to be included in this second trial. All parents were approached for their consent, and those children where consent was given were randomised to receive either the vaccine or a placebo injection. The trial was double blind with parents, children and investigators unaware of who had received the vaccine and who had not.

The results from the randomised controlled trial were conclusive. The incidence of paralytic polio, for example, was 0.057 per cent in the placebo group compared to 0.016 per cent in the active group, and there were four deaths in the placebo group compared to none in the active group. The results from the observed control trial, however, were less convincing with a smaller observed difference (0.046 per cent vs. 0.017 per cent). In addition, in the cases where consent could not be obtained, the incidence of paralytic polio was 0.036 per cent in the randomised trial and 0.037 per cent in the observed control trial, event rates considerably lower than those among placebo patients and in the untreated controls, respectively. This has no impact on the conclusions from the randomised trial, which is robust against this absence of consent; the randomised part is still comparing like with like. In the observed control part however, the fact that the no consent (grade 2) children have a lower incidence than those children (grades 1 and 3) who were never offered the vaccine potentially causes some confusion in a non-randomised comparison; does it mean that grade 2 children naturally have lower incidence than those in grades 1 and 3? Whatever the explanation, the presence of this uncertainty reduced confidence in the results from the observed control trial.

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The randomised part of the Salk Polio Vaccine trial has all the hallmarks of modern-day trials – randomisation, control group and blinding – and it was experiences of these kinds that helped convince researchers that only under such conditions can clear, scientifically valid conclusions be drawn.

1.2 Control groups

We invariably evaluate our treatments by making comparisons – active compared to control. It is very difficult to make absolute statements about specific treatments, and conclusions regarding the efficacy and safety of a new treatment are made relative to an existing treatment or placebo.

ICH E10 (2001): ‘Note for Guidance on Choice of Control Group in Clinical Trials'

‘Control groups have one major purpose: to allow discrimination of patient outcomes (for example, changes in symptoms, signs, or other morbidity) caused by the test treatment from outcomes caused by other factors, such as the natural progression of the disease, observer or patient expectations, or other treatment'.

Control groups can take a variety of different forms; here are just a few examples of trials with alternative types of control group:

• Active versus placebo
• Active A versus active B (vs. active C)
• Placebo versus dose level 1 versus dose level 2 versus dose level 3 (dose finding)
• Active A + active B versus active A + placebo (add-on)

The choice will depend on the objectives of the trial.

Open trials with no control group can nonetheless be useful in an exploratory, maybe early phase setting, but it is unlikely that such trials will be able to provide confirmatory, robust evidence regarding the performance of the new treatment.

Similarly, external concurrent or historical controls (groups of subjects external to the study either in a different setting or previously treated) cannot provide definitive evidence in most settings. We will discuss such trials in Chapter 17. The focus in this book however is the randomised controlled trial.

1.3 Placebos and blinding

It is important to have blinding of both the subject and the investigator wherever possible to avoid unconscious bias creeping in, either in terms of the way a subject reacts psychologically to treatment or in relation to the way the investigator interacts with the subject or records subject outcome.

ICH E9 (1998): ‘Note for Guidance on Statistical Principles for Clinical Trials'

‘Blinding or masking is intended to limit the occurrence of conscious or unconscious bias in the conduct and interpretation of a clinical trial arising from the influence which the knowledge of treatment may have on the recruitment and allocation of subjects, their subsequent care, the attitudes of subjects to the treatments, the assessment of the end-points, the handling of withdrawals, the exclusion of data from analysis, and so on'.

Ideally, the trial should be double-blind with both the subject and the investigator being blind to the specific treatment allocation. If this is not possible for the investigator, for example, then the next best thing is to have an independent evaluation of outcome, both for efficacy and for safety. A single-blind trial arises when either the subject or investigator, but not both, is blind to treatment.

An absence of blinding can seriously undermine the validity of an endpoint in the eyes of regulators and the scientific community more generally, especially when the evaluation of that endpoint has an element of subjectivity. In situations where blinding is not possible, it is important to use hard, unambiguous endpoints and to use independent recording of that endpoint.

The use of placebos and blinding goes hand in hand. The existence of placebos enables trials to be blinded and accounts for the placebo ef...

Table of contents

• Cover
• Title page
• Copyright page
• Preface to the second edition
• Preface to the first edition
• Abbreviations
• Chapter 1: Basic ideas in clinical trial design
• Chapter 2: Sampling and inferential statistics
• Chapter 3: Confidence intervals and p-values
• Chapter 4: Tests for simple treatment comparisons
• Chapter 5: Adjusting the analysis
• Chapter 6: Regression and analysis of covariance
• Chapter 7: Intention-to-treat and analysis sets
• Chapter 8: Power and sample size
• Chapter 9: Statistical significance and clinical importance
• Chapter 10: Multiple testing
• Chapter 11: Non-parametric and related methods
• Chapter 12: Equivalence and non-inferiority
• Chapter 13: The analysis of survival data
• Chapter 14: Interim analysis and data monitoring committees
• Chapter 15: Bayesian statistics
• Chapter 16: Adaptive designs
• Chapter 17: Observational studies
• Chapter 18: Meta-analysis
• Chapter 19: Methods for the safety analysis and safety monitoring
• Chapter 20: Diagnosis
• Chapter 21: The role of statistics and statisticians
• References
• Index
• End User License Agreement