optimizing the design of a ring-prophylaxis study to prevent dengue … · 2016. 12. 9. · 1...

Faculty of Sciences

In collaboration with Janssen PharmaceuticalCompanies of Johnson & Johnson

Optimizing the Design of a Ring-ProphylaxisStudy to Prevent Dengue Infection

Nina Dhollander

Master dissertation submitted toobtain the degree of

Master of Statistical Data Analysis

Promotor: Dr. An VandeboschCo-promotor: Dr. Joris Menten

Academic year 2015 - 2016

The author and the promoter give permission to consult this master dissertation and to copy itor parts of it for personal use. Each other use falls under the restrictions of the copyright, inparticular concerning the obligation to mention explicitly the source when using results of thismaster dissertation.

Nina DhollanderMonday 5th September, 2016

Foreword

To my knowledge, this Master Thesis is the first to investigate the use of a ring design in thecontext of developing a chemoprophylaxis against dengue. All programming code and resultswere 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 itsevaluation and may not be disclosed to any third parties without explicit written permission byJanssen.

It would not have been possible to write this Master Thesis without the help and support ofthe people around me. First of all, I would like to thank Dr. An Vandebosch and Dr. JorisMenten for the opportunity to do my Master Thesis at Janssen, for providing such an interestingresearch topic and for their guidance throughout all stages of this thesis. In addition, I have tothank Cristina Sotto for her critical reading and helpful remarks. Finally, I would like to thankmy friends and family for their support.

Table of Contents

1 Introduction 11.1 What is dengue? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1

1.2 Dengue transmission . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 2

1.3 Epidemiology of dengue . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 2

1.4 Treatment and prevention . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 4

1.5 Clinical development of a chemoprophylactic agent for dengue . . . . . . . . . 6

1.6 Cluster randomised trials . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 9

1.7 Sample size re-estimation . . . . . . . . . . . . . . . . . . . . . . . . . . . . 11

1.8 Research questions and objectives . . . . . . . . . . . . . . . . . . . . . . . . 12

2 Methods 132.1 Cluster-level analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 13

2.2 Individual-level analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 16

3 Phase 1Determining the best statistical method 193.1 Data generation . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 19

3.2 Simulation set-up . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 22

3.3 Size and power estimation . . . . . . . . . . . . . . . . . . . . . . . . . . . . 24

3.4 Results and discussion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 24

4 Phase 2Determining the optimal sample size 334.1 Simulation set-up . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 33

4.2 Sample size estimation . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 35


5 Phase 3Sample size re-estimation 415.1 Simulation set-up . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 41

5.2 Sample size re-estimation . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 42


6 Conclusion 49

References 50

A ICC Assumptions 61

B Phase 1 Tables and Figures 63

C Phase 2 Tables and Figures 77

Abstract

According to the World Health Organization, dengue currently is one of the most importantmosquito-borne viral diseases in the world. Nonetheless there remains an unmet need for effec-tive preventive measures. The development of a dengue chemoprophylaxis would greatly aidthe battle against dengue. The aim of this Master Thesis is therefore to explore design possibil-ities 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 diagnoseddengue cases. Rings are then randomised to either placebo or prophylaxis. Because participantsare recruited from a high risk population, incident dengue rates are expected to be higher thanin 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 designshould 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 meth-ods (t-test, Wilcoxon test, logistic and Poisson regression with sandwich estimator or based onthe quasi-likelihood approach, logistic GEE with an exchangeable correlation structure, logisticGLMM with a random intercept) were compared. The simple two-sample t-test seemed mostrobust 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 epidemio-logical 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 samplesize re-estimation based on nuisance parameters were investigated. The dynamic design greatlyimproved the power of the study when the initial nuisance parameters estimates had been in-correct, with only minimal inflation of the type I error. However, the results suggested that forspecific combinations of nuisance parameters, different than the ones investigated here, moresevere type I error inflation might occur. Thus, while more extensive research remains necessaryfor the use of ring trials and the use of blinded sample size re-estimation and its alternatives, theresults from this thesis strongly favour their implementation in future studies evaluating dengue(chemo)prophylaxis.

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

List of Figures

1.1 Course of dengue infection. . . . . . . . . . . . . . . . . . . . . . . . . . . . . 21.2 Transmission of the dengue virus. . . . . . . . . . . . . . . . . . . . . . . . . 31.3 Distribution of the global dengue risk. . . . . . . . . . . . . . . . . . . . . . . 31.4 The biopharmaceutical research and development process. . . . . . . . . . . . 61.5 Schematic representation of the design of a ring prophylaxis trial. . . . . . . . 8

3.1 Association between the distance of the participant’s house to the house of theindex case and different measures for dengue incidence or prevalence. . . . . . 24

3.2 Algorithm used to estimate the size, power and bias of different statistical meth-ods in a ring trial design. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 25

3.3 Size properties of various statistical methods under different scenarios. . . . . . 273.4 Size properties of various statistical methods under different scenarios. . . . . . 283.5 Power of various statistical methods under different scenarios. . . . . . . . . . 283.6 Power of various statistical methods under different scenarios. . . . . . . . . . 293.7 Median relative bias of the prophylaxis effect for various statistical methods

under different scenarios. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 30

4.1 Algorithm used to determine the number of clusters needed to obtain the desiredpower level. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 36

4.2 Estimated power for different study designs. . . . . . . . . . . . . . . . . . . . 374.3 Estimated power for different study designs. . . . . . . . . . . . . . . . . . . . 384.4 Estimated cost in million dollars for different study designs. . . . . . . . . . . 394.5 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. 39

5.1 Algorithm used to evaluate the effect of sample size re-estimation based onnuisance parameters on the type I error, power and final sample size. . . . . . . 43

5.2 Blinded baseline incidence estimate at interim point. . . . . . . . . . . . . . . 445.3 Blinded ICC estimate at interim point. . . . . . . . . . . . . . . . . . . . . . . 455.4 Re-estimated total number of clusters. . . . . . . . . . . . . . . . . . . . . . . 45

List of Tables

3.1 Comparison of the observed and simulated outcomes for various studies. . . . . 213.2 Short description of the studies used for estimation of the baseline incidence. . 23

5.1 Effect of sample size re-estimation on the type I error and power for three dif-ferent scenarios. The number of modifications is given for the type I error sim-ulation (based on 2000 random samples) and for the power simulation (basedon 1000 random samples) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 43

1Introduction

Dengue ranks as one of the most important mosquito-borne viral diseases in the world accordingto the World Health Organization (WHO), with almost half of the world population being atrisk of disease. Development of a dengue-specific antiviral (chemo)prophylaxis would aid inthe prevention and treatment of dengue, which is currently still mostly limited to vector controland 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 ofwhich 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 areRNA viruses belonging to the Flavivirus genus/Flaviviridae family, which also includes otherwell-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 of4-6 days, infection with any of the DENV serotypes may remain asymptomatic or result in aspectrum 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 decreasedresistance of blood vessel walls leading to bruising, and fluid accumulation in the chest or

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abdomen. In addition, DSS is also characterized by hypovolemic shock, during which severeblood and fluid loss makes the heart unable to pump enough blood through the body, possiblyleading 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 par-ticular serotype, immunity against other DENV variants is only short-lived [7, 8]. Secondaryinfection with a different dengue serotype has consistently been associated with an increasedrisk of DHF/DSS, although DHF/DSS has also been observed with primary infections, indicat-ing 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 denguevectors (figure 1.2). As a highly domesticated mosquito with a high affinity for human bloodand high susceptibility to infection, Aedes aegypti is an extremely efficient vector, well-knownfor transmitting other diseases such as yellow fever and Zika [1, 4]. When a mosquito takes itsblood 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]. Transmissionby blood products [11] or vertical transmission during pregnancy [12, 13] can occur, althoughreported cases are rare.

1.3 Epidemiology of dengue

1.3.1 Global distribution

The distribution of dengue is related to the spread of its vector Aedes aegypti, which dwellsin tropical and subtropical regions all over the world, mainly in regions where the winter tem-perature does not drop below 10 ◦C (figure 1.3). The worldwide incidence of dengue has risen

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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 30-55 % of the world population (2.0-3.9billion people) being at risk of dengue [1, 16]. An estimated 50-390 million new infections oc-cur annually in more than 125 endemic countries, with a further spread to previously unaffectedareas [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. Thistrend is likely due to increases in long-distance travel, population growth and an increase in thesurveillance and reporting of dengue cases [1, 14, 17].

Figure 1.3: Distribution of the global dengue risk according to the WHO (2012) [1].

1.3.2 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 dependingon the temperature and rainfall. Furthermore, the transmission and occurrence of dengue canvary strongly between countries and between rural and urban areas. Stanaway et. al. (2016)

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[15] estimated the one-year incidence of symptomatic and asymptomatic dengue in 2013, withestimates ranging from less than 1 % for Central America to 3.4-3.7 % for regions such asSouth-east Asia and the Caribbean. However, one-year incidence rates of over 10 % have alsobeen reported [18]. Unfortunately, the number of asymptotic dengue cases often needs to beapproximated based on a limited amount of information, leading to additional uncertainty aboutthe incidence estimates.

