An introduction to clinical trial design

Accepted Manuscript Review An Introduction to Clinical Trial Design A. Schultz, BR. Saville, JA. Marsh, TL. Snelling PII: DOI: Reference:

S1526-0542(19)30060-0 https://doi.org/10.1016/j.prrv.2019.06.002 YPRRV 1332

To appear in:

Paediatric Respiratory Reviews

Received Date: Accepted Date:

28 March 2019 18 June 2019

Please cite this article as: A. Schultz, BR. Saville, JA. Marsh, TL. Snelling, An Introduction to Clinical Trial Design, Paediatric Respiratory Reviews (2019), doi: https://doi.org/10.1016/j.prrv.2019.06.002

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An Introduction to Clinical Trial Design Schultz A1,2,3, Saville BR4,5, Marsh JA3,6, Snelling TL3,7,8,9 1Faculty

of Health and Medical Sciences, University of Western Australia Medical School, Crawley, Australia 2Department

of Respiratory Medicine, Perth Children’s Hospital, Nedlands, Australia

3Wesfarmers

Centre of Vaccines & Infectious Diseases, Telethon Kids Institute, University of Western Australia, Nedlands, Australia 4Berry

Consultants, Austin, USA

5Vanderbilt

University Department of Biostatistics, Nashville, TN, USA

6School

of Population & Global Health, University of Western Australia, Nedlands, Australia

7School

of Public Health, Curtin University, Bentley, Australia

8Department 9Menzies

of Infectious Diseases, Perth Children’s Hospital, Nedlands, Australia

School of Health Research and Charles Darwin University, Darwin, Northern Territory,

Australia

Keywords Clinical trial design, randomisation, adaptive trial design

Educational Aims The reader will be able to:   

Understand core considerations for designing and evaluating confirmatory clinical trials Know the basic types of confirmatory clinical trials used to inform clinical practice Appreciate the main strengths and weaknesses of the different types of confirmatory clinical trial designs

Future directions for clinical research The future will see more platform trials that allows for multiple questions to be addressed sequentially with the same trial infrastructure. Bayesian informed study designs that allows for multiple specialised features will increasingly be used. Adaptive study designs will allow for greater trial efficiency.

Summary 1

Clinicians and other decision makers in healthcare use results from clinical trials to inform practice. Interpretation of clinical trial results can be challenging, as weaknesses in trial design, data collection, analysis or reporting, can compromise the usefulness of results. A good working knowledge of clinical trial design is essential to expertly interpret and determine the validity and generalizability of the results. This manuscript will give a brief overview of clinical trial design including the strengths and limitations of various approaches. The focus will be on confirmatory clinical trials.

Introduction In the era of evidence based medicine, randomised controlled clinical trials have a position of primacy in informing clinicians and other decision-makers about the comparative efficacy and safety of treatments. Information generated by a clinical trial is generally only useful if the trial was well designed. This requires clearly articulated research questions and appropriate definitions of eligible participants, outcomes and study structures to minimise confounding and other biases. No single trial design is uniformly best across all possible settings; therefore a sound understanding of the strengths and weaknesses of various clinical trial designs is important. The purpose of this manuscript is to provide a very broad overview of fundamental considerations in trial design. For a deeper understanding of the issues and nuances accompanying each topic, we encourage readers to pursue the cited works and other related publications. Although there seem to be an endless number of important trial considerations to ensure trial validity (e.g. data collection, data analysis, transparent reporting), this manuscript will limit its focus to some of the key

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design issues for clinical trial trials designed to demonstrate evidence of efficacy or safety.

Important concepts in trial design Clinical trial design starts with the formulation of the research question1 and the identification of potential sources of bias. The research question should explicitly articulate the population, intervention, comparator, and outcomes (PICO) to be measured2.

Study population The study population should be clearly defined in terms of age, gender, physical condition and disease status and/or biomarker status. Narrow eligibility criteria will increase the homogeneity of the study population and thereby reduce variability in participant characteristics that could influence treatment response – this tends to improve precision of treatment effect estimates, but at the cost of reduced generalisability of the study results. Broader eligibility criteria may increase the applicability of study results to the general population3 and also facilitate participant accrual. For example, including only otherwise healthy, younger individuals in a trial may reduce the variability in the outcome but the efficacy and safety observed in the trial may not be applicable to older people.

