Conditions: Coronavirus Infection Coronavirus Infectious Disease
Keywords: coronavirus COVID-19 hydrochloroquine placebo
Allocation: RANDOMIZED | Intervention model: PARALLEL
Enrollment: 368
Healthy volunteers: no

Brief summary:
A novel coronavirus, SARS-CoV-2, is responsible for a rapidly spreading pandemic that has reached 160 countries, infecting over 500,000 individuals and killing more than 24,000 people. SARS-CoV-2 causes an acute and potentially lethal respiratory illness, known as COVID-19, that is threatening to overwhelm health care systems due to a dramatic surge in hospitalized and critically ill patients. Patients hospitalized with COVID-19 typically have been symptomatic for 5-7 days prior to admission, indicating that there is a window during which an effective intervention could significantly alter the course of illness, lessen disease spread, and alleviate the stress on hospital resources.

There is no known treatment for COVID-19, though in vitro and one poorly controlled study have identified a potential antiviral activity for HCQ. The rationale for this clinical trial is to measure the efficacy and safety of hydroxychloroquine for reducing viral load and shedding in adult outpatients with confirmed COVID-19.

Detailed description:
Background COVID-19 is pandemic with high mortality among hospitalized patients despite a benign course in the large majority of patients infected. Limited data are available from small outpatient studies and have not shown efficacy in preventing hospitalization. Hydroxychloroquine (HCQ) and chloroquine have antiviral and immune-modulating effects, but there are no data concerning their efficacy in reducing viral load and shedding in outpatients.

Evidence supporting possible efficacy for hydroxychloroquine. In cell models, chloroquine both interferes with terminal glycosylation of the ACE2 receptor (the cell surface receptor by which SARS-CoV2 enters human cells) and increases endosomal pH, which interferes (at least in vitro) with a crucial step in viral replication.1,2 HCQ is 5x more potent than chloroquine in a Vero cell model of SARS-CoV-2 infection. In independent experiments, chloroquine has confirmed in vitro activity against SARS-CoV-2. Additionally, HCQ has in vitro efficacy against SARS-CoV-1. According to news releases, an as-yet-unpublished set of case series in China (N reportedly 120) suggests the possibility of rapid viral clearance and low rates of progression to critical illness. In addition to in vitro anti-viral effects chloroquine and HCQ appear to have immune-modulatory effects, especially via suppression of release of TNF and IL6, especially in macrophages.

Evidence against efficacy for hydroxychloroquine. Chloroquine and HCQ have been promoted as extremely broad anti-infective agents for decades. The reported effects include suppression of fungi, atypical bacteria, and viruses. Other than the effects on ACE2 glycosylation, the mechanisms invoked as evidence for efficacy against SARS-CoV-2 have also been invoked for a wide range of viruses. However, when chloroquine and HCQ have been studied in humans, neither agent has demonstrated consistent efficacy in clinical trials, including in HIV, influenza, hepatitis, and Dengue. In one trial, chloroquine resulted in increased viral replication in Chikungunya virus \[Roques et al, Viruses 2018 May 17;10(5)\] while in another hydroxychloroquine was associated with increased HIV viral load \[Paton et al, JAMA 2012 Jul 25;308(4):353\]. Expert opinion advises against HCQ for MERS, another serious coronavirus. An underpowered (n=30) study of HCQ in COVID-19 recently published in China did not demonstrate any clinical benefit \[Chen et al, J Zhejiang University, 2020 March 9\]. The long history of clinical failure despite in vitro anti-viral activity suggests a low probability of efficacy.

Rationale for Trial There is significant publicity concerning the potential use of HCQ in this pandemic, and many patients are seeking access to this unproven therapy. The ANZICS guidelines emphasize that novel treatments should be administered within clinical trials; the Surviving Sepsis Campaign guidelines (http://bit.ly/SSCCOVID-19) also affirm the lack of evidence to support the clinical use of (hydroxy)chloroquine. WHO guidance (https://apps.who.int/iris/bitstream/handle/10665/331446/WHO-2019-nCoV-clinical-2020.4-eng.pdf) also strongly affirms that "investigational anti-COVID-19 therapeutics should be done under ethically approved, randomized, controlled trials." The evidence thus strongly favors equipoise.

Arms:
arm 1: Participants randomized to the HCQ arm will receive HCQ 400mg po BID x 1 day, then 200mg po BID x 4 days. The drug dose (2.4 gm over 5 days) falls at the lower end of doses proposed in various international trials, but it has proven in vitro efficacy, with a ratio of lung tissue trough concentrations to the EC50 (effective concentration to suppress 50% of viral activity) of \>20. arm 2: Those randomized to placebo will receive a placebo to be taken on the same schedule.

Interventions: intervention 1: Hydroxychloroquine intervention 2: Placebo oral tablet
Intervention descriptions: intervention 1: HCQ 400mg po BID x 1 day, then 200mg po BID x 4 days intervention 2: Placebo to be taken on the same schedule as HCQ.

Protocol document:
Prot_000.pdf: 
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Protocol version 1.6 
 
 
 
 
 
CLINICAL STUDY PROTOCOL 
 
UTAH One (Understanding Treatment And Health in the Ongoing coroNa Epidemic): A 
Hydroxychloroquine Outpatient Study  
 
 
 
Principal Investigators 
 
Adam Spivak, MD 
Assistant Professor of Medicine 
Infectious Diseases 
University of Utah 
 
Rachel Hess, MD, MS 
Professor of Population Health Science and Internal Medicine 
University of Utah 
 
 
 
 
STATEMENT OF COMPLIANCE 
 
 
This study will be carried out in accordance with Good Clinical Practice (GCP) and information 
privacy/security as required by the following: 
 
• 
United States (US) Code of Federal Regulations (CFR) 45 CFR Part 46 (The Common 
Rule) 
• 
International Council on Harmonization (ICH) E6 (R2) 
• 
45 CFR Part 160 and Part 164, Subparts A, C, and E  
 
 
All key personnel (all individuals responsible for the design and conduct of this study) have 
completed Human Subjects Protection Training. 
 
 
 
 


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KEY ROLES 
 
 
Individuals:  
 
 
 
Principal Investigators:  Adam Spivak, Rachel Hess 
 
Data Coordinating Center Principal Investigators:  Tom Greene, Rich 
Holubkov 
 
Medical Monitor:  Brandon Webb 
 
 
Committees:   
Trial Executive Committee:  Adam Spivak, Rachel Hess, Tom Greene, 
Rich Holubkov, J. Michael Dean, Emily Spivak, Brandon Webb, Samuel 
Brown, Raj Srivastava, Ithan Peltan 
 
Trial Advisory Committee: Willard Dere, Mark Briesacher, Angela Dunn 
 
 
 
 
 
 
 
 


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1.0 
Definitions 
 
Definitions 
 
Eligible patients: All patients who meet all inclusion criteria and no exclusion criterion.  
 
Consented participants: All eligible patients who have completed the consenting process.  
 
Enrolled participants:  All participants who have been randomized. 
 
Intention-to-treat (ITT) Population: All enrolled participants, regardless of whether they 
received study drug or completed study procedures. This is the primary analysis population. 
 
