Best Practice & Research Clinical Rheumatology 28 (2014) 247–262
Contents lists available at ScienceDirect
Best Practice & Research Clinical Rheumatology journal homepage: www.elsevierhealth.com/berh
5
Methodology of clinical trials for rare diseases Catrin Tudur Smith a,1, Paula R. Williamson a, 2, Michael W. Beresford b, c, * a
MRC North West Hub for Trials Methodology Research, Department of Biostatistics, Institute of Translational Medicine, University of Liverpool, Liverpool, UK b Department of Women’s and Children’s Health, Institute of Translational Medicine, University of Liverpool, Liverpool, UK c Department of Paediatric Rheumatology, Alder Hey Children’s NHS Foundation Trust, Liverpool, UK
a b s t r a c t Keywords: Rare disease trials Paediatric rheumatology Trial design
Evidence from clinical trials, ideally using randomisation and allocation concealment, is essential for informing clinical decisions regarding the benefits and harms of treatments for patients. Where diseases are rare, such as in paediatric rheumatic diseases, patient recruitment into clinical trials can be a major obstacle, leading to an absence of evidence and patients receiving treatments based on anecdotal evidence. There are numerous trial designs and modifications that can be made to improve efficiency and maximise what little data may be available in a rare disease clinical trial. These are discussed and illustrated with examples from paediatric rheumatology. Regulatory incentives and support from research networks have helped to deliver these trials, but more can be done to continue this important research. Ó 2014 Elsevier Ltd. All rights reserved.
* Corresponding author. Department of Women’s and Children’s Health, Institute of Translational Medicine, University of Liverpool, Liverpool, UK. Tel.: þ44 151 252 5693. E-mail addresses: [email protected] (C. Tudur Smith), [email protected] (P.R. Williamson), [email protected] (M.W. Beresford). 1 Tel.: þ44 151 706 4266. 2 Tel.: þ44 151 706 4958.
http://dx.doi.org/10.1016/j.berh.2014.03.004 1521-6942/Ó 2014 Elsevier Ltd. All rights reserved.
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C. Tudur Smith et al. / Best Practice & Research Clinical Rheumatology 28 (2014) 247–262
Introduction Clinical trials provide a framework for evaluating the benefits and harms of interventions and contribute to the evidence base which informs clinical decision-making. They are designed to address at least one specific research question such as ‘Does early treatment with combination therapy improve physical function compared to monotherapy in patients with juvenile idiopathic arthritis (JIA)?’A number of clinical trial design characteristics are possible and the choice of which to adopt will depend on multiple factors including the research question, the phase of evaluation, the condition of interest, the type of intervention and comparator, ethical issues, available resources and logistical constraints. The randomised controlled trial (RCT), and systematic review of RCTs, provides the highest level of evidence for judging the benefits of treatment [1]. Randomly allocating treatments to patients ensures that groups of patients are comparable and any observed difference in outcome between groups can be attributed to the difference in treatment. Adequate concealment of allocation, whereby the knowledge about which treatment will be allocated to the next patient is concealed, is a further requirement to prevent the potential for selection bias. Comparative clinical trials evaluating the effects of interventions should aim to incorporate both randomisation and allocation concealment whenever possible. An important consideration for almost any clinical trial is the sample size. If a trial is too small, there may be insufficient data to reliably answer the research question. If a trial is too big, resources are wasted and patients may potentially be exposed to ineffective treatments for longer than is absolutely necessary. Therefore, an estimate of the sample size required to detect a clinically relevant treatment effect of a particular magnitude with a certain level of power (chance of detecting a true difference) is usually calculated at the design stage. The sample size required will become larger if the power (chance of detecting a true difference) is increased, or if the significance level (chance of incorrectly finding a difference) or magnitude of treatment effect is reduced. For a full description of sample size in clinical trials, see Ref. [2]. Rare diseases are defined by a prevalence of 23 h/day. The authors quote a total fixed sample size of at least 336 patients for a traditional RCT based on detecting an improvement of 15% with a 5% significance level (one sided) and 90% power. In their sequential trial design, after 163 patients were randomised and 41 patients had reached a clinical end point, the sequential monitoring indicated that the test statistic had crossed the lower boundary and the null hypothesis of no difference between the two treatment arms could be accepted. The sequential trial design and analysis allowed inclusion of half the fixed sample size and the trial could be discontinued approximately 3 years earlier than a traditional fixed sample size RCT. The flexibility of the adaptive design framework is attractive for rare diseases, particularly as many of the design options can lead to increased efficiency with trials that are smaller or of shorter duration. However, substantial care should be taken to ensure that adaptations are pre-planned and are undertaken using a rigorous methodology. The possibility of interim analyses being inadvertently disseminated is also of concern as this could