The disease profile of dengue varies between regions and can depend on population character-istics such as age profile and previously circulating DENV serotypes. Symptomatic and severedengue tend to develop more readily in children and adolescents, who often have not yet devel-oped cross-reactive immunity against all serotypes [7,17]. When also considering asymptomaticdengue infection some studies still indicate a similar age trend [15], while others observe no dif-ference in the incidence between age groups [19, 20]. Overall this makes it difficult to providereliable and generalizable estimates of dengue incidence.

Travellers International travel to dengue-endemic regions has played a significant role in theglobal spread of dengue. Prospective studies of travellers have indicated an incidence rateof 10-30 cases per 1000 person-months [21–24]. As some of these studies were only ableto detect symptomatic dengue, the true incidence is likely to be higher. The population ofmosquito species that capable of spreading the dengue virus has been growing in many non-endemic countries, possibly leading to autochthonous cycles of infection established by infectedtravellers. Locally acquired dengue infections have been reported in Europe, the USA andAustralia [17, 24, 25].

1.4 Treatment and prevention

1.4.1 Treatment

With correct and timely intervention the management of DF is relatively simple, inexpensiveand effective. Supportive treatments such as intravenous fluid replacement can reduce diseaseseverity and almost eliminate mortality. In practice a correct diagnosis of DF often does not oc-cur until a few days after the onset of symptoms. Furthermore, there are no accurate biomarkersto predict which cases are likely to develop DHF or DSS. The development of a dengue-specificantiviral drug is likely to further aid the treatment of dengue. [1, 9].

1.4.2 Prevention

Current prevention measures Currently the reduction and prevention of dengue virus trans-mission is mostly limited to vector control and environmental management (e.g. insecticides, in-stallation of water supply systems). This strategy has been largely ineffective due to insufficient

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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 ofsymptomatic dengue infections, which are too late to have an impact and are neither sustainednor evaluated [1].

Vaccine development Ideally the prevention and control of dengue would consist of an inte-grated approach based on vaccination regimes and effective vector control strategies [1]. As ofDecember 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 inindividuals 9-45 years of age living in endemic areas. Early 2016, the first public vaccinationprogram started in the Philippines [27].

Pooled analysis of the Dengvaxia phase III clinical trials indicated that vaccine efficacy was ap-proximately 80% for dengue hospitalization and 90% for severe dengue in children and adoles-cents 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 hospi-talization and severe dengue were reported three years after vaccination. Other considerationswere its low vaccine efficacy against DENV-1 and 2 (resp. 54.7% and 43.0%) in comparisonto DENV-3 and 4 (resp. 71.6% and 76.9%) and its low vaccine efficacy in children who wereseronegative 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 offeringsufficient protection after the final dose [28–30]. Long-term follow-up for vaccine efficacy andsafety is still ongoing. Because of the association between secondary infections and diseaseseverity, immunity against all four serotypes needs to be long-lasting. A vaccine which onlyaffords short-lived protection for one or more serotypes could theoretically make populationsmore susceptible to severe dengue [8, 31].

While vaccination programs with Dengvaxia are expected to significantly reduce the diseaseburden of dengue in endemic areas, the use of Dengvaxia is limited. In addition the vaccinedoes 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 withregard to new prevention and treatment measures remains necessary.

Antiviral drugs as prophylaxis While a safe and effective DENV vaccine would be an ideallong-term solution, other strategies are needed to combat the current dengue problem. Antiviraldrugs can be given after a patient has already become symptomatic [32], and can in somecases also be used as a prophylaxis. In the case of a dengue this would provide an alternativeprevention measure to vaccination for young children or immunosuppressive patients, or whenthe vaccination schedule cannot be completed before arrival in an endemic country [33]. Theuse of antiviral drugs before onset of disease has been used as a prevention strategy before.

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For example, when individuals travel to an area where malaria is prevalent, they are advised totake malaria medication before, during and after travel to prevent infection. Examples of viraldiseases where prophylaxis has been used successfully are certain types of influenza [33] andHIV [34].

1.5 Clinical development of a chemoprophylactic agent fordengue

1.5.1 Introduction to drug discovery and development

The drug discovery and development process spans over multiple years, comprising of differentphases (figure 1.4). Drug discovery entails both the discovery of new potential drug candidatesthrough insights into disease processes or high-throughput screening of molecular compounds,and early testing with regard to potency, metabolic stability, bioavailability, etc. While theprocess of early research and development is relatively flexible, the course of preclinical inves-tigations is regulated much more strictly and typically comprises of in vitro and in vivo animalstudies evaluating a range of toxicological aspects. These studies provide indications with re-gard to the safety of a compound when given acutely or repeatedly over a period of time, andwhich organs and physiological systems might suffer from adverse effects. Typical examplesinclude 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 abasis 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 newdrug 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 tol-erability and to characterize the pharmacology of the drug compared to a placebo in healthy

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volunteers. Next, exploratory efficacy and tolerability are evaluated in a small number of pa-tients in phase IIa studies (proof-of-concept), followed by phase IIb studies to confirm efficacyand safety and to find the optimal dose range in the patient population. Thereafter, the desireddose of the drug is selected. Pivotal phase III studies are then conducted to demonstrate efficacyand safety of the selected dose in large patient population studies. While a placebo is sometimesused in phase II and phase III studies, comparison of the drug against standard care is often con-sidered to be more ethical. If the data suggest a favourable risk-benefit relationship, a new drugapproval application is filed, that allows the drug to be marketed if approved. Post-licensing orPhase IV studies are often required to further evaluate safety [35].

1.5.2 Clinical development of a prophylactic agent using a ring design

In reality, the development process is often tailored to the specific needs and requirements ofthe drug candidate, and development of a (chemo)prophylaxis will therefore differ slightly fromthe 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 theentire population at risk of disease. Therefore recruitment for phase II and III studies shouldtake place at the level of the population at risk. Consequently, prophylaxis studies usually re-quire large sample sizes, as the incidence rate in the population at risk tends to be lower thanthe recovery rate in patients, even in endemic areas. For example, while phase II and phase IIIstudies for therapeutic agents usually comprise of respectively a few hundred and a few thou-sand subjects [35], over 4000 subjects were recruited for the phase II proof-of-concept study forDengvaxia [37] and over 31 000 subjects were enrolled over three phase III studies for Deng-vaxia [29]. While vaccine studies only require a few treatment administrations and are thereforerelatively easy to conduct in large populations, the use of chemoprophylaxis necessitates sus-tained intake and thus evaluation requires more intensive monitoring.

The required sample size for a prophylaxis safety and efficacy trial is inversely proportionalto the disease incidence in the study population. Thus, performing trials in populations with ahigh risk of infection could reduce the sample size and/or the duration of follow-up requiredto conclude the study. Additionally, evaluation takes place in the population that stands tobenefit most from a safe and efficacious prophylaxis [31]. One recently proposed approach forfinding populations at high risk of disease is that of a ring trial or a ring study: a person newlydiagnosed with infection becomes an index case around whom an epidemiologically definedring is formed (e.g. based on social or geographical connections). Within this ring, individualswho 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 comparethe disease incidence between rings and to evaluate the prophylaxis efficacy [38]. A schematicrepresentation of the design of a ring prophylaxis trial for dengue is given in figure 1.5.

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

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Originally the concept of ring vaccination or ring prophylaxis was used as a targeted program-matic 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 thesurveillance-containment strategy that was central to the eradication of small pox throughoutAsia, Africa and Latin-America in the 1970s [39]. The use of ring prophylaxis has also beenindicated to slow down transmission of various types of influenza when used in semi-closed orclosed environments (e.g. schools, military compounds) [40–42]. Recently, however, the ringdesign was implemented for the first time in a cluster-randomised phase 3 trial which took placein Guinea. Its aim was to assess the safety and efficacy of the rVSV-ZEBOV candidate vaccinefor the prevention of Ebola virus disease. Interim analysis of the trial data successfully indicatedvaccine efficacy [43], demonstrating the use of ring study designs for the evaluation of vaccineor prophylaxis efficacy. The final results were expected to be published midway 2016, but werenot 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 hypotheticaldengue 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 withthe aim to evaluate efficacy of a dengue chemoprophylaxis when compared to a placebo. Effi-cacy is expressed as the proportion of participants with evidence of incident dengue infectionduring the follow-up period among adults who were seronegative at the start of chemoprophy-laxis / placebo intervention.

