Optimizing the Design of a Ring-Prophylaxis Study to Prevent Dengue Infection

Transcription

1 Faculty of Sciences In collaboration with Janssen Pharmaceutical Companies of Johnson & Johnson Optimizing the Design of a Ring-Prophylaxis Study to Prevent Dengue Infection Nina Dhollander Master dissertation submitted to obtain the degree of Master of Statistical Data Analysis Promotor: Dr. An Vandebosch Co-promotor: Dr. Joris Menten Academic year

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3 Faculty of Sciences In collaboration with Janssen Pharmaceutical Companies of Johnson & Johnson Optimizing the Design of a Ring-Prophylaxis Study to Prevent Dengue Infection Nina Dhollander Master dissertation submitted to obtain the degree of Master of Statistical Data Analysis Promotor: Dr. An Vandebosch Co-promotor: Dr. Joris Menten Academic year

4 The author and the promoter give permission to consult this master dissertation and to copy it or parts of it for personal use. Each other use falls under the restrictions of the copyright, in particular concerning the obligation to mention explicitly the source when using results of this master dissertation. Nina Dhollander Monday 5 th September, 2016

5 Foreword To my knowledge, this Master Thesis is the first to investigate the use of a ring design in the context of developing a chemoprophylaxis against dengue. All programming code and results were derived by myself, and belong to Janssen, the Pharmaceutical Companies of Johnson & Johnson. The contents of this Master Thesis may not be used for any other purpose than its evaluation and may not be disclosed to any third parties without explicit written permission by Janssen. It would not have been possible to write this Master Thesis without the help and support of the people around me. First of all, I would like to thank Dr. An Vandebosch and Dr. Joris Menten for the opportunity to do my Master Thesis at Janssen, for providing such an interesting research topic and for their guidance throughout all stages of this thesis. In addition, I have to thank Cristina Sotto for her critical reading and helpful remarks. Finally, I would like to thank my friends and family for their support.

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7 Table of Contents 1 Introduction What is dengue? Dengue transmission Epidemiology of dengue Treatment and prevention Clinical development of a chemoprophylactic agent for dengue Cluster randomised trials Sample size re-estimation Research questions and objectives Methods Cluster-level analysis Individual-level analysis Phase 1 Determining the best statistical method Data generation Simulation set-up Size and power estimation Results and discussion Phase 2 Determining the optimal sample size Simulation set-up Sample size estimation Results and discussion Phase 3 Sample size re-estimation Simulation set-up Sample size re-estimation

8 5.3 Results and discussion Conclusion 49 References 50 A ICC Assumptions 61 B Phase 1 Tables and Figures 63 C Phase 2 Tables and Figures 77

9 Abstract According to the World Health Organization, dengue currently is one of the most important mosquito-borne viral diseases in the world. Nonetheless there remains an unmet need for effective preventive measures. The development of a dengue chemoprophylaxis would greatly aid the battle against dengue. The aim of this Master Thesis is therefore to explore design possibilities for a hypothetical early phase clinical trial in the context of a dengue chemoprophylaxis. In particular, the possibilities for implementing a ring design will be investigated. In a ring trial participants are recruited from an epidemiological ring around newly diagnosed dengue cases. Rings are then randomised to either placebo or prophylaxis. Because participants are recruited from a high risk population, incident dengue rates are expected to be higher than in a conventional design, which could decrease the required sample size and cost of the study. However, because participants from the same ring are likely to be correlated, the ring design should take into account those design and analysis issues typical for cluster randomized trials. Therefore, in the first phase of this thesis, different cluster- and individual-level statistical methods (t-test, Wilcoxon test, logistic and Poisson regression with sandwich estimator or based on the quasi-likelihood approach, logistic GEE with an exchangeable correlation structure, logistic GLMM with a random intercept) were compared. The simple two-sample t-test seemed most robust in terms of size, power and bias, and was therefore selected for further investigation. Sample size calculations were carried out for multiple designs using different sized epidemiological rings, after which a design using a 40 m radius seemed the most cost efficient. Finally, for this design the possibilities of implementing an internal pilot study and using blinded sample size re-estimation based on nuisance parameters were investigated. The dynamic design greatly improved the power of the study when the initial nuisance parameters estimates had been incorrect, with only minimal inflation of the type I error. However, the results suggested that for specific combinations of nuisance parameters, different than the ones investigated here, more severe type I error inflation might occur. Thus, while more extensive research remains necessary for the use of ring trials and the use of blinded sample size re-estimation and its alternatives, the results from this thesis strongly favour their implementation in future studies evaluating dengue (chemo)prophylaxis.

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11 Acronyms ANOVA analysis of variance BLA Biologics License Application CI confidence interval CRT cluster randomised trial DE design effect DF dengue fever DHF dengue hemorrhagic fever DSS dengue shock syndrome FDA Food and Drug Administration GEE Generalized Estimating Equations GLMM Generalized Linear Mixed Models ICC intraclass correlation coefficient IND Investigational New Drug Application NDA New Drug Application RR relative risk WHO World Health Organization

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13 List of Figures 1.1 Course of dengue infection Transmission of the dengue virus Distribution of the global dengue risk The biopharmaceutical research and development process Schematic representation of the design of a ring prophylaxis trial Association between the distance of the participant s house to the house of the index case and different measures for dengue incidence or prevalence Algorithm used to estimate the size, power and bias of different statistical methods in a ring trial design Size properties of various statistical methods under different scenarios Size properties of various statistical methods under different scenarios Power of various statistical methods under different scenarios Power of various statistical methods under different scenarios Median relative bias of the prophylaxis effect for various statistical methods under different scenarios Algorithm used to determine the number of clusters needed to obtain the desired power level Estimated power for different study designs Estimated power for different study designs Estimated cost in million dollars for different study designs Dependence of the estimated power on the ICC and the number of clusters for a study design recruiting participants within a 40 m radius from the index case Algorithm used to evaluate the effect of sample size re-estimation based on nuisance parameters on the type I error, power and final sample size Blinded baseline incidence estimate at interim point Blinded ICC estimate at interim point Re-estimated total number of clusters

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15 List of Tables 3.1 Comparison of the observed and simulated outcomes for various studies Short description of the studies used for estimation of the baseline incidence Effect of sample size re-estimation on the type I error and power for three different scenarios. The number of modifications is given for the type I error simulation (based on 2000 random samples) and for the power simulation (based on 1000 random samples)

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17 1 Introduction Dengue ranks as one of the most important mosquito-borne viral diseases in the world according to the World Health Organization (WHO), with almost half of the world population being at risk of disease. Development of a dengue-specific antiviral (chemo)prophylaxis would aid in the prevention and treatment of dengue, which is currently still mostly limited to vector control and supportive care [1]. 1.1 What is dengue? Dengue fever is caused by four serotypes: DENV-1, DENV-2, DENV-3, and DENV-4, all of which have spread throughout South-Asia, the Western Pacific, Africa, Central- and South- America and the Eastern Mediterranean regions [1]. In addition, a possible new fifth serotype, DENV-5, has been discovered in the Sarawak forest of Malaysia [2, 3]. Dengue viruses are RNA viruses belonging to the Flavivirus genus/flaviviridae family, which also includes other well-known viruses, such as the yellow fever virus and Zika virus [4]. The course of dengue infection is summarized in figure 1.1. After an incubation period of 4-6 days, infection with any of the DENV serotypes may remain asymptomatic or result in a spectrum of clinical symptoms, ranging from mild flu-like symptoms known as dengue fever (DF), to severe forms known as dengue hemorrhagic fever (DHF) and dengue shock syndrome (DSS). DHF and DSS are characterized by an impaired ability to form blood clots, a decreased resistance of blood vessel walls leading to bruising, and fluid accumulation in the chest or

18 2 abdomen. In addition, DSS is also characterized by hypovolemic shock, during which severe blood and fluid loss makes the heart unable to pump enough blood through the body, possibly leading to severe organ damage and death [5, 6]. Figure 1.1: Course of dengue infection [7]. While infection with any of the DENV serotypes confers long-lasting immunity for that particular serotype, immunity against other DENV variants is only short-lived [7, 8]. Secondary infection with a different dengue serotype has consistently been associated with an increased risk of DHF/DSS, although DHF/DSS has also been observed with primary infections, indicating the role of other viral and/or host factors [5, 7 9]. 1.2 Dengue transmission The dengue virus is spread through a human-to-mosquito-to-human cycle, with Aedes aegypti as the primary vector, although other Aedes species also have a limited ability to serve as dengue vectors (figure 1.2). As a highly domesticated mosquito with a high affinity for human blood and high susceptibility to infection, Aedes aegypti is an extremely efficient vector, well-known for transmitting other diseases such as yellow fever and Zika [1, 4]. When a mosquito takes its blood meal during a period of viraemia, it can transmit dengue to other people after 8-12 days, and can continue to do so for the remaining 3-4 weeks of its life span [6, 10]. Transmission by blood products [11] or vertical transmission during pregnancy [12, 13] can occur, although reported cases are rare. 1.3 Epidemiology of dengue Global distribution The distribution of dengue is related to the spread of its vector Aedes aegypti, which dwells in tropical and subtropical regions all over the world, mainly in regions where the winter temperature does not drop below 10 C (figure 1.3). The worldwide incidence of dengue has risen

19 3 Figure 1.2: Transmission of the dengue virus occurs through a human-to-mosquito-to-human cycle [10]. 30-fold over the last 50 years [1,14,15], with currently % of the world population ( billion people) being at risk of dengue [1, 16]. An estimated million new infections occur annually in more than 125 endemic countries, with a further spread to previously unaffected areas [1, 14, 15]. Most countries in Southern Asia, the Western Pacific and Central- and South- America have been declared hyper-endemic, with all four dengue virus serotypes present. This trend is likely due to increases in long-distance travel, population growth and an increase in the surveillance and reporting of dengue cases [1, 14, 17]. Figure 1.3: Distribution of the global dengue risk according to the WHO (2012) [1] Populations at risk Endemic countries The epidemiology of dengue is heterogeneous in both space and time, with incidence rates varying between years and often assuming seasonal patterns depending on the temperature and rainfall. Furthermore, the transmission and occurrence of dengue can vary strongly between countries and between rural and urban areas. Stanaway et. al. (2016)