Study day: The calendar day of enrollment (randomization) is study day zero. The next day is 
study day one, and so on.  
 
Assessment day: This corresponds to the survey instrument (day one survey is given on 
assessment day one). 
 
Study Drug Discontinuation: Participant chooses to discontinue study drug, for any reason.  
Other study procedures may continue as decision of participant. 
 
Study withdrawal: Participant discontinues study drug and does not wish to provide further 
study samples or data.  Data recorded up to the time of withdrawal will be included in the study 
analysis. 
 
Serious unexpected suspected adverse event (SUSAR). A serious adverse event or drug 
reaction that is unexpected and believed related to participation in study. 
 
 
 


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2.0 
Study Summary 
 
2.1 
Study title: Hydroxychloroquine for Outpatients with Confirmed COVID-19 (HCQ Trial).  
 
2.2 
Study objectives: Assess the efficacy and safety of hydroxychloroquine (HCQ) for 
reduction of viral shedding and hospitalization in outpatients with confirmed COVID-19.  
 
2.3 
Study hypothesis: Hydroxychloroquine is effective in reducing viral shedding and need 
for hospitalization in outpatients with confirmed COVID-19. 
 
2.4 
Study design: Phase 2, prospective, open-label, parallel group, randomized controlled 
trial 
 
2.5 
Inclusion criteria 
Inclusion Criteria for Randomized Group: 
• 
Patient age ≥18 years, competent to provide consent 
• 
Within 72 hours of positive nucleic acid test for SARS-CoV-2 
 
Inclusion Criteria for Household Contact Group: 
• 
Individual age ≥18 living in the same house as someone diagnosed with COVID, 
competent to provide consent 
 
2.6 
Exclusion criteria 
• 
Patient already prescribed chloroquine or hydroxychloroquine 
• 
Allergy to hydroxychloroquine  
• 
History of bone marrow or solid organ transplant 
• 
Known G6PD deficiency 
• 
Chronic hemodialysis, peritoneal dialysis, continuous renal replacement therapy or 
Glomerular Filtration Rate < 20ml/min/1.73m2 
• 
Known liver disease (e.g. Child Pugh score ≥ B or AST>2 times upper limit) 
• 
Psoriasis 
• 
Porphyria 
• 
Known cardiac conduction delay (QTc > 500mSec) 
• 
Concomitant use of digitalis, flecainide, amiodarone, procainamide, propafenone, or any 
other prescription medication known to prolong the QT interval 
• 
Seizure disorder 
• 
Prisoner 
• 
Weight < 45kg 
• 
Inability to follow-up – no cell phone or no address or not Spanish or English speaking  
• 
Receipt of any experimental treatment for SARS-CoV-2 (off-label, compassionate use, or 
trial related) within the 30 days prior to the time of the screening evaluation 
• 
Patient or another member of patient’s household has been already enrolled in this study. 
• 
History of ventricular arrhythmia 
 
2.7 
Sample size: The study will enroll up to approximately 200 participants in each arm (total 
400 participants).  
 
2.8 
Primary Endpoint:  


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• 
Duration of viral shedding, as defined by time from randomization to the first of two 
consecutive negative swabs, measured on days 1 - 14. 
 
2.9  
Interim Monitoring: 
Formal safety review by Data Safety Monitoring Board (DSMB) after 100, 200, and 300 subjects 
enrolled.  No interim efficacy analyses or monitoring. 
3.0 STUDY DESCRIPTION 
 
3.1 
Background 
COVID-19 is a pandemic illness caused by the SARS-CoV-2 virus and has a high mortality 
among hospitalized patients despite a benign course in the large majority of patients infected. 
Limited data are available from small outpatient studies and have not shown efficacy in 
preventing hospitalization.  Hydroxychloroquine (HCQ) and chloroquine have antiviral and 
immune-modulating effects1, but there are no data concerning their efficacy in reducing viral 
load and shedding in outpatients.   
 
3.1.1 Evidence supporting possible efficacy for hydroxychloroquine.  
In cell models, chloroquine both interferes with terminal glycosylation of the ACE2 receptor (the 
cell surface receptor by which SARS-CoV-2 enters human cells) and increases endosomal pH, 
which interferes (at least in vitro) with a crucial step in viral replication.1,2 HCQ is 5x more potent 
than chloroquine in a Vero cell model of SARS-CoV-2 infection.3 In independent experiments, 
chloroquine has confirmed in vitro activity against SARS-CoV-2.4 Additionally, HCQ has in vitro 
efficacy against SARS-CoV-1.5  According to news releases, an as-yet-unpublished set of case 
series in China (N reportedly 120) suggests the possibility of rapid viral clearance and low rates 
of progression to critical illness. In addition to in vitro anti-viral effects chloroquine and HCQ 
appear to have immune-modulatory effects, especially via suppression of release of TNF and 
IL6, especially in macrophages.1,7-10 
 
3.1.2 Evidence against efficacy for hydroxychloroquine. 
Chloroquine and HCQ have been promoted as extremely broad anti-infective agents for 
decades. The reported effects include suppression of fungi, atypical bacteria, and viruses. Other 
than the effects on ACE2 glycosylation, the mechanisms invoked as evidence for efficacy 
against SARS-CoV-2 have also been invoked for a wide range of viruses. However, when 
chloroquine and HCQ have been studied in humans, neither agent has demonstrated consistent 
efficacy in clinical trials, including in HIV, influenza, hepatitis, and Dengue.11 In one trial, 
chloroquine resulted in increased viral replication in Chikungunya virus [Roques et al, Viruses 
2018 May 17;10(5)] while in another hydroxychloroquine was associated with increased HIV 
viral load [Paton et al, JAMA 2012 Jul 25;308(4):353]. Expert opinion advises against HCQ for 
MERS, another serious coronavirus.12 An underpowered (n=30) study of HCQ in COVID-19 
recently published in China did not demonstrate any clinical benefit [Chen et al, J Zhejiang 
University, 2020 March 9]. The long history of clinical failure despite in vitro anti-viral activity 
suggests a low probability of efficacy. 
 
3.1.3. Rationale for Trial 
There is significant publicity concerning the potential use of HCQ in this pandemic, and many 
patients are seeking access to this unproven therapy. The ANZICS guidelines emphasize that 
novel treatments should be administered within clinical trials; the Surviving Sepsis Campaign 
guidelines (http://bit.ly/SSCCOVID-19) also affirm the lack of evidence to support the clinical use 


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Hydrochloroquine Outpatient Study 
 
UTAH One Protocol Version 1.6 
                
 
 
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of (hydroxy)chloroquine. WHO guidance 
(https://apps.who.int/iris/bitstream/handle/10665/331446/WHO-2019-nCoV-clinical-2020.4-
eng.pdf) also strongly affirms that “investigational anti-COVID-19 therapeutics should be done 
under ethically approved, randomized, controlled trials.” The evidence thus strongly favors 
equipoise.13  
 
3.2  
Study Design 
Phase 2, prospective, placebo-controlled, parallel group, randomized trial 
 
3.3  
Study Objective 
A novel coronavirus, SARS-CoV-2, is responsible for a rapidly spreading pandemic that has 
reached 160 countries, infecting over 500,000 individuals and killing more than 24,000 people. 
SARS-CoV-2 causes an acute and potentially lethal respiratory illness, known as COVID-19, 
that is threatening to overwhelm health care systems due to a dramatic surge in hospitalized 
and critically ill patients. Patients hospitalized with COVID-19 typically have been symptomatic 
for 5-7 days prior to admission, indicating that there is a window during which an effective 
intervention could significantly alter the course of illness, lessen disease spread, and alleviate 
the stress on hospital resources. 
 
