Cardiovascular Clinical Trials E-Book

• Herausgeber: John Wiley & Sons
• Kategorie: Fachliteratur
• Sprache: Englisch

Seitenzahl: 779

Veröffentlichungsjahr: 2012

Beschreibung

The pace of therapeutic advances in the treatment of cardiovascular diseases is rapid, and new clinically-relevant information appears with such frequency that it can be extremely challenging for clinicians to keep up.

Still, knowledge and interpretation of major clinical trials is crucial for the range of clinicians who manage cardiovascular patients, especially since important trial evidence often needs to be implemented soon after it is published.

Confidently apply gold standard treatment for 10 of the most critical areas of cardiology
Written by an international team of experts, Cardiovascular Clinical Trials: Putting the Evidence into Practice:

• Provides a succinct overview of recent major clinical trials - the gold standard for all medical treatment - across all the major cardiovascular subspecialties, to ensure you’re up-to-date on the most critical findings
• Guides cardiology trainees and clinicians on how cardiovascular clinical trials are designed and conducted, including statistical methodology, so you can conduct and/or appraise future trials yourself
• Addresses methodology as well as clinical effectiveness
• Offers evidence-based assessments on the most effective treatments and authoritative clinical information on management of the conditions so you can confidently apply what you learn

Physicians, surgeons, specialist nurses – any clinician seeking an accessible resource for designing and conducting cardiovascular trials and then translating their results into practice will appreciate this book’s clear guidance and succinct and practical approach.

Leseprobe

Table of Contents

Cover

Title page

Copyright page

Dedication

List of contributors

Preface

List of abbreviations

CHAPTER 1 Introduction to randomized clinical trials in cardiovascular disease

What is a randomized clinical trial?

Concept of randomization

Clinical trial phases

Study objective

Study populations

Efficacy variables

Control groups

Study design (samples)

Comparisons

Study protocol

Trial monitoring

Data analysis sets

Unit of analysis

Missing data

Sample size and power

Safety evaluation

Subsets and more

Types of significance

How have trials contributed to medical care?

Conducting reliable trials: issues of size and simplicity

Costs, cost-effectiveness, and health economics

Practical issues: managing a trial, funding, and regulation

What does the future hold?

CHAPTER 2 Publishing results of clinical trials and reviewing papers for publication

General considerations

Reviewing a submitted article for a journal

CHAPTER 3 Management of chronic coronary artery disease

Introduction

Pathophysiology

Medical management of myocardial ischemia

Non-pharmacological antianginal approaches

Role of myocardial revascularization

CHARISMA trial

COURAGE trial

Conclusions

CHAPTER 4 Acute coronary syndromes (ST elevation and non-ST elevation)

Definition and pathophysiology

Epidemiology and healthcare costs

Diagnosis

Examination

Investigation

Management

Appraisal of selected clinical trials that have changed the management of acute coronary syndromes

Conclusions

CHAPTER 5 Heart failure

Epidemiology

Pathophysiology

Clinical presentation: registry data

Standard management strategies

Current challenges of heart failure: acute heart failure syndromes

Conclusion

CHAPTER 6 Atrial fibrillation

Introduction

Epidemiology

Clinical classification

Management

New-onset atrial fibrillation

Paroxysmal atrial fibrillation

Persistent atrial fibrillation

Permanent atrial fibrillation

Non-pharmacological treatments

Thromboembolism prevention

Conclusion

CHAPTER 7 Electrophysiology and pacing

Arrhythmias

Pacing and pacing technologies

Electrophysiological assessment

Ablation procedures

Implantable defibrillators

Cardiac resynchronization

Review of key clinical trials

Review of key trials evaluating atrial fibrillation ablation versus medical therapy

Conclusion

Disclaimer

CHAPTER 8 Percutaneous coronary intervention

Introduction

Balloon PTCA

Bare metal stents

Drug-eluting stents

Local antiproliferative treatment for in-stent restenosis

Directional coronary atherectomy

Cutting balloon angioplasty

Rotational atherectomy

Excimer laser angioplasty

Mechanical thrombectomy

Special issues

Conclusions

CHAPTER 9 Randomized controlled trials in cardiac surgery: is there any alternative?

Controversies and uncertainties in cardiac surgery

Need for a hierarchical system to stratify the evidence

What are the most common difficulties encountered in performing RCTs in cardiac surgery?

Need for a variety of endpoints and patient-reported based outcomes

Need to improve reporting of RCTs in cardiac surgery

A palliative treatment for the problem: the need for progress in statistical methodology of non-randomized designs

Recent clinical trials in cardiac surgery: where are we?

Conclusions

CHAPTER 10 Adult congenital heart disease

Introduction

Atrial septal defects

Patent foramen ovale

Tetralogy of Fallot

Eisenmenger syndrome

Pregnancy in patients with adult congenital heart disease

CHAPTER 11 Cardiac imaging

Introduction

Myocardial perfusion imaging with SPECT or PET

Echocardiography

Cardiovascular magnetic resonance

Coronary CT angiography

Acknowledgement

CHAPTER 12 Prevention of cardiovascular disease

Introduction

Cardiovascular disease: etiology and assessment

Landmark studies of cardiovascular disease risk

Key risk factors

Risk assessment

Population-based prevention

Clinical trials that have informed our management of preventing CAD and other vascular diseases

Update

Index

This edition first published 2013, © 2013 by Blackwell Publishing.