20 4 [15] estimated the one-year incidence of symptomatic and asymptomatic dengue in 2013, with estimates ranging from less than 1 % for Central America to % for regions such as South-east Asia and the Caribbean. However, one-year incidence rates of over 10 % have also been reported [18]. Unfortunately, the number of asymptotic dengue cases often needs to be approximated based on a limited amount of information, leading to additional uncertainty about the incidence estimates. The disease profile of dengue varies between regions and can depend on population characteristics such as age profile and previously circulating DENV serotypes. Symptomatic and severe dengue tend to develop more readily in children and adolescents, who often have not yet developed cross-reactive immunity against all serotypes [7,17]. When also considering asymptomatic dengue infection some studies still indicate a similar age trend [15], while others observe no difference in the incidence between age groups [19, 20]. Overall this makes it difficult to provide reliable and generalizable estimates of dengue incidence. Travellers International travel to dengue-endemic regions has played a significant role in the global spread of dengue. Prospective studies of travellers have indicated an incidence rate of cases per 1000 person-months [21 24]. As some of these studies were only able to detect symptomatic dengue, the true incidence is likely to be higher. The population of mosquito species that capable of spreading the dengue virus has been growing in many nonendemic countries, possibly leading to autochthonous cycles of infection established by infected travellers. Locally acquired dengue infections have been reported in Europe, the USA and Australia [17, 24, 25]. 1.4 Treatment and prevention Treatment With correct and timely intervention the management of DF is relatively simple, inexpensive and effective. Supportive treatments such as intravenous fluid replacement can reduce disease severity and almost eliminate mortality. In practice a correct diagnosis of DF often does not occur until a few days after the onset of symptoms. Furthermore, there are no accurate biomarkers to predict which cases are likely to develop DHF or DSS. The development of a dengue-specific antiviral drug is likely to further aid the treatment of dengue. [1, 9] Prevention Current prevention measures Currently the reduction and prevention of dengue virus transmission is mostly limited to vector control and environmental management (e.g. insecticides, installation of water supply systems). This strategy has been largely ineffective due to insufficient

21 5 knowledge about the spread of dengue, lack of resources and logistic shortcomings [9, 19, 26]. Endemic countries often only carry out short-term interventions in response to the detection of symptomatic dengue infections, which are too late to have an impact and are neither sustained nor evaluated [1]. Vaccine development Ideally the prevention and control of dengue would consist of an integrated approach based on vaccination regimes and effective vector control strategies [1]. As of December 2015 the first dengue vaccine, Dengvaxia (CYD-TDV) developed by Sanofi Pasteur, has been approved in Mexico, Brazil, El Salvador, Costa Rica and the Philippines for use in individuals 9-45 years of age living in endemic areas. Early 2016, the first public vaccination program started in the Philippines [27]. Pooled analysis of the Dengvaxia phase III clinical trials indicated that vaccine efficacy was approximately 80% for dengue hospitalization and 90% for severe dengue in children and adolescents aged 2-16 years. While Dengvaxia represents a major advance for the control of dengue, it does not provide a final solution. For children =< 9 years of age increased cases of hospitalization and severe dengue were reported three years after vaccination. Other considerations were its low vaccine efficacy against DENV-1 and 2 (resp. 54.7% and 43.0%) in comparison to DENV-3 and 4 (resp. 71.6% and 76.9%) and its low vaccine efficacy in children who were seronegative at the time of vaccination (38.1%) in comparison to seropositive children (78.2%). The immunisation regime requires a 3-dose series on a 0/6/12 month schedule, only offering sufficient protection after the final dose [28 30]. Long-term follow-up for vaccine efficacy and safety is still ongoing. Because of the association between secondary infections and disease severity, immunity against all four serotypes needs to be long-lasting. A vaccine which only affords short-lived protection for one or more serotypes could theoretically make populations more susceptible to severe dengue [8, 31]. While vaccination programs with Dengvaxia are expected to significantly reduce the disease burden of dengue in endemic areas, the use of Dengvaxia is limited. In addition the vaccine does not provide 100 % protection against dengue infection and development of severe disease, and the 0/6/12 month dosing regime renders it unsuitable for travellers. Further research with regard to new prevention and treatment measures remains necessary. Antiviral drugs as prophylaxis While a safe and effective DENV vaccine would be an ideal long-term solution, other strategies are needed to combat the current dengue problem. Antiviral drugs can be given after a patient has already become symptomatic [32], and can in some cases also be used as a prophylaxis. In the case of a dengue this would provide an alternative prevention measure to vaccination for young children or immunosuppressive patients, or when the vaccination schedule cannot be completed before arrival in an endemic country [33]. The use of antiviral drugs before onset of disease has been used as a prevention strategy before.

22 6 For example, when individuals travel to an area where malaria is prevalent, they are advised to take malaria medication before, during and after travel to prevent infection. Examples of viral diseases where prophylaxis has been used successfully are certain types of influenza [33] and HIV [34]. 1.5 Clinical development of a chemoprophylactic agent for dengue Introduction to drug discovery and development The drug discovery and development process spans over multiple years, comprising of different phases (figure 1.4). Drug discovery entails both the discovery of new potential drug candidates through insights into disease processes or high-throughput screening of molecular compounds, and early testing with regard to potency, metabolic stability, bioavailability, etc. While the process of early research and development is relatively flexible, the course of preclinical investigations is regulated much more strictly and typically comprises of in vitro and in vivo animal studies evaluating a range of toxicological aspects. These studies provide indications with regard to the safety of a compound when given acutely or repeatedly over a period of time, and which organs and physiological systems might suffer from adverse effects. Typical examples include screening for immunotoxicity and embryotoxicity. When there are no safety concerns, drug development can progress to the clinical phase, for which preclinical data can provide a basis to determine starting doses and dosing regimens for the initial clinical trials [35]. Figure 1.4: The biopharmaceutical research and development process [36]. IND: investigational new drug application; NDA: new drug application; BLA: biologics license application; FDA: food and drug administration. Phase I studies, including first-in-human studies, are conducted to demonstrate safety and tolerability and to characterize the pharmacology of the drug compared to a placebo in healthy

23 7 volunteers. Next, exploratory efficacy and tolerability are evaluated in a small number of patients in phase IIa studies (proof-of-concept), followed by phase IIb studies to confirm efficacy and safety and to find the optimal dose range in the patient population. Thereafter, the desired dose of the drug is selected. Pivotal phase III studies are then conducted to demonstrate efficacy and safety of the selected dose in large patient population studies. While a placebo is sometimes used in phase II and phase III studies, comparison of the drug against standard care is often considered to be more ethical. If the data suggest a favourable risk-benefit relationship, a new drug approval application is filed, that allows the drug to be marketed if approved. Post-licensing or Phase IV studies are often required to further evaluate safety [35] Clinical development of a prophylactic agent using a ring design In reality, the development process is often tailored to the specific needs and requirements of the drug candidate, and development of a (chemo)prophylaxis will therefore differ slightly from the scenario described in section 1.5.1, which is commonly conducted in a therapeutic setting. Primarily, the target population of a prophylaxis is not limited to patients, but consists of the entire population at risk of disease. Therefore recruitment for phase II and III studies should take place at the level of the population at risk. Consequently, prophylaxis studies usually require large sample sizes, as the incidence rate in the population at risk tends to be lower than the recovery rate in patients, even in endemic areas. For example, while phase II and phase III studies for therapeutic agents usually comprise of respectively a few hundred and a few thousand subjects [35], over 4000 subjects were recruited for the phase II proof-of-concept study for Dengvaxia [37] and over subjects were enrolled over three phase III studies for Dengvaxia [29]. While vaccine studies only require a few treatment administrations and are therefore relatively easy to conduct in large populations, the use of chemoprophylaxis necessitates sustained intake and thus evaluation requires more intensive monitoring. The required sample size for a prophylaxis safety and efficacy trial is inversely proportional to the disease incidence in the study population. Thus, performing trials in populations with a high risk of infection could reduce the sample size and/or the duration of follow-up required to conclude the study. Additionally, evaluation takes place in the population that stands to benefit most from a safe and efficacious prophylaxis [31]. One recently proposed approach for finding populations at high risk of disease is that of a ring trial or a ring study: a person newly diagnosed with infection becomes an index case around whom an epidemiologically defined ring is formed (e.g. based on social or geographical connections). Within this ring, individuals who are connected to the case and are therefore at increased risk of infection, are recruited. Rings can be seen as clusters which are randomized to receive either prophylaxis or placebo. The statistical literature on cluster randomised trials (CRTs) can therefore be applied to compare the disease incidence between rings and to evaluate the prophylaxis efficacy [38]. A schematic representation of the design of a ring prophylaxis trial for dengue is given in figure 1.5.

24 8 Figure 1.5: Schematic representation of the design of a ring prophylaxis trial. Intervention = prophylaxis or placebo. Efficacy = comparison of the primary outcome between intervention arms. Figure adapted from Henao-Restrepo et al. (2015) [38].