1.6 Cluster randomised trials

In CRTs clusters of individuals are randomized to interventions. General advantages of CRTsinclude preventing contamination between intervention groups and capturing the indirect effectsof prophylaxis. Since dengue is a communicable disease treating only some of the ring membersmight lower disease transmission and incidence in the entire ring. An individually randomizedtrial cannot take these effects into account [45, 46]. Additionally, a ring trial has the advantageof 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 anincreased 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) compensatedby 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 ratherthan independent. The variability in the data then consists of two components: the within-clusterand between-cluster variance. When these components are not taken into account properly, thevariability in the data is underestimated. Intuitively this makes sense: when two individualshave correlated outcomes, their data provides less information and thus less certainty than if

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their outcomes had been independent. As a consequence, the standard statistical methods willoverestimate the significance of the intervention effect and underestimate the required samplesize. In order to account for correlated data during the design and analysis of a study, a quantita-tive measure is needed which reflects the extent to which individuals from the same cluster arecorrelated, the most common one being the intraclass correlation coefficient (ICC) [45,47]. Sev-eral methods exist to estimate the ICC from binary data. Here the analysis of variance (ANOVA)estimator as described by Wu et al. 2012 [48] was used:

ICC =MSB −MSW

MSB + (na − 1)MSW

with

MSB =1

K − 1

(∑ Z2k

ni

− (∑Zk)2

N

)

MSW =1

N −K

(∑Zk −

∑ Z2k

nk

)

na =1

K − 1

(N −

∑n2k

N

)

where K equals the number of clusters, Zk the number of incident dengue cases in cluster k,nk the number of individuals in cluster k, and N the total number of individuals in the study.Here, na corresponds to the average cluster size and MSB and MSW correspond to the betweenand within cluster mean squares from a one-way ANOVA of the binary data [48]. The ICC willusually 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 varianceas a result from randomizing clusters instead of individuals. Since the variance is inverselyproportional to the required sample size, it can also be used as a straightforward method toapproximate the required sample size for CRTs:

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 becalculated based on the ICC as follows:

DE = 1 + (na − 1) ICC

with na being the mean cluster size. The DE increases with the ICC, but also with na. Subse-quently, increasing the number of clusters in a CRTs is more efficient than increasing the meancluster size with regard to statistical power [45, 46]. Note however that for CRTs there can be

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a large discrepancy between which design is most efficient in terms of power and in terms ofbudget, especially when the cost ratio, i.e. the cost of cluster initialization compared to the costof enrolling an extra subject in an already existing cluster, is high. In the design stage of a CRTboth the statistical and cost efficiency should be investigated for different combinations of thenumber of clusters and the cluster size [49–51].

A variety of approaches have been developed to take correlated data into account during anal-ysis. One of the simplest is the comparison of cluster specific summary measures between theprophylaxis and placebo group. In case of the dengue study, the summary measure of primaryinterest would likely be the proportion of participants in each cluster with evidence of inci-dent dengue infection as defined in section 1.5.2. By only considering one summary measurefor each cluster, the ICC is naturally accounted for since clusters are assumed to be indepen-dent [45, 52]. When implemented correctly, methods based on cluster-level summary measuresare usually robust under a wide range of circumstances [45]. A potential disadvantage of thismethod 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 largecluster sizes [52] or when there is substantial variation in the sample size per cluster [45]. Otherdisadvantages include the inability to adjust for possibly important individual-level covariates.

In contrast, individual-level regression methods do allow for the adjustment of individual-levelcovariates and can be more efficient since the data is not reduced to cluster-based summary mea-sures. However, they are not always reliable when the number of clusters is small. Accordingto Hayes & Moulton (2009) [45] the individual-level analysis methods that will be discussedin section 2.2 require at least 15 clusters per arm, while Murray et al. (2004) [53]) mentionsneeding at least 40 clusters in total. Especially when the ICC is high, parameter estimates canbecome biased, and significance tests and confidence intervals may not have the correct sizeand coverage [45, 52].

1.7 Sample size re-estimation

Despite the crucial role of the ICC in power and sample size calculations, there are oftenonly few reports available on its observed value in a similar study set-up. Moreover, ICCestimates can vary considerably between studies, even when they have a similar set-up andendpoint [45, 48, 54]. This is partially due to population differences, uncertainty (as studiesoften are not designed to give accurate estimates of the ICC), and differences in the design andanalysis approach [48]. A possible solution to this problem is the use of an internal pilot studydesign. In the design, nuisance parameters are estimated at an interim time point in the studyand the sample size is re-estimated. Overpowered studies may then be stopped early, while un-derpowered studies can be correctly expanded in order to obtain the desired power level. Since

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the nuisance parameters at the interim point are based on trial data, they are more likely to ac-curately reflect the true values than those based on the literature. Therefore, the re-estimatedsample 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 sucha way that the desired power level is achieved and the type I error rate inflation is kept to aminimum [56]. Blinded sample size re-estimation is based on estimates of the ICC and possiblyalso 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 dependon the intervention effect. While no studies were found investigating the effect of blindedsample 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 onthe 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 estimatedICC was pooled over the control and treatment group, and found only minor increases of thetype I error rate, with the largest observed type I error from both studies being 0.061 (nominalvalue = 0.050). No studies were found investigating the effect of sample size re-estimationbased 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 de-sign 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 onliterature data and simulation studies.

2. To determine the optimal sample size and number of clusters for the selected method withregard to coverage, power and cost through simulation studies.

3. To assess the possibilities of incorporating adaptive elements in the study design, such assample size re-estimation and interim analysis.

2Methods

Different statistical methods were considered for the analysis of clustered data from a ring de-sign, including both cluster-level and individual-level analysis. Each method was used to testthe one-sided null hypothesis of no decrease in dengue incidence when comparing prophy-laxis against placebo. All analyses and calculations were done in R v3.2.3 with the RStudiov0.98.501 interface [58].

2.1 Cluster-level analysis

2.1.1 Two-sample t-test

The simple two-sample t-test evaluates whether the mean proportion of incident dengue casesdiffers between the prophylaxis and placebo group. The test statistics is calculated as

t =x0 − x1√s20K0

+s21K1

where xi equals the mean proportion in intervention i (0 = placebo, 1 = prophylaxis), si thestandard deviation and Ki the number of clusters. The t-test statistic is compared against at-distribution with degrees of freedom equal to K0 + K1 − 2. The intervention effect x0 − x1

corresponds to a risk difference. The t-test assumes normally distributed data, but is generallyrobust against small to moderate deviations from this assumptions [59].

14

2.1.2 Regression with sandwich estimator

It is possible to regress the cluster-summary measures on the intervention using conventionallogistic and Poisson regression. However, this does require adjustment of the variance estimatorto correct for its underestimation. For example, the sandwich variance estimator is asymptot-ically 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 inflationof the type I error. Although its use is often associated with Generalized Estimating Equa-tions (GEE), it can be applied to any type of regression, as was done here [53, 60, 61]. First, ina logistic regression model the probability of incident dengue in each cluster was regressed onthe intervention:

πk =exp(β0 + β1 I(prophylaxis)k)

1 + exp(β0 + β1 I(prophylaxis)k)(2.1)

using a binomial random component and the logit link function:

log( πk

1 − πk

)= logit(πk) = β0 + β1 I(prophylaxis)k

where πk equals the expected probability of incident dengue in cluster k, β0 equals the meanlogit probability of incident dengue cases for the placebo group, β1 equals the mean differencein logit probability between the placebo and prophylaxis groups, and I(prophylaxis)k indicateswhether the jth individual received placebo (0) or prophylaxis (1). exp(β1) corresponds to anodds ratio. Conventional logistic regression (without use of the sandwich estimator) assumedthat, conditional on the intervention, the number of incident dengue cases follows a Binomialdistribution with mean and variance:

E (number of incident dengue cases)k = πknk

Var (number of incident dengue cases)k = πk(1 − πk)(2.2)

Note that equation 2.2 underestimates the true variability in the data when clustering occurs, forwhich the sandwich estimator was used as a correction.

Alternatively, we might choose to model the rate or the number of incident dengue cases in eachcluster with a Poisson regression model:

µk = exp(β0 + β1 I(prophylaxis)k) mk (2.3)

assuming a Poisson distribution and using the log link function:

log(µk) = β0 + β1 I(prophylaxis)k + log(nk)

where µk equals the expected rate of incident dengue cases in cluster k, β0 equals the mean lograte in the placebo group, β1 equals the mean difference in log rates between the placebo and

15

prophylaxis groups, I(prophylaxis)k indicates whether the kth cluster received placebo (0) orprophylaxis (1) and nk is an off-set variable indicating the cluster size of each cluster. exp(β1)corresponds to a relative risk. Conventional Poisson regression assumes that the number ofincident dengue cases follows a Poisson distribution conditional on the intervention, with meanand variance:

E (number of incident dengue cases)k = µk

Var (number of incident dengue cases)k = µk

(2.4)

Again, note that equation 2.4 underestimates the true variability in the data when clusteringoccurs, for which the sandwich estimator was used as a correction.

2.1.3 Quasi-likelihood approach

In addition to the regression approach described in the previous section, quasi-likelihood theoryhas also been suggested as a method to account for correlated data. Quasi-likelihood theoryoffers a robust approach to regression analysis by only making assumptions about the mean-variance relationship. The unadjusted variance estimate is multiplied by a scale parameter φwhose value depends on the degree of clustering in the data. Here φwas set equal to the Pearsonχ2 goodness-of-fit statistic divided by its degrees of freedom (the number of observations minusthe 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 param-eter φ instead of the sandwich estimator to account for correlated data.