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Library of Congress Cataloging-in-Publication Data

Cardiovascular clinical trials : putting the evidence into practice / edited by Marcus D. Flather, Deepak L. Bhatt, Tobias Geisler.

p. ; cm.

 Includes bibliographical references and index.

 ISBN 978-1-4051-6215-9 (pbk. : alk. paper)

 I. Flather, M. II. Bhatt, Deepak L. III. Geisler, Tobias.

 [DNLM: 1. Cardiovascular Diseases–prevention & control. 2. Clinical Trials as Topic. WG 120]

 616.100724–dc23

2012009758

A catalogue record for this book is available from the British Library.

Wiley also publishes its books in a variety of electronic formats. Some content that appears in print may not be available in electronic books.

Cover images: iStock © Christian Jasiuk and Anthony A. Bavry et al. Eur Heart J (2008) 29(24): 2989–3001 by permission of Oxford University Press

Cover design by Grounded Design

MDF: To my family Ruth, Hannah, and Alex, and the team at the Royal Brompton Clinical Trials and Evaluation Unit.

DLB: To my wife Shanthala and my sons Vinayak, Arjun, Ram, and Raj, with the deepest gratitude for allowing me to pursue my passion for clinical trials.

TG: To my wife Katja and my daughters Marlene and Mathilde for persevering with me through all endeavors and giving me liberty to develop my dedication to clinical research.

List of Contributors

Aiden Abidov, MD, PhD, FACC, FAHAAssociated Professor of Medicine and RadiologyThe University of Arizona College of MedicineTucson, AZ, USA

Thanos Athanasiou, MD, PhD, FETCS, FRCSCardiothoracic SurgeonHammersmith HospitalImperial CollegeLondon, UK

Thomas M. Bashore, MDProfessor of MedicineDivision of CardiologyDuke University Medical CenterDurham, NC, USA

Daniel S. Berman, MD, FACC, FAHA, FSCCTProfessor of MedicineDepartment of Imaging and Department of MedicineCedars-Sinai Medical Center;Department of MedicineDavid Geffen School of Medicine, UCLALos Angeles, CA, USA

Deepak L. Bhatt, MD, MPH, FACC, FAHA, FESCChief of Cardiology, VA Boston Healthcare System;Director, Integrated Interventional Cardiovascular Program, Brigham and Women’s Hospital & VA Boston Healthcare System;Professor of MedicineHarvard Medical School;Senior Investigator, TIMI Study GroupBoston, MA, USA

William E. Boden, MD, FACC, FAHAProfessor of Medicine, Albany Medical College;Chief of MedicineSamuel S. Stratton VA Medical Center;Vice-Chairman, Department of Medicine,Albany Medical CenterAlbany, NY, USA

Ralph B. D’Agostino, SrDepartment of MathematicsBoston UniversityBoston, MA, USA

Sabine Ernst, MD, PhD, FESCNational Heart and Lung InstituteImperial College;Royal Brompton and Harefield HospitalLondon, UK

Marcus D. Flather, MBBS, FRCPProfessor of Medicine and Clinical TrialsUniversity of East Anglia and Norfolk and Norwich University HospitalNorwich, UK

Tobias Geisler, MDAssociate Professor of MedicineConsultant, CardiologyUniversity Hospital TübingenTübingen Medical SchoolTübingen, Germany

J. Kevin Harrison, MDProfessor of MedicineDivision of CardiologyDuke University Medical CenterDurham, NC, USA

Chee W. Khoo, MRCPResearch FellowUniversity of Birmingham Centre for Cardiovascular SciencesCity HospitalBirmingham, UK

Dharam J. Kumbhani, MD, SMDivision of Cardiovascular MedicineBrigham and Women’s HospitalHarvard Medical SchoolBoston, MA, USA

Gregory Y.H. Lip, MD, FRCPProfessor of Cardiovascular MedicineUniversity of Birmingham Centre for Cardiovascular SciencesCity HospitalBirmingham, UK

Christopher M. O’Connor, MDProfessor of Medicine and DirectorDuke Heart CenterDuke University Medical CenterDurham, NC, USA

Alice J. Owen, PhDDepartment of Epidemiology & Preventive MedicineMonash UniversityMelbourne, VIC, Australia

John Pepper, MA, MChir, FRCSCardiothoracic SurgeonRoyal Brompton HospitalLondon, UK

Christopher M. Reid, PhDProfessor of Cardiovascular EpidemiologyDepartment of Epidemiology & Preventive MedicineMonash UniversityMelbourne, VIC, Australia

Amir Sepehripour, BSc, MBBS, MRCSSpecialist Registrar Cardiothoracic SurgeryImperial CollegeLondon, UK