25 9 Originally the concept of ring vaccination or ring prophylaxis was used as a targeted programmatic public health measure: by creating a buffer of immune people around each new case, further spread of the infection might be prevented. Perhaps its first use was as part of the surveillance-containment strategy that was central to the eradication of small pox throughout Asia, Africa and Latin-America in the 1970s [39]. The use of ring prophylaxis has also been indicated to slow down transmission of various types of influenza when used in semi-closed or closed environments (e.g. schools, military compounds) [40 42]. Recently, however, the ring design was implemented for the first time in a cluster-randomised phase 3 trial which took place in Guinea. Its aim was to assess the safety and efficacy of the rvsv-zebov candidate vaccine for the prevention of Ebola virus disease. Interim analysis of the trial data successfully indicated vaccine efficacy [43], demonstrating the use of ring study designs for the evaluation of vaccine or prophylaxis efficacy. The final results were expected to be published midway 2016, but were not yet available at the time of writing this thesis [44]. For the purpose of this thesis some assumptions were made about the set-up of a hypothetical dengue chemoprophylaxis study, which from now on will be referred to as the dengue study. The dengue study is assumed to be a cluster-randomised double-blinded early phase study with the aim to evaluate efficacy of a dengue chemoprophylaxis when compared to a placebo. Efficacy is expressed as the proportion of participants with evidence of incident dengue infection during the follow-up period among adults who were seronegative at the start of chemoprophylaxis / placebo intervention. 1.6 Cluster randomised trials In CRTs clusters of individuals are randomized to interventions. General advantages of CRTs include preventing contamination between intervention groups and capturing the indirect effects of prophylaxis. Since dengue is a communicable disease treating only some of the ring members might lower disease transmission and incidence in the entire ring. An individually randomized trial cannot take these effects into account [45, 46]. Additionally, a ring trial has the advantage of evaluating intervention in those who are most likely to benefit from it [38]. In contrast, the disadvantages of CRTs include a potentially substantial loss of statistical efficiency and an increased risk of selection bias, imbalances between study arms and lack of generalisability [45]. Note that in a prophylaxis ring trial the efficiency loss might be (partially) compensated by the increase in disease incidence [38] and the inclusion of indirect effects [45]. A key feature of CRTs is that the outcomes of individuals within a cluster are correlated rather than independent. The variability in the data then consists of two components: the within-cluster and between-cluster variance. When these components are not taken into account properly, the variability in the data is underestimated. Intuitively this makes sense: when two individuals have correlated outcomes, their data provides less information and thus less certainty than if

26 10 their outcomes had been independent. As a consequence, the standard statistical methods will overestimate the significance of the intervention effect and underestimate the required sample size. In order to account for correlated data during the design and analysis of a study, a quantitative measure is needed which reflects the extent to which individuals from the same cluster are correlated, the most common one being the intraclass correlation coefficient (ICC) [45,47]. Several methods exist to estimate the ICC from binary data. Here the analysis of variance (ANOVA) estimator as described by Wu et al [48] was used: with ICC = MSB MSW MSB + (n a 1)MSW ( MSB = 1 Z 2 k ( ) Zk ) 2 K 1 n i N ( 1 MSW = Zk ) Zk 2 N K ( n a = 1 K 1 N n 2 k N where K equals the number of clusters, Z k the number of incident dengue cases in cluster k, n k the number of individuals in cluster k, and N the total number of individuals in the study. Here, n a corresponds to the average cluster size and MSB and MSW correspond to the between and within cluster mean squares from a one-way ANOVA of the binary data [48]. The ICC will usually fall between zero and one, with a higher ICC indicating more strongly correlated data. The ICC is related to the design effect (DE), which is a measure for the increase in variance as a result from randomizing clusters instead of individuals. Since the variance is inversely proportional to the required sample size, it can also be used as a straightforward method to approximate the required sample size for CRTs: ) n k Sample size in a CRT = Sample size in an individual randomized trial DE Larger design effects will thus lead to larger sample sizes for CRTs. The design effects can be calculated based on the ICC as follows: DE = 1 + (n a 1) ICC with n a being the mean cluster size. The DE increases with the ICC, but also with n a. Subsequently, increasing the number of clusters in a CRTs is more efficient than increasing the mean cluster size with regard to statistical power [45, 46]. Note however that for CRTs there can be

27 11 a large discrepancy between which design is most efficient in terms of power and in terms of budget, especially when the cost ratio, i.e. the cost of cluster initialization compared to the cost of enrolling an extra subject in an already existing cluster, is high. In the design stage of a CRT both the statistical and cost efficiency should be investigated for different combinations of the number of clusters and the cluster size [49 51]. A variety of approaches have been developed to take correlated data into account during analysis. One of the simplest is the comparison of cluster specific summary measures between the prophylaxis and placebo group. In case of the dengue study, the summary measure of primary interest would likely be the proportion of participants in each cluster with evidence of incident dengue infection as defined in section By only considering one summary measure for each cluster, the ICC is naturally accounted for since clusters are assumed to be independent [45, 52]. When implemented correctly, methods based on cluster-level summary measures are usually robust under a wide range of circumstances [45]. A potential disadvantage of this method is the loss of information by reducing multiple responses into one outcome measure, leading to inefficiency [45,52]. Loss of information can be especially large for studies with large cluster sizes [52] or when there is substantial variation in the sample size per cluster [45]. Other disadvantages include the inability to adjust for possibly important individual-level covariates. In contrast, individual-level regression methods do allow for the adjustment of individual-level covariates and can be more efficient since the data is not reduced to cluster-based summary measures. However, they are not always reliable when the number of clusters is small. According to Hayes & Moulton (2009) [45] the individual-level analysis methods that will be discussed in section 2.2 require at least 15 clusters per arm, while Murray et al. (2004) [53]) mentions needing at least 40 clusters in total. Especially when the ICC is high, parameter estimates can become biased, and significance tests and confidence intervals may not have the correct size and coverage [45, 52]. 1.7 Sample size re-estimation Despite the crucial role of the ICC in power and sample size calculations, there are often only few reports available on its observed value in a similar study set-up. Moreover, ICC estimates can vary considerably between studies, even when they have a similar set-up and endpoint [45, 48, 54]. This is partially due to population differences, uncertainty (as studies often are not designed to give accurate estimates of the ICC), and differences in the design and analysis approach [48]. A possible solution to this problem is the use of an internal pilot study design. In the design, nuisance parameters are estimated at an interim time point in the study and the sample size is re-estimated. Overpowered studies may then be stopped early, while underpowered studies can be correctly expanded in order to obtain the desired power level. Since

28 12 the nuisance parameters at the interim point are based on trial data, they are more likely to accurately reflect the true values than those based on the literature. Therefore, the re-estimated sample size is more likely to provide the study with the desired power level [55]. For the internal pilot to be useful, the re-estimated sample size needs to be correct in such a way that the desired power level is achieved and the type I error rate inflation is kept to a minimum [56]. Blinded sample size re-estimation is based on estimates of the ICC and possibly also of other nuisance parameters that were lumped over the placebo and prophylaxis group. However, even then the type I error might still be affected as the blinded estimates may depend on the intervention effect. While no studies were found investigating the effect of blinded sample size re-estimation for CRTs, results for individual-randomized studies indicated a small, but negligible increase in the type I error rate [57] when re-estimating the sample size based on the lumped variance. Previous simulation studies by Lake et al. (2002) [55] and Schie et al. (2014) [55] investigated unblinded sample size re-estimation for CRTs, where the estimated ICC was pooled over the control and treatment group, and found only minor increases of the type I error rate, with the largest observed type I error from both studies being (nominal value = 0.050). No studies were found investigating the effect of sample size re-estimation based on estimates of the baseline incidence for CRTs. 1.8 Research questions and objectives The overall aim of this thesis was to investigate the potential benefits of implementing a ring design using the context of a hypothetical early phase clinical trial evaluating a dengue (chemo)prophylaxis. For this purposed, the thesis was divided into three phases: 1. To determine the best statistical method with regard to coverage and power, based on literature data and simulation studies. 2. To determine the optimal sample size and number of clusters for the selected method with regard to coverage, power and cost through simulation studies. 3. To assess the possibilities of incorporating adaptive elements in the study design, such as sample size re-estimation and interim analysis.

29 2 Methods Different statistical methods were considered for the analysis of clustered data from a ring design, including both cluster-level and individual-level analysis. Each method was used to test the one-sided null hypothesis of no decrease in dengue incidence when comparing prophylaxis against placebo. All analyses and calculations were done in R v3.2.3 with the RStudio v interface [58]. 2.1 Cluster-level analysis Two-sample t-test The simple two-sample t-test evaluates whether the mean proportion of incident dengue cases differs between the prophylaxis and placebo group. The test statistics is calculated as t = x 0 x 1 s 2 0 K 0 + s2 1 K 1 where x i equals the mean proportion in intervention i (0 = placebo, 1 = prophylaxis), s i the standard deviation and K i the number of clusters. The t-test statistic is compared against a t-distribution with degrees of freedom equal to K 0 + K 1 2. The intervention effect x 0 x 1 corresponds to a risk difference. The t-test assumes normally distributed data, but is generally robust against small to moderate deviations from this assumptions [59].

30 Regression with sandwich estimator It is possible to regress the cluster-summary measures on the intervention using conventional logistic and Poisson regression. However, this does require adjustment of the variance estimator to correct for its underestimation. For example, the sandwich variance estimator is asymptotically robust to misspecifications of the mean-variance relationship and correlation structure. Unfortunately, it is biased downward when the number of clusters is small, leading to inflation of the type I error. Although its use is often associated with Generalized Estimating Equations (GEE), it can be applied to any type of regression, as was done here [53, 60, 61]. First, in a logistic regression model the probability of incident dengue in each cluster was regressed on the intervention: π k = exp(β 0 + β 1 I(prophylaxis) k ) 1 + exp(β 0 + β 1 I(prophylaxis) k ) using a binomial random component and the logit link function: ( πk ) log = logit(π k ) = β 0 + β 1 I(prophylaxis) k 1 π k (2.1) where π k equals the expected probability of incident dengue in cluster k, β 0 equals the mean logit probability of incident dengue cases for the placebo group, β 1 equals the mean difference in logit probability between the placebo and prophylaxis groups, and I(prophylaxis) k indicates whether the jth individual received placebo (0) or prophylaxis (1). exp(β 1 ) corresponds to an odds ratio. Conventional logistic regression (without use of the sandwich estimator) assumed that, conditional on the intervention, the number of incident dengue cases follows a Binomial distribution with mean and variance: E (number of incident dengue cases) k = π k n k Var (number of incident dengue cases) k = π k (1 π k ) (2.2) Note that equation 2.2 underestimates the true variability in the data when clustering occurs, for which the sandwich estimator was used as a correction. Alternatively, we might choose to model the rate or the number of incident dengue cases in each cluster with a Poisson regression model: µ k = exp(β 0 + β 1 I(prophylaxis) k ) m k (2.3) assuming a Poisson distribution and using the log link function: log(µ k ) = β 0 + β 1 I(prophylaxis) k + log(n k ) where µ k equals the expected rate of incident dengue cases in cluster k, β 0 equals the mean log rate in the placebo group, β 1 equals the mean difference in log rates between the placebo and