2.1.4 Wilcoxon’s rank sum test

All of the previously described methods make parametric assumptions about the data. Whilesome methods, such as the t-test, are known to be quite robust against violations of its dis-tributional assumptions, it might be preferred to use a non-parametric alternative, especiallywhen the number of clusters is small and it becomes difficult to make a reliable assessment ofthe data distribution. The Wilcoxon’s Rank Sum Test is a non-parametric test, which has theadvantage 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 obtaina non-parametric estimate or confidence interval [45, 59].

The Wilcoxon’s rank sum test pools and ranks the cluster-specific proportions from both inter-vention arms. Let Ti be the sum of the ranks in the ith intervention arm, then the test statistic iscalculated as

z =T1 −K1(K1 +K0 + 1)/2√K1K0(K1 +K0 + 1)/12

16

with K0 and K1 being the number of cluster in the placebo and prophylaxis group. The teststatistic is compared against a the standard normal distribution. The null hypothesis is that thetwo sets of observations are samples from the same underlying distribution. If the mean rank forthe placebo clusters is significantly higher than that for the prophylaxis clusters, this providesevidence that the distribution of cluster summaries in the prophylaxis group is shifted to theleft. In other words, the proportion of incident dengue cases is then generally lower for thoseclusters receiving prophylaxis when compared to clusters receiving placebo [59].

2.2 Individual-level analysis

2.2.1 Generalized Estimating Equations

The basic logistic GEE model for binary data is similar to the one shown in equation 2.1 forstandard logistic regression. However, instead of regressing the cluster summary-measures theindividual-level data is used:

πk =exp(β0 + β1 I(prophylaxis)k)

1 + exp(β0 + β1 I(prophylaxis)k)

where k refers to the kth cluster and πk refers to the probability that a participant from the kthcluster acquires dengue. While the model is fitted using individual-level data, no adjustmentsare made for individual-level variables (e.g. age). In other words, the probability of acquiringdengue is assumed to be equal for all individuals from the same cluster and therefore πk stillrepresents a cluster-specific probability. While standard logistic regression based on individual-level data assumes that the observed outcomes are independent, GEE allows observations fromthe same cluster to be correlated according to some correlation matrix. Here exp(β1) representsthe population-average odds ratio associated with the prophylaxis effect.

GEE relies on an iterative generalized least squares methods instead of likelihood-based ap-proaches for parameter estimation. Standard errors are obtained using sandwich estimators.GEE models are fitted with the geeglm function from the geepack package [62–64], whichincludes several pre-specified options for the correlation structure. For the purpose of thisthesis an exchangeable structure was used, as this was considered the most appropriate. Anexchangeable correlation structure assumes that participants from different clusters are uncor-related, while participants from the same cluster all have the same correlation coefficient [45].

2.2.2 Generalized Linear Mixed Models

A Generalized Linear Mixed Models (GLMM) or random effects model for binary data was fit-ted based on individual-level outcomes. However, similarly as discussed for GEE no adjustmentwere made for individual-level data, and the probability of acquiring dengue was thus assumed

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to be equal for all individuals from the same cluster:

πk = β0 + β1 I(prophylaxis)k + uk

where πk equals the probability of acquiring dengue during follow-up for the kth cluster, β0equals the expected logit outcome for individuals in the placebo group, β1 represents the pro-phylaxis effect on the logit scale, and I(prophylaxis)k indicates whether the kth cluster receivedplacebo (0) or prophylaxis (1). The term uk is a random effect relating to the kth cluster, andthis is the term in the model which the between-cluster variation into account. Random effectsare assumed to be sampled from a standard normal distribution, while the data within clustersis assumed to follow a binomial distribution. exp(β) represents the subject-specific odds ra-tio of the prophylaxis effect, conditional on the random effect [45, 60]. According to Bellamyet al. (2000) [52] regression parameters from a population-averaged GEE model are approxi-mately equal to those from a subject-specific GLMM model multiplied by a bias term which isa function of the ICC: βpa = βss(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 wasfitted using the glmer function from the lme4 package [65].

3Phase 1

Determining the best statistical method

During the first phase of this thesis, differences in size, power and bias among statistical meth-ods were investigated for a range of ICC values and effect sizes under different scenarios: onewith 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 interven-tion group and for a given number of clusters, mean cluster size, baseline incidence (π0), effectof prophylaxis (expressed as a relative risk) and ICC.

First cluster sizes were generated as a random Poisson variable, to reflect the random variationin cluster size, and truncated at a minimum of four participants per cluster. The incidence inthe prophylaxis group (π1) was calculated as π0 multiplied by the effect size. Next, randomcorrelated data was generated using a Beta-binomial distribution, as proposed by Bellamy et.al. (2000) [52]. Random probabilities πk were generated for each cluster from a Beta(a,b)distribution with:

20

a =πiR

b =1 − πiR

R =ρ

1 − ρ

where πi equals the expected incidence for intervention i (π0 = control, π1 = prophylaxis) andρ equals the ICC. Next random binary responses Yjk were generated from a Bernoulli(πk)distribution, where Yjk equals the outcome of the jth participant from the kth cluster. When theICC equalled zero Yjk were generated from a Bernoulli(πi) distribution.

Generated datasets where only one the placebo or only the prophylaxis group contained noevents complicate estimation of the prophylaxis effect. When this occurred, one event wasadded to each of the intervention groups to facilitate analysis. The output of the data generatingfunction included an indicator showing whether the dataset was modified, which allowed forcounting the number of modified random samples in a simulation. While there exist moresophisticated methods to handle effect estimation under these circumstances, these were notapplied because of the exploratory nature of these simulation studies and the relatively smallnumber of simulations in which this situation occurred.

To assess the reliability of the data generating process, data was generated for a range of ICCvalues (0.00-0.27) using summary measures from the studies listed in table 3.1. As none ofthese studies evaluated an intervention, the relative risk (RR) was set equal to one. For eachstudy 5000 random samples were generated and the mean number of participants and incidentdengue cases were calculated. Table 3.1 shows that the simulated outcomes correspond well toobserved measures, regardless of the ICC. Intuitively this makes sense: the ICC does not affectthe mean number of events, but determines how those events are distributed over clusters. Asthe ICC increases, the underlying cluster-specific incidences πk will differ more strongly fromeach other. Note that a comparison of the observed against the simulated distribution of eventswas 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 com-pared to the variability observed by the studies listed in table 3.1. For this comparison thenumber of eligble participants in each cluster was used, as this was the only appropriate mea-sure all three studies reported on. Anders et al. (2015) [19] reported a median cluster size of30, with values ranging from 18 to 41. Similarly, the simulation returned on average a mediancluster 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

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Observed

No. of clusters No. of participants Incidence (%) Events

Mammen et. al. (2008) [66] 12 217 0.124 27Yoon et. al. (2012) [67] 50 749 0.084 63

Anders et. al. (2015) [19] 52 1182 0.069 82

Simulated

No. of participants Simulated number of events for ICC range

0.00 0.01 0.03 0.09 0.18 0.27

Mammen et. al. (2008) [66] 217 27 27 27 27 27 27Yoon et. al. (2012) [67] 749 63 63 63 63 63 63

Anders et. al. (2015) [19] 1183 82 81 82 81 82 81

Table 3.1: Comparison of the observed and simulated outcomes for various studies. For each study 5000random samples were generated and the mean number of participants and incident denguecases was calculated.

25.5 ± 4.9. Thus while the generated range seemed representative of the real-life situation, thevariability of the cluster sizes might have been too low.

Throughout the thesis, the effect of prophylaxis intervention on the ICC assumption was al-lowed to depend on the data generating mechanism. It was assumed this would lead to equalICCs in the placebo and prophylaxis group. However, during the final stages of this thesis itwas discovered that the reliability of the data generating mechanism with regard to the ICCdepended on the incidence, with lower incidences leading to lower ICC estimates (AppendixA). Consequently, the ICC was only equal for the placebo and prophylaxis groups when the RRequalled 1.00, and was lower for the prophylaxis groups when the RR was smaller. This dis-crepancy grew larger as the ICC increased. In practice, the assumption of equal ICCs often doesnot hold. However, in contrast to the results of the data generating mechanism, the ICC is oftenexpected to be higher for the group receiving active treatment [45], since cluster variability thendepends 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 itmentioned by Bellamy et al. 2000 [52]. Unfortunately, no relevant studies were found whichreported the ICC for both the control and treatment group and the plausibility of the ICC as-sumptions 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 mech-anism. While this is not expected to affect the general conclusions with regard to whether or notring trials and sample size re-estimation are favourable study designs, the optimal design mightdiffer than the one derived here in terms of the radius around the index case and the sample size.