lead to unintended changes in the participant recruitment which can lead to bias and subsequent difficulties interpreting results. Other possibilities of adaptive design which are not covered here include the ranking and selection design, multi-arm-multistage designs and seamless phase II/III designs, all of which are discussed in detail by Chow et al. [34] and might be attractive in paediatric rheumatology if a number of alternative treatments are available for a particular condition. In the treatment of childhood connective tissue disorders or vasculitis, such approaches may be helpful as currently there are a number of immunosuppressant therapies available for either the induction or the maintenance phases of therapy (Table 1). Randomised withdrawal design (or randomised discontinuation design) The International Conference on Harmonisation (ICH) E10 guidance on Choice of Control Group in Clinical Trials [35] defines the randomised withdrawal design as follows: “In a randomized withdrawal trial, subjects receiving a test treatment for a specified time are randomly assigned to continued treatment with the test treatment or to placebo (i.e., withdrawal of active therapy). Subjects for such a trial could be derived from an organized open single-arm study, from an existing clinical cohort (but usually with a protocol-specified ‘wash-in’ phase to establish the initial on-therapy baseline), from the active arm of a controlled trial, or from one or both arms of an active control trial. Any difference that emerges between the group receiving continued treatment and the group randomized to placebo would demonstrate the effect of the active treatment. The pre-randomization observation period on treatment can be of any length; this approach can therefore be used to study long-term persistence of effectiveness when long-term placebo treatment would not be acceptable. The post-withdrawal observation period could be of fixed duration or could use early escape or time to event (e.g., relapse of depression) approaches. As with the early escape design, careful attention should be paid to procedures for monitoring patients and assessing study endpoints to ensure that patients failing on an assigned treatment are identified rapidly.” A particular type of withdrawal design that uses an ‘enrichment strategy’ selects patients to enter the randomised phase based on their response to active treatment during a pre-randomisation phase. This ensures that patients who are most likely to benefit from the active treatment are selected for randomisation. Kopec et al. [36] recommend that this design is “particularly useful in studying the
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C. Tudur Smith et al. / Best Practice & Research Clinical Rheumatology 28 (2014) 247–262
effect of long-term, non-curative therapies, especially when the clinically important effect is relatively small and the use of placebo should be minimized for ethical or feasibility reasons.” In a randomised, double-blind, placebo-controlled withdrawal trial, Ruperto et al. [37] recruited 190 children with a history of active JIA. All 190 patients were given the experimental drug, abatacept, during a 4-month open-label pre-randomisation period. The 123 (65%) patients who had improved by 30% according to the American College of Rheumatology (ACR) paediatric definition were then entered into a 6-month randomised double-blind phase whereby patients were randomly allocated to abatacept or placebo. The trial was able to demonstrate that the risk of flare in patients who continued abatacept was less than a third of that for controls (hazard ratio 0.31, 95% confidence interval (CI) 0.16– 0.95) and the frequency of adverse events did not differ between the two treatment groups during the double-blind period [37] (Table1). A similar trial design had been used earlier by Lovell et al. [38] (Table1) to evaluate the safety and efficacy of etanercept in children with polyarticular juvenile rheumatoid arthritis who did not tolerate or had an inadequate response to MTX. Following a pre-randomisation phase whereby all 69 patients were administered etanercept for up to 3 months, 51 (74%) responders were selected to enter the second, double-blind randomised phase. The median time to flare was significantly increased (P < 0.001) with etanercept (>116 days) compared with placebo (28 days) with no significant differences between groups in the frequency of adverse events. Advantages of the randomised withdrawal design are that patients are offered the opportunity to be treated with the active drug from the beginning of the study, and the time exposed to inactive placebo is minimised. This may be a particular attraction for rare disease trials in paediatric rheumatology where a treatment has already been established as a standard of care in the absence of good quality randomised evidence. Moreover, since responding patients are likely to be more homogeneous and more likely to benefit, such designs may offer improved efficiency compared to a traditional RCT which randomises all patients regardless of their individual initial response status. This has been demonstrated by Kopec et al. [36] for trials with a binary outcome but it is not always the case. For example, Capra [39] concluded that due to the loss of information on those patients enrolled but not randomised, the traditional RCT can be more powerful in detecting treatment differences across a range of realistic situations. This was demonstrated for studies measuring time to event end points, such as the JIA trial by Ruperto et al. [37] The design is most useful when responders represent a relatively small proportion of the overall enrolled population and is particularly powerful when the drug effect is large and responders represent