31 15 prophylaxis groups, I(prophylaxis) k indicates whether the kth cluster received placebo (0) or prophylaxis (1) and n k is an off-set variable indicating the cluster size of each cluster. exp(β 1 ) corresponds to a relative risk. Conventional Poisson regression assumes that the number of incident dengue cases follows a Poisson distribution conditional on the intervention, with mean and variance: E (number of incident dengue cases) k = µ k Var (number of incident dengue cases) k = µ k (2.4) Again, note that equation 2.4 underestimates the true variability in the data when clustering occurs, for which the sandwich estimator was used as a correction Quasi-likelihood approach In addition to the regression approach described in the previous section, quasi-likelihood theory has also been suggested as a method to account for correlated data. Quasi-likelihood theory offers a robust approach to regression analysis by only making assumptions about the meanvariance relationship. The unadjusted variance estimate is multiplied by a scale parameter φ whose value depends on the degree of clustering in the data. Here φ was set equal to the Pearson χ 2 goodness-of-fit statistic divided by its degrees of freedom (the number of observations minus the number of parameters), as is common practice for logistic and Poisson regression [45]. The same models described in equation 2.1 and 2.3 were fitted, this time using the scale parameter φ instead of the sandwich estimator to account for correlated data Wilcoxon s rank sum test All of the previously described methods make parametric assumptions about the data. While some methods, such as the t-test, are known to be quite robust against violations of its distributional assumptions, it might be preferred to use a non-parametric alternative, especially when the number of clusters is small and it becomes difficult to make a reliable assessment of the data distribution. The Wilcoxon s Rank Sum Test is a non-parametric test, which has the advantage of providing valid p-values irrespective of the data s underlying distributional form. Disadvantages are that it is somewhat less powerful when the normality assumptions is valid, and that the main emphasis is on significance testing with no straightforward methods to obtain a non-parametric estimate or confidence interval [45, 59]. The Wilcoxon s rank sum test pools and ranks the cluster-specific proportions from both intervention arms. Let T i be the sum of the ranks in the ith intervention arm, then the test statistic is calculated as z = T 1 K 1 (K 1 + K 0 + 1)/2 K1 K 0 (K 1 + K 0 + 1)/12

32 16 with K 0 and K 1 being the number of cluster in the placebo and prophylaxis group. The test statistic is compared against a the standard normal distribution. The null hypothesis is that the two sets of observations are samples from the same underlying distribution. If the mean rank for the placebo clusters is significantly higher than that for the prophylaxis clusters, this provides evidence that the distribution of cluster summaries in the prophylaxis group is shifted to the left. In other words, the proportion of incident dengue cases is then generally lower for those clusters receiving prophylaxis when compared to clusters receiving placebo [59]. 2.2 Individual-level analysis Generalized Estimating Equations The basic logistic GEE model for binary data is similar to the one shown in equation 2.1 for standard logistic regression. However, instead of regressing the cluster summary-measures the individual-level data is used: π k = exp(β 0 + β 1 I(prophylaxis) k ) 1 + exp(β 0 + β 1 I(prophylaxis) k ) where k refers to the kth cluster and π k refers to the probability that a participant from the kth cluster acquires dengue. While the model is fitted using individual-level data, no adjustments are made for individual-level variables (e.g. age). In other words, the probability of acquiring dengue is assumed to be equal for all individuals from the same cluster and therefore π k still represents a cluster-specific probability. While standard logistic regression based on individuallevel data assumes that the observed outcomes are independent, GEE allows observations from the same cluster to be correlated according to some correlation matrix. Here exp(β 1 ) represents the population-average odds ratio associated with the prophylaxis effect. GEE relies on an iterative generalized least squares methods instead of likelihood-based approaches for parameter estimation. Standard errors are obtained using sandwich estimators. GEE models are fitted with the geeglm function from the geepack package [62 64], which includes several pre-specified options for the correlation structure. For the purpose of this thesis an exchangeable structure was used, as this was considered the most appropriate. An exchangeable correlation structure assumes that participants from different clusters are uncorrelated, while participants from the same cluster all have the same correlation coefficient [45] Generalized Linear Mixed Models A Generalized Linear Mixed Models (GLMM) or random effects model for binary data was fitted based on individual-level outcomes. However, similarly as discussed for GEE no adjustment were made for individual-level data, and the probability of acquiring dengue was thus assumed

33 17 to be equal for all individuals from the same cluster: π k = β 0 + β 1 I(prophylaxis) k + u k where π k equals the probability of acquiring dengue during follow-up for the kth cluster, β 0 equals the expected logit outcome for individuals in the placebo group, β 1 represents the prophylaxis effect on the logit scale, and I(prophylaxis) k indicates whether the kth cluster received placebo (0) or prophylaxis (1). The term u k is a random effect relating to the kth cluster, and this is the term in the model which the between-cluster variation into account. Random effects are assumed to be sampled from a standard normal distribution, while the data within clusters is assumed to follow a binomial distribution. exp(β) represents the subject-specific odds ratio of the prophylaxis effect, conditional on the random effect [45, 60]. According to Bellamy et al. (2000) [52] regression parameters from a population-averaged GEE model are approximately equal to those from a subject-specific GLMM model multiplied by a bias term which is a function of the ICC: β pa = β ss (1 ICC). Because the likelihood for logistic regression random effects models is difficult to maximize [45, 60], a quadrature approximation using 20 quadrature points was used. This model was fitted using the glmer function from the lme4 package [65].

34 18

35 3 Phase 1 Determining the best statistical method During the first phase of this thesis, differences in size, power and bias among statistical methods were investigated for a range of ICC values and effect sizes under different scenarios: one with many small clusters, one with few large clusters and an intermediate scenario. 3.1 Data generation Random data was generated under the assumption of an equal number of clusters per intervention group and for a given number of clusters, mean cluster size, baseline incidence (π 0 ), effect of prophylaxis (expressed as a relative risk) and ICC. First cluster sizes were generated as a random Poisson variable, to reflect the random variation in cluster size, and truncated at a minimum of four participants per cluster. The incidence in the prophylaxis group (π 1 ) was calculated as π 0 multiplied by the effect size. Next, random correlated data was generated using a Beta-binomial distribution, as proposed by Bellamy et. al. (2000) [52]. Random probabilities π k were generated for each cluster from a Beta(a,b) distribution with:

36 20 a = π i R b = 1 π i R R = ρ 1 ρ where π i equals the expected incidence for intervention i (π 0 = control, π 1 = prophylaxis) and ρ equals the ICC. Next random binary responses Y jk were generated from a Bernoulli(π k ) distribution, where Y jk equals the outcome of the j th participant from the k th cluster. When the ICC equalled zero Y jk were generated from a Bernoulli(π i ) distribution. Generated datasets where only one the placebo or only the prophylaxis group contained no events complicate estimation of the prophylaxis effect. When this occurred, one event was added to each of the intervention groups to facilitate analysis. The output of the data generating function included an indicator showing whether the dataset was modified, which allowed for counting the number of modified random samples in a simulation. While there exist more sophisticated methods to handle effect estimation under these circumstances, these were not applied because of the exploratory nature of these simulation studies and the relatively small number of simulations in which this situation occurred. To assess the reliability of the data generating process, data was generated for a range of ICC values ( ) using summary measures from the studies listed in table 3.1. As none of these studies evaluated an intervention, the relative risk (RR) was set equal to one. For each study 5000 random samples were generated and the mean number of participants and incident dengue cases were calculated. Table 3.1 shows that the simulated outcomes correspond well to observed measures, regardless of the ICC. Intuitively this makes sense: the ICC does not affect the mean number of events, but determines how those events are distributed over clusters. As the ICC increases, the underlying cluster-specific incidences π k will differ more strongly from each other. Note that a comparison of the observed against the simulated distribution of events was not possible, as none of the listed studies reported an ICC or related measure. Next, the distribution of the generated cluster sizes (based on 5000 random samples) was compared to the variability observed by the studies listed in table 3.1. For this comparison the number of eligble participants in each cluster was used, as this was the only appropriate measure all three studies reported on. Anders et al. (2015) [19] reported a median cluster size of 30, with values ranging from 18 to 41. Similarly, the simulation returned on average a median cluster size of 30, with values ranging from 18 to 43. Mammen et al. (2008) [66] and Yoon et al. (2012) [67] reported a mean cluster size and standard deviation of 25.5 ± 9.7 and 24.5 ± 9.3 respectively. Here the simulation returned average values of respectively 24.5 ± 4.93 and

37 21 Observed No. of clusters No. of participants Incidence (%) Events Mammen et. al. (2008) [66] Yoon et. al. (2012) [67] Anders et. al. (2015) [19] Simulated No. of participants Simulated number of events for ICC range Mammen et. al. (2008) [66] Yoon et. al. (2012) [67] Anders et. al. (2015) [19] Table 3.1: Comparison of the observed and simulated outcomes for various studies. For each study 5000 random samples were generated and the mean number of participants and incident dengue cases was calculated ± 4.9. Thus while the generated range seemed representative of the real-life situation, the variability of the cluster sizes might have been too low. Throughout the thesis, the effect of prophylaxis intervention on the ICC assumption was allowed to depend on the data generating mechanism. It was assumed this would lead to equal ICCs in the placebo and prophylaxis group. However, during the final stages of this thesis it was discovered that the reliability of the data generating mechanism with regard to the ICC depended on the incidence, with lower incidences leading to lower ICC estimates (Appendix A). Consequently, the ICC was only equal for the placebo and prophylaxis groups when the RR equalled 1.00, and was lower for the prophylaxis groups when the RR was smaller. This discrepancy grew larger as the ICC increased. In practice, the assumption of equal ICCs often does not hold. However, in contrast to the results of the data generating mechanism, the ICC is often expected to be higher for the group receiving active treatment [45], since cluster variability then depends on differences in baseline incidence and differences in the prophylaxis effect. The inequality of the ICC was not discovered until the final stages of this thesis, neither was it mentioned by Bellamy et al [52]. Unfortunately, no relevant studies were found which reported the ICC for both the control and treatment group and the plausibility of the ICC assumptions resulting from the data generating mechanism could thus not be further investigated. Therefore no changes were made to the ICC assumption imposed by the data generating mechanism. While this is not expected to affect the general conclusions with regard to whether or not ring trials and sample size re-estimation are favourable study designs, the optimal design might differ than the one derived here in terms of the radius around the index case and the sample size.