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3.2 Simulation set-up

3.2.1 ICC

Few reports were available on the observed ICC of dengue incidence at the household or com-munity 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 dengueinfection based on 20 control clusters of approximately 100 participants. In a follow-up studyevaluating the added effect of community mobilization on pesticide-free intervention, Anders-son et. al. (2015) [69] reported an ICC for self-reported and serological-confirmed evidence ofrecent dengue infection of respectively 0.021 and 0.031 based on 75 control clusters of approxi-mately 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 asimilar set-up and endpoint. Other issues with ICC estimation include the difference in settingbetween 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 onindex 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. WhileBayesian methods are available which can derive a prior distribution of the ICC, it is generallyrecommended to investigate the impact of a range of ICC values for power and sample sizecalculations. For this thesis, the latter approach was used, selecting a range of 0.00, 0.01, 0.03,0.09, 0.18 and 0.27.

3.2.2 Baseline incidence

The dengue incidence rate was chosen based on studies investigating dengue incidence in asimilar setting as the dengue study (table 3.2). A weighted average, with weights determined bysample size, led to an estimated incidence of 8.0 %. This might be a conservative estimate, sincethe studies listed in table 3.2 a large radius around the index case. For this initial simulationstudy, a radius of 50-60 m was assumed, although the optimal radius might be adapted later onduring phase 2. As participants live closer to the index case, their risk of dengue increases, andthus 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 indexcase. 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 mradius would have given an estimate of 11.4 % instead of 8.0 %. Therefore a correction of 8.0⁄11.4

was applied, leading to an estimate of 12.3 % for the baseline incidence of dengue within a 60m radius.

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Study Study aim Population No. of clusters(sample size)

Incidence mea-sure

Observedincidence

Mammen et. al.(2008) [66]

Fine-spatialclusteringpattern ofdengue

Children in ru-ral Thailand

12 (217) 15-day inci-dence in a 100m radius fromthe index case

12.4 %

Yoon et. al.(2012) [67]


Children in ru-ral Thailand

50 (749) 15-day inci-dence in a 100m radius

8.4 %

Anders et. al.(2015) [19]


Adults andchildren inurban Vietnam

52 (1182) 14-day inci-dence in a 100m radius fromthe index case

6.9 %

Table 3.2: Short description of the studies used for estimation of the baseline incidence.

3.2.3 Scenarios

The adequacy of different statistical methods depends on the ICC, the number of clusters andthe cluster size. All methods are expected to perform better for settings with a large number ofclusters and a low ICC. As the number of clusters decreases or the ICC increases the size prop-erties of an analysis may break down and parameter estimates might show bias [52]. Thereforethe selected range of ICC values and effect sizes were investigated under three different scenar-ios, each one with an average sample size of 623-641 participants and 77-79 incident denguecases:

• Scenario 1 - many small clusters: 50 clusters per intervention arm with an average clustersize of 6 participants.

• Scenario 2 - few large clusters: 4 clusters per intervention arm with an average clustersize of 80 participants.

• Scenario 3 - intermediate, with the cluster size based on the estimated number of partic-ipants within a 50-60 m radius from the index case [66, 67]: 26 clusters per interventionarm with an average cluster size of 12.31 participants.

The first and second scenario represent quite extreme situations with a very large or small num-ber of clusters. While this makes it easier to detect the shortcomings of the different statisticalmethods, it is unlikely that either of these scenarios would be used in practice for the denguestudy. Therefore the third and intermediate scenario was selected, which is expected to be morerepresentative of the dengue study.

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Figure 3.1: Association between the distance of the participant’s house to the house of the index caseand different measures for dengue incidence or prevalence. Left: the proportion of partici-pants experiencing DENV seroconversion (mean and 95% C.I.). The numbers in parenthesisindicate the number of participants with incident dengue infection and the total number ofparticipants in the distance interval [66]. Right: RD = recent dengue (N = 15), ES = en-rolment seroconversion (N = 41), PES = post-enrolment seroconversion (N = 63), day 15PCR-positive (N = 10). For this thesis the measure of interest is PES (incident dengue casesconfirmed 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 rangeof RRs of the prophylaxis versus the placebo (0.25, 0.50, 0.75, 1.00). Under each scenarioand for each combination of ICC and RR, 5000 random samples were generated and analysedusing all of the cluster- and individual-level analysis methods described in section 2. For eachrandom 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 everymethod. The absolute bias was determined by subtracting the true prophylaxis effect from theestimated prophylaxis effect and the relative bias by taking the ratio of the estimated over thetrue prophylaxis effect. The true subject-specific odds ratio was approximated as discussed insection 2.2.2. Finally, for each method the size of the test was calculated as the proportionof random samples with a significant result under a RR of 1.00, power as the proportion ofrandom samples with a significant result under a RR of 0.25, 0.50 and 0.75 and relative bias asthe median relative bias. This algorithm is graphically depicted in figure 3.2.

3.4 Results and discussion

In each scenario a small number of the random generated samples were modified: respectively5, 533 and 20 out of 120 000 samples for scenario 1, 2 and 3. The results for Poisson andquasipoisson regression were very similar to those for logistic regression using a binomial orquasibinomial distribution, and were therefore only included in Appendix B. The estimatedsize for the different scenarios and methods is shown in figures 3.3 and 3.4. Since p-values

25

Figure 3.2: Algorithm used to estimate the size, power and bias of different statistical methods in a ringtrial design.

were calculated based on one-sided tests, the nominal size equalled 0.025. In scenarios 1 and 3all methods had a size relatively close to the nominal value, ranging from 0.019 to 0.041. Gen-erally, the t-test and Wilcoxon test stayed closer to the nominal value (0.020 - 0.029) than theother methods (0.019 - 0.041). Most methods became slightly oversized as the ICC increased,going from 0.019 - 0.030 at ICC = 0 (no clustering) to 0.024 - 0.041 at ICC = 0.27. In scenario2, the t-test and Wilcoxon test behaved similarly as in scenarios 1 and 3, but were more con-servative, ranging from 0.005 to 0.019. In contrast, quasibinomial and quasipoisson regressionand GLMM were generally too liberal, with a size ranging from 0.022 to 0.067. Binomial andPoisson regression and GEE performed much worse than in scenarios 1 and 3, with the sizeincreasing from 0.069 - 0.073 at ICC = 0 to 0.120 - 0.125 at ICC = 0.27.

The estimated power at RR = 0.25 for the different scenarios and methods is shown in figures3.5 and 3.6. In scenario 1 all methods had good power, never dropping below 0.77. Generallythe Wilcoxon test and GLMM performed best, with the power never dropping below 0.88. Inscenario 2 the power decreased drastically, dropping below 0.40 as the ICC increased for allmethods except Binomial and Poisson regression and GEE. For the latter, the power dropped toapproximately 0.50 as the ICC increased. Since these methods were oversized in this scenario

26

(figure 3.3-3.4), a higher power was more likely to be the consequence of statistical propertiesbreaking down than of better efficiency. In the intermediate scenario 3, the Wilcoxon test againperformed best, with a minimal power of 0.75, followed by GLMM with 0.73. All other meth-ods have a minimal power of 0.59-0.62. Similar but less pronounced trends were seen at a RRof 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 occurredin the prophylaxis group might have affected the size. Since for these samples the observedprophylaxis effect was underestimated, one would expect fewer significant results and thus alower size. However, as the ICC increased, for most tests the size became too liberal. Incontrast, data modifications might have been partially responsible for conservative sizes andlow 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. Resultsfrom Wu et al. (2012) [48] based on simulations studies suggested that random effects modelsoften were more prone to estimate the ICC with negative bias than GEE. While this was notthe case in the simulation study by Bellamy et al. (2000) [52], they did find that both GEE andGLMM 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 thatbecause the investigated regression methods for clustered data often rely on approximate meth-ods for parameter estimation and depend more strongly on parametric assumptions, that theyare less robust against designs with a low number of clusters. In contrast, the Wilcoxon test is anon-parametric method, while the t-test is parametric, but known to be robust against moderatedeviations of its assumptions. While this could explain some of the differences between theinvestigated statistical methods, more research is necessary to find out to what extent the break-down of test properties was related to the data modifications. This was not further investigatedfor this thesis.

27

Figure 3.3: Size properties of various statistical methods under different scenarios. The dotted lineindicates the nominal size of the test (equal to 0.025). Logistic regression was performedusing a sandwich estimator.

28

Figure 3.4: Size properties of various statistical methods under different scenarios. The dotted lineindicates 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 = 0.25.The dotted line indicates the 0.80 power mark.

29

Figure 3.6: Power of various statistical methods under different scenarios and assuming a RR = 0.25.The dotted line indicates the 0.80 power mark. Logistic regression was performed using asandwich estimator. cor = correlation structure.

30

Figure 3.7: Median relative bias of the prophylaxis effect for various statistical methods under differentscenarios and assuming a RR = 0.25. The dotted line indicates unbiased estimates (relativebias = 1). Logistic regression used a sandwich estimator. cor = correlation structure.