There is no known treatment for COVID-19, though in vitro and one poorly controlled study have 
identified a potential antiviral activity for HCQ. The rationale for this clinical trial is to measure 
the efficacy and safety of hydroxychloroquine for reducing viral load and shedding in adult 
outpatients with confirmed COVID-19. 
 
3.4 
Study Hypothesis 
HCQ is effective in reducing viral shedding in outpatients with confirmed COVID-19.   
 
3.5  Primary endpoint 
• 
Duration of viral shedding, as defined by time from randomization to the first of two 
consecutive negative swabs, measured on days 1 - 14. 
 
3.6 Secondary endpoints 
• 
Average level of select COVID-19-attributable symptoms 
• 
Hospitalization within 14 days of enrollment. 
• 
Persistence of viral shedding on day 28. 
• 
Adult household contact viral acquisition 
 
4.0  
Study population 
Ambulatory patients for whom SARS-CoV-2 testing is obtained at University of Utah testing 
sites after evaluation via telehealth services or  by providers in University affiliated clinical 
facilities.  
 
4.1  
Screening 
Patients undergoing testing for SARS-CoV-2 will be informed of this actively enrolling 
interventional trial and provided with informed consent documentation (hard copy or electronic) 
at the time of testing. Patients will be asked if they would be interested in considering trial 
participation if their test is positive. Investigators will monitor test results of individuals who 
indicate interest in the trial and contact those with positive tests to verify eligibility and provide 
remote informed consent by telephone, electronic consent, or videoconference.  The consenting 


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process will be performed via a consenting mechanism that confirms the identity of the patient, 
provides access to the consent form, and obtains a signature to complete documentation, 
without requiring physical proximity of research staff and the study subject.  The informed 
consent documentation will include HIPAA authorization for access to the medical record. 
 
4.2  
Inclusion and Exclusion Criteria 
See sections 2.5 and 2.6. 
5.0 Study Procedures 
 
5.1 Intake medication review. 
 Prior to randomization, study personnel and/or clinical pharmacists will review medications 
being prescribed for patients on study to confirm eligibility. Study personnel will advise patients 
to contact the study team if any new medications are prescribed during the 5 day treatment 
course so that the medication may be reviewed for risk of prolonging QTc. 
 
5.2 Cardiac review.  
Prior to randomization, study personnel will review if patient has electrocardiograms (ECG) and 
will verify that prolongation of QTc has not been diagnosed clinically or on ECG. 
 
5.3 Randomization.  
After obtaining informed consent, participants will be randomized using variable block sizes 
stratified by patient age group (age ≤ 44, 45-59, 60-74, 75+ years).  The randomization system 
at the Data Coordinating Center will require entry of patient initials, date of birth and sex.  This 
will assure that patients do not attempt to enroll multiple times in order to secure active drug.   
 
5.4 Study drug.  
This is an open label, variable block randomized placebo controlled trial.  If a participant is 
admitted to the hospital at any time during the active treatment period, the clinical team will 
decide whether or not to continue study drug treatment during hospitalization. 
 
Participants randomized to the HCQ arm will receive HCQ 400mg po BID x 1 day, then 200mg 
po BID x 4 days3. The drug dose (2.4 gm over 5 days) falls at the lower end of doses proposed 
in various international trials, but it has proven in vitro efficacy, with a ratio of lung tissue trough 
concentrations to the EC50 (effective concentration to suppress 50% of viral activity) of >20.3   
 
Those randomized to placebo will receive a placebo to be taken on the same schedule. 
 
5.5 Study Assessments.  
Coordinators will obtain baseline information at the time of randomization.  This will include 
review of all medications being prescribed for patients on study. Study personnel will advise 
patients to contact the study team if any new medications are prescribed during the 5 day 
treatment course so that the medication may be reviewed for risk of prolonging QTc, or having a 
drug interaction with HCQ (see Appendix 3). 
 
Daily assessments (assessment days 1 through 15) will include review for hospitalization and 
current symptoms.  Daily assessments will also explicitly solicit occurrence of rash, symptomatic 
hypoglycemia, seizure, oxygen supplementation, nausea, vomiting, and impaired vision. Quality 
of life assessments will be made at baseline, day 28 - 2 days/+2 weeks, and six months - 1 


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week/+2 months, using the EQ-5D-5L, PHQ-9, GAD 7, and PLC 5. If the six-month survey is 
missed during the above outlined window, the study team may attempt to collect it for up to a 
year following the six-month timepoint.  
 
Participants will be taught how to perform self-collection of oral swabs for SARS-CoV-2 on 
assessment days 1 – 14 and 28 +/- 2 (considering day 1 as day of study drug delivery).  Oral 
swabs will not be required during hospitalizations, but patients will be asked to provide a swab 
on the day following discharge from the hospital, even if this occurs after day 28. These will be 
refrigerated after collection and collected by a courier associated with the study for transport to 
the central laboratory (ARUP) for testing. Training will be provided with written instructions, 
video, and discussion with the research coordinators. 
 
Phlebotomy will be performed at day 1, day 7 (+/-2 day),day 28 (+/-2 day) and 6 months- 1 
week/+2 months.  This will require personal protective equipment (PPE) for the phlebotomy-
certified research staff. Note that the 6 months blood draw is being added mid-study, after 
subjects have been enrolled, Therefore, already enrolled participants will be notified of the 6 
months blood draw, provided with a new copy of the consent form, and told that they do not 
have to participate in the 6 month blood draw. If the six-month blood draw is missed during the 
above outlined window, the study team may attempt to collect it for up to a year following the 
six-month timepoint.  
Blood samples will be used to assess the immune response to SARS-CoV-2, drug screening, 
investigation of viral biology, cardiac biomarkers, and development of diagnostic assays.  
Plasma and peripheral blood mononuclear cells (PBMCs) will be stored in the University of Utah 
Center for Clinical and Translational Science (CCTS) biospecimen repository.  If there is 
remaining sample after these analyses, they may be used to study other diseases. 
 
Six months after enrollment, study staff will verify subsequent hospitalizations and vital status of 
the participant.   
 
5.6 Household Contacts  
Household contacts 18 years or older will be asked to self-collect oral swabs in the same 
manner and same daily schedule as the study participant.  Provision of the oral swabs will be 
considered implied consent, waiving the need for consent documentation. 
 