38 Simulation set-up ICC Few reports were available on the observed ICC of dengue incidence at the household or community level. Arostegui et.al. (2008) [68] evaluated a pecticide-free intervention aimed at Aedes mosquitoes in Nicaragua, reporting an ICC of 0.18 for serological evidence of recent dengue infection based on 20 control clusters of approximately 100 participants. In a follow-up study evaluating the added effect of community mobilization on pesticide-free intervention, Andersson et. al. (2015) [69] reported an ICC for self-reported and serological-confirmed evidence of recent dengue infection of respectively and based on 75 control clusters of approximately 40 participants. As has been pointed out before by Hayes & Moulton (2008) and Donner & Klar (2004), ICC estimates can vary considerably between studies, even when they have a similar set-up and endpoint. Other issues with ICC estimation include the difference in setting between the dengue study and the studies by Arostegui et. al. (2008) and Andersson et. al. (2015). While the latter both adopted a cluster randomised design, clusters were not based on index cases and the average cluster sizes were larger than the one expected for the dengue study. Additionally these studies were conducted in Latin-America instead of South-East Asia. While Bayesian methods are available which can derive a prior distribution of the ICC, it is generally recommended to investigate the impact of a range of ICC values for power and sample size calculations. For this thesis, the latter approach was used, selecting a range of 0.00, 0.01, 0.03, 0.09, 0.18 and Baseline incidence The dengue incidence rate was chosen based on studies investigating dengue incidence in a similar setting as the dengue study (table 3.2). A weighted average, with weights determined by sample size, led to an estimated incidence of 8.0 %. This might be a conservative estimate, since the studies listed in table 3.2 a large radius around the index case. For this initial simulation study, a radius of m was assumed, although the optimal radius might be adapted later on during phase 2. As participants live closer to the index case, their risk of dengue increases, and thus dengue incidence is expected to increase (figure 3.1) [66,67]. Mammen et. al. (2008) [66] and Yoon et. al (2012) [67] reported dengue incidences for different radiuses around the index case. A weighted average of dengue incidence within a 60 m radius led to an estimate of 17.5 %. Note however that these two studies reported higher incidence than Anders et. al. (2015) [19]: based on the first two studies alone a weighted average of dengue incidence within a 100 m radius would have given an estimate of 11.4 % instead of 8.0 %. Therefore a correction of was applied, leading to an estimate of 12.3 % for the baseline incidence of dengue within a 60 m radius.

39 23 Study Study aim Population No. of clusters (sample size) Incidence measure Observed incidence Mammen et. al. (2008) [66] Fine-spatial clustering pattern dengue of Children in rural Thailand 12 (217) 15-day incidence in a 100 m radius from the index case 12.4 % Yoon et. (2012) [67] al. Fine-spatial clustering pattern dengue of Children in rural Thailand 50 (749) 15-day incidence in a 100 m radius 8.4 % Anders et. (2015) [19] al. Fine-spatial clustering pattern dengue of Adults and children in urban Vietnam 52 (1182) 14-day incidence in a 100 m radius from the index case 6.9 % Table 3.2: Short description of the studies used for estimation of the baseline incidence Scenarios The adequacy of different statistical methods depends on the ICC, the number of clusters and the cluster size. All methods are expected to perform better for settings with a large number of clusters and a low ICC. As the number of clusters decreases or the ICC increases the size properties of an analysis may break down and parameter estimates might show bias [52]. Therefore the selected range of ICC values and effect sizes were investigated under three different scenarios, each one with an average sample size of participants and incident dengue cases: Scenario 1 - many small clusters: 50 clusters per intervention arm with an average cluster size of 6 participants. Scenario 2 - few large clusters: 4 clusters per intervention arm with an average cluster size of 80 participants. Scenario 3 - intermediate, with the cluster size based on the estimated number of participants within a m radius from the index case [66, 67]: 26 clusters per intervention arm with an average cluster size of participants. The first and second scenario represent quite extreme situations with a very large or small number of clusters. While this makes it easier to detect the shortcomings of the different statistical methods, it is unlikely that either of these scenarios would be used in practice for the dengue study. Therefore the third and intermediate scenario was selected, which is expected to be more representative of the dengue study.

40 24 Figure 3.1: Association between the distance of the participant s house to the house of the index case and different measures for dengue incidence or prevalence. Left: the proportion of participants experiencing DENV seroconversion (mean and 95% C.I.). The numbers in parenthesis indicate the number of participants with incident dengue infection and the total number of participants in the distance interval [66]. Right: RD = recent dengue (N = 15), ES = enrolment seroconversion (N = 41), PES = post-enrolment seroconversion (N = 63), day 15 PCR-positive (N = 10). For this thesis the measure of interest is PES (incident dengue cases confirmed by seroconversion) [67]. 3.3 Size and power estimation Data was generated for a range of ICC values (0.00, 0.01, 0.03, 0.09, 0.18, 0.27) and for a range of RRs of the prophylaxis versus the placebo (0.25, 0.50, 0.75, 1.00). Under each scenario and for each combination of ICC and RR, 5000 random samples were generated and analysed using all of the cluster- and individual-level analysis methods described in section 2. For each random sample the estimated prophylaxis effect, standard error, 95 % confidence interval (CI), one-sided p-value and absolute and relative bias of the prophylaxis effect were saved for every method. The absolute bias was determined by subtracting the true prophylaxis effect from the estimated prophylaxis effect and the relative bias by taking the ratio of the estimated over the true prophylaxis effect. The true subject-specific odds ratio was approximated as discussed in section Finally, for each method the size of the test was calculated as the proportion of random samples with a significant result under a RR of 1.00, power as the proportion of random samples with a significant result under a RR of 0.25, 0.50 and 0.75 and relative bias as the median relative bias. This algorithm is graphically depicted in figure Results and discussion In each scenario a small number of the random generated samples were modified: respectively 5, 533 and 20 out of samples for scenario 1, 2 and 3. The results for Poisson and quasipoisson regression were very similar to those for logistic regression using a binomial or quasibinomial distribution, and were therefore only included in Appendix B. The estimated size for the different scenarios and methods is shown in figures 3.3 and 3.4. Since p-values

41 25 Figure 3.2: Algorithm used to estimate the size, power and bias of different statistical methods in a ring trial design. were calculated based on one-sided tests, the nominal size equalled In scenarios 1 and 3 all methods had a size relatively close to the nominal value, ranging from to Generally, the t-test and Wilcoxon test stayed closer to the nominal value ( ) than the other methods ( ). Most methods became slightly oversized as the ICC increased, going from at ICC = 0 (no clustering) to at ICC = In scenario 2, the t-test and Wilcoxon test behaved similarly as in scenarios 1 and 3, but were more conservative, ranging from to In contrast, quasibinomial and quasipoisson regression and GLMM were generally too liberal, with a size ranging from to Binomial and Poisson regression and GEE performed much worse than in scenarios 1 and 3, with the size increasing from at ICC = 0 to at ICC = The estimated power at RR = 0.25 for the different scenarios and methods is shown in figures 3.5 and 3.6. In scenario 1 all methods had good power, never dropping below Generally the Wilcoxon test and GLMM performed best, with the power never dropping below In scenario 2 the power decreased drastically, dropping below 0.40 as the ICC increased for all methods except Binomial and Poisson regression and GEE. For the latter, the power dropped to approximately 0.50 as the ICC increased. Since these methods were oversized in this scenario

42 26 (figure ), a higher power was more likely to be the consequence of statistical properties breaking down than of better efficiency. In the intermediate scenario 3, the Wilcoxon test again performed best, with a minimal power of 0.75, followed by GLMM with All other methods have a minimal power of Similar but less pronounced trends were seen at a RR of 0.75 and 0.50 (Appendix B). The breakdown of size properties was unlikely to be the consequence of data modifications. Since one-sided tests were investigated, only those modifications where no events occurred in the prophylaxis group might have affected the size. Since for these samples the observed prophylaxis effect was underestimated, one would expect fewer significant results and thus a lower size. However, as the ICC increased, for most tests the size became too liberal. In contrast, data modifications might have been partially responsible for conservative sizes and low power in some settings, especially those with a high ICC under scenario 2. Murray et al. (2004) [53] discussed that when the total number of clusters is less than 40, sandwich estimators will suffer from negative bias, leading to an inflated type I error. Results from Wu et al. (2012) [48] based on simulations studies suggested that random effects models often were more prone to estimate the ICC with negative bias than GEE. While this was not the case in the simulation study by Bellamy et al. (2000) [52], they did find that both GEE and GLMM were more prone to negative bias of the ICC when the number of clusters was small. Underestimation of the ICC could again inflate the type I error. Generalizing, it is possible that because the investigated regression methods for clustered data often rely on approximate methods for parameter estimation and depend more strongly on parametric assumptions, that they are less robust against designs with a low number of clusters. In contrast, the Wilcoxon test is a non-parametric method, while the t-test is parametric, but known to be robust against moderate deviations of its assumptions. While this could explain some of the differences between the investigated statistical methods, more research is necessary to find out to what extent the breakdown of test properties was related to the data modifications. This was not further investigated for this thesis.

43 Figure 3.3: Size properties of various statistical methods under different scenarios. The dotted line indicates the nominal size of the test (equal to 0.025). Logistic regression was performed using a sandwich estimator. 27

44 28 Figure 3.4: Size properties of various statistical methods under different scenarios. The dotted line indicates the nominal size of the test (equal to 0.025). cor = correlation structure. Figure 3.5: Power of various statistical methods under different scenarios and assuming a RR = The dotted line indicates the 0.80 power mark.

45 Figure 3.6: Power of various statistical methods under different scenarios and assuming a RR = The dotted line indicates the 0.80 power mark. Logistic regression was performed using a sandwich estimator. cor = correlation structure. 29

46 30 Figure 3.7: Median relative bias of the prophylaxis effect for various statistical methods under different scenarios and assuming a RR = The dotted line indicates unbiased estimates (relative bias = 1). Logistic regression used a sandwich estimator. cor = correlation structure.