31

At a RR = 0.25 all methods were prone to downward bias of the estimated prophylaxis effectas 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 allmethods except for the t-test. Downward biases might partially be the consequence of modify-ing some of the random samples. Situations in which methods were expected to perform worsecorresponded to those situations which were most likely to require data modifications (low in-cidence, few clusters, large ICC). Indeed, for scenario 2 much more samples were modifiedthan for scenarios 1 and 3 (respectively 533 instead of 5 and 20) and in all three scenarios thenumber of modifications increased with the ICC. However, by using the median relative biasthese results should have been somewhat protected against the influence of modifications. Fur-thermore, previous studies have already indicated that regression methods for clustered data canstill give biased intervention estimates, especially when the number of clusters is small and / orthe ICC is large [45,47,52,53]. It is likely that the observed trends in relative bias result from acombination of the breakdown of properties and of the data modifications, although the extentto which one was most responsible was not further investigated. Similar trends were seen at arelative 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 ofclusters 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, theWilcoxon test had good size and power properties, but can not provide us with an estimate of thetreatment effect. Logistic and Poisson regression and GEE showed good power, but this was theconsequence of liberal size properties. GLMM and quasibinomial and quasipoisson regressionsuffered from low power and biased estimates. Finally, while the t-test had low power whenthere were few clusters, its size properties were adequate and its estimates showed relativelylittle 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 advantagesthat it is simple to perform, well understood and that its estimate is expressed in terms of a riskdifference, which is more easily interpreted than an odds ratio. For all of these reasons, the t-testseems an appropriate method for evaluating the intervention effect of an antiviral prophylacticagainst dengue in a ring trial design.

Since the dengue study was assumed to be a randomized trial, the study clusters were expectedto be balanced in terms of their covariables. In this case, data analysis does not require adjust-ment for additional variables and a cluster-level analysis would suffice for effect estimation. Iflater studies decide it is necessary to adjust for individual data, one would have to weigh thedisadvantages of GEE (oversized) against those of GLMM (more prone to bias). For a smallnumber of clusters neither method seemed appropriate. Choosing between the two may dependon the main goal of the analysis (effect estimation versus testing), but nevertheless it should be

32

stressed that both methods are likely to give unreliable results. Especially when the observedICC is large both methods can only give an indication of the prophylaxis effect. As the numberof clusters increases, the size properties of GEE improved and both methods return less biasedestimates, which corresponds well with the results from Bellamy et al. (2000) [52]. Nonethe-less, it remains advisable to investigate the properties of both methods for the specific studysetting.

During this first part of the thesis, the t-test was selected the evaluation of an antiviral prophy-lactic against dengue in a ring trial design. Besides using an appropriate analysis method, it isimportant to compare the cost-efficiency of different designs, which will be done in the nextphase.

4Phase 2

Determining the optimal sample size

The cost-efficiency of a CRT depends on the number of clusters, the cluster size and the costratio, i.e. how much does it cost to initialize a cluster compared to the cost of enrolling anew subject in an existing cluster. For a ring trial the cost-efficiency will also depend on theclustering pattern of dengue. When recruiting close to the index case, the potential loss inpower from having smaller clusters might be compensated by the gain in power from recruitingparticipants with a higher risk of dengue. Therefore, during the second phase of this thesis, thecost-efficiency was compared of recruiting strategies using different radiuses around the indexcase and assuming a range of possible cost ratios.


4.1.1 ICC

For sample size and cost calculations the range of ICC values from phase 1 was narroweddown. One ICC value was selected based on the literature [68,69], and sensitivity analyses wereperformed for a lower and higher estimate. For determining the ICC, more weight was given tostudies with a larger number of clusters by calculating a weighted average with weights equalto Ks/K, where Ks is the number of clusters in study s and K is the number of clusters summedover all studies. Based on Arostegui et. al. (2008) [68] and Andersson et. al. (2015) [69]

34

this approach led to an ICC estimate of 0.062 for serological evidence of dengue in mediumsized communities. Note that the ICC reported by these studies was based only on the controlclusters, 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. 0.18 and 0.031). While severalother studies have evaluated the spatial clustering pattern of dengue using a ring design, noneof them reported the ICC or related measures [19, 66, 67, 70–72]. When expanding the searchfor ICC estimates to studies investigating the incidence of other infectious diseases, only a fewadditional studies were found [73–75], with values ranging from 0.004 to 0.13. Based on thesestudies 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 whena study investigated multiple infectious diseases, an estimate of 0.053 was obtained. While thismethod might provide some idea of ”robustness” when little information is available, it is notrecommended to base ICC estimates on studies with a different endpoint or setting. Howeverif other clustered studies investigating infectious diseases had consistently reported larger ICCvalues, it might have been advisable to use a more conservative estimate. Since this was not thecase here, the original estimate of 0.062 was not adjusted. For sensitivity analyses an ICC of0.031 and 0.124 were selected.

By using a weighted average based on the number of clusters we assume that studies withmore 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 clus-ters and cluster size might also have inherently different ICCs. In practice, finding reliableinformation about this association is infeasible and proposed methods for sample size calcula-tions are therefore (almost) always based on a constant ICC [49, 77, 78].

4.1.2 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 sizewas 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 describedin section 3.2.2, leading to estimates of respectively 21.6, 15.7, 12.3, 9.0 and 8.0 %.

4.1.3 Cost ratio

Despite the upcoming use of clustered studies and the general agreement that the most efficientdesign depends on the cost per person and the cost per cluster, no cost estimates for CRT werefound. A limited number of papers has investigated how the cost ratio affects the efficiencyof a CRT design, using values ranging from 2 to 100 [49–51, 79]. Moerbeek (2005) [51] and

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Raudenbush & Liu (2000) [50] did not report the reasoning behind their cost-ratios. The USDemographic and Health Surveys Program (2006) [79] reported eight cost ratios from pastobservational survey-based studies, although they did not refer to the actual studies. These costratios 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 knowof” which reported a cost ratio of 26. As there was very little information to base the selectionof cost ratios on, a range of estimates was selected for further investigation, in which clusterinitialization 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 todetermine the cost per person or cost per cluster. PhRMA reported that the average estimatedcost per person for infectious disease trials in the US was $16,500 [80] in 2013. However, thisnumber includes overhead costs which would be associated with cluster initialization in a CRTdesign. 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 theselected cost ratios, the cost of cluster initialization is then resp. $35,000, $70,000, $140,000 or$280,000.

4.2 Sample size estimation

Data was generated under the assumption of a RR = 0.25, a given initial value for the numberof clusters and other input variables as described in the previous sections. The data generatingprocedure was similar as the one described in section 3.1, except for the design based on a 20m radius, for which cluster sizes were truncated at a minimum of one and a maximum of threeparticipants. Each data set was analysed using an unweighted two-sample t-test. After 5000random samples the power was estimated as the proportion of simulations which rejected thenull hypothesis of no intervention effect. If the power was below 0.80 a new simulation of 5000random samples was run using one extra cluster per intervention arm. Once the power wasgreater than or equal to 0.80 four more simulations of 5000 random samples were run, each oneusing 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, thetotal sample size and cost of the study can easily be calculated using the formulas:

N =k=K∑k=1

mk

where N is the total sample size, K the total number of clusters and mk the number of partici-pants in the kth cluster; and

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Figure 4.1: Algorithm used to determine the number of clusters needed to obtain the desired power level.

B =k=K∑k=1

c+ pmk

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 runsimilar to the ones performed in phase 1 to evaluate the effect of the ICC on the power of theselected designs.


No random samples had to be modified or disregarded. The association between study powerand the number of clusters or the sample size for a RR equal to 0.25 and an ICC equal to 0.062is shown in figure 4.2 and 4.3 for a variety of designs.

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Figure 4.2: Simulated power based on 5000 random generated samples of different study designs usinga range of different radiuses around the index case. The red line indicates the 0.80 powermark.

In a conventional CRT, one would expect that a study with more participants per cluster requiresfewer clusters, especially when the ICC is small. However, because of the ring design, dengueincidence is higher in smaller clusters. In this case, the increase in power by sampling only a fewpeople around each index case has sometimes outweighed the increase in power by samplingmore participants per cluster. Consequently, the expected association between cluster size andnumber of clusters is not as strong, and with the exception of the 20 m radius, all the differentdesigns 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 ofinfection 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 witha 20 m radius requires the smallest sample size, neither of them may be the most efficient interms of budget. A level plot of the estimated cost in million dollars for an ICC equal to 0.062(figure 4.4) shows that the cost efficiency of the study design seems optimal for a 40 m radiusover the entire range of cost ratios. However, at the largest investigated cost ratio, the 40 and 60m 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 samplesize became smaller, especially for designs with a large cluster size. In contrast, for a higherICC (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 costof different designs (figures in Appendix C). Assuming an ICC = 0.031 and a high cost ratio, adesign with a 60 m radius became slightly more cost efficient than one with a 40 m radius (resp.

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Figure 4.3: Simulated power based on 5000 random generated samples of different study designs usinga range of different radiuses around the index case. The red line indicates the 0.80 powermark.

11.1 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 prophy-laxis. When choosing the appropriate cluster size, smaller clusters with recruitment closer tothe index case can lead to more cost efficient designs over a range of ICCs and cost ratios. Thissimulation 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 interven-tion arm is estimated to be sufficient for obtaining a power ≥ 0.80. A second power simulationfor this design is shown in figure 4.5 and indicated that this number of clusters is expected toprovide a power ≥ 0.80 for ICC values up to approximately 0.08.

