[ps2id id=’background-and-rationale’ target=”/]6. BACKGROUND AND RATIONALE
6a. Background and rationale
Description of research question and justification for undertaking the trial, including summary of relevant studies (published and unpublished) examining benefits and harms for each intervention.
Example
“Background
Introduction: For people at ages 5 to 45 years, trauma is second only to HIV/AIDS as a cause of death . . .
Mechanisms: The haemostatic system helps to maintain the integrity of the circulatory system after severe vascular injury, whether traumatic or surgical in origin.[Reference X] Major surgery and trauma trigger similar haemostatic responses . . . Antifibrinolytic agents have been shown to reduce blood loss in patients with both normal and exaggerated fibrinolytic responses to surgery, and do so without apparently increasing the risk of post-operative complications . . .
Existing knowledge: Systemic antifibrinolytic agents are widely used in major surgery to prevent fibrinolysis and thus reduce surgical blood loss. A recent systematic review [Reference X] of randomised controlled trials of antifibrinolytic agents (mainly aprotinin or tranexamic acid) in elective surgical patients identified 89 trials including 8,580 randomised patients (74 trials in cardiac, eight in orthopaedic, four in liver, and three in vascular surgery). The results showed that these treatments reduced the numbers needing transfusion by one third, reduced the volume needed per transfusion by one unit, and halved the need for further surgery to control bleeding. These differences were all highly statistically significant. There was also a statistically non-significant reduction in the risk of death (RR=0.85: 95% CI 0.63 to 1.14) in the antifibrinolytic treated group
. . .
Need for a trial: A simple and widely practicable treatment that reduces blood loss following trauma might prevent thousands of premature trauma deaths each year and secondly could reduce exposure to the risks of blood transfusion. Blood is a scarce and expensive resource and major concerns remain about the risk of transfusion-transmitted infection . . . A large randomised trial is therefore needed of the use of a simple, inexpensive, widely practicable antifibrinolytic treatment such as tranexamic acid . . . in a wide range of trauma patients who, when they reach hospital are thought to be at risk of major haemorrhage that could significantly affect their chances of survival.
Dose selection
The systematic review of randomised controlled trials of antifibrinolytic agents in surgery showed that dose regimens of tranexamic acid vary widely.[Reference X] . . .
In this emergency situation, administration of a fixed dose would be more practicable as determining the weight of a patient would be impossible. Therefore a fixed dose within the dose range which has been shown to inhibit fibrinolysis and provide haemostatic benefit is being used for this trial . . . The planned duration of administration allows for the full effect of tranexamic acid on the immediate risk of haemorrhage without extending too far into the acute phase response seen after surgery and trauma.” 65
Explanation
The value of a research question, as well as the ethical and scientific justification for a trial, depend to a large degree on the uncertainty of the comparative benefits or harms of the interventions, which depends in turn on the existing body of knowledge on the topic. The background section of a protocol should summarise the importance of the research question, justify the need for the trial in the context of available evidence, and present any available data regarding the potential effects of the interventions (efficacy and harms).66;67 This information is particularly important to the trial participants and personnel, as it provides motivation for contributing to the trial.69 It is also relevant to funders, REC/IRBs, and other stakeholders who evaluate the scientific and ethical basis for trial conduct.
To place the trial in the context of available evidence, it is strongly recommended that an up-to-date systematic review of relevant studies be summarised and cited in the protocol.70 Several funders request this information in grant applications.71;72 Failure to review the cumulated evidence can lead to unnecessary duplication of research or to trial participants being deprived of effective, or exposed to harmful, interventions.73-76 A minority of published trial reports cite a systematic review of pre-existing evidence,77;78 and in one survey only half of trial investigators were aware of a relevant existing review when they had designed their trial.79 Given that about half of trials remain unpublished,80-82 and that published trials often represent a biased subset of all trials,80;83 it is important that systematic reviews include a search of online resources such as trial registries, results databases, and regulatory agency websites[ps2id id=’choice-of-comparators’ target=”/].84
6b. Choice of comparators
Explanation for choice of comparators.
Example
“Choice of comparator
In spite of the increasing numbers of resistant strains, chloroquine monotherapy is still recommended as standard blood-stage therapy for patients with P. [Plasmodium] vivax malaria in the countries in which this trial will be conducted. Its selection as comparator is therefore justified. The adult dose of chloroquine will be 620 mg for 2 days followed by 310 mg on the third day and for children 10 mg/kg for the first two days and 5 mg/kg for the third day. Total dose is in accordance with the current practice in the countries where the study is conducted. The safety profile of chloroquine is well established and known. Although generally well tolerated, the following side-effects of chloroquine treatment have been described:
Gastro-intestinal disturbances, headache, hypotension, convulsions, visual disturbances, depigmentation or loss of hair, skin reactions (rashes, pruritus) and, rarely, bone-marrow suppression and hypersensitivity reactions such as urticaria and angioedema. Their occurrence during the present trial may however be unlikely given the short (3-day) duration of treatment.” 85
Explanation
The choice of control interventions has important implications for trial ethics, recruitment, results, and interpretation. In trials comparing an intervention to an active control or usual care, a clear description of the rationale for the comparator intervention will facilitate understanding of its appropriateness.86;87 For example, a trial in which the control group receives an inappropriately low dose of an active drug will overestimate the relative efficacy of the study intervention in clinical practice; conversely, an inappropriately high dose in the control group will lead to an underestimate of the relative harms of the study intervention.87;88
The appropriateness of using placebo-only control groups has been the subject of extensive debate and merits careful consideration of the existence of other effective treatments, the potential risks to trial participants, and the need for assay sensitivity–that is, ability to distinguish an effective intervention from less effective or ineffective interventions.89;90 In addition, surveys have demonstrated that a potential barrier to trial participation is the possibility of being allocated a placebo-only or active control intervention that is perceived to be less desirable than the study intervention.68;69;91;92 Evidence also suggests that enrolled participants perceive the effect of a given intervention differently depending on whether the control group consists of an active comparator or only placebo.93-96
Finally, studies suggest that some ‘active’ comparators in head-to-head randomised trials are presumed by trial investigators to be effective despite having never previously been shown to be superior to placebo.74;97 In a systematic review of over 100 head-to-head antibiotic trials for mild to moderate chronic obstructive pulmonary disease74 cumulative meta-analysis of preceding placebo-controlled trials did not show a significant effect of antibiotics over placebo. Such studies again highlight the importance of providing a thorough background and rationale for a trial and the choice of comparators – including data from an up-to-date systematic review – to enable potential participants, physicians, REC/IRBs, and funders to discern the merit of the trial.[ps2id id=’objectives’ target=”/]
[ps2id id=’objectives’ target=”/] 7. OBJECTIVES
Specific objectives or hypotheses.