47 31 At a RR = 0.25 all methods were prone to downward bias of the estimated prophylaxis effect as the ICC increased, regardless of the scenario (figure 3.7). While under scenarios 1 and 3, most methods only showed small biases, substantial bias was observed under scenario 2 for all methods except for the t-test. Downward biases might partially be the consequence of modifying some of the random samples. Situations in which methods were expected to perform worse corresponded to those situations which were most likely to require data modifications (low incidence, few clusters, large ICC). Indeed, for scenario 2 much more samples were modified than for scenarios 1 and 3 (respectively 533 instead of 5 and 20) and in all three scenarios the number of modifications increased with the ICC. However, by using the median relative bias these results should have been somewhat protected against the influence of modifications. Furthermore, previous studies have already indicated that regression methods for clustered data can still give biased intervention estimates, especially when the number of clusters is small and / or the ICC is large [45,47,52,53]. It is likely that the observed trends in relative bias result from a combination of the breakdown of properties and of the data modifications, although the extent to which one was most responsible was not further investigated. Similar trends were seen at a relative risk of 0.75 and 0.50 (Appendix B), but to a lesser extent. When the number of clusters was high, most methods were comparable. As the number of clusters decreased / the ICC increased, the choice of statistical method became more important. Somewhat surprisingly cluster-level analyses performed similarly as individual-level analyses, even for scenario 2 which only included 4 clusters per intervention arm. Under this scenario, the Wilcoxon test had good size and power properties, but can not provide us with an estimate of the treatment effect. Logistic and Poisson regression and GEE showed good power, but this was the consequence of liberal size properties. GLMM and quasibinomial and quasipoisson regression suffered from low power and biased estimates. Finally, while the t-test had low power when there were few clusters, its size properties were adequate and its estimates showed relatively little bias. In practice however, the dengue study would likely include many more clusters, for which the t-test still showed reasonable power. The t-test had the additional advantages that it is simple to perform, well understood and that its estimate is expressed in terms of a risk difference, which is more easily interpreted than an odds ratio. For all of these reasons, the t-test seems an appropriate method for evaluating the intervention effect of an antiviral prophylactic against dengue in a ring trial design. Since the dengue study was assumed to be a randomized trial, the study clusters were expected to be balanced in terms of their covariables. In this case, data analysis does not require adjustment for additional variables and a cluster-level analysis would suffice for effect estimation. If later studies decide it is necessary to adjust for individual data, one would have to weigh the disadvantages of GEE (oversized) against those of GLMM (more prone to bias). For a small number of clusters neither method seemed appropriate. Choosing between the two may depend on the main goal of the analysis (effect estimation versus testing), but nevertheless it should be

48 32 stressed that both methods are likely to give unreliable results. Especially when the observed ICC is large both methods can only give an indication of the prophylaxis effect. As the number of clusters increases, the size properties of GEE improved and both methods return less biased estimates, which corresponds well with the results from Bellamy et al. (2000) [52]. Nonetheless, it remains advisable to investigate the properties of both methods for the specific study setting. During this first part of the thesis, the t-test was selected the evaluation of an antiviral prophylactic against dengue in a ring trial design. Besides using an appropriate analysis method, it is important to compare the cost-efficiency of different designs, which will be done in the next phase.

49 4 Phase 2 Determining the optimal sample size The cost-efficiency of a CRT depends on the number of clusters, the cluster size and the cost ratio, i.e. how much does it cost to initialize a cluster compared to the cost of enrolling a new subject in an existing cluster. For a ring trial the cost-efficiency will also depend on the clustering pattern of dengue. When recruiting close to the index case, the potential loss in power from having smaller clusters might be compensated by the gain in power from recruiting participants with a higher risk of dengue. Therefore, during the second phase of this thesis, the cost-efficiency was compared of recruiting strategies using different radiuses around the index case and assuming a range of possible cost ratios. 4.1 Simulation set-up ICC For sample size and cost calculations the range of ICC values from phase 1 was narrowed down. One ICC value was selected based on the literature [68,69], and sensitivity analyses were performed for a lower and higher estimate. For determining the ICC, more weight was given to studies with a larger number of clusters by calculating a weighted average with weights equal to Ks /K, where K s is the number of clusters in study s and K is the number of clusters summed over all studies. Based on Arostegui et. al. (2008) [68] and Andersson et. al. (2015) [69]

50 34 this approach led to an ICC estimate of for serological evidence of dengue in medium sized communities. Note that the ICC reported by these studies was based only on the control clusters, and thus only these clusters were taken into account when weighing. Despite the similar set-up and endpoint of Arostegui et. al. (2008) and Andersson et. al. (2015), there is a large discrepancy in their reported ICC values (resp and 0.031). While several other studies have evaluated the spatial clustering pattern of dengue using a ring design, none of them reported the ICC or related measures [19, 66, 67, 70 72]. When expanding the search for ICC estimates to studies investigating the incidence of other infectious diseases, only a few additional studies were found [73 75], with values ranging from to Based on these studies the ICC was re-estimated as an informal check for the robustness of the original estimate. Weighing the non-dengue studies by Ks 2 /K instead of Ks /K and using only the largest ICC when a study investigated multiple infectious diseases, an estimate of was obtained. While this method might provide some idea of robustness when little information is available, it is not recommended to base ICC estimates on studies with a different endpoint or setting. However if other clustered studies investigating infectious diseases had consistently reported larger ICC values, it might have been advisable to use a more conservative estimate. Since this was not the case here, the original estimate of was not adjusted. For sensitivity analyses an ICC of and were selected. By using a weighted average based on the number of clusters we assume that studies with more clusters can estimate the between-cluster variability more reliably. However, Eldridge (2001) [76] and Hayes (2009) [45] have indicated that studies with a different number of clusters and cluster size might also have inherently different ICCs. In practice, finding reliable information about this association is infeasible and proposed methods for sample size calculations are therefore (almost) always based on a constant ICC [49, 77, 78] Cluster size Five cluster sizes were selected assuming recruitment of participants in a radius of 20, 40, 60, 80 or 100 m around the index case. The average number of participants for each cluster size was estimated to be respectively 2.0, 7.9, 17.7, 31.5 and 49.2 adults per cluster, assuming an 80 % participation rate [66, 67]. Baseline incidences were estimated for each radius as described in section 3.2.2, leading to estimates of respectively 21.6, 15.7, 12.3, 9.0 and 8.0 % Cost ratio Despite the upcoming use of clustered studies and the general agreement that the most efficient design depends on the cost per person and the cost per cluster, no cost estimates for CRT were found. A limited number of papers has investigated how the cost ratio affects the efficiency of a CRT design, using values ranging from 2 to 100 [49 51, 79]. Moerbeek (2005) [51] and

51 35 Raudenbush & Liu (2000) [50] did not report the reasoning behind their cost-ratios. The US Demographic and Health Surveys Program (2006) [79] reported eight cost ratios from past observational survey-based studies, although they did not refer to the actual studies. These cost ratios ranged from 10 to 52, although their relevance to clinical trials is unclear. Van Breukelen & Candel (2012) [49] used cost ratios based on the only publication stating costs that we know of which reported a cost ratio of 26. As there was very little information to base the selection of cost ratios on, a range of estimates was selected for further investigation, in which cluster initialization costs 5, 10, 20 or 40 times more than enrolling a subject in an existing cluster. To be able to estimate the cost of a proposed design given the cost ratio, one still needs to determine the cost per person or cost per cluster. PhRMA reported that the average estimated cost per person for infectious disease trials in the US was $16,500 [80] in However, this number includes overhead costs which would be associated with cluster initialization in a CRT design. Additionally, the cost per person is expected to be up to 70 % lower in East and South- East Asia [81, 82]. Therefore the cost per person was estimated to be $7000. Based on the selected cost ratios, the cost of cluster initialization is then resp. $35,000, $70,000, $140,000 or $280, Sample size estimation Data was generated under the assumption of a RR = 0.25, a given initial value for the number of clusters and other input variables as described in the previous sections. The data generating procedure was similar as the one described in section 3.1, except for the design based on a 20 m radius, for which cluster sizes were truncated at a minimum of one and a maximum of three participants. Each data set was analysed using an unweighted two-sample t-test. After 5000 random samples the power was estimated as the proportion of simulations which rejected the null hypothesis of no intervention effect. If the power was below 0.80 a new simulation of 5000 random samples was run using one extra cluster per intervention arm. Once the power was greater than or equal to 0.80 four more simulations of 5000 random samples were run, each one using one extra cluster per intervention arm, and the results from the final 10 runs were saved. This algorithm is graphically depicted in figure 4.1. Given the cluster size and number of clusters needed to obtain a minimum power of 0.8, the total sample size and cost of the study can easily be calculated using the formulas: N = k=k k=1 where N is the total sample size, K the total number of clusters and m k the number of participants in the k th cluster; and m k

52 36 Figure 4.1: Algorithm used to determine the number of clusters needed to obtain the desired power level. B = k=k k=1 c + pm k where B is the required budget, c the cost per cluster and p the cost per participant. Finally, for the most cost-efficient design(s) with sufficient power, a simulation will be run similar to the ones performed in phase 1 to evaluate the effect of the ICC on the power of the selected designs. 4.3 Results and discussion No random samples had to be modified or disregarded. The association between study power and the number of clusters or the sample size for a RR equal to 0.25 and an ICC equal to is shown in figure 4.2 and 4.3 for a variety of designs.

53 37 Figure 4.2: Simulated power based on 5000 random generated samples of different study designs using a range of different radiuses around the index case. The red line indicates the 0.80 power mark. In a conventional CRT, one would expect that a study with more participants per cluster requires fewer clusters, especially when the ICC is small. However, because of the ring design, dengue incidence is higher in smaller clusters. In this case, the increase in power by sampling only a few people around each index case has sometimes outweighed the increase in power by sampling more participants per cluster. Consequently, the expected association between cluster size and number of clusters is not as strong, and with the exception of the 20 m radius, all the different designs require a similar number of clusters to obtain a power of 0.80 (ranging from 17 to 20). Thus, when evaluating a dengue antiviral prophylaxis, smaller clusters with a higher risk of infection can contribute a similar amount of information as large clusters with a lower risk. While the design with a 60 m radius requires the least amount of clusters and the design with a 20 m radius requires the smallest sample size, neither of them may be the most efficient in terms of budget. A level plot of the estimated cost in million dollars for an ICC equal to (figure 4.4) shows that the cost efficiency of the study design seems optimal for a 40 m radius over the entire range of cost ratios. However, at the largest investigated cost ratio, the 40 and 60 m design are almost equivalent. As the ICC decreases / increases, participants from the same cluster contribute relatively more / less information. Thus, for a lower ICC (0.031) the required number of clusters and sample size became smaller, especially for designs with a large cluster size. In contrast, for a higher ICC (0.124) the required number of clusters and sample size increased. Subsequently, a lower / higher ICC led to less / more expensive studies, with less / more variation between the cost of different designs (figures in Appendix C). Assuming an ICC = and a high cost ratio, a design with a 60 m radius became slightly more cost efficient than one with a 40 m radius (resp.