Assuming a fixed design, the optimal number of clusters and cluster size has been determinedfor an ICC equal to 0.062. In the third and final part of this thesis the (dis)advantages of a fixedversus a dynamic design will be discussed, and possibilities for sample size re-estimation willbe explored.

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Figure 4.4: Estimated cost in million dollars of different study designs. Plot points indicate values forwhich simulations were run.

Figure 4.5: Dependence of the estimated power on the ICC and the number of clusters for a study designrecruiting participants within a 40 m radius from the index case. The plot labels indicate thenumber of clusters per intervention arm.

5Phase 3

Sample size re-estimation

Sample size approximations strongly depend on the ICC and baseline incidence of dengue, aswas demonstrated in the second phase of this thesis. Because of the difficulty in obtainingreliable estimates for these nuisance parameters, a natural approach would be to undertake aninternal pilot study and re-estimate the sample size as described in section 1.7. During the thirdand final phase of this thesis, the effect of sample size re-estimation on the type I error, powerand final sample size will be investigated under different scenarios.


The effect of sample size re-estimation on the type I error, power and sample size were investi-gated for three different scenarios:

• Scenario 1 - the initial design was overpowered: the true underlying ICC and baselineincidence are 0.031 and 0.236 % (respectively 50 and 150 % of the original estimates).

• Scenario 2 - the initial design was powered correctly: the true underlying ICC and base-line incidence are 0.062 and 0.157 %.

• Scenario 3 - the initial design was underpowered: the true underlying ICC and baselineincidence are 0.124 and 0.079 % (respectively 200 and 50 % of the original estimates).

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5.2 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 asdescribed in section 3.1 assuming a mean cluster size equal to 7.9. The unblinded baseline in-cidence, 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 andbaseline incidence were estimated based on blinded data. The ICC was calculated using theANOVA estimator, as described in section 1.6. Since both the previous literature and our ownsmall simulation study had indicated that ICC estimation based on a limited number of clustersled to highly variable estimates with both excessively small and large values [48, 56] (results inAppendix A), the interim estimate of the ICC was truncated at 0.01 and 0.18, which was deemeda realistic range [68, 69]. The baseline incidence was calculated under the assumption of a RRequal to 0.25 by multiplying the mean cluster-specific incidence by 1.6. The required samplesize was then determined as described in section 4.2 based on 750 random generated datasetsand assuming a RR equal to 0.25 and nuisance parameters equal to the blinded estimates. Ad-ditionally, a limit of 100 clusters per intervention arm was set during sample size re-estimationto prevent the algorithm from looping indefinitely. Next, if the initial 14 clusters were alreadyexpected to give sufficient power (> 0.80) no additional clusters were sampled. If the requirednumber of clusters was higher, additional clusters were sampled similarly as described in sec-tion 3.1, but without modifying the dataset. Finally, a two-sample t-test was performed and itsoutput saved. The type I error (based on 2000 random samples) or power (based on 1000 ran-dom samples) was estimated as the proportion of simulations which rejected the null hypothesisof no prophylaxis effect when the true RR equalled 1.00 or 0.25 respectively. This algorithm isgraphically depicted in figure 5.1.

Unfortunately, because of the computer-intensiveness of this algorithm only a limited amountof simulation runs could be performed. The results of this phase will therefore only serve as aninitial indication of how sample size re-estimation affects the type I error and power.


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 1this inflation corresponded with a power much larger than the desired level of 0.80, this was notthe case for scenario 3. On the other hand, for scenario 2 the estimated power was above thedesired level, even though no type I error inflation had been observed. Further exploration ofthe estimated nuisance parameters at the interim point and the final sample size might explainthe different effect of sample size re-estimation for each scenario.

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Figure 5.1: Algorithm used to evaluate the effect of sample size re-estimation based on nuisance param-eters 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) 0.030 0.92Scenario 2: initial design was powered correctly (0 / 23) 0.023 0.86Scenario 3: initial design was underpowered (13 / 236) 0.028 0.80

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 randomsamples) and for the power simulation (based on 1000 random samples)

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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 accu-rately at a RR equal to 0.25 (figure 5.2). This was expected, since the method of estimationapplied a correction for the prophylaxis effect on the overall incidence assuming a RR equalto 0.25. The blinded ICC estimate showed negative bias at a RR equal to one, with estimatesshowing more bias as the true underlying ICC increased (figure 5.3). For a RR equal to 0.25 theICC was overestimated for scenarios 1 and 2. This was expected because the variation betweenclusters due to the prophylaxis effect could not be taken into account during blinded estima-tion. Notable was that for the third scenario there was substantial negative bias both under aRR equal to 1.00 and 0.25. 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 thatthis was not associated with the value of the true underlying ICC. The last scenario had both ahigher ICC and a lower baseline incidence. Subsequently, the absolute risk difference betweenthe placebo and prophylaxis clusters was also smaller. Possibly in this case, the difference be-tween clusters due to the prophylaxis effect seemed relatively small compared to the naturallyoccurring cluster differences, which could lead to the blinded ICC still being underestimatedat a RR equal to 0.25. However, this did not explain the association between the negative biasand the true underlying value of the ICC. It is likely that this association was related to the thebaseline incidence of each scenario. Evaluation of the ICC assumptions imposed by the datagenerating mechanism showed that data generation under a low incidence led to ICC estimatesthat were too low (Appendix A). The large number of data modifications for the power simu-lation under scenario 3 might also have played a role, although these did not seem to affect thequality 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 RRequal to 0.25 (figure 5.4). At a RR equal to 1.00, the number of random samples for which morethan 14 clusters had to be sampled was 0.05, 19.90 and 98.85 % and the number of samples for

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Figure 5.3: Blinded ICC estimated at interim point. The dotted line indicates the true unblinded ICCfor the control group.

which the required sample size was larger than the limit of 100 clusters per intervention armwas 0.00, 0.00 and 0.15 %. At RR equal to 0.25 these numbers were respectively 47.3, 84.3,100.0 % and 0.0, 0.0, 2.1 %.

Those random samples responsible for type I errors had a larger median effect size and un-blinded baseline incidence, and a lower median blinded ICC estimate at the interim point. Thisexplained why these samples led to significant results. However, the median blinded baselineincidence at the interim point, on which sample size re-estimation was based, differed only verylittle from the median based on all random samples, with the largest difference occurring underscenario 2 (resp. 0.238 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 ofcluster to obtain > 0.80 power in a fixed design. For scenario 1, this number equalled 12,which falls below of the plotted range.

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a more important role during sample size re-estimation and its effect on type I error inflationthan the blinded baseline incidence. The blinded ICC estimate at interim was indeed positivelycorrelated with the standard error during the final analysis, meaning that those random sampleswho by chance have a low blinded ICC estimate at the interim point were more likely to falselyreject the null hypothesis. While this might have explained the reason behind type I errors, wewere not able to distinguish why the type I error inflated slightly under scenarios 1 and 3, butnot under scenario 2. There was no clear association between the type I error rate and any ofthe saved output variables. One possible explanation is simply that the effect of the blindedestimated ICC and baseline incidence differs between scenarios.

Scenario 1 had the highest true underlying baseline incidence, and subsequently the absolutebias 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 randomsamples. This was in contrast with scenarios 2 and 3, for which respectively 398 (19.9 %) and1977 (98.9 %) of the random samples required additional recruitment of clusters. CRTs witha small number of clusters are often more prone to inflation of the type I error [52, 56]. Theso-called unrestricted re-estimation design which was applied here, where the final sample sizeis allowed to be both smaller and larger than the originally planned design, might therefore bemore sensitive to type I errors. A simulation study by by Lake et al. (2002) [55] on differentre-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. Lessadditional clusters were then recruited, which otherwise might have provided more informationleading to more accurate estimates of the ICC. While this process might give rise to type I errorfor all the investigated scenarios, its effect was seemingly magnified for scenario 3 because ofthe large negative bias during blinded ICC estimation.