Choice of intervention

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Trial interventions should be described as clearly as possible, e.g. with regard to formulation, dose, route and duration in the case of drugs. More complex interventions may comprise multi-component ‘bundles’ which may require a degree of flexibility in their application across different contexts. The approach to evaluating complex interventions has been described in detail elsewhere4.

Choice of comparator In most clinical trials the outcomes of participants in the intervention arm(s) are compared to those in one or more comparator or ‘control’ groups. A control group allows one to infer whether the outcomes observed in the intervention group are superior or non-inferior to the standard of care. The use of a control arm also allows an assessment of whether any improvement in the outcome in the treatment group is attributable to the trial intervention or just a natural progression of the disease over time. Physiological parameters, like blood pressure, vary around their mean value; if the individual must have an abnormal measurement at baseline to reach the criteria for inclusion (e.g. high blood pressure), then this measurement will tend towards their mean value over time - a phenomenon known as ‘regression to the mean’. Use of historical controls or comparison to a historical rate, typically from a patient registry, can be an inexpensive method for the evaluation of new treatments5. However, this assumes that the distribution of other factors, such as those discussed under Study Population, have remained unchanged. For diseases where the outcome is universally bad, for example a disease which is universally fatal or where spontaneous recovery almost never occurs, an argument may be made that a control group is unnecessary and, in the case of highly promising treatments, may be unethical. 4

Observational data, no matter how large the data source, may be subject to multiple sources of bias, such as confounding by factors that influence clinician treatment choices, systematic differences between treatment and comparator groups in how outcomes are ascertained, drift over time in the characteristics of the patient population, presence of comorbidities and changes in concomitant patient care. In addition to enrolling a contemporaneous (parallel) control arm, bias can be further minimised by randomly assigning participants to the active or control arm6.

Randomisation

Observed differences in the risk or rate of an outcome between an intervention and comparator group in a trial may occur because of: (1.) a true effect of the treatment, (2.) a chance occurrence, or (3.) confounding by systematic differences in baseline characteristics between the two groups. Confounding occurs when some factor which impacts on the outcome also influences whether an individual is in the intervention or comparator group. For example, if patients are allocated to treatments at clinician discretion rather than by random assignment, and if those with more severe disease are preferentially allocated to receive the standard of care rather than an investigational treatment, then the results will tend to show better outcomes in the investigational group than in the standard of care group even if the investigational treatment confers no benefit.

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Randomisation is a method for ensuring assignment to intervention or comparator groups is not influenced by any factors that might also be associated with the outcome. Participants are allocated, often equally, to the intervention or control arms using a process with a random component, which is usually computer generated. The overall probability of being allocated to any one group is known, but the each assignment occurs as a random process. For example, an unbiased coin can be used to allocate people equally to two groups (1:1 or 50%:50%) but the outcome for each toss of the coin cannot be known in advance. This reduces the potential for selection bias and confounding6, 7. Randomisation schemes may be simple, restricted or adaptive.

Simple randomisation is when each new intervention assignment is completely independent of all previous assignments. Typically the ratio of assignment to the intervention and comparator groups is 1:1, and this usually results in the best precision of effect estimates. If 1:1 assignment is used and the number of study participants is large, the number assigned to each group should be approximately equal; but there may be moderate imbalance in the size of groups by chance, especially if the study size is small8. Unequal allocation ratios may be valid and considered in particular circumstances9 e.g. in situations where enrolment will be facilitated if participants are more likely to be allocated to the active treatment group than to a placebo, or to generate more safety data on the experimental arm.

Restricted randomisation schemes are used to minimise chance imbalance in the size of the intervention and comparator groups, especially when the study size is

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small. These techniques may increase the precision of the effect estimate by improving the balance of baseline factors across the groups10.However, often the gains in terms of the power to test a hypothesis are modest compared to simple randomisation11. Two main schemes for restricted randomisation exist: blocking and stratification. With blocking, randomisation occurs according to allocation ratios and where these ratios are guaranteed within a smaller block of a pre-specified size which contains all possible randomisation sequences within12. A block size of four with 1:1 allocation to the two groups A and B could contain the sequences AABB, BBAA, ABAB, BABA, ABBA or BAAB. During trial execution all interventions within a block are assigned in order before moving to the next block. By ensuring that the proportion of participants assigned to the intervention and comparator groups closely approximates the allocation ratios at all stages of the trial, blocking can help to achieve covariate balance for time-related factors that might otherwise influence the outcome1. A risk of blocking is that if site staff are un-blinded (or inadequately blinded) to previous allocations they may be able to partially anticipate future assignments, and this might influence their decision to enrol a participant. For example, site staff may decline to enrol a participant with severe disease if they can anticipate the next assignment is more likely to be for an investigational treatment than for the standard of care, thereby introducing bias. Varying the size of the block can mitigate against this risk. Knowledge of block sizes should be strictly limited to the statistician generating the allocation sequence and only in exceptional circumstances should it be revealed to trial staff or investigators.