54 38 Figure 4.3: Simulated power based on 5000 random generated samples of different study designs using a range of different radiuses around the index case. The red line indicates the 0.80 power mark instead of 11.9 million dollars). However, for all other combinations of ICC and cost ratio, a 40 m radius was more advantageous. These results clearly favour the use of a ring design for evaluating a dengue antiviral prophylaxis. When choosing the appropriate cluster size, smaller clusters with recruitment closer to the index case can lead to more cost efficient designs over a range of ICCs and cost ratios. This simulation suggests that a design recruiting participants in a 40 m radius from the index case (mean cluster size = 7.9) is recommended. Assuming an ICC of 0.062, 20 clusters per intervention arm is estimated to be sufficient for obtaining a power A second power simulation for this design is shown in figure 4.5 and indicated that this number of clusters is expected to provide a power 0.80 for ICC values up to approximately Assuming a fixed design, the optimal number of clusters and cluster size has been determined for an ICC equal to In the third and final part of this thesis the (dis)advantages of a fixed versus a dynamic design will be discussed, and possibilities for sample size re-estimation will be explored.

55 39 Figure 4.4: Estimated cost in million dollars of different study designs. Plot points indicate values for which simulations were run. Figure 4.5: Dependence of the estimated power on the ICC and the number of clusters for a study design recruiting participants within a 40 m radius from the index case. The plot labels indicate the number of clusters per intervention arm.

56 40

57 5 Phase 3 Sample size re-estimation Sample size approximations strongly depend on the ICC and baseline incidence of dengue, as was demonstrated in the second phase of this thesis. Because of the difficulty in obtaining reliable estimates for these nuisance parameters, a natural approach would be to undertake an internal pilot study and re-estimate the sample size as described in section 1.7. During the third and final phase of this thesis, the effect of sample size re-estimation on the type I error, power and final sample size will be investigated under different scenarios. 5.1 Simulation set-up The effect of sample size re-estimation on the type I error, power and sample size were investigated for three different scenarios: Scenario 1 - the initial design was overpowered: the true underlying ICC and baseline incidence are and % (respectively 50 and 150 % of the original estimates). Scenario 2 - the initial design was powered correctly: the true underlying ICC and baseline incidence are and %. Scenario 3 - the initial design was underpowered: the true underlying ICC and baseline incidence are and % (respectively 200 and 50 % of the original estimates).

58 Sample size re-estimation Sample size re-estimation was performed after accrual of 14 clusters in each intervention arm (66 % of the required number of clusters according to the fixed design). Data was generated as described in section 3.1 assuming a mean cluster size equal to 7.9. The unblinded baseline incidence, effect size and p-value according to a t-test were determined for informative purposes, as these unblinded estimates were not used for sample size re-estimation. Instead, the ICC and baseline incidence were estimated based on blinded data. The ICC was calculated using the ANOVA estimator, as described in section 1.6. Since both the previous literature and our own small simulation study had indicated that ICC estimation based on a limited number of clusters led to highly variable estimates with both excessively small and large values [48, 56] (results in Appendix A), the interim estimate of the ICC was truncated at 0.01 and 0.18, which was deemed a realistic range [68, 69]. The baseline incidence was calculated under the assumption of a RR equal to 0.25 by multiplying the mean cluster-specific incidence by 1.6. The required sample size was then determined as described in section 4.2 based on 750 random generated datasets and assuming a RR equal to 0.25 and nuisance parameters equal to the blinded estimates. Additionally, a limit of 100 clusters per intervention arm was set during sample size re-estimation to prevent the algorithm from looping indefinitely. Next, if the initial 14 clusters were already expected to give sufficient power (> 0.80) no additional clusters were sampled. If the required number of clusters was higher, additional clusters were sampled similarly as described in section 3.1, but without modifying the dataset. Finally, a two-sample t-test was performed and its output saved. The type I error (based on 2000 random samples) or power (based on 1000 random samples) was estimated as the proportion of simulations which rejected the null hypothesis of no prophylaxis effect when the true RR equalled 1.00 or 0.25 respectively. This algorithm is graphically depicted in figure 5.1. Unfortunately, because of the computer-intensiveness of this algorithm only a limited amount of simulation runs could be performed. The results of this phase will therefore only serve as an initial indication of how sample size re-estimation affects the type I error and power. 5.3 Results and discussion The type I error for an internal pilot design remained close to the nominal value for all scenarios, although some inflation was observed for scenarios 1 and 3 (table 5.1). While for scenario 1 this inflation corresponded with a power much larger than the desired level of 0.80, this was not the case for scenario 3. On the other hand, for scenario 2 the estimated power was above the desired level, even though no type I error inflation had been observed. Further exploration of the estimated nuisance parameters at the interim point and the final sample size might explain the different effect of sample size re-estimation for each scenario.

59 43 Figure 5.1: Algorithm used to evaluate the effect of sample size re-estimation based on nuisance parameters on the type I error, power and final sample size. Scenario (number of modifications per 2000 / 1000 samples) Type I error Power Scenario 1: initial design was overpowered (0 / 3) Scenario 2: initial design was powered correctly (0 / 23) Scenario 3: initial design was underpowered (13 / 236) Table 5.1: Effect of sample size re-estimation on the type I error and power for three different scenarios. The number of modifications is given for the type I error simulation (based on 2000 random samples) and for the power simulation (based on 1000 random samples)

60 44 Figure 5.2: The dotted line indicates the true unblinded baseline incidence. The blinded baseline incidence was overestimated at a RR equal to 1.00, but estimated accurately at a RR equal to 0.25 (figure 5.2). This was expected, since the method of estimation applied a correction for the prophylaxis effect on the overall incidence assuming a RR equal to The blinded ICC estimate showed negative bias at a RR equal to one, with estimates showing more bias as the true underlying ICC increased (figure 5.3). For a RR equal to 0.25 the ICC was overestimated for scenarios 1 and 2. This was expected because the variation between clusters due to the prophylaxis effect could not be taken into account during blinded estimation. Notable was that for the third scenario there was substantial negative bias both under a RR equal to 1.00 and This was in contrast with a simulation study by Wu et al. (2012), which showed that the ANOVA estimator of the ICC often suffered from negative bias, but that this was not associated with the value of the true underlying ICC. The last scenario had both a higher ICC and a lower baseline incidence. Subsequently, the absolute risk difference between the placebo and prophylaxis clusters was also smaller. Possibly in this case, the difference between clusters due to the prophylaxis effect seemed relatively small compared to the naturally occurring cluster differences, which could lead to the blinded ICC still being underestimated at a RR equal to However, this did not explain the association between the negative bias and the true underlying value of the ICC. It is likely that this association was related to the the baseline incidence of each scenario. Evaluation of the ICC assumptions imposed by the data generating mechanism showed that data generation under a low incidence led to ICC estimates that were too low (Appendix A). The large number of data modifications for the power simulation under scenario 3 might also have played a role, although these did not seem to affect the quality of estimation for the baseline incidence. The final number of clusters in each scenario was lower for a RR equal to 1.00 compared to a RR equal to 0.25 (figure 5.4). At a RR equal to 1.00, the number of random samples for which more than 14 clusters had to be sampled was 0.05, and % and the number of samples for

61 45 Figure 5.3: Blinded ICC estimated at interim point. The dotted line indicates the true unblinded ICC for the control group. which the required sample size was larger than the limit of 100 clusters per intervention arm was 0.00, 0.00 and 0.15 %. At RR equal to 0.25 these numbers were respectively 47.3, 84.3, % and 0.0, 0.0, 2.1 %. Those random samples responsible for type I errors had a larger median effect size and unblinded baseline incidence, and a lower median blinded ICC estimate at the interim point. This explained why these samples led to significant results. However, the median blinded baseline incidence at the interim point, on which sample size re-estimation was based, differed only very little from the median based on all random samples, with the largest difference occurring under scenario 2 (resp and 0.250). This might have indicated that the blinded ICC played Figure 5.4: Re-estimated total number of clusters. The red dotted line indicates the required number of cluster to obtain > 0.80 power in a fixed design. For scenario 1, this number equalled 12, which falls below of the plotted range.