Wendy Gattis Stough, PharmDAssistant Consulting ProfessorDuke University Medical CenterDurham, NC;Associate Professor of Clinical ResearchCampbell University School of PharmacyBuies Creek, NC, USA

Irina Suman-Horduna, MD, MScNational Heart and Lung InstituteImperial College;Royal Brompton and Harefield HospitalLondon, UK

Sabu Thomas, MD, FACC, FRCPCAssistant ProfessorDivision of CardiologyUniversity of Rochester School of MedicineRochester, NY, USA

Cary Ward, MDAssistant ProfessorDivision of CardiologyDuke University Medical CenterDurham, NC, USA

Preface

Randomized controlled trials (RCTs) represent the highest standard to test whether a therapeutic intervention is safe and effective. RCTs are of pivotal importance for regulatory authorities, healthcare providers, and medical associations for the introduction of new treatments in clinical practice. Cardiovascular medicine is a rapidly growing field with enormous innovation in the last decade. RCTs in cardiovascular medicine are usually performed under enormous time pressure to keep up with the dynamic advances in this field, but they need to comply with standards of quality. This apparent conflict between timely completion and reporting of RCTs, and the growing demands on good clinical research practice, creates a clear challenge to investigators and sponsors of clinical research. Additionally, as healthcare steadily improves, it is more difficult to show superiority of new treatments compared with established therapies; larger patient cohorts are often required to show that a new treatment is superior to its comparator. Despite these barriers, a myriad of landmark RCTs have been conducted in the last few years, leading to a major change in the treatment landscape and contributing to current guidelines in the cardiovascular field.

This book provides a unique overview of quality standards for clinical trials and guides the reader through methodological design, results, and interpretation of RCTs, using examples of recent important trials in major fields of cardiovascular medicine. Each of the major cardiovascular specialties is covered and modern concepts of diagnosis and management are described. This book is intended for clinicians who want an update on current developments in clinical trials in cardiovascular medicine, for those who plan to conduct a clinical trial, and last but not least, to assist in translating the evidence into practice. We would like to thank all the chapter authors for sharing their expert insights in this book. We would also like to thank Helen Whyte of the Royal Brompton Hospital for administrative support, Mary Banks (Wiley-Blackwell) for encouraging us to pursue the book, and Jon Peacock (Wiley-Blackwell) for editorial support in completing the manuscript.

Marcus D. Flather, Deepak L. Bhatt and Tobias Geisler

List of Abbreviations

CHAPTER 1

Introduction to Randomized Clinical Trials in Cardiovascular Disease

Tobias Geisler,1 Marcus D. Flather,2 Deepak L. Bhatt,3 and Ralph B. D’Agostino, Sr4

1University Hospital Tübingen, Tübingen Medical School, Tübingen, Germany

2University of East Anglia and Norfolk and Norwich University Hospital, Norwich, UK

3VA Boston Healthcare System; Brigham and Women’s Hospital and Harvard Medical School, Boston, MA, USA

4Boston University, Boston, MA, USA

What is a Randomized Clinical Trial?

The question “does it work” is common when a treatment is being considered for a patient. How do we know whether treatments “work” and what is the best way to demonstrate the efficacy and safety of new treatments? The main rationale behind a clinical trial is to perform a prospective evaluation of a new treatment in a rigorous and unbiased manner to provide reliable evidence of safety and efficacy. This is done by comparing the new treatment to a comparator or control treatment. Defining the term “clinical trial” is not as straightforward as it seems. In its simplest form, a clinical trial is any comparative evaluation of treatments involving human beings. Randomized clinical trials (RCTs) are the optimal means we use to achieve this demonstration. In this chapter we explore the relevance of RCTs to modern medicine and review strengths and weaknesses of this methodology (Table 1.1). As we will discuss below, RCTs represent the highest form of a clinical trial. Since the results of RCTs inform clinical practice guidelines, it is increasingly important for clinicians to understand their methodology, including their strengths and weaknesses. In this chapter we provide an overview of the main methodological aspects of well-designed RCTs.

Table 1.1 Issues for design/conduct and analysis of randomized clinical trials.

Study objective

Study populations

Efficacy variables

Control groups

Study design (bias)

Study design (samples)

Comparisons

Trial monitoring

Data analysis sets

Unit of analysis

Missing data

Analysis methods

Sample size/power

Safety

Subsets and more

Number of studies

Clinical significance

Concept of Randomization

The RCT is the most powerful design to prove whether or not there is a valid effect of a therapeutic intervention compared to a control. Randomization is a process of allocating treatments to groups of subjects using the play of chance. It is the mechanism that controls for factors except for the treatments, and allows comparison of the treatment under investigation with the control in an unbiased manner. It is important that information on the process of randomization is included in the trial protocol. The number of subjects allocated to each group, those who actually received the assigned treatment and reasons for non-compliance need to be recorded. In a representative analysis of trials listed in the free MEDLINE reference and abstract database at the United States National Library of Medicine (PubMed) in 2000, an adequate approach to random sequence generation was reported in only 21% of the trials [1]. This increased to 34% for a comparable cohort of PubMed-indexed trials in 2006 [2].