5.7 Data collection.  
Research coordinators and/or investigators will collect data and record them on paper and/or 
electronic CRF provided by the Data Coordinating Center (DCC). Data quality will be monitored 
by clinical data managers at the DCC. Note that given concerns for contagion during the 
pandemic, coordinators will practice “no-touch” practices for data collection and entry.  
 
6.0 Analysis and interpretation of data.  
A formal statistical analysis plan (SAP) will be written and finalized before the conclusion of 
enrollment and prior to the beginning of data analysis. The principles of this SAP are outlined 
here. 
 
We note that in the unique circumstances of this trial setting, it is possible that information may 
become available that would lead to modifications of prespecified analysis.  A hypothetical 
example would be evidence from multiple global studies that a particular underlying condition is 
strongly associated with outcomes such as shedding or hospitalization rates in response to 
hydroxychloroquine.  In such circumstances, a modification to this study’s analysis plan could 


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be considered, if possible with the investigators blinded to the effect of the modification on the 
analysis, and in consultation with the DSMB.  If the statistical analysis plan were to be modified, 
the analytic plan would be updated, with the previous version retained, and the modification 
explicitly noted in the presentation of the trial results. 
 
The primary prespecified analysis for efficacy is a comparison of duration of viral shedding 
during the first 14 days after randomization between the two treatment arms. For each 
participant, this outcome will be defined as the number of days until an oral swab sample shows 
no shedding, as confirmed by a sample from the subsequent day. Thus, for example, a 
participant with their first negative samples on days 7 and 8 would be treated as having stopped 
shedding on Day 7. The requirement for confirmation will be waived for patients who are 
negative for shedding on Day 14.  
 
Due to the nature of the data collected over a 14-day interval, and uncertainty about the 
distribution of shedding duration and the resulting hazard function, our primary analysis will 
apply the stratified log-rank test to compare the distribution of shedding duration between the 
hydroxychloroquine and control groups, with administrative right censoring at day 14. The 
primary analysis will be conducted using a 2-sided α=0.05. The log-rank test will be stratified by 
the age group randomization stratum. The Efron approach will be used to account for tied 
shedding duration times. Kaplan-Meier curves will summarize the shedding time distributions in 
the two randomized groups.  
 
Special handling will be required in our primary analysis of shedding duration for periods in 
which patients are hospitalized because swabs will not be obtained during hospitalizations. In 
our primary analysis, we will apply a last value carried forward imputation approach during 
hospitalization, and assume continued viral shedding during hospitalizations for patients whose 
last pre-hospitalization assessment is positive. A sensitivity analysis will right censor follow-up 
on the day of hospital admission. These two analyses represent the range of plausible 
scenarios for shedding during hospitalization under the assumption that any association 
between hospitalization and shedding must be positive; i.e., conditional on past history, the risk 
of viral shedding on any given day is at least as large for hospitalized as for non-hospitalized 
patients. We expect a relatively small proportion of subjects to be hospitalized, limiting the 
impact of assumptions concerning shedding during hospitalizations on the primary analysis. 
Additional sensitivity analyses, including analyses in which the end date of shedding is modeled 
as a latent variable will be considered.  
 
Quantification of the magnitude of “treatment effect”, and indeed the interpretation of the trial 
results, will depend on the specific patterns of the shedding distribution.  For example, in the 
unexpected scenario where the cumulative incidence curves for the ending of shedding actually 
cross during the 14-day evaluation period, the treatment arm with lower 14-day shedding rate 
would likely be preferred regardless of any shorter-term benefit observed in the other arm.  
Assuming, however, that the assumption of proportional hazards is found to be consistent with 
the data, the effect of the treatment will be expressed as a hazard ratio with 95% confidence 
interval. We will also report the differences between the randomized groups in truncated mean 
shedding duration to 14 days and in median shedding duration with 95% confidence intervals 
based on estimates derived from Kaplan-Meier curves.  
 
The comparison of proportion of patients hospitalized by day 14 between the randomized 
hydroxychloroquine and placebo groups will be performed with a two-sided Mantel-Cochran-
Haenszel test stratifying by the age categories as used for randomization, with 2-sided 


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alpha=0.05.  In the unlikely event that some patients die within 14 days after randomization 
without being hospitalized, these patients will be assigned to the hospitalization category in the 
analysis. Results will be presented as relative risks with 95% confidence intervals within each 
age stratum, and then pooled across strata. 
 
The average symptom level for assessment days 1 through 15 will be compared between 
treatment groups, as described in the Statistical Analysis Plan. The duration of COVID-19 
attributable symptoms through assessment day 15 will be summarized graphically across 
evaluation time points using Kaplan-Meier curves, and compared between randomized groups 
by applying the log rank test with stratification by the age randomization strata.  Participants 
who are hospitalized by assessment day 15 will be treated as having symptoms each day they 
are in the hospital. Follow-up time will be right censored at assessment day 15  
 
 
Our main analysis of adult household contact viral acquisition will be restricted to households 
with at least 2 adults for which no other adult besides the index study subject tests positive for 
COVID-19 at baseline. We will evaluate the effect of the hydroxychloroquine intervention on the 
risk of adult household viral acquisition by applying a Mantel-Cochran-Haenszel test stratifying 
by the randomization age categories and total number of adults within the household. Results 
will be presented as relative risks with 95% confidence intervals within each stratum, and then 
pooled across strata. A secondary analysis will assess the effect of treatment arm on rate of 
household viral acquisition rates averaged across all adults within the household by using a 
modified Poisson regression model incorporating correlation between participants in the same 
household, and controlling for age category and number of household members. 
 
The Statistical Analysis plan will detail additional analyses to be performed, including additional 
exploratory analysis as well as reporting of six-month outcomes among participants.   
 
Safety—already well established in studies of thousands of patients and in post-marketing 
surveillance—will be assessed through counts (proportions) of adverse events, with special 
attention to those listed in the package insert for hydroxychloroquine and careful investigation of 
any SUSARs.  As noted elsewhere in this protocol, safety data will be reported to the trial DSMB 
after every (approximately) 100 subjects have been enrolled in the trial. 
 
We do not anticipate applying formal stopping rules for either efficacy or futility in this trial. It is 
expected that the trial will remain open for up to 12 months, as the cyclic nature of the illness is 
not well understood.  Thus, if enrollment is not accomplished in this first wave of infection, the 
trial will not be suspended for futility, anticipating that subsequent waves may occur and enable 
full enrollment. 
 
6.1 Power and sample size analysis 
 
For a survival analysis, statistical power is readily expressed as a function of the number of 
events or event rate.  Table 2 below shows minimum increases in the hazard rate due to 
hydroxychloroquine detectable with 80% power, under different overall event rates by 14 days in 
the trial (calculations done in PASS assuming a conventional proportional hazards model with 
treatment arm as a single predictor, using a two-sided test with alpha=0.05).  With 400 enrolled 
participants, within our expected range of observed shedding rates, we expect the trial to have 
substantial power to detect a treatment effect if hydroxychloroquine increases the “successful 


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outcome” rate (at each timepoint) 1.4-fold or greater compared to the rates observed with 
placebo. 
 