Example
“1.1 Research Hypothesis
Apixaban is noninferior to warfarin for prevention of stroke (hemorrhagic, ischemic or of unspecified type) or systemic embolism in subjects with atrial fibrillation (AF) and additional risk factor(s) for stroke.
. . .
2 STUDY OBJECTIVES
2.1 Primary Objective
To determine if apixaban is noninferior to warfarin (INR [international normalized ratio] target range 2.0-3.0) in the combined endpoint of stroke (hemorrhagic, ischemic or of unspecified type) and systemic embolism, in subjects with AF [atrial fibrillation] and at least one additional risk factor for stroke.
2.2 Secondary Objectives
2.2.1 Key Secondary Objectives
The key secondary objectives are to determine, in subjects with AF and at least one additional risk factor for stroke, if apixaban is superior to warfarin (INR target range 2.0 – 3.0) for,
- the combined endpoint of stroke (hemorrhagic, ischemic or of unspecified type) and systemic embolism
- major bleeding [International Society of Thrombosis and Hemostasis]
- all-cause death
2.2.2 Other Secondary Objectives
- To compare, in subjects with AF and at least one additional risk factor for stroke, apixaban and warfarin with respect to:
— the composite endpoint of stroke (ischemic, hemorrhagic, or of unspecified type), systemic embolism and major bleeding, in warfarin naive subjects
. . .
- To assess the safety of apixaban in subjects with AF and at least one additional risk factor for stroke.” 98
Explanation
The study objectives reflect the scientific questions to be answered by the trial, and define its purpose and scope. They are closely tied to the trial design (Item 8) and analysis methods (Item 20). For example, the sample size calculation and statistical analyses for superiority trials will differ from those investigating non-inferiority.
The objectives are generally phrased using neutral wording (e.g., “to compare the effect of treatment A versus treatment B on outcome X”) rather than in terms of a particular direction of effect.99 A hypothesis states the predicted effect of the interventions on the trial outcomes. For multi-arm trials, the objectives should clarify the way in which all the treatment groups will be compared (e.g., A versus B; A versus C).
[ps2id id=’trial-design’ target=”/]
8. TRIAL DESIGN
Description of trial design including type of trial (e.g., parallel group, crossover, factorial, single group), allocation ratio, and framework (e.g., superiority, equivalence, non-inferiority, exploratory).
Example
“The PROUD trial is designed as a randomised, controlled, observer, surgeon and patient blinded multicenter superiority trial with two parallel groups and a primary endpoint of wound infection during 30 days after surgery . . . randomization will be performed as block randomization with a 1:1 allocation.” 100
Explanation
The most common design for published randomised trials is the parallel group, two-arm, superiority trial with 1:1 allocation ratio.101 Other trial types include crossover, cluster, factorial, split-body, and n-of-1 randomised trials, as well as single-group trials and non-randomised comparative trials.
For trials with more than one study group, the allocation ratio reflects the intended relative number of participants in each group (e.g., 1:1 or 2:1). Unequal allocation ratios are used for a variety of reasons, including potential cost savings, allowance for learning curves, and ethical considerations when the balance of existing evidence appears to be in favour of one intervention over the other.102 Evidence also suggests a preference of some participants for enrolling in trials with an allocation ratio that favours allocation to an active treatment.92
The framework of a trial refers to its overall objective to test the superiority, non-inferiority, or equivalence of one intervention with another, or in the case of exploratory pilot trials, to gather preliminary information on the intervention (e.g., harms, pharmacokinetics) and the feasibility of conducting a full-scale trial.
It is important to specify and explain the choice of study design because of its close relation to the trial objectives (Item 7) and its influence on the study methods, conduct, costs,103 results,104-106 and interpretation. For example, factorial and non-inferiority trials can involve more complex methods, analyses, and interpretations than parallel group superiority trials.107;108 In addition, the interpretation of trial results in published reports is not always consistent with the pre-specified trial framework,6;109;110 especially among reports claiming post hoc equivalence based on a failure to demonstrate superiority rather than a specific test of equivalence.109
There is increasing interest in adaptive designs for clinical trials, defined as the use of accumulating data to decide how to modify aspects of a study as it continues, without undermining the validity and integrity of the trial.111;112 Examples of potential adaptations include stopping the trial early, modifying the allocation ratio, re-estimating the sample size, and changing the eligibility criteria. The most valid adaptive designs are those in which the opportunity to make adaptations is based on pre-specified decision rules that are fully documented in the protocol (Item 21b).