The procedure to assign interventions to trial participants is a critical aspect of clinical trial design. Randomization balances for known and unknown prognostic factors (covariates) allows the use of probability theory to express the likelihood that any difference in outcome between intervention groups merely reflects chance [3]. It facilitates blinding the identity of treatments to the investigators, participants, and evaluators, possibly by use of a placebo, which reduces bias after assignment of treatments [4]. Successful randomization is dependent on two related elements—generation of an unpredictable allocation sequence and concealment of that sequence until assignment takes place [5].

There are many procedures for randomization in the setting of a clinical trial and these will be discussed in detail below [see Study design (bias)]. For now we call attention to its importance in allowing the unbiased comparison of the investigational treatment and a control in a clinical trial.

Clinical Trial Phases

Preclinical Studies

Preclinical studies of potentially useful treatments are usually carried out to understand mechanisms of action, effect of different doses, and possible unwanted effects. There are two main types of preclinical studies—those using whole animal models and those using components of living tissue, usually cells or organs. Preclinical studies help to build up hypotheses about how and why treatments may work. Most of these experiments are not randomized and there may be substantial reporting bias (i.e., only interesting results are reported), but they are an essential step in the development of new treatments.

Phase 1 Clinical Trials

The first step to evaluate the safety of a new drug or biological substance after successful experiments in animals is to evaluate how well it can be tolerated in a small number of individuals. This phase is intended to test the safety, tolerability, pharmacokinetics (PK), and pharmacodynamics (PD) of a drug. Although it does not strictly meet the definition criteria of a clinical trial, this phase is often termed a phase 1 clinical trial. Usually, if the drug has a tolerable toxicological profile, a small number of healthy volunteers are recruited. If the drug has an increased toxicological profile, often critically ill patients are included in whom standard, guideline-based therapy fails. The design of phase 1 clinical trial is usually simple. In general, drugs are tested at different doses to determine the maximum tolerated dose (MTD) before signs of toxicity occur. The most difficult challenge in the planning of phase 1 trials is finding ways to adequately translate the animal experimental data into a dosing scheme and not to exceed the maximum tolerated dose in humans. Phase 1 clinical trials are dose-ranging studies to identify a tolerable dose range that can be evaluated further for safety in phase 2 trials. There are different ways to adjust doses in a phase 1 clinical trial, e.g., single ascending and multiple ascending dosing schemes. Studies in apparently healthy human volunteers usually involve short exposure to new treatments to understand the effects of different doses on human physiology. Starting at low or subtherapeutic doses, especially with novel immunogenic agents, is essential to ensure that unexpected serious side effects are reduced.

Phase 2 Clinical Trials

Phase 2 clinical trials refer to the results of phase 1 trials. Once the maximum tolerated dose has been defined and an effective and tolerable dose range has been determined, phase 2 trials are designed to investigate how well a drug works in a larger set of patients (usually 100–600 subjects and sometimes up to 4000 patients, depending on the number of groups to be investigated) and to continue measurements of PK and PD in a more global population. Some phase 2 trials are designed as case series where selected patients all receive the drug or as randomized trials where candidate doses of a drug are tested against placebo. Usually, different doses of a pharmacological treatment will be compared against placebo in a randomized study design with outcomes based on the mechanistic action of the treatment being evaluated. For example, phase 2 trials of anticoagulants will usually document laboratory measures of anticoagulant effect, incidence of major and minor bleeding, and effects on relevant clinical outcomes. Minimizing risk to patients is essential as most treatments evaluated in phase 2 trials will never be approved for human use. Strategy-based treatments such as new methods for percutaneous coronary intervention (PCI) or surgical procedures also have their equivalent “phase 2” trials in which the new techniques are systematically tested in smaller number of patients to ensure safety and feasibility before being tested in larger trials. For obvious reasons these trials cannot be “placebo controlled,” but should compare the new strategy with an established one. Sometimes “phase 2” trials of treatment strategies are not randomized, which often makes it difficult to draw conclusions about safety and feasibility, and to plan further larger trials.

As an example, in the phase 2 trial Anti-Xa Therapy to Lower cardiovascular events in Addition to standard therapy in Subjects with Acute Coronary Syndrome–Thrombolysis in Myocardial Infarction 46 (ATLAS-1-TIMI 46 trial), the oral factor Xa inhibitor rivaroxaban was tested in several doses (5 mg, 10 mg, or 20 mg total daily dose, given either once or twice daily) in a total of 3491 patients with acute coronary syndromes (ACS) being treated with aspirin or aspirin and clopidogrel and compared with placebo. There was a dose-related increase in bleeding and a trend toward a reduction in ischemic events with the addition of rivaroxaban to antiplatelet therapy in patients with recent ACS. The researchers found that patients assigned to 2.5 mg and 5.0 mg twice-daily rivaroxaban in both the aspirin alone and aspirin plus clopidogrel groups had the most efficacious results versus placebo [6]. These results led to a selection of these dosing groups for transition into a large phase 3 trial that enrolled 15 526 patients (ATLAS-2-TIMI-51) [7].