 
Table 2. Minimum Increase in Hazard Rate Yielding 80% Power with 2-sided α=0.05, with 
N=400 randomized and evaluable subjects  
Assumed Overall 
Rate of No Shedding 
by 14 Days 
Minimum Hazard Ratio for “No Shedding” Outcome due to 
Hydroxychloroquine for which Power is 80%  
 
50% 
1.49 
55% 
1.46 
60% 
1.44 
65% 
1.42 
70% 
1.40 
75% 
1.38 
80% 
1.37 
 
  
 
 
7.0 Human Subjects Considerations. 
 
If a person without insurance is hospitalized for illness related to COVID-19, he or she is eligible 
for emergency Medicaid. This is beyond usual Medicaid eligibility and related to special rules 
related to COVID-19 illness. In 2019, the United States government issued new rules in the form 
of an executive order restricting the ability for immigrants who use public benefits, including 
Medicaid, from obtaining permanent residency. For many individuals who are not citizens or 
permanent residents of the United States—whether they are documented or not—this has made 
them reluctant to use public programs for which they are eligible, including Medicaid and 
COVID-19 related health benefits.  
 
In order to uphold principle of justice for all research participants, and to ensure that everyone 
who participates in this study will be appropriately respected for volunteering, we have 
partnered with U Health to offer participants who are uninsured and for whom completing 
paperwork regarding financial assistance would put them at risk in their judgement, the ability to 
receive the same level of care for COVID-19 as other people, should this be needed during their 
participation.  
 
All participants will be provided with information during their first visit by the study nurse that if 
they require hospitalization, are uninsured, and if in their judgement completing paperwork 
regarding financial assistance would put them at risk, they should, upon presenting to a U 
Health emergency department, identify themselves to the registrar and financial counselor. The 
financial counselor will identify their participation in the electronic health record and note this in 
the hospital billing system. 
 
Participants will be provided with a card identifying them as study participants and with 
instructions on it so as to remind them of what to do if they need to be hospitalized. They will 
also be provided with a handout to keep at home in case they are unable to speak to the 
financial counselor and hospital rules restrict visitors so the person contacted regarding the 
patient at home has the same information. 


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7.1 Institutional Review Board oversight.  
Institutional Review Board (IRB) approval is required and will be secured before any subject is 
enrolled at the study site. The DCC will not enable access to the electronic data capture or 
randomization systems until IRB documentation is received. 
 
7.2 Informed consent.  
Informed consent will be obtained from participants prior to randomization.  Proxy consent will 
not be used.  Informed consent will be obtained without an original paper signature because of 
the contagious nature of the virus.  Adult household contacts who agree to provide daily swabs 
are presumed to be consenting, and documentation of consent will be waived for them. 
 
7.3 Potential risks 
Risks associated with participation in this study include risks associated with HCQ 
administration and potential loss of confidentiality. 
 
The package insert for HCQ lists visual impairment, cardiac impairment, QTc prolongation, 
worsening of psoriasis or porphyria, proximal myoneuropathy, suicidality, and hypoglycemia. All 
of these risks are quite rare and where observed are seen after prolonged administration, 
generally in the range of years. While ocular examinations are recommended after a year (and 
for acute symptoms), routine ocular examinations have never been recommended for brief 
duration of therapy. While QTc prolongation has been described with HCQ, it is generally 
modest, and routine EKG monitoring is not normally practiced even during long-term 
administration of hydroxychloroquine. HCQ may be associated with prolongation of QTc.  We 
chose a conservative threshold of 500msec as an exclusion criterion after consultation with 
electrophysiology cardiologists. 
 
7.4 Mitigation of risks 
In order to mitigate the risk of prolongation of QTc, we have chosen a conservative exclusion 
threshold of 500 msec after consultation with electrophysiology cardiologists.  Daily 
assessments will specifically ask about the adverse events listed above on a daily basis.  Our 
eligibility criteria exclude patients with elevated risk of HCQ toxicity, and we have selected 
dosages in the lower end of the therapeutic range.  Further, treatment is restricted to 5 days.   
 
Risk of loss of confidentiality is mitigated by securing all paper materials used by coordinators 
for data collection, and IT security maintained at the DCC. Direct patient identifiers (names, 
contact information, medical record numbers) will not be recorded at the DCC, but will be 
secured at the study sites.  The study sites will maintain lists that correlate medical record 
numbers with study ID numbers recorded in the DCC electronic data capture system. 
 
7.5 Discontinuance of HCQ 
Patients may choose to discontinue HCQ for any reason, and HCQ will be discontinued if a 
known contraindication arises.  Study procedures should otherwise continue. This is not the 
same as withdrawal from the study.  
 
7.6 Withdrawal from study.  
Patients may withdraw from the study at any time. Data recorded up to the time of withdrawal 
will be included in the study analysis.   
 


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7.7 Protocol deviations and violations.  
The investigator will not implement any deviation from, or changes of the protocol without prior 
review and documented approval/favorable opinion from the IRB of an amendment, except 
where necessary to eliminate immediate hazard(s) to study subjects or research personnel,, or 
when the change(s) involves only logistical or administrative aspects of the trial (e.g., change of 
telephone number(s)). Protocol deviations will be reported to the DCC within 24 hours of the site 
becoming aware of the deviation. The study team will provide explanation of the deviation to the 
DCC.  The DCC will notify the IRB of protocol deviations that have potential impact on human 
subjects safety or trial integrity.  The investigator may implement a deviation from, or a change 
of, the protocol to eliminate immediate hazard(s) to trial subjects without prior IRB 
approval/favorable opinion. As soon as possible, the implemented deviation must be reported to 
the DCC, which will notify the medical monitor and the IRB.   
8.0 Adverse Events 
Patient safety is central to this study protocol. 
 
8.1 Adverse event reporting. Adverse events will be recorded from randomization through day 
14 or hospitalization, whichever occurs first. The following adverse events will be collected in 
the adverse event case report forms and entered into the DCC electronic data capture system:  
 
• 
Serious adverse events  
• 
Non-serious adverse events that are considered by the investigator to be related to 
study drug or study procedures or of uncertain relationship 
• 
Adverse events that lead to permanent discontinuation of the study drug. 
 
The following adverse events will be collected prospectively as part of the study-specific 
outcomes and do not require additional adverse event reporting with the DCC unless they meet 
criteria for being serious (defined below): 
 
• Rash 
• 
Symptomatic hypoglycemia 
• 
Seizure 
• 
Cardiac arrhythmias 
• 
Worsening requirement for oxygen supplementation and support  
• 
Nausea/vomiting 
• 
Impaired vision 
 
8.2 Serious Adverse Events  
All serious adverse events (SAE) will be reported to the DCC.  As per federal definitions 
(primarily in 21 CFR 312.32(a)), a serious adverse event is any adverse event that results in 
one of the following outcomes:  
 
• 
Death 
• 
A life-threatening event, one that places the subject at immediate risk of death (this does 
not include an event that, had it been more serious, would have placed the subject at 
immediate risk of death) 
• 
Prolonged inpatient hospitalization or rehospitalization  


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• 
Persistent or significant disability/incapacity, indicating a substantial disruption of a 
person's ability to conduct normal life functions (i.e., the adverse event resulted in a 
significant, persistent or permanent change, impairment, damage or disruption in the 
patient's body function/structure, physical activities and/or quality of life).  
 