Scenario 1 was overpowered because of the type I error inflation, and because the numberof 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 ofclusters per intervention arm was only 12. While scenario 3 also suffered from some type I errorinflation, the mean power was much closer to the nominal level. In this case the required numberof 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 underpoweredstudies. Indeed, when comparing the distribution of final samples sizes with the required samplesize 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 5.3indicated that while the blinded baseline incidence is quite reliable, the blinded ICC estimateis overestimated, leading to recruitment of more clusters than necessary. According to phase

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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 simulatedstudies 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 thetype I error, empirical levels remained close to the nominal value and studies generally weresufficiently powered to detect the anticipated prophylaxis effect. Our results were similar tothose 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 introducedby using blinded estimates. The internal pilot design was expected to allow for substantialgains in power when the original sample size was underestimated due to poor estimation ofthe ICC or baseline incidence. However, because of the limited number of simulations, furtherresearch is needed to evaluate the effect of blinded sample size re-estimation on the type I errorand power. The effect of blinded re-estimation seemed to depend on the combined effect ofbiases in the blinded estimates for the baseline incidences and ICC. These results indicatedthat this combined effect might depend on the specific variables of the study setting. Settingswith a larger ICC suffered from larger negative bias which made the interim sample seem morepowered, leading to re-estimation designs that were more prone to type I errors. Large baselineincidences could have led to blinded incidences that are too large at the interim point when theprophylaxis effect was smaller than expected, making the interim sample seem more poweredthan it actually was and leading to underpowered studies. Unintentionally, the settings studiesin this thesis are such that large ICC and large baseline incidence never coincided, but it wouldbe interesting to further investigate the separate effects of ICC and baseline incidence on samplesize re-estimation. Possibly there were settings for which the effect of sample size re-estimationon size and power is much more severe, for example in a setting with a high ICC and highbaseline incidence. Furthermore, investigating different settings might give more insight intothe extent to which data modifications affect the results.

Alternatively, it might be preferred to use unblinded estimation, which would have allowed formore accurate determination of the ICC and baseline incidence. This might have preventedthe effect of sample size re-estimation from depending on the specific combination of nuisanceparameters. 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 againsttype 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

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a large number of clusters, as little as 25 % of the data may be considered sufficient to estimatenuisance 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 theICC 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 importantwhen investigating the effect of sample size re-estimation for scenarios with few clusters. Hereearlier sample size re-estimation led to more imprecise estimates of the variance componentsand more underpowered studies.

During sample size re-estimation a maximum limit was set on the number of clusters per in-tervention arm equal to 100. In practice, when the required sample size is only expected to be20 clusters per intervention arm, the catch-area for index cases might not be large enough toallow for the recruitment of so many clusters. In this case, the trial may need to be prolongedto recruit clusters from the following dengue season. However, dengue incidence is known tovary between years and subsequently the ICC might vary as well. Interim estimates of nuisanceparameters from one year might therefore not translate well to the next year, leading to uncer-tainty about how many additional clusters should be recruited. It would be advisable to takeinto 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 samplesize and the cluster size are allowed to change (e.g. if the ICC is much lower than expected itmight be more efficient to sample larger clusters), etc.

6Conclusion

This thesis was the first to investigate the concept of a ring trial and the use blinded samplesize re-estimation in the context of a dengue prophylaxis. Comparison of several methods foranalysing correlated data suggested that cluster-level analysis often performed equivalently toindividual-level analysis. The simple two-sample t-test was selected as the analysis method ofchoice because of its good statistical properties and its convenient use. Next, the comparisonof multiple designs using different radiuses around the index case clearly indicated the benefitsof using a ring design. For most designs, the loss in power due to sampling less participantsper cluster was compensated by sampling from a population at a higher risk of dengue, leadingto similar requirements for the number of clusters to obtain the desired power level. Afteraccounting for the cost ratio, the design recruiting participants within a 40 m radius (20 clustersper intervention arm, mean cluster size of 7.9 participants) was selected as the most cost efficientdesign. Finally, blinded sample size re-estimation showed some potential for correctly adjustingthe 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 Ierror 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 regardto the use of ring designs in general and the implementation of sample size re-estimation meth-ods. Nonetheless, future trials investigating dengue, or other communicable diseases for whichsimilar clustering pattern might be expected, should consider the use of a ring design in orderto improve the statistical and cost efficiency of the trial.

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Appendices

List of Figures and Tables in Appendices

A.1 Cumulative distribution of the estimated ICC (ICC = 0.031) . . . . . . . . . . . 61



B.1 Modified number of random samples (phase 1). . . . . . . . . . . . . . . . . . 63

B.2 Power under scenario 1 (RR = 0.25.) . . . . . . . . . . . . . . . . . . . . . . . 64

B.3 Median relative bias of the prophylaxis effect under scenario 1 (RR = 0.25). . . 64





B.8 Size properties under scenario 1 (RR = 1.00) . . . . . . . . . . . . . . . . . . . 67


















C.1 Estimated power for different study designs (ICC = 0.031). . . . . . . . . . . . 77

C.2 Estimated power for different study designs (ICC = 0.031). . . . . . . . . . . . 78

60

C.3 Estimated cost in million dollars for different study designs (ICC = 0.031). . . . 78C.4 Estimated power for different study designs (ICC = 0.124). . . . . . . . . . . . 79C.5 Estimated power for different study designs (ICC = 0.124). . . . . . . . . . . . 79C.6 Estimated cost in million dollars for different study designs (ICC = 0.124). . . . 80C.7 Modified number of random samples (phase 2). . . . . . . . . . . . . . . . . . 80C.8 Power of a 40 m ring design RR = 0.25.) . . . . . . . . . . . . . . . . . . . . . 81C.9 Median relative bias of the prophylaxis effect of a 40 m ring design (RR = 0.25). 81C.10 Power of a 40 m ring design (RR = 0.50.) . . . . . . . . . . . . . . . . . . . . 82C.11 Median relative bias of the prophylaxis effect of a 40 m ring design (RR = 0.50). 82C.12 Power of a 40 m ring design (RR = 0.75.) . . . . . . . . . . . . . . . . . . . . 83C.13 Median relative bias of the prophylaxis effect of a 40 m ring design (RR = 0.75). 83C.14 Size properties of a 40 m ring design (RR = 1.00) . . . . . . . . . . . . . . . . 84C.15 Median relative bias of the prophylaxis effect of a 40 m ring design (RR = 1.00). 84

AICC Assumptions

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

62



BPhase 1 Tables and Figures

Figure B.1: Modified number of random samples for each setting under each scenario (per 5000 gener-ated samples).

64

Figure B.2: Power of various statistical methods under scenario 1 (many small clusters) and assum-ing a RR = 0.25. The dotted line indicates the 0.80 power mark. Logistic regression wasperformed using a sandwich estimator. cor = correlation structure.

Figure B.3: Median relative bias of the prophylaxis effect for various statistical methods under scenario1 (many small clusters) and assuming a RR = 0.25. The dotted line indicates unbiased esti-mates (relative bias = 1). Logistic regression used a sandwich estimator. cor = correlationstructure.

65



66



67

Figure B.8: Size properties of various statistical methods under scenario 1 (many small clusters). Thedotted line indicates the nominal size of the test (equal to 0.025). Logistic regression wasperformed using a sandwich estimator. cor = correlation structure.


68

Figure B.10: Power of various statistical methods under scenario 2 (few large clusters) and assuminga RR = 0.25. The dotted line indicates the 0.80 power mark. Logistic regression wasperformed using a sandwich estimator. cor = correlation structure.

Figure B.11: Median relative bias of the prophylaxis effect for various statistical methods under scenario2 (few large clusters) and assuming a RR = 0.25. The dotted line indicates unbiased esti-mates (relative bias = 1). Logistic regression used a sandwich estimator. cor = correlationstructure.

69



70



71

Figure B.16: Size properties of various statistical methods under scenario 2 (few large clusters). Thedotted line indicates the nominal size of the test (equal to 0.025). Logistic regression wasperformed using a sandwich estimator. cor = correlation structure.


72

Figure B.18: Power of various statistical methods under scenario 3 (intermediate) and assuming a RR= 0.25. The dotted line indicates the 0.80 power mark. Logistic regression was performedusing a sandwich estimator. cor = correlation structure.

Figure B.19: Median relative bias of the prophylaxis effect for various statistical methods under scenario3 (intermediate) and assuming a RR = 0.25. The dotted line indicates unbiased estimates(relative bias = 1). Logistic regression used a sandwich estimator. cor = correlation struc-ture.

73



74



75

Figure B.24: Size properties of various statistical methods under scenario 3 (intermediate). The dot-ted line indicates the nominal size of the test (equal to 0.025). Logistic regression wasperformed using a sandwich estimator. cor = correlation structure.


CPhase 2 Tables and Figures

Figure C.1: Simulated power based on 5000 random generated samples of different study designs usinga range of different radiuses around the index case. The red line indicates the 0.80 powermark.

78


Figure C.3: Estimated cost in million dollars of different study designs. Plot points indicate values forwhich simulations were run.

79



80

Figure C.6: Estimated cost in million dollars of different study designs. Plot points indicate values forwhich simulations were run.

Figure C.7: Modified number of random samples for the different power investigations of a 40 m ringdesign.

81

Figure C.8: Power of various statistical methods of a 40 m ring design and assuming a RR = 0.25.The dotted line indicates the 0.80 power mark. Logistic regression was performed using asandwich estimator. cor = correlation structure.

Figure C.9: Median relative bias of the prophylaxis effect for various statistical methods of a 40 m ringdesign and assuming a RR = 0.25. The dotted line indicates unbiased estimates (relativebias = 1). Logistic regression used a sandwich estimator. cor = correlation structure.

82



83



84

Figure C.14: Size properties of various statistical methods of a 40 m ring design. The dotted line indi-cates the nominal size of the test (equal to 0.025). Logistic regression was performed usinga sandwich estimator. cor = correlation structure.


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