Contents lists available at ScienceDirect
Best Practice & Research Clinical Rheumatology journal homepage: www.elsevierhealth.com/berh
5
Methodology of clinical trials for rare diseases Catrin Tudur Smith a,1, Paula R. Williamson a, 2, Michael W. Beresford b, c, * a
MRC North West Hub for Trials Methodology Research, Department of Biostatistics, Institute of Translational Medicine, University of Liverpool, Liverpool, UK b Department of Women’s and Children’s Health, Institute of Translational Medicine, University of Liverpool, Liverpool, UK c Department of Paediatric Rheumatology, Alder Hey Children’s NHS Foundation Trust, Liverpool, UK
a b s t r a c t Keywords: Rare disease trials Paediatric rheumatology Trial design
Evidence from clinical trials, ideally using randomisation and allocation concealment, is essential for informing clinical decisions regarding the benefits and harms of treatments for patients. Where diseases are rare, such as in paediatric rheumatic diseases, patient recruitment into clinical trials can be a major obstacle, leading to an absence of evidence and patients receiving treatments based on anecdotal evidence. There are numerous trial designs and modifications that can be made to improve efficiency and maximise what little data may be available in a rare disease clinical trial. These are discussed and illustrated with examples from paediatric rheumatology. Regulatory incentives and support from research networks have helped to deliver these trials, but more can be done to continue this important research. Ó 2014 Elsevier Ltd. All rights reserved.
* Corresponding author. Department of Women’s and Children’s Health, Institute of Translational Medicine, University of Liverpool, Liverpool, UK. Tel.: þ44 151 252 5693. E-mail addresses: [email protected] (C. Tudur Smith), [email protected] (P.R. Williamson), [email protected] (M.W. Beresford). 1 Tel.: þ44 151 706 4266. 2 Tel.: þ44 151 706 4958.
http://dx.doi.org/10.1016/j.berh.2014.03.004 1521-6942/Ó 2014 Elsevier Ltd. All rights reserved.
248
C. Tudur Smith et al. / Best Practice & Research Clinical Rheumatology 28 (2014) 247–262
Introduction Clinical trials provide a framework for evaluating the benefits and harms of interventions and contribute to the evidence base which informs clinical decision-making. They are designed to address at least one specific research question such as ‘Does early treatment with combination therapy improve physical function compared to monotherapy in patients with juvenile idiopathic arthritis (JIA)?’A number of clinical trial design characteristics are possible and the choice of which to adopt will depend on multiple factors including the research question, the phase of evaluation, the condition of interest, the type of intervention and comparator, ethical issues, available resources and logistical constraints. The randomised controlled trial (RCT), and systematic review of RCTs, provides the highest level of evidence for judging the benefits of treatment [1]. Randomly allocating treatments to patients ensures that groups of patients are comparable and any observed difference in outcome between groups can be attributed to the difference in treatment. Adequate concealment of allocation, whereby the knowledge about which treatment will be allocated to the next patient is concealed, is a further requirement to prevent the potential for selection bias. Comparative clinical trials evaluating the effects of interventions should aim to incorporate both randomisation and allocation concealment whenever possible. An important consideration for almost any clinical trial is the sample size. If a trial is too small, there may be insufficient data to reliably answer the research question. If a trial is too big, resources are wasted and patients may potentially be exposed to ineffective treatments for longer than is absolutely necessary. Therefore, an estimate of the sample size required to detect a clinically relevant treatment effect of a particular magnitude with a certain level of power (chance of detecting a true difference) is usually calculated at the design stage. The sample size required will become larger if the power (chance of detecting a true difference) is increased, or if the significance level (chance of incorrectly finding a difference) or magnitude of treatment effect is reduced. For a full description of sample size in clinical trials, see Ref. [2]. Rare diseases are defined by a prevalence of 23 h/day. The authors quote a total fixed sample size of at least 336 patients for a traditional RCT based on detecting an improvement of 15% with a 5% significance level (one sided) and 90% power. In their sequential trial design, after 163 patients were randomised and 41 patients had reached a clinical end point, the sequential monitoring indicated that the test statistic had crossed the lower boundary and the null hypothesis of no difference between the two treatment arms could be accepted. The sequential trial design and analysis allowed inclusion of half the fixed sample size and the trial could be discontinued approximately 3 years earlier than a traditional fixed sample size RCT. The flexibility of the adaptive design framework is attractive for rare diseases, particularly as many of the design options can lead to increased efficiency with trials that are smaller or of shorter duration. However, substantial care should be taken to ensure that adaptations are pre-planned and are undertaken using a rigorous methodology. The possibility of interim analyses being inadvertently disseminated is also of concern as this could lead to unintended changes in the