Stratification is a form of restricted randomisation where separate randomisation schedules are used for subgroups of study participants13. Subgroups or strata should 7

be based on factors that influence the outcome. When there is block randomisation, stratification helps to ensure that the treatment and comparator groups are relatively balanced for these factors in smaller trials and may thereby improve precision by reducing residual variability in the statistical analysis of the outcome. Gains in precision are generally modest and limited to situations where: the study size is small and the influence of the stratifying variable on the outcome is large; when the influence is minor, and when a stratum is small or ‘sparse,’ over-stratification of the study population may reduce precision, so it should be limited to a small number of important factors13. Intervention and control arms need not be exactly balanced with respect to baseline characteristics (including potential confounders) for valid statistical inference. Rather, the validity of the analysis depends on the assignment being generated by a truly random process. Blinding Blinding, also known as masking, is a design feature of clinical trials that prevents investigators and/or study participants from knowing which treatment the study participant has been assigned. Blinding promotes objectivity in data collection and data reporting and reduces the risk of measurement bias16, 17, i.e. systematic errors in measuring outcomes than can occur when non-blinded investigators or participants have preconceived ideas about the effect of a study treatment18, 19. For example, investigators and participants who are hopeful that an investigational treatment will be more effective than standard of care may subconsciously tend to interpret and report outcomes more positively in the investigational group than in the standard care group (reporting bias)19; conversely, they may be more likely to report

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adverse side effects for an investigational treatment than for a placebo. Knowledge of the treatment assignment might also influence study retention (placebo recipients may be more inclined to drop out) and might also influence subsequent management (placebo recipients may be more likely to receive alternative therapy or even crossover to the active arm). Different levels of blinding can be implemented. While there are no standard definitions, Table 1 lists examples of types of blinding that are commonly used. {Insert table 1 here}

Blinding can increase the logistical complexity and cost of studies and might not always be possible e.g. when a study treatment has a distinctive effect which is difficult to replicate (e.g. peculiar taste or odour of a drug) or where the intervention is invasive (e.g. surgery) or complex. When blinding is not possible, the bias may be mitigated against by avoiding outcomes which are subjective.

Importance of the primary outcome measure in trial design The choice of the primary outcome is central to the design of a clinical trial1, and must be reflective of its primary aim. The primary outcome variable should be chosen a priori during trial design and before the commencement of enrolment20. Essential characteristics of the primary outcome variable are summarised in Table 2. {Insert Table 2 here}

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Outcomes are captured and measured using defined endpoints which are typically dichotomous (e.g. dead or alive) or continuous (e.g. forced expiratory lung volume), but may also be categorical or ordinal (e.g. underweight, normal weight, overweight, or obese); they may also represent the (continuous) time from enrolment to a (dichotomous) event (e,g. discharge from hospital), or a rate of events per unit of time (e.g. number of asthma exacerbations per year). Each may be suited to a particular research question and each has its own inherent limitations. If an outcome can be measured as a continuous endpoint (e.g. the time-to-asthma exacerbation), information is lost if that is converted to a dichotomous endpoint (e.g. whether an exacerbation occurred at any time over a given period of follow up) and as such power may be lost. It could be argued, however, that comparisons of the risk of a dichotomous endpoint are more easily understood than comparisons of the time to that event across two groups. With increasing recognition of the importance of patient perspectives in healthcare (patient-centred care), patient reported outcomes are increasingly used in clinical trials. Health-related quality of life measures are one type of patient reported outcome. Condition specific quality of life measures, discussed in detail elsewhere21, have been developed and validated for a number of conditions encountered in paediatric respiratory medicine. There may be a compromise between selecting an outcome that is important to decision-makers (including patients) and one that can be measured objectively and with little error. For example, the most important outcomes may relate to quality of life which is impacted by a range of extraneous factors and may be difficult to