62 46 a more important role during sample size re-estimation and its effect on type I error inflation than the blinded baseline incidence. The blinded ICC estimate at interim was indeed positively correlated with the standard error during the final analysis, meaning that those random samples who by chance have a low blinded ICC estimate at the interim point were more likely to falsely reject the null hypothesis. While this might have explained the reason behind type I errors, we were not able to distinguish why the type I error inflated slightly under scenarios 1 and 3, but not under scenario 2. There was no clear association between the type I error rate and any of the saved output variables. One possible explanation is simply that the effect of the blinded estimated ICC and baseline incidence differs between scenarios. Scenario 1 had the highest true underlying baseline incidence, and subsequently the absolute bias of the blinded baseline incidence under a RR equal to 1.00 was also much higher. In fact, it was so high that, with one exception, no further recruitment was done for any of the random samples. This was in contrast with scenarios 2 and 3, for which respectively 398 (19.9 %) and 1977 (98.9 %) of the random samples required additional recruitment of clusters. CRTs with a small number of clusters are often more prone to inflation of the type I error [52, 56]. The so-called unrestricted re-estimation design which was applied here, where the final sample size is allowed to be both smaller and larger than the originally planned design, might therefore be more sensitive to type I errors. A simulation study by by Lake et al. (2002) [55] on different re-estimation designs for CRTs seemed to confirm this. Under scenario 3, the blinded ICC estimate showed a large negative bias. As a consequence, random samples at the interim point often seemed more powered than they actually were. Less additional clusters were then recruited, which otherwise might have provided more information leading to more accurate estimates of the ICC. While this process might give rise to type I error for all the investigated scenarios, its effect was seemingly magnified for scenario 3 because of the large negative bias during blinded ICC estimation. Scenario 1 was overpowered because of the type I error inflation, and because the number of clusters at the interim point was already too large for obtaining the desired power level: when estimating the sample size under this scenario for a fixed design, the required number of clusters per intervention arm was only 12. While scenario 3 also suffered from some type I error inflation, the mean power was much closer to the nominal level. In this case the required number of clusters was larger than the maximum limit for some of the random samples. Furthermore, the large negative bias of the blinded ICC might have led to a larger proportion of underpowered studies. Indeed, when comparing the distribution of final samples sizes with the required sample size for a fixed design (49), approximately 60 % of the studies were underpowered. Finally, scenario 2 was overpowered despite not showing type I error inflation. Figures 5.2 and 5.3 indicated that while the blinded baseline incidence is quite reliable, the blinded ICC estimate is overestimated, leading to recruitment of more clusters than necessary. According to phase

63 47 2, under scenario 2 only 20 clusters per intervention arm were needed to obtain > 0.80 power. While the median cluster size after sample size re-estimation was 21, 27 % of the simulated studies were overpowered according to the conventional design, in comparison to only 19 % being underpowered. Overall blinded sample size re-estimation performs well. While there was some inflation of the type I error, empirical levels remained close to the nominal value and studies generally were sufficiently powered to detect the anticipated prophylaxis effect. Our results were similar to those described for unblinded sample size re-estimation by Lake et al. (2002) and Schie et al. (2014), except our studies were more often overpowered as a consequence of biases introduced by using blinded estimates. The internal pilot design was expected to allow for substantial gains in power when the original sample size was underestimated due to poor estimation of the ICC or baseline incidence. However, because of the limited number of simulations, further research is needed to evaluate the effect of blinded sample size re-estimation on the type I error and power. The effect of blinded re-estimation seemed to depend on the combined effect of biases in the blinded estimates for the baseline incidences and ICC. These results indicated that this combined effect might depend on the specific variables of the study setting. Settings with a larger ICC suffered from larger negative bias which made the interim sample seem more powered, leading to re-estimation designs that were more prone to type I errors. Large baseline incidences could have led to blinded incidences that are too large at the interim point when the prophylaxis effect was smaller than expected, making the interim sample seem more powered than it actually was and leading to underpowered studies. Unintentionally, the settings studies in this thesis are such that large ICC and large baseline incidence never coincided, but it would be interesting to further investigate the separate effects of ICC and baseline incidence on sample size re-estimation. Possibly there were settings for which the effect of sample size re-estimation on size and power is much more severe, for example in a setting with a high ICC and high baseline incidence. Furthermore, investigating different settings might give more insight into the extent to which data modifications affect the results. Alternatively, it might be preferred to use unblinded estimation, which would have allowed for more accurate determination of the ICC and baseline incidence. This might have prevented the effect of sample size re-estimation from depending on the specific combination of nuisance parameters. When unblinding the data, one could also consider possibilities for interim analysis, which requires a more stringent control of the type I error [83]. Other aspects might still be investigated in the future, such as the use of restricted designs, where the number of clusters is allowed to increase but not decrease. According to Lake et al. (2002) [55] restricted designs were more likely to be overpowered, but protected better against type I error inflation. Another interesting aspect would be the optimal timing of the pilot study, which might depend on the set-up of the study. For individual-randomized studies or CRTs with

64 48 a large number of clusters, as little as 25 % of the data may be considered sufficient to estimate nuisance parameters [55]. In case of the dengue study, this timing would likely be undesirable: only 5 clusters per intervention would have been recruited, likely leading to severe bias of the ICC and subsequently also to more severe effect on the size and power of different designs. Indeed, Schie et al. (2014) [56] found the timing of the interim point to be more important when investigating the effect of sample size re-estimation for scenarios with few clusters. Here earlier sample size re-estimation led to more imprecise estimates of the variance components and more underpowered studies. During sample size re-estimation a maximum limit was set on the number of clusters per intervention arm equal to 100. In practice, when the required sample size is only expected to be 20 clusters per intervention arm, the catch-area for index cases might not be large enough to allow for the recruitment of so many clusters. In this case, the trial may need to be prolonged to recruit clusters from the following dengue season. However, dengue incidence is known to vary between years and subsequently the ICC might vary as well. Interim estimates of nuisance parameters from one year might therefore not translate well to the next year, leading to uncertainty about how many additional clusters should be recruited. It would be advisable to take into account the possible increases in sample size when deciding on the catch-area. Finally, future studies might also evaluate the effect of re-estimating other nuisance parameters (e.g. the mean and variance of the cluster size), internal pilot designs in which both the sample size and the cluster size are allowed to change (e.g. if the ICC is much lower than expected it might be more efficient to sample larger clusters), etc.

65 6 Conclusion This thesis was the first to investigate the concept of a ring trial and the use blinded sample size re-estimation in the context of a dengue prophylaxis. Comparison of several methods for analysing correlated data suggested that cluster-level analysis often performed equivalently to individual-level analysis. The simple two-sample t-test was selected as the analysis method of choice because of its good statistical properties and its convenient use. Next, the comparison of multiple designs using different radiuses around the index case clearly indicated the benefits of using a ring design. For most designs, the loss in power due to sampling less participants per cluster was compensated by sampling from a population at a higher risk of dengue, leading to similar requirements for the number of clusters to obtain the desired power level. After accounting for the cost ratio, the design recruiting participants within a 40 m radius (20 clusters per intervention arm, mean cluster size of 7.9 participants) was selected as the most cost efficient design. Finally, blinded sample size re-estimation showed some potential for correctly adjusting the sample size when the initial nuisance parameters were estimated incorrectly. However, results indicated that for different settings than the ones investigated here, more severe type I error inflation might occur. Overall these results have demonstrated the potential benefits of implementing a ring design, albeit in an exploratory setting. Therefore further research remains necessary both with regard to the use of ring designs in general and the implementation of sample size re-estimation methods. Nonetheless, future trials investigating dengue, or other communicable diseases for which similar clustering pattern might be expected, should consider the use of a ring design in order to improve the statistical and cost efficiency of the trial.

66 50

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73 Appendices

74

75 List of Figures and Tables in Appendices A.1 Cumulative distribution of the estimated ICC (ICC = 0.031) A.2 Cumulative distribution of the estimated ICC (ICC = 0.062) A.3 Cumulative distribution of the estimated ICC (ICC = 0.124) B.1 Modified number of random samples (phase 1) B.2 Power under scenario 1 (RR = 0.25.) B.3 Median relative bias of the prophylaxis effect under scenario 1 (RR = 0.25) B.4 Power under scenario 1 (RR = 0.50.) B.5 Median relative bias of the prophylaxis effect under scenario 1 (RR = 0.50) B.6 Power under scenario 1 (RR = 0.75.) B.7 Median relative bias of the prophylaxis effect under scenario 1 (RR = 0.75) B.8 Size properties under scenario 1 (RR = 1.00) B.9 Median relative bias of the prophylaxis effect under scenario 1 (RR = 1.00) B.10 Power under scenario 2 (RR = 0.25.) B.11 Median relative bias of the prophylaxis effect under scenario 2 (RR = 0.25) B.12 Power under scenario 2 (RR = 0.50.) B.13 Median relative bias of the prophylaxis effect under scenario 2 (RR = 0.50) B.14 Power under scenario 2 (RR = 0.75.) B.15 Median relative bias of the prophylaxis effect under scenario 2 (RR = 0.75) B.16 Size properties under scenario 2 (RR = 1.00) B.17 Median relative bias of the prophylaxis effect under scenario 2 (RR = 1.00) B.18 Power under scenario 3 (RR = 0.25.) B.19 Median relative bias of the prophylaxis effect under scenario 3 (RR = 0.25) B.20 Power under scenario 3 (RR = 0.50.) B.21 Median relative bias of the prophylaxis effect under scenario 3 (RR = 0.50) B.22 Power under scenario 3 (RR = 0.75.) B.23 Median relative bias of the prophylaxis effect under scenario 3 (RR = 0.75) B.24 Size properties under scenario 3 (RR = 1.00) B.25 Median relative bias of the prophylaxis effect under scenario 3 (RR = 1.00) C.1 Estimated power for different study designs (ICC = 0.031) C.2 Estimated power for different study designs (ICC = 0.031)

76 60 C.3 Estimated cost in million dollars for different study designs (ICC = 0.031) C.4 Estimated power for different study designs (ICC = 0.124) C.5 Estimated power for different study designs (ICC = 0.124) C.6 Estimated cost in million dollars for different study designs (ICC = 0.124) C.7 Modified number of random samples (phase 2) C.8 Power of a 40 m ring design RR = 0.25.) C.9 Median relative bias of the prophylaxis effect of a 40 m ring design (RR = 0.25). 81 C.10 Power of a 40 m ring design (RR = 0.50.) C.11 Median relative bias of the prophylaxis effect of a 40 m ring design (RR = 0.50). 82 C.12 Power of a 40 m ring design (RR = 0.75.) C.13 Median relative bias of the prophylaxis effect of a 40 m ring design (RR = 0.75). 83 C.14 Size properties of a 40 m ring design (RR = 1.00) C.15 Median relative bias of the prophylaxis effect of a 40 m ring design (RR = 1.00). 84

77 A ICC Assumptions Figure A.1: Cumulative distribution of the estimated ICC based on 2000 random generated samples. The ICC was estimated using the ANOVA estimator. The vertical dotted line indicates the true underlying ICC value. The horizontal dotted line indicates the median.

78 62 Figure A.2: Cumulative distribution of the estimated ICC based on 2000 random generated samples. The ICC was estimated using the ANOVA estimator. The vertical dotted line indicates the true underlying ICC value. The horizontal dotted line indicates the median. Figure A.3: Cumulative distribution of the estimated ICC based on 2000 random generated samples. The ICC was estimated using the ANOVA estimator. The vertical dotted line indicates the true underlying ICC value. The horizontal dotted line indicates the median.

79 B Phase 1 Tables and Figures Figure B.1: Modified number of random samples for each setting under each scenario (per 5000 generated samples).