participant recruitment which can lead to bias and subsequent difficulties interpreting results. Other possibilities of adaptive design which are not covered here include the ranking and selection design, multi-arm-multistage designs and seamless phase II/III designs, all of which are discussed in detail by Chow et al. [34] and might be attractive in paediatric rheumatology if a number of alternative treatments are available for a particular condition. In the treatment of childhood connective tissue disorders or vasculitis, such approaches may be helpful as currently there are a number of immunosuppressant therapies available for either the induction or the maintenance phases of therapy (Table 1). Randomised withdrawal design (or randomised discontinuation design) The International Conference on Harmonisation (ICH) E10 guidance on Choice of Control Group in Clinical Trials [35] defines the randomised withdrawal design as follows: “In a randomized withdrawal trial, subjects receiving a test treatment for a specified time are randomly assigned to continued treatment with the test treatment or to placebo (i.e., withdrawal of active therapy). Subjects for such a trial could be derived from an organized open single-arm study, from an existing clinical cohort (but usually with a protocol-specified ‘wash-in’ phase to establish the initial on-therapy baseline), from the active arm of a controlled trial, or from one or both arms of an active control trial. Any difference that emerges between the group receiving continued treatment and the group randomized to placebo would demonstrate the effect of the active treatment. The pre-randomization observation period on treatment can be of any length; this approach can therefore be used to study long-term persistence of effectiveness when long-term placebo treatment would not be acceptable. The post-withdrawal observation period could be of fixed duration or could use early escape or time to event (e.g., relapse of depression) approaches. As with the early escape design, careful attention should be paid to procedures for monitoring patients and assessing study endpoints to ensure that patients failing on an assigned treatment are identified rapidly.” A particular type of withdrawal design that uses an ‘enrichment strategy’ selects patients to enter the randomised phase based on their response to active treatment during a pre-randomisation phase. This ensures that patients who are most likely to benefit from the active treatment are selected for randomisation. Kopec et al. [36] recommend that this design is “particularly useful in studying the
254
C. Tudur Smith et al. / Best Practice & Research Clinical Rheumatology 28 (2014) 247–262
effect of long-term, non-curative therapies, especially when the clinically important effect is relatively small and the use of placebo should be minimized for ethical or feasibility reasons.” In a randomised, double-blind, placebo-controlled withdrawal trial, Ruperto et al. [37] recruited 190 children with a history of active JIA. All 190 patients were given the experimental drug, abatacept, during a 4-month open-label pre-randomisation period. The 123 (65%) patients who had improved by 30% according to the American College of Rheumatology (ACR) paediatric definition were then entered into a 6-month randomised double-blind phase whereby patients were randomly allocated to abatacept or placebo. The trial was able to demonstrate that the risk of flare in patients who continued abatacept was less than a third of that for controls (hazard ratio 0.31, 95% confidence interval (CI) 0.16– 0.95) and the frequency of adverse events did not differ between the two treatment groups during the double-blind period [37] (Table1). A similar trial design had been used earlier by Lovell et al. [38] (Table1) to evaluate the safety and efficacy of etanercept in children with polyarticular juvenile rheumatoid arthritis who did not tolerate or had an inadequate response to MTX. Following a pre-randomisation phase whereby all 69 patients were administered etanercept for up to 3 months, 51 (74%) responders were selected to enter the second, double-blind randomised phase. The median time to flare was significantly increased (P < 0.001) with etanercept (>116 days) compared with placebo (28 days) with no significant differences between groups in the frequency of adverse events. Advantages of the randomised withdrawal design are that patients are offered the opportunity to be treated with the active drug from the beginning of the study, and the time exposed to inactive placebo is minimised. This may be a particular attraction for rare disease trials in paediatric rheumatology where a treatment has already been established as a standard of care in the absence of good quality randomised evidence. Moreover, since responding patients are likely to be more homogeneous and more likely to benefit, such designs may offer improved efficiency compared to a traditional RCT which randomises all patients regardless of their individual initial response status. This has been demonstrated by Kopec et al. [36] for trials with a binary outcome but it is not always the case. For example, Capra [39] concluded that due to the loss of information on those patients enrolled but not randomised, the traditional RCT can be more powerful in detecting treatment differences across a range of realistic situations. This was demonstrated for studies measuring time to event end points, such as the JIA trial by Ruperto et al. [37] The design is most useful when responders represent a relatively small proportion of the overall enrolled population and is particularly powerful when the drug effect is large and responders represent