Phase 3 Clinical Trials

Phase 3 trials are usually RCTs, often multicenter, and including up to several thousand patients (the sample size depending upon the disease and medical condition being investigated). Due to the study size and duration, phase 3 trials are the most expensive, time-consuming, and complex trials to design and run, especially in therapies for chronic medical conditions, and are usually the “pivotal” trials for registration and marketing approval. Other possible motives for conducting phase 3 trials include plans to extend the label by the sponsor (i.e., to demonstrate the drug is effective for subgroups of patients/disease conditions beyond the use for which the drug was originally approved); to collect additional safety data; or to secure marketing claims for the drug. Trials at this stage are sometimes classified as “phase 3B trials” in contrast to “phase 3A trials,” denoting RCTs performed before marketing approval [8]. Once a drug has proved acceptable in phase 3 trials, the trial results are usually combined into a large comprehensive document describing the methods and results of animal (preclinical) and human (clinical studies), manufacturing processes, product characteristics (e.g., formulation, shelf-life). This document serves as a “regulatory submission” to be reviewed by the appropriate regulatory authorities in different countries before providing approval to market the drug.

Phase 4 Clinical Trials

In phase 4 trials, post-marketing studies delineate additional information, including the drug’s risks, benefits, and optimal use. They also aim to see if a treatment or medication can be used in other circumstances beyond the originally approval indications. Phase 4 clinical trials are done after a treatment has gone through all the other phases and is already approved by the regulatory health authorities. Phase 4 clinical trials may not necessarily be RCTs. A large body of phase 4 trials is made up of registries and observational studies.

The following discussion about the methodology will mainly focus on phase 3 confirmatory RCTs.

Study Objective

The search for new treatments is an evolutionary process, starting with a series of questions and eventually providing answers through a complex route that involves epidemiology (pattern and impact of disease in the population), basic science (cellular, mechanical, and genetic nature of the disease), and clinical trials to understand the response of patients to the new treatment. Trials that show clear benefits of treatments are usually followed by an assessment of cost and “affordability” to understand if the new treatment can actually be used in clinical practice. Some of these pathways are illustrated in Figure 1.1.

Figure 1.1 Generating evidence for new treatments.

The quest to find effective and safe treatments arises from the needs of patients who present with illness and suffering. Thus, most clinical research is responsive in nature; we are not trying to improve on the healthy human but rather to treat and prevent illness and disease. However, in order to find an effective treatment, it is essential to understand the cause and pathology of the disease. Once specific causes are identified, whether they are protein deficiencies, transport errors, metabolic problems or genetic defects, it becomes possible to identify potential treatments that can then be tested in clinical trials. The challenge is that clinical trials take time and are costly to run, which means that they should be reserved for clinically important questions. Most clinical trials are set up and run by industry for commercial gain—often as industry/academic partnerships—but it should be emphasized that important health issues should be supported by the major healthcare providers, including governments and insurance agencies as part of their programs to improve health [1]. At present, most independent, non-commercial medical research is funded by competitive grants from governments or charities. While the competitive process helps to maintain high standards, it is an unpredictable method of funding and can lead to delays in carrying out important clinical trials. Lastly, well-intentioned but bureaucratic regulations applied to medical research are actually leading to substantial delays in important and effective treatments reaching patients in a timely manner. Thus, randomized trials are needed as the final pathway to test the hypothesis “Does it work?”. To answer this question reliably, large trials involving many patients from many centers are needed, which means that trial procedures including data collection and analysis need to be as simple and streamlined as possible [9,10].

Given all the above, when a specific phase 3 clinical trial is being designed, the first question is “What is the specific objective?”. For example, with the ATLAS-2 trial mentioned above, the objective was to establish the safety and effectiveness of rivaroxaban with both aspirin alone and aspirin and clopidogrel in reducing ischemic events in patients with ACS. The study objective must be explicitly stated in the study protocol (see below) and drives the study design, implementation, and analysis.

Study Populations

The characteristics and features of the subjects to be enrolled in the clinical trial becomes the next issue and should be defined beforehand, using unequivocal inclusion (eligibility) criteria. A complete report of the eligibility criteria used to enrol the trial participants is required to assist readers in the interpretation of the study. In particular, a clear knowledge of these criteria is needed to evaluate to whom the results of a trial apply, i.e., the trial’s generalizability (applicability) and importance for clinical or public health practice [11,12]. Since eligibility criteria are applied before randomization, they do not have an impact on the internal validity of a trial, but they are central to its external validity. It is important to differentiate between sample population and target population with regard to generalizability of results. The sample population is the population from which study subjects will be enrolled. The target population is the population to which the clinical trial results will be generalized. These are not necessarily the same. The eligibility criteria create a sample population that might significantly deviate from the target population. Thus, eligibility criteria should be kept as general and as realistic as possible. Ideally, study subjects should correspond to those to whom the product will be marketed. Demographic factors (age, gender, and race) and, when appropriate, socioeconomic status should be representatively covered. In addition, there is a sentiment that the study conditions should be realistic. For example, for over-the-counter drugs, regulatory authorities often require, before a drug is approved, the performance of clinical trials in settings similar to those in which the drug will actually be taken. These studies are called “actual use” studies.