• 
Important medical events that may not result in death, be life-threatening, or require 
hospitalization may be considered serious adverse events when, based upon 
appropriate medical judgment, they may jeopardize the patient and may require medical 
or surgical intervention to prevent one of the outcomes listed in this definition.  
 
SAEs must be reported to the DCC within 24 hours of becoming aware of the SAE.  This may 
be accomplished by telephone call or email and can be succinct notification. 
 
Investigators must assess serious adverse events for expectedness and relatedness.   
Expected SAE include known side effects of study drug as well as clinical events consistent with 
worsening of COVID, or consistent with pre-existing co-morbidities of individual patients.  
Relatedness must be assessed by an investigator, and is based on clinical judgment that the 
event is related to having participated in this study.  This is assessed as not related, possibly 
related, and related.  This information must be provided to the DCC within 48 hours of becoming 
aware of the SAE.  
 
Deaths from worsening of viral infection or underlying co-morbidities are expected, and do not 
automatically require expedited reporting.  Sudden deaths or deaths believed related to cardiac 
arrhythmias must be reported to the DCC within 24 hours of becoming aware of the death.  The 
DCC or medical monitor will report these deaths to the DSMB chair within 24 hours of 
notification.  As these are expected complications of study drug, these do not require expedited 
reporting to the FDA or IRB as described in the next paragraph. 
 
Serious adverse events that are unexpected and related to study participation must be reported 
to the FDA and the IRB within 7 days of the DCC becoming aware of the classification of the 
SAE.  The DSMB chair will also be notified.  All other SAE do not need to reported to the IRB or 
FDA.  All SAE will be tabulated by study arm and presented to the DSMB at its regular 
meetings. 
 
 
 
8.3 Unanticipated Problems  
Investigators must also report Unanticipated Problems associated with the study drug or study 
procedures to the DCC within 24 hours. An unanticipated problem is any incident, experience, 
or outcome that meets all of the following criteria:  
• 
Unexpected, in terms of nature, severity, or frequency, given the research procedures 
that are described in the protocol-related documents, such as the IRB-approved 
research protocol and informed consent document; and the characteristics of the subject 
population being studied;  
• 
Related or possibly related to participation in the research. Possibly related means there 
is a reasonable possibility that the incident, experience, or outcome may have been 
caused by the procedures involved in the research; it is not intended to identify the event 
as possibly related imply because it cannot be proven to be unrelated.  


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• 
Suggests that the research places subjects or others at a greater risk of harm (including 
physical, psychological, economic, or social harm) than was previously known or 
recognized.  
 
9.0 Miscellaneous Topics 
 
9.1 Reporting and Regulatory Compliance. 
 All relevant information will be reported in compliance with relevant regulations and Good 
Clinical Practice. This is not a registrational trial but will be performed under an IND exemption. 
 
9.2 ClinicalTrials.gov registration. 
This trial is registered with ClinicalTrials.gov (NCT04342169).  Updates to the Clinicaltrials.gov 
entry will be made in compliance with relevant regulations.  
 
9.3 Records retention. Study sites will arrange for the retention of raw data as per institutional 
protocol but for a minimum of 3 years after publication of the primary paper. All data and 
documents will be made available when requested by appropriate authorities. Records will be 
maintained to verify the existence of each patient in the study, as per standard protocol. 
 
 


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APPENDICES 
 
Appendix 1. Visit schedule 
 
 
 
Visit 
Procedure 
Baseline 
Daily 
through 
15 days 
14 
days 
Hospitalization  
28 
days 
6 
months 
Screening procedures 
X 
 
 
 
 
 
Informed consent  
X 
 
 
 
 
 
Data collection 
X 
X 
X 
X 
X 
X 
Active Adverse Event review 
 
X 
 
 
 
 
Passive Adverse Event review 
 
 
 
X 
 
 
EQ-5D-5L, PHQ-9, GAD 7, PLC 5 
X 
 
 
 
X 
X 
EQ-5D-5L: EuroQol-5 dimensions-5 level; PHQ-9: Patient Health Questionnaire-9, GAD 7: Generalized 
Anxiety Disorder 7-item scale, PLC 5: PTSD Checklist for DSMB-5 scale 
 
 
 


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Appendix    2: Biospecimen collection schedule:  
 
 
 
 
Day 
0
1
2
3
4
5
6
7
8
9
10
11
12
13
14
28
6 months
COVID-19 PCR swab positive
1
Inclusion / Exclusion criteria
1
Informed consent discussion / signatures
1
1
Adverse event review
1
1
1
1
1
1
1
1
1
1
1
1
1
1
1
Surveys (EQ-5D-5L / PHQ-9 / GAD7 / PLC5)
1
1
1
HCQ or Placebo administration
1
1
1
1
1
Research Specimen Collection
Oropharyngeal self-swab for SARS-CoV-2
1
1
1
1
1
1
1
1
1
1
1
1
1
1
1
Household contact over age 18 oropharyngeal 
self-swab for SARS-CoV-2
1
1
1
1
1
1
1
1
1
1
1
1
1
1
1
Peripheral blood (PBMC / plasma biobank)
1
1
1
1
Study Events
40 mL (five yellow top 
ACD tubes)
HCQ or Placebo


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Appendix 3. Potential medication interactions with hydroxychloroquine 
 
A. Medications considered contraindicated, which if ordered on a subject during the 5-day 
study period will prompt study personnel or clinical pharmacists to discuss with treating 
clinicians whether stopping the study drug is appropriate or whether this medication 
could be stopped or substituted: amiodarone; cimetidine; dofetilide; phenobarbital; 
phenytoin; sotalol. 
 
B. Medications considered to present a potential interaction with hydroxychloroquine, which 
if ordered on an inpatient during the 5-day study period, will prompt study personnel or 
clinical pharmacists to discuss with treating clinicians the risk-benefit assessment of this 
medication and potential need for additional monitoring: ampicillin, antacids, 
cyclosporine, digoxin, flecainide, mefloquine, methotrexate, mexilitine, rifampicin, 
rifapentine. 
 