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measure objectively and without error. As such, a study with such a primary outcome may require a larger sample in order to demonstrate a treatment effect compared to a trial with an outcome which can be measured accurately but which is of mechanistic relevance rather than clinical importance. In the ISIS trial, a large multicentre phase 3 randomised controlled trial of inhaled hypertonic saline in young children with cystic fibrosis, the primary outcome was the rate of pulmonary exacerbations. When no significant difference was found in between the treatment and control group22, it was commented that although important, pulmonary exacerbations are infrequent among young children and so the trial may have been insufficiently powered to detect a relevant beneficial effect. In the SHIP CT study (NCT02950883), another study of the efficacy of inhaled hypertonic saline in young children, investigators have chosen instead to nominate a scored structured assessment of a computed tomography of the chest as it is thought to be a more sensitive measure of lung health.

Clinical trial design Various designs are used depending on the context and purpose of the trial. The demarcation between design types is not always rigid with some trials having characteristics of more than one design. Parallel versus crossover designs: Most trials are conducted as parallel designs which typically compare one treatment against no treatment, placebo, or the standard of care. Parallel trials can have more than one active arm, for example if multiple doses of a drug are being evaluated. Each participant is assigned to receive just one treatment and outcomes are measured and compared across groups. 11

In a crossover design participants are randomised to one study arm for a set period and then, after a washout period, they are allocated to the other study arm. This allows outcomes to be measured in each participant both on and off treatment, and for the differences to be aggregated across all study participants. Crossover designs eliminate variation in baseline factors between the study arms increasing the power to detect a significant treatment effect23. Crossover designs can only be used where any treatment effect is predictably time limited (e.g. inhaled short-acting bronchodilators in asthma), and can’t be used if the treatment is curative (e.g. antibiotics for pneumonia), or long lasting. A washout period is used to reduce the chance of carry-over treatment effects so that the effect of the first treatment is not erroneously attributed to the next. All participants receive active treatment so enrolment may be high with a crossover design, although if participants are not willing to receive placebo or to be on no treatment during the washout period, the risk of study drop-out may be high.

Superiority vs Non-inferiority and Equivalence studies: Typically, investigators will aim to demonstrate that a new treatment is superior to no treatment (placebo) or to the standard of care. Sometimes, for example when evaluating an alternative formulation of an effective treatment, the aim is to show that the new treatment is equivalent to an existing one. No two treatments are ever likely to be identical, and it would be impossible to prove that they are, so investigators need to propose a priori the maximum difference in treatment effects that would still allow the treatments to be considered equivalent. To be convincing, such a difference should be small, and the ability to demonstrate such a difference, if it exists, should be high. To be

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considered truly equivalent, there must be confidence that the new treatment is both no better and no worse than the comparator. This is generally important when the outcome is a drug concentration, for example, where there needs to be confidence that the new treatment will result in essentially the same treatment effect as the comparator. For equivalence trials, a large sample size is typically needed24.

More often, when an effective treatment for a condition is already available, investigators aim to show ‘non-inferiority’, that is that a new treatment is no worse (and possibly better) than the effective comparator. Demonstration of non-inferiority rather than superiority may be adequate if the new treatment has other advantages over the comparator, for example fewer side-effects or lower cost. Similar to the equivalence studies, investigators need to set the maximum acceptable difference between the treatment25; in the non-inferiority design, the treatment effect needs to be confidently above this margin, but unlike the equivalence design it is not necessary to be confident that the treatment effect is below some acceptable superiority margin. With non-inferiority designs one-sided hypothesis testing is used. For example a recent study compared azithromycin with co-amoxyclavulinic acid for the treatment of exacerbations of bronchiectasis in children26. Azithromycin was found to be non-inferior to co-amoxyclavulinic acid. The interpretation of this result was that azithromycin is at least as good as co-amoxyclavulinic acid, although there was no claim that it is better.

Group randomisation/Cluster allocation studies: Where possible, it is usually best to individually randomise participants to alternative treatment groups because this is most statistically efficient. When it is not practical or feasible to do so, or when 13

it is inappropriate, randomisation to alternative treatments may occur at the group level. For example, researchers may wish to evaluate the effect of a health promotion campaign on positive health behaviours in a community. A health promotion campaign is generally designed to be delivered at a whole of community level and so it would be appropriate to assign an entire community to the intervention or control, rather than individually assign members of the same community to intervention or control. The individual outcomes can be measured, but because the outcomes among individuals in the group are likely to be correlated, a number of groups and many individual participants are typically required.