Typical selection criteria include the nature and stage of the disease being studied, the exclusion of persons who may be harmed by the study treatment, and issues required to ensure that the study satisfies legal and ethical norms. Informed consent by study participants, for example, is a mandatory inclusion criterion in all clinical trials. The information about the number of patients being screened and meeting the eligibility criteria should be provided in flow diagrams (an example according to the CONSORT statement is shown in Figure 1.2).

Figure 1.2 Flow diagram showing the progress through different stages of a parallel randomized trial of two groups (i.e., enrolment, intervention allocation, follow-up, and data analysis). (According to http://www.consort-statement.org/consort-statement and Moher et al. [106].)

Efficacy Variables

Clinical trials can have numerous efficacy variables. However, it is essential that the primary efficacy variables should be kept to a minimum. The study objectives and efficacy variables should relate clearly and sharply to each other. Since large amounts of data can be collected and stored electronically, weighting their importance and relevance to the study objectives is crucial, and excess data collection is an important cause of poor trial performance. The primary efficacy variable should be the variable capable of providing the most clinically relevant and convincing evidence directly related to the primary objective of the trial. Ideally, there should only be one or a small number of primary variables. Multiple primary efficacy variables, however, are sometimes used in clinical trials with the hope of increasing the statistical power while keeping the sample size low. These can be counterproductive and increase the chance of producing inconclusive results. Careful consideration of how to deal with “multiple testing” or “alpha spending” is recommended [13,14]. The latter term describes how to distribute the type I or alpha error associated with testing the primary efficacy variables. Other efficacy variables are classified as secondary and usually summarize variables that further support the primary variables and/or provide more information on the study objectives. Quality of life scales are an example of standard secondary efficacy variables in many clinical trials.

Remarkable effort has been made to solve the multiple testing problems associated with the primary variables. Exclusive testing of individual variables is one approach. The development of composite variables has been shown to be very helpful. These range from the combinations of endpoints, such as combining ischemic stroke, fatal and non-fatal coronary events ,and hospitalizations in cardiovascular studies, to scoring scales developed by sophisticated psychometric techniques. Global assessment variables are also used to measure an overall composite.

Another issue of focus concerns the allocation of the alpha error to secondary variables, especially when the effects on the primary variables are not statistically significant [15–17]. For example, in a cardiovascular disease trial, how should the results be interpreted when the primary outcome variable (e.g., exercise testing or improvement of NYHA classification) is not significant at the 0.05 level, but the significance level for a secondary variable related to overall mortality is highly significant at 0.001? [18]. It is hard to ignore such a finding when it refers to a hard clinical endpoint such as mortality. A prior allocation of alpha may need to be applied to major secondary endpoints. Future clinical trials in the same field should have the latter variables as the primary variables.

Surrogate Variables

A surrogate endpoint is an intermediate endpoint that serves as a surrogate for a true endpoint if it can be used in lieu of the true endpoint to assess treatment benefit (i.e., reliable predictor of the clinical benefit). A surrogate variable should also be able to capture adverse effects. More specifically, it is a laboratory parameter or a physical sign used as a substitute for a clinically meaningful endpoint (e.g., measures of brain natriuretic peptide or 6-minute walking distance as surrogate for worsening heart failure; blood pressure or cholesterols levels as surrogates for coronary events; cardiac necrosis marker levels, Holter-detected ischemia, or microvascular obstruction detected on MRI as surrogates for severity of ischemic heart disease). As a surrogate variable usually represents an intermediate endpoint, it is obtained much sooner than the clinical endpoint of interest. It is usually much cheaper to obtain and has a more frequent incidence than the original endpoint. Surrogate variables have received increasing attention [19,20]. The challenge is to choose a surrogate variable that correlates strongly with the desired clinical endpoint. As an example, a commonly proposed intermediate surrogate variable for stroke is common carotid artery intima–media thickness (IMD) progression as measured by carotid ultrasound [21]. The progression of IMD occurs much earlier than stroke. The question is how well this relates to later development of the event. The value of measuring surrogate variables has been questioned, e.g., regulatory agencies claim that if the surrogate parameter has an effect on a “hard” clinical outcome (e.g., death or myocardial infarction), then the surrogate outcome should be a direct measurement of these. Additionally, history tells us that surrogate outcomes are not always related to the desired clinical outcome [25]. In the classic examples of the Cardiac Arrhythmia Pilot Study (CAPS) and the Cardiac Arrhythmia Suppression Trial (CAST), a combination of encainide/flecainide showed a reduction of the surrogate endpoint of ventricular extrasystoles and arrhythmias, but total mortality and arrhythmic deaths were significantly increased in the treatment arm [22,23]. More recently, in the Heart and Estrogen/Progestin Replacement Study (HERS), estrogen use in post-menopausal women with coronary disease was associated with a modest reduction in cholesterol, but this was not associated with any reduction in cardiovascular deaths or myocardial infarction [24]. Finally, in the Antihypertensive and Lipid-Lowering Treatment to prevent Heart Attack Trial (ALLHAT), of a total of 44 000 patients, 9067 were randomized to doxazosin and 15 268 to chlorthalidone. Blood pressure was lowered by both treatments. However, treatment with doxazosin was significantly associated with a higher incidence of congestive heart failure, whereas chlorthalidone had beneficial effects on heart failure incidence [25]. Analysis of the data suggests that chlorthalidone may have some beneficial effect beyond the blood pressure effect. If blood pressure reduction, a surrogate endpoint, had been the primary endpoint variable, this conclusion would not have been reached.