 


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REFERENCES 
 
 
1. 
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Vincent MJ, Bergeron E, Benjannet S, et al. Chloroquine is a potent inhibitor of SARS 
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Wang M, Cao R, Zhang L, et al. Remdesivir and chloroquine effectively inhibit the 
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Biot C, Daher W, Chavain N, et al. Design and synthesis of hydroxyferroquine 
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Gautret P, al e. Hydroxychloroquine and azithromycin as a treatment of COVID-19: 
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Dijkmans B, Verweij C. Chloroquine and hydroxychloroquine equally affect tumor 
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Picot S, Peyron F, Vuillez J-P, Polack B, Ambroise-Thomas P. Chloroquine inhibits 
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Jang C-H, Choi J-H, Byun M-S, Jue D-M. Chloroquine inhibits production of TNF-α, IL-
1β and IL-6 from lipopolysaccharide-stimulated human monocytes/macrophages by different 
modes. Rheumatology (Oxford) 2006;45:703-10. 
10. 
Sperber K, Quraishi H, Kalb T, Panja A, Stecher V, Mayer L. Selective regulation of 
cytokine secretion by hydroxychloroquine: inhibition of interleukin 1 alpha (IL-1-alpha) and IL-6 
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Akpovwa H. Chloroquine could be used for the treatment of filoviral infections and other 
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Mo Y, Fisher D. A review of treatment modalities for Middle East respiratory syndrome. J 
Antimicrob Chemother 2016;71:3340-50. 
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Cortegiani A, Ingoglia G, Ippolito M, Giarratano A, Einav S. A systematic review on the 
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Walkey AJ, Wiener RS. Macrolide antibiotics and survival in patients with acute lung 
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Kawamura K, Ichikado K, Takaki M, et al. Efficacy of azithromycin in sepsis-associated 
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Simonis FD, de Iudicibus G, Cremer OL, et al. Macrolide therapy is associated with 
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Postma DF, Van Werkhoven CH, Van Elden LJ, et al. Antibiotic treatment strategies for 
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Ray WA, Murray KT, Hall K, Arbogast PG, Stein CM. Azithromycin and the risk of 
cardiovascular death. N Engl J Med 2012;366:1881-90. 
19. 
Robinson KA, Dennison CR, Wayman DM, Pronovost PJ, Needham DM. Systematic 
review identifies number of strategies important for retaining study participants. J Clin Epidemiol 
2007;60:757-65. 


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Hydrochloroquine Outpatient Study 
 
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20. 
Tansey CM, Matte AL, Needham D, Herridge MS. Review of retention strategies in 
longitudinal studies and application to follow-up of ICU survivors. Intensive Care Med 
2007;33:2051-7. 
21. 
Hunt JR, White E. Retaining and tracking cohort study members. Epidemiol Rev 
1998;20:57-70. 
22. 
Hall EA, Zuniga R, Cartier J, et al. Staying in touch: a fieldwork manual of tracking 
procedures for locating substance abusers in follow-up studies. 2d ed. Los Angeles: UCLA 
Integrated Substance Abuse Programs; 2003. 
23. 
Ginde AA, Brower RG, Caterino JM, et al. Early High-Dose Vitamin D3 for Critically Ill, 
Vitamin D-Deficient Patients. N Engl J Med 2019. 
24. 
Colantuoni E, Scharfstein DO, Wang C, et al. Statistical methods to compare functional 
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25. 
Novack V, Beitler JR, Yitshak-Sade M, et al. Alive and Ventilator Free: A Hierarchical, 
Composite Outcome for Clinical Trials in the Acute Respiratory Distress Syndrome. Crit Care 
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26. 
Canner PL. Covariate adjustment of treatment effects in clinical trials. Control Clin Trials 
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27. 
Hernandez AV, Steyerberg EW, Habbema JD. Covariate adjustment in randomized 
controlled trials with dichotomous outcomes increases statistical power and reduces sample 
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28. 
Lingsma H, Roozenbeek B, Steyerberg E. Covariate adjustment increases statistical 
power in randomized controlled trials. J Clin Epidemiol 2010;63:1391; author reply 2-3. 
29. 
Ciolino JD, Martin RH, Zhao W, Jauch EC, Hill MD, Palesch YY. Covariate imbalance 
and adjustment for logistic regression analysis of clinical trial data. J Biopharm Stat 
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30. 
National Bioethics Advsory Committee. Research involving Persons with Mental 
Disorders that May Affect Decision-making Capacity. Rockville, MD: U.S. Government Printing 
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31. 
Compliance Determination Letters. 2002. at http://ohrp.osophs.dhhs.gov/detrm_letrs/.) 
 

SAP_001.pdf: 
Statistical Analysis Plan
Protocol Title: UTAH One (Understanding Treatment And Health in the Ongoing coroNa
Epidemic): A Hydroxychloroquine Outpatient Study; formerly Hydroxychloroquine for Out-
patients with Conﬁrmed COVID-19 (HCQ Trial)
Protocol Version and Eﬀective Date: v 1.6; July 6, 2021
Past Protocol Versions and Eﬀective Dates: First (misnumbered as 0.1 but should have been
1.00, April 10, 2020); 1.01 (April 17, 2020); 1.2 (April 27, 2020); 1.3 (May 13, 2020); 1.4
(June 16, 2020); 1.5 (September 24, 2020)
SAP Authors: Bradley Barney, PhD; Tom Greene, PhD; Richard Holubkov, PhD (with
contributions from Cody Olsen, MS, and reusing some DCC language)
SAP Version and Date: v1.4; February 23, 2022
SAP Version 1.3 Date: July 30, 2021 (created); Eﬀective August 3, 2021
SAP Version 1.2 Date: May 26, 2021 (created); Eﬀective May 27, 2021
SAP Version 1.1 Date: February 19, 2021 (created); Eﬀective March 8, 2021
SAP Version 1.0 Date: November 18, 2020 (created); Eﬀective December 1, 2020
CONFIDENTIAL
i


UTAH One: Statistical Analysis Plan
Page ii
Approvals:
Approved By:
Adam Spivak
Principal Investigator
Date
Rachel Hess
Principal Investigator
Date
Richard Holubkov
Trial Statistician
Date
Tom Greene
Trial Statistician
Date
Bradley Barney
Trial Statistician
Date
February 23, 2022
v1.4
CONFIDENTIAL
"EBN.4QJWBL.%
'FCSVBSZ
R
h l H
Rachel Hess, MD, MS
23 February 2022
Richard Holubkov, PhD
March 7 2022
March 10, 2022
Tom Greene, PhD
Tom Greene
Bradley Barney
Bradley J. Barney, PhD
March 10, 2022
Greene
Greene
Digitally signed by Bradley J. Barney, PhD 
Date: 2022.03.10 16:03:46 -07'00'


UTAH One: Statistical Analysis Plan
Page iii
Partial List of SAP Revisions:
Batch of changes for preliminary version of 24 May 2020
• Section 2.1.3: Changed a secondary outcome from duration of symptoms to average
symptom level. Moved the duration of symptom outcomes to an exploratory outcome.
• Section 5.4: Added descriptions pertaining to the average of COVID-19 attributable
symptoms. Added information to derive EQ-5D-5L VAS and index measure outcomes.
• Section 7.4.5: Revised analyses to incorporate baseline and Day 28 assessments, and
detailed the statistical analyses of the two outcomes.
• Section 7.4.6: Revised analyses to incorporate baseline and Day 28 assessments.
• Section 7.4.7: Revised analyses to incorporate baseline and Day 28 assessments.
• Section 7.4.8: Revised analyses to incorporate baseline and Day 28 assessments
Batch of changes for preliminary version of 30 June 2020
• Section 4.2.6: Modiﬁed deﬁnition of per-protocol eﬃcacy population (which doubles
as the principal safety population) to require at least 80% of the assigned pills/tablets.
• Section 2.1.3: Included two additional core symptoms (chills and diarrhea).
• Section 5.4: Modiﬁed deﬁnition of symptom duration and start/end dates. Restricted
to individuals symptomatic at baseline. Applied censoring at 15 days rather than using
symptom assessments through 28 days because there is not daily symptom information
after Day 15 (diﬀerent from protocol). Added details for post-imputation processing
of certain values for participants missing some assessments because they were deceased
when the assessment was to have been administered.
• Section 7.4: Removed analysis of numerical viral shedding values.
• Section 7.4.5: Updated imputation approach and analytical methods of the EQ-5D-5L
assessments (and subsequent assessments).
Batch of changes for preliminary version of 16 July 2020
• Signature Page: Restricted to PIs and trial statisticians, removing the clinical data
manager line as this was deemed unnecessary.
• Section 2.1.3: Changed a secondary outcome from “Duration of viral shedding, mea-
sured on days 1 - 14 and 28” to “Persistence of viral shedding on day 28.”
The
secondary outcome had essentially been the primary outcome with one later measure-
ment and as such duration is not accurately captured beyond what is available in
the primary outcome. The replacement secondary outcome maintains complementary
status with the primary outcome and is straightforward.
February 23, 2022
v1.4
CONFIDENTIAL