Groups may be randomised and followed in parallel, or groups can be made to crossover between interventions with some intervening washout period. Sometimes it is not feasible or possible for groups to crossover in both directions; for example it may not be possible for a group assigned to a health promotion campaign to then be assigned to no intervention because it is not possible to undo the exposure to the campaign. In a stepped wedge cluster randomised trial, groups or clusters are followed for a period prior to intervention and then randomised to receive the intervention at various time points until all groups are receiving it27. Comparisons are made of the groups’ outcomes while receiving the intervention versus beforehand, and the differences are aggregated across the groups. An advantage of this design is that all groups end up on the intervention, which can facilitate participation27.

Factorial design: While some studies evaluate two treatments against a comparator, it is sometimes of interest to not only compare each treatment alone but 14

to also evaluate the effect of the treatments together. A factorial design enables the effects of each treatment to be simultaneously evaluated against a comparator alone and in combination, and against each other28. In a typical example of a factorial design, intrapleural tissue plasminogen activator (t-PA) and DNase were evaluated for the treatment of pleural infections in adults29. The four possible treatment assignments are illustrated in Figure 1. Intrapleural tPA combined with DNase therapy was found to improve fluid drainage (primary outcome) and the duration of hospital stay, whereas treatment with DNase or tPA alone were not found to be effective. {insert Figure 1 below} Two separate equally powered trials of tPA and DNase alone versus placebo may have enrolled as many participants (owing to duplication of the placebo groups) and may have missed the combined effect of tPA and DNase.

Pragmatic designs: Pragmatic trials are used when the objective is to evaluate the clinically relevant benefit of a treatment when used under real-world or programmatic conditions; they tend to enrol large numbers of participants from the whole target patient population using broad eligibility criteria 30. Follow-up is generally made to be as simple as possible and data collection requirements minimal to reduce the burden on participants and thereby maximise participation and minimise drop-out, i.e. typically limited to one or two contacts per participant. Such trials might also preclude monitoring of adverse events if the safety of drug is already established.

Adaptive trial design 15

According to the FDA an adaptive design is one that “allows for prospectively planned modifications to one or more aspects of the design based on accumulating data from subjects in the trial”31. Adaptive trials may allow for improved efficiency and statistical power compared to more conventional designs, thereby allowing clinical questions to be answered in shorter time or with fewer participants than with non-adaptive designs. Adaptive trials have their own potential sources of bias which need to be avoided by careful design32. Different types of adaptation can be implemented. The most common are adaptive group sequential design, flexible sample size re-estimation, adaptive randomisation, biomarker adaptive design and multi-arm platform design. These designs will be discussed briefly below. Group sequential design: The group sequential design allows for one or more planned interim analysis during the course of the trial with pre-specified stopping rules at each analysis. At each interim analysis, the trial can be stopped early if there is either strong evidence of treatment efficacy or futility i.e. if the trial is unlikely to demonstrate efficacy even when the total sample size is reached. Each analysis for efficacy may increase the risk of a type-1 statistical error (the risk of incorrectly declaring a difference if none exists)33, and methods are used to ensure the overall risk for type-1 error across all analyses is acceptable34. Typically, the thresholds for stopping early or for declaring success, especially at early analyses, are set to be very conservative.

Sample size re-estimation design: Power calculations for clinical trials are typically based on an estimate of the expected response rate in the comparator group, and 16

the expected difference in response rates between the treatment and comparator group. When the actual response rate in the comparator group is smaller than was expected, the trial may be under-powered to demonstrate a clinically important difference even if it is present. Conversely, if the actual effect size is larger than expected, more study participants may be randomised than is necessary to demonstrate a difference. Sample size re-estimation allows for the sample size to be adjusted based on trial data before trial completion, thereby reducing the likelihood of an inconclusive trial and possibly reducing the number of participants enrolled. Sample size re-estimation design studies typically plan for a specific sample size based on an expected effect size. The sample size can then be increased if the observed effect is smaller than initially expected35. Here too, various methods are used to control for type-1 errors36. Interim analyses of the data are often recommended to be blinded to avoid bias and facilitate interpretability of results34. However, un-blinded analyses can also be very effective for selecting the appropriate sample size. For example, the Bayesian “Goldilocks” design specifies a large maximum sample size, and uses frequent un-blinded interim analyses that can stop accrual early (for success or for futility) based on the observed treatment effect at the interims37. Such trials need to have strict protocols and procedural safeguards corresponding to information flow, so that investigators and participants remain blinded to the observed treatment effect.