Control Groups

In principle, there are two ways to show that a therapy is effective. One can demonstrate that a new therapy is better or roughly equivalent to a known effective treatment, or better than a placebo. In many RCTs, one group of patients is given an experimental drug or treatment, while the control group receives either a standard treatment for the illness or a placebo. Control groups in clinical trials can be defined using two different classifications: the type of treatment allocated and the method of determining who will be in the control group. The type of treatment can be categorized as followed: placebo or vehicle; no treatment; different dose or regimen from the study treatment, or different active treatment. The principal methods of creating a control group are by randomized allocation of a prospective control group or by selection of a control population separate from the investigated population (external or historical control) [26].

Placebo-Controlled Trials

A placebo-controlled trial is a way of testing a therapy against a separate control group receiving a sham “placebo” treatment, which is specifically designed to have no real pharmacological effect, and is a key strategy to reduce bias by avoiding knowledge of treatment allocation. Placebo treatment is usually a characteristic of blinded trials, where subjects and/or investigators do not know whether they are receiving a real or placebo treatment. The main purpose of the placebo group is to take account of the “placebo” effect, which consists of symptoms or signs that occur through the taking of a placebo treatment.

Active-Control Trials

In an active-control (also called positive-control) trial, subjects are randomly assigned to the test treatment or to an active-control drug. Such trials are usually double blind, but this is not always possible due to different treatment regimens, routes of administration, monitoring of drug effects, or obvious side effects. Active-control trials can have different objectives with respect to demonstrating efficacy.

The ability to conduct a placebo-controlled trial ethically in a given situation does not necessarily mean that placebo-controlled trials should be conducted when effective therapy exists. Patients and treating physicians might still favor a trial in which every participant receives an active treatment. Still, placebo-controlled trials are frequently needed to demonstrate the effectiveness of new treatments and often cannot be replaced by active-control trials that show that a new drug is equivalent or non-inferior to an established agent. The limitations of active-control equivalence trials that are intended to show the effectiveness of a new drug have long been recognized [27–29], but are perhaps not as widely appreciated as they should be.

Study Design (Bias)

Bias can be loosely defined as “any influence that causes the results of a trial to deviate from the truth.” This broad definition implies that any element of study design or conduct (including analysis of results) could contribute to bias. In practice, we are particularly concerned about the method of randomization, compliance with treatment, systematic differences in concomitant treatments after randomization (especially in unblinded trials), completeness of follow-up, quality of data, and reporting of outcome measures . Systematic bias occurs when there is a difference in the treatment groups that does not occur by chance, and therefore the measurement of treatment effect may be unduly influenced. Systematic biases are mainly observed in non-randomized comparisons of treatment effects, such as those carried out in observational studies. Randomization, if performed correctly, can balance group differences and minimize systematic bias, to enable the quantification of the true effects of the interventions. Random allocation does not, however, protect RCTs against other types of bias.

Methods of Randomization

Several methods exist to generate allocation sequences. Besides true random allocation, the sequence may be generated by the process of minimization, a non-random but generally acceptable method (see Table 1.2).

Table 1.2 Methods of sequence generation [30].

Simple (unrestricted) randomization

Restricted randomization

Stratified randomization

Minimization

Simple (Unrestricted) Randomization

This method is the most basic of allocation approaches. Analogous to repeated fair coin-tossing, this method is associated with complete unpredictability of each intervention assignment. No other allocation generation approach, irrespective of its complexity and sophistication, surpasses the unpredictability and bias prevention of simple randomization.

Restricted Randomization

Restricted randomization procedures control the probability of obtaining an allocation sequence with an undesirable sample size imbalance in the intervention groups. In other words, if researchers want treatment groups of equal sizes, they should use restricted randomization.

Stratified Randomization

Randomization can create chance imbalances on baseline characteristics of treatment groups. Investigators sometimes avert imbalances by using prerandomization stratification on important prognostic factors, such as age or disease severity. In such instances, researchers should specify the method of restriction (usually blocking). To reap the benefits of stratification, investigators must use a form of restricted randomization to generate separate randomization schedules for stratified subsets of participants defined by the potentially important prognostic factors.