UTAH One: Statistical Analysis Plan
Page iv
• Section 4.2.4: Changed the statement that the ITT population “will be the primary
population for most eﬃcacy and safety analyses” to “will be the primary population
for eﬃcacy analyses.”
• Section 4.2.5: Changed wording re sensitivity analyses of eﬃcacy outcomes on the dITT
population from stating they will be conducted to stating they may be conducted.
Also clariﬁed that the dITT population is restricted to subjects who are delivered the
assigned study drug.
• Section 4.2.7: Deﬁned the safety population to require only one pill/tablet of the
delivered study drug to be administered, and that the arms for the SAFETY population
are based on what was delivered rather than what was assigned, in case there are
discrepancies. Previously the principal safety population for adverse events not already
described as an outcome was the per-protocol population.
• Section 5.4: Added deﬁnition of assessment days and deﬁned how to handle drug days
and assessment days if the anchoring events (drug delivery and assessment surveys) are
not available. Corrected censoring explanation for symptom duration to censor on last
symptomatic day, as applicable. Added deﬁnition of comorbidity presence/absence.
• Section 7.1: Added the SAFETY population as a component of the CONSORT-like
diagram. Clariﬁed that footnotes may be used to describe some populations.
• Section 7.3.2: Modiﬁed to include all 15 daily assessments in deﬁning the univariate
average symptom level outcome. Further restricted imputation and analysis to indi-
viduals who are not known to have been hospitalized or died on or before DayA15,
and who have at least one day with a non-missing average symptom level for DayA1–
DayA15. Previous restriction had speciﬁed those not meeting the primary outcome or
died within 14 days.
• Section 7.3.3: Moved what had been described in Section 7.4 as Viral shedding at
DayD28 to this section. This reﬂects the substitution of a secondary outcome from
viral shedding duration through Day 28 to persistence of viral shedding on day 28.
• Section 7.4.1: Added a sensitivity analysis for symptom duration that assumes symp-
tom resolution on the ﬁrst asymptomatic day, regardless of subsequent symptom levels.
Also emphasized the departure from the originally speciﬁed outcome in the protocol
which also considered the Day 28 measurements.
• Section 7.4: Reinserted numerical viral shedding values as an exploratory outcome and
described a tentative analysis plan.
• Section 7.5: Stated when safety (rather than per-protocol) and intent-to-treat popula-
tions would be used for safety analyses.
Batch of changes for preliminary version of 22 July 2020
February 23, 2022
v1.4
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UTAH One: Statistical Analysis Plan
Page v
• Section 2.1.3: Explained the change from a secondary outcome of Duration of viral
shedding, measured on days 1-14 and 28 to Persistence of viral shedding on day 28.
• Sections 5.4, 7.3.3: Described when and how missing Day 28 viral shedding values will
be assumed positive or negative, with other values imputed unless the participant has
died on or before DayR + 30. Explained there is a window for obtaining the Day 28
swabs.
• Section 5.4: Adjusted the deﬁnition of the adult household acquisition variable to
replace “test” with “swab,” assuming only the outcome of study-associated swabs will
be systematically collected in the database. Also, changed from considering results
“at any time” to looking at the results of the collected swabs because it is unclear
that tests other than from non-study swabs will be available, and there is a bounded
interval for when study swabs are to be collected.
• Section 7.3.2: Made the restriction less narrow to not exclude subjects who were hospi-
talized or who died on or before DayA15. Described how the last value carried forward
approach will be used in conjunction with multiple imputation.
• Section 7.2.1: Clariﬁed that the restricted mean duration and median duration analyses
of the primary outcome will be stratiﬁed by age group. Explained how the conﬁdence
intervals will be created via nonparametric-bootstrap resampling and empirical per-
centiles.
• Section 7.4: Removed the viral shedding numerical outcome analysis paragraph (and
from the list in Section 5.4).
Batch of changes for preliminary version of 27 July 2020
• Section 5.4: Clariﬁed how assessment days after DayA1 are deﬁned. Also noted that
“swab days” are intended to align with drug-delivery days, and that like assessment
days, a window is allowed for the DayD28 measurements.
Batch of changes for preliminary version of 28 July 2020
• Section 5.4: Clariﬁed what to do if there are multiple daily averages on the same
calendar day or if there are multiple swabs on the same calendar day. Aﬀects the
deﬁnition of the viral shedding duration (the primary outcome), the average symptom
level (a secondary outcome), the persistence of viral shedding on day 28 (a secondary
outcome), and the symptom duration (an exploratory outcome).
• Section 5.4: Amended the deﬁnition of the primary outcome to clarify that swabs
after DayD14 are ignored when deﬁning the primary outcome, even for purposes of
conﬁrmation of an earlier negative result.
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• Section 5.4: Edited the ﬁrst sentences describing the persistence of viral shedding on
day 28 outcome to emphasize this is an outcome that replaced the originally speciﬁed
outcome of viral shedding duration from days 1-14, 28.
• Section 7.4: Added a note about a possible exploratory analysis for numerical viral
shedding measurements. The note was added to reconcile why the analysis of this
exploratory outcome is not described in the current version of the SAP, despite the
inclusion of such language in the original protocol.
Batch of changes for preliminary version of 29 July 2020
• Section 5.4: Deﬁned several distinct outcomes for adult household contact viral acqui-
sition. The main such outcome is now at the household level rather than at the person
level. Additional outcomes are at the person level, as a dichotomous outcome and as a
count outcome. These household contact acquisition outcomes, and the analysis meth-
ods applied to them, are still subject to change after consulting with an experienced
infectious disease modeling person and better understanding incoming data.
• Section 7.3.2: Clariﬁed Step 4 for post-processing of imputed values on hospitalized
days.
• Section 7.4.1: Inserted a missing word, “a,” in the ﬁrst sentence.
Batch of changes for preliminary version of 03 August 2020
• Section 5.2: Added: “When multiple imputation is employed, it will be performed
separately within each treatment arm if possible (by ITT arm for analyