Multiple primary endpoints clinical trials

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Check out PowerShow. There is truly something for everyone! If end-users are going to make decisions based on measured differences in one or more endpoints between treatment groups, they must understand what those differences are; but endpoints have properties and characteristics that have strengths and limitations that are critical to their interpretation.

It is a responsibility of those who design and conduct trials to choose endpoints which will influence decision-making by clinicians and policymakers.

Endpoint selection is a complex process. End-users bring differing needs and perspectives. Poor selection of endpoints makes interpretation and implementation of findings difficult or impossible, limits evidence synthesis, and thereby diminishes the value of the research, resulting in wasted use of resources [ 4 ]. A single endpoint may not capture the important effects of an intervention to the satisfaction of all end-user groups, so multiple endpoints are usually selected, which are categorized as primary, secondary or tertiary.

Primary endpoint s are typically efficacy measures that address the main research question [ 3 ]. Secondary endpoints are generally not sufficient to influence decision-making alone, but may support the claim of efficacy by demonstrating additional effects or by supporting a causal mechanism [ 2 ].

If tertiary endpoints are nominated, they typically capture outcomes that occur less frequently or which may be useful for exploring novel hypotheses [ 3 ]. The primary aim of this review is to summarise the range of clinical and non-clinical endpoints used in late phase trials and their relative strengths and weaknesses. The secondary aims are to describe their evolution and consider which characteristics of endpoints are valuable for evaluating treatment effects.

This review is intended to serve as a reference to assist researchers when choosing primary endpoints, and for the end-users of clinical trial data tasked with translating this evidence into clinical practice or policy. Early phase trials may have a more proximal aim such as establishing proof-of-principle, trial feasibility, or assessing the mechanistic effects of an intervention; this review does not discuss endpoints relevant to these types of trials.

Further, whilst we recognise that statistical and regulatory considerations are also important factors weighing into overall endpoint selection, a detailed analysis of these topics is beyond the scope of this review. Our full search strategy including additional limits is detailed in Appendix A and B. The search was performed by a single reviewer CM and findings are reported by narrative synthesis. Endpoints for late phase trials can be broadly classified as either clinical or non-clinical see Fig.

Clinically meaningful endpoints relate to outcomes which capture how a person feels, functions or survives [ 3 ]. These endpoints may be measured objectively or subjectively, and are either i reported by clinicians ClinRO , which involves judgement or interpretation of clinical signs or events such as stroke, myocardial infarct or cancer remission , ii assessed by standardised performance measures 6-min walk test , iii patient-reported PRO , which are directly reported by patients such as self-reported symptoms or function, or a measure of perceived quality of life or iv observer-reported ObsRO , such as a parent log of seizure activity in a child [ 5 ].

Non-clinical endpoints, including biomarkers, do not relate directly to how a person feels, functions or survives, but are instead objectively measured indicators of a biological or pathogenic process, for example a pharmacological response to a treatment intervention.

Some endpoints may be clinically important even though they are non-clinical and not meaningful to all end-users See Fig. Such endpoints do not directly reflect or describe how a patient feels, functions and survives and therefore hold no intrinsic value to patients, but are nonetheless important because they are strongly associated with a meaningful outcome, and therefore compellingly influence clinical decision making, for example a troponin result or a measured blood pressure.

Trial endpoints may be used to derive metrics which are used to further evaluate the impact of an intervention, for example from a population or policy perspective, such as number needed to treat or harm, or the incremental cost per quality-adjusted-life-years gained. These metrics are important from a societal, and consequently translation perspective [ 3 ]. Surrogates are those endpoints that do not directly measure how a person feels, functions or survives, but which are so closely associated with a clinically meaningful endpoint that they are taken to be a reliable substitute for them [ 2 ].

The quality of a surrogate endpoint is therefore determined by the extent to which a treatment effect on that surrogate corresponds to a treatment effect against one or more clinically meaningful outcomes. Conceptually, the best surrogate endpoints directly measure causal intermediaries of the effect of an intervention on a clinically meaningful outcome, where essentially all effects on that outcome are mediated through that intermediary, and where there is little attenuation between the effect of a treatment on the intermediary and the intermediary's effect on the clinically meaningful outcome [ 5 ].

Surrogates which do not causally influence the meaningful outcome may still be statistically associated with it for a given treatment in a given context, but this association may not generalise well to other clinical contexts, populations or interventions. A validated surrogate is one which reliably captures a treatment effect against one or more clinically meaningful endpoints, bearing in mind that the strength of this association may be context dependent, and reliability cannot be inferred unless there are multiple randomised, controlled trials of interventions that have the same or similar effect on both the surrogate and the clinically meaningful end-point [ 5 ].

The US Food and Drug Administration FDA provides a list of validated and likely surrogates [ 6 ], for example HbA1c is listed as a marker of risk of long term microvascular complications in type 2 diabetes mellitus. However, unvalidated surrogates are sometimes selected for lack of a validated surrogate, and there is no standardised process or agreed criteria that must be met for validation.

Prentice first described the criteria for scientific validation [ 7 ], proposing the surrogate should be statistically correlated with the clinical outcome of interest, and also fully capture the effect of the intervention on the outcome.

The latter criterion has been critiqued as being too stringent [ 5 ]. Fulfilment of the Prentice criteria requires an understanding of the causal pathways of disease and the effects of an intervention on this pathway, and such complexities might never be confidently understood entirely.

Alternative approaches for validation of surrogates have been described elsewhere [ 8 , 9 ]. The first is failure of the surrogate to lie on the causal disease pathway. An example is the use of laboratory measures to evaluate the impact of HIV treatment in pregnancy to reduce mother to child transmission of HIV infection [ 10 ].

The maternal CD4 count and HIV viral load are both statistically correlated with the risk of transmission in untreated women; low CD4 count and high viral load are both associated with increased risk. HIV viral load, which measures the amount of circulating virus in the mother's blood, is thought to lie on the causal pathway between treatment and transmission because circulating virus is thought to be a prerequisite for transmission.

Any treatment that reduces the maternal viral load can therefore reasonably be expected to reduce the risk of transmission.

The CD4 count however, which measures the status of the mother's immune system, may not be causally related to transmission. Instead, high viral load in untreated women causes low CD4 count, so the association between low CD4 count and risk of transmission may be confounded by the higher viral loads in women with low CD4 count.

This means that treatments that impact on CD4 count and not the viral load may not influence the risk of transmission. HIV viral load is therefore prima facie a more reasonable surrogate than the CD4 count for capturing the effect of maternal interventions on risk of mother to child transmission. The second reason for failure of a surrogate is the existence of more than one causal pathway impacting on the outcome, where the surrogate lies on one pathway only [ 11 ].

In the above example, maternal viral load might only be a reasonable surrogate for mother-to-child-transmission for those treatments that mediate their protective effects by inhibiting viral replication. Caesarean section is also protective against transmission, but through alternative pathways, presumably by decreasing exposure of the newborn to maternal blood and secretions. Maternal viral load would not be expected to be a useful surrogate in that context. Thirdly, the intervention may produce off-target effects that impact on the measured outcome [ 11 ].

The Cardiac Arrhythmia Suppression Trial CAST was designed to test the hypothesis that suppression of asymptomatic or mildly symptomatic ventricular arrhythmias with anti-arrhythmic agents flecanide or encainide would reduce the risk of death or cardiac arrest requiring resuscitation in survivors of myocardial infarction [ 12 ]. Although the pilot study for this trial found these agents suppressed arrhythmias adequately in the target population [ 13 ], mortality increased 3-fold in the CAST owing to effects of these drugs on mortality through alternative pathways, possibly through unanticipated pro-arrhythmic effects [ 12 ], prompting withdrawal of these drugs from the market [ 5 ].

Conceptually, an ideal endpoint should be a valid and applicable measure of how a patient feels, functions or survives [ 2 ] and be perceived by end-users of the research as having meaning and value. To be valid, an endpoint should capture the outcome of interest accurately measure what is intended , precisely with minimal error or uncertainty and consistently with repeated measurements [ 14 ].

This is easiest to achieve when the outcome of interest can be measured directly, such as death. An ideal endpoint should also be measured easily, without additional risk, at low cost, at minimal inconvenience to the patient [ 15 ], and, if possible, captured as part of routine data collected as part of clinical care. Death is one example of an endpoint for interventions of highly fatal conditions which fulfils all these criteria, including the fact that this endpoint is meaningful to all end-user groups.

For the majority of conditions where death is rare, or where survival may be associated with significant suffering or disability, death will not capture all relevant and meaningful outcomes.

Standardization of endpoints is increasing through the development and adoption of core outcome sets [ 16 ]. Core outcomes are the effect s of a health intervention which are agreed as being important to end-users, including patients.

A core outcome set COS is a minimum agreed list of outcomes that should be measured and reported in trials [ 17 ]. Guidelines are available to inform development of core outcomes sets and identification of optimal methods for outcome measurement [ 16 , 17 ]. Patients, clinicians, policy-makers, industry representatives, and members of the public may be involved in the development of core outcome sets depending on existing subject matter knowledge, the rationale for development, and feasibility constraints [ [16] , [17] , [18] ].

It may be helpful to consider when and why the use of different endpoint types has evolved over time; this is summarized in Fig. Because interventions impact patients in different ways and may have more than one consequence positive or negative , decision making around the use of an intervention should consider the net benefit versus risk [ 17 ]. Increasingly complex endpoints have evolved in parallel to advances in trial design and data capture in order to assess multiple important effects of an intervention in aggregate, or to determine whether the intervention is likely to have a net benefit to a patient overall.

In the current era of patient-centered healthcare, individualised endpoints have also been recently proposed as a framework for evaluating personally defined risk and benefit [ 23 ]. No endpoint type is universally better than all others, but rather, the different characteristics and properties of each type make them better suited for use in different contexts; this is considered in further detail below. A summary of the strengths and limitations of various types of endpoints described in the literature are presented in Table 1 [ 14 , 19 , 21 , 24 ].

Multiple or combination primary endpoints may be required to capture the aggregate risk-benefit effect of an intervention [ 3 , 25 ]. This may be considered when multiple disparate outcomes have comparable importance, if each of those outcomes are individually rare, or if no consensus can be reached regarding which is most important [ 3 ].

Multiple endpoints can be chosen and evaluated separately, such that a significant treatment effect against any one of the endpoints may be taken as evidence of efficacy. This approach may be useful in diseases that have multiple sequelae, where improvement in any pre-specified endpoint is clinically meaningful even in the absence of improvement in any other [ 3 , 19 ]. Because the risk of type 1 error increases with every additional endpoint assessed, appropriate statistical adjustments for multiplicity are generally needed to contain the risk of a false positive trial result; regulatory authorities are particularly focussed on this issue and have given guidance on managing this risk [ 3 ].

An example of co-primary endpoints includes both cognitive and functional assessments in studies of Alzheimer's disease [ 3 , 26 ] in which for a treatment to be considered efficacious it must demonstrate a beneficial effect on both cognition and function.

There is no risk from multiplicity when co-primary endpoints are used [ 3 ]; conversely, the power of a study is typically diminished by the requirement to demonstrate significant efficacy against more than one endpoint, unless those endpoints are highly correlated.

Combination endpoints may be either composite or multi-component [ 3 , 19 ]. Some trials combine measures of multiple outcomes such as death and major morbidity events into a single measure of effect, or composite endpoint [ 3 ].

This helps to avoid the multiplicity issues inherent when multiple endpoints are assessed separately [ 14 , 21 ]. Composite endpoints are sometimes used to aggregate the total benefit when the goal of therapy is to prevent or delay a number of important but uncommon clinical events [ 21 ]. One example is a composite endpoint which comprises any of death, myocardial infarction, stroke or revascularisation in cardiovascular trials [ 3 ].

The value of composites is influenced by the relative importance of its components. The components of a standard composite endpoint are implicitly ascribed equal weight. Among the various statistical approaches presented in the guidance, each has pros and cons depending on the number and correlation levels of the endpoints CDER, Efficacy endpoints are clinical events that vary depending on the intended effects of a drug on a particular disease.

The clinical endpoints may be clinical events, patient symptoms, measures of function, or a family of events such as scores depending on the disease e. In some cases, such as when the occurrence of a single event is low, efficacy can be based on a combination of several events e. There is a consensus that for a clinical trial with a single endpoint, the probability of finding a difference between treatment groups is set at 0.

For three independent endpoints, the Type I error rate increases to 14 percent. Post hoc analyses cannot be used to demonstrate efficacy in trials intended to serve as the basis for FDA approval. The calculation of sample size or power is a difficult task when multiple primary endpoints MPE are considered, which means when there is more than one primary endpoint.

In general, these MPE are categorized into multiple co-primary and multiple primary endpoints. The package mpe can be used to calculate sample size and power for MPE. First, we give some details about the methods and formulas.

Next, we illustrate how to apply our functions in simple examples. The co-primary endpoints are:. In this section, we briefly state the relevant formulas from Chapter 2 of the book by Sozu et al.

That is, we consider the following hypotheses. As we are assuming the covariance to be known, the hypotheses can be tested using a multivariate intersection-union z-test implemented in function mpe.

The test statistic reads. Next, we demonstrate how to calculate the sample size for a trial with two co-primary endpoints with known covariance. On the other hand, we can also calculate the power for a given sample size.

In the above example with two multiple co-primary endpoints with known covariance we get. Furthermore, we can perform the corresponding multivariate intersection-union z-test by applying our function mpe.

Here we use simulated data for the demonstration. In this section, we give the formulas from Chapter 2 of [12] where we assume the covariance as unknown. The hypotheses given above in Sec. The test statistic is. Now, we demonstrate how to calculate the sample size for a trial with two co-primary endpoints with unknown covariance. Here, we follow three steps to determine the sample size.