Adaptive randomisation: Adaptive randomisation is a dynamic process where treatment allocation probabilities change over time depending on the composition of study groups and/or preliminary outcomes within study groups as determined at

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predefined intervals. Two main types of adaptive randomisation are ‘covariateadaptive treatment assignment’ and ‘response adaptive randomisation’. Minimisation is a form of covariate-adaptive randomisation that aims to limit differences in important baseline characteristics between treatment groups38. The rationale is that even when randomised, treatment and comparator groups can still differ by chance in baseline characteristics that are known to influence the study outcome, especially if the study is small, and this reduces the efficiency of the trial. If an imbalance in one or more specific characteristics emerges between the groups during the course of a trial, the randomisation probability is weighted so that a new participant with a characteristic is more likely to be allocated to the group underrepresented by that characteristic39. Response adaptive randomisation is the progressive, rule-based allocation of an increasing proportion of new participants to treatment groups which appear to be performing the best, and the potential suspension of enrolment or elimination of treatment groups which are performing poorly40, 41. Randomisation probabilities are adapted based on analyses at predefined intervals using accruing data, such that there is increasing chance that study participants will be randomised to the best performing treatments42. A unique risk of bias occurs with adaptive randomisation when there is drift in outcomes over time, perhaps because of a change over time in the distribution of patient characteristics or because of changes in other aspects of care, as might happen if new study sites are included over time43. However, statistical models can be used to account for the drift in patient response over time, such as those currently used in the ISPY-2 trial44. Type-1 error rates need not be increased if appropriate

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statistical techniques are applied. While departure from 1:1 randomisation typically reduces the power of two-arm study, efficiencies can be gained when there are multiple arms by targeting enrolment to whichever arms are most promising. Under these conditions, adaptive randomisation can lead to shorter trials, smaller sample sizes and/or greater statistical power31. Trials with relatively short follow-up and long accrual will provide more information by which to adapt, whereas trials with relatively fast accrual and long-term outcomes (e.g. 5-year survival) may lack sufficient data to inform adaptations.

Platform designs: A platform trial is designed to find the best combination of interventions for a disease by concurrently studying several different treatments (alone or in combination) using adaptive randomisation together with specialized statistical tools for analysis of results. Treatments may be dropped for futility through the adaptive process, while new questions can be addressed and trial interventions introduced using the same trial platform and infrastructure40. A pre-specified master protocol45 governs the structure of the trial, including inclusion/exclusion criterion and general adaptive features of the trial. An example of a platform trial is the I-SPY 2 study44, a phase-2 clinical trial investigating multiple neoadjuvant breast cancer therapies that may have differential benefit depending on patient biomarker profiles. Platform trial designs may increase trial efficiency through the sharing of common trial infrastructure, and by addressing specific hypotheses with fewer patients, with greater statistical power, and better outcomes for participants46. Many specialised features of platform trials are made possible through the use of Bayesian methods.

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Conclusion In conclusion, appropriate clinical trial design is essential if clinical trials are to generate reliable evidence. Multiple considerations have to be carefully addressed to produce robust design. Different types of design can be implemented, each with particular strengths and weaknesses. Once the design stage is completed, the challenges lie in meticulous data collection, correct analysis and accurate reporting.

Figure 1

tPA YES

NO

YES

tPA + DNase

DNase + placebo

NO

tPA + Pacebo

Double placebo

DNase

Factorial design comparing treatments for pleural infection. tPA = intrapleural tissue plasminogen activator.

Table 1. Examples of types of blinding used in clinical trials Single blinding

Double binding

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Further blinding

Typically involves blinding

Both the participant and

May involve analysts or

of the study participants

the clinical investigator (or others directly or indirectly

only.

the observer of the

involved in the research

endpoint) are unaware of

including the monitoring

treatment allocation

committee and study sponsors19.

Table 2. The primary outcome variable should be: 1)

Clinically relevant and plausibly influenced by treatment

2)

Measurable and relatively free of measurement or ascertainment errors

3)

Capable of being observed independent of the treatment assignment

4)

Practical to observe or measure in all trial participants.

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