Minimization

Minimization is a dynamic randomization algorithm designed to reduce disparity between treatments by taking stratification factors into account. Important prognostic factors are identified before the trial starts and the assignment of a new subject to a treatment group is determined in order to minimize the differences between the groups regarding these stratification factors. In contrast to stratified randomization, minimization intends to minimize the total imbalance for all factors together, instead of considering only predefined subgroups [31].Concerns over the use of minimization have focused on the fact that treatment assignments may be anticipated in some situations and on the impact on the analysis methods being used [32].

The practicality of randomization in a clinical trial can be complicated [33]. The conventional method is for a random number list to be generated by computer and a then treatment allocation list drawn up using the last digit (even or odd) to determine the treatment group. Patients entering the trial are then allocated according to the preprepared randomization list. It is essential that investigators do not have access to this list as they will of course then know the next allocation which can lead to a range of biases. Most trials use a method of central randomization using a telephone- or internet-based system for investigators to randomize patients. This method ensures that all patients are registered in the trial database and that prior knowledge of treatment allocation is not possible. Trials of double-blind pharmacological treatments (i.e., those in which the “active” and “placebo” treatments appear identical) have additional practical issues as the randomization list is used in the production and labeling process. Drug supplies must be provided to centers in “blocks” usually consisting of even amounts of active and placebo in identical packages, except for unique study identification numbers that can be used in emergencies to link the drug pack to the original randomization list for unblinding purposes.

The term “random” is often misused in the literature to describe trials in which non-random, deterministic allocation methods were applied, such as alternation or assignment based on date of birth, case record number, or date of presentation. These allocation techniques are sometimes referred to as “quasi-random.” A central weakness with all systematic methods is that concealing the allocation is usually impossible, which allows anticipation of intervention and biased assignments. The application of non-random methods in clinical trials likely yields biased results [4,34,35].

Readers cannot judge adequacy from terms such as “random allocation,” “randomization,” or “random” without further elaboration. Thus, investigators should clarify the method of sequence generation, such as a random-number table or a computerized random number generator.

In some trials, participants are intentionally allocated in unequal numbers to each intervention and control: e.g., to gain more experience with a new procedure or to limit the size and costs of the trial. In such cases, the randomization ratio (e.g., 2:1 or two treatment participants per each control participant) is reported.

Random and Systematic Error

When the clinical trial results are produced, the differences observed between treatments may represent true outcome differences. However, it is essential that the investigator (and the reader) consider the chance that the observed effects are due to either random error or systematic error. Random error is the result of either biological or measurement variation, whereas systematic error is the result of a variety of biases that can affect the results of a trial (Table 1.3). The process of analyzing the outcomes of a study for random error includes both estimation and statistical testing. Estimates describing the distribution of measured parameters may include point estimates (such as means or proportions) and measures of precision (such as confidence intervals).

Table 1.3 Potential sources of systematic bias at different stages in the course of a trial.

Planning phase

Choice of research question

Type of research study

Recruitment phase

Allocation of participants to study groups

Selection bias (eligible individuals are excluded, because the investigator knows the allocation to treatment group)

Delivery of interventions

Measurement of outcomes

Post-recruitment phase

Loss to follow-up

Analysis

Dissemination of results

Interpretation of the results by the study group or external persons (e.g., reviewer)

Study Design Issues to Overcome Systematic Bias

As stated above, the most important design techniques to overcome bias in clinical trials are blinding and randomization. Most trials follow a double-blind approach in which treatments are prepacked in accordance with a suitable randomization schedule, and supplied to the trial center(s) labeled only with the subject number and the treatment period: no one involved in the conduct of the trial is aware of the specific treatment allocated to any particular subject, not even as a code letter. Bias can also be reduced at the design stage by specifying procedures in the protocol aimed at minimizing any anticipated irregularities in trial conduct that might impair a satisfactory analysis, including various types of protocol violations, withdrawals, and missing values. The study design should consider ways both to minimize the frequency of such problems, and also to handle the problems that do occur in the analysis of data.

Blinding

Blinding or masking is used in clinical trials to curtail the occurrence of conscious and unconscious bias in the conduct and interpretation of a clinical trial, caused by the impact that the insight into treatment may have on the enrolment and allocation of subjects, their subsequent care, the compliance of subjects with the treatments, the evaluation of endpoints, the handling of drop-outs, the analysis of data, etc.

A double-blind trial is a trial in which neither the investigator nor the study participant or sponsor who is involved in the treatment or investigation of the subjects is aware of the treatment received. This includes anyone who evaluates eligibility criteria or analyses endpoints, or assesses protocol. The principle of blinding is maintained throughout the whole course of the trial, and only when the data are cleaned to an appropriate level, can particular personnel can be unblinded. If unblinding to the allocation code to any staff who are not involved in the treatment or clinical evaluation of the subjects is required (e.g., bioanalytical scientists, auditors, those involved in serious adverse event reporting), adequate standard operating procedures should exist to guard against inappropriate publication of treatment codes. In a single-blind trial, the investigator and/or his/her staff are conscious of the treatment but the subject is not, or vice versa. In an open-label trial, the identity of treatment is known to all participants/study personal. Double-blind trials are the optimal approach, but are associated with greater complexity in providing placebo and the process of drug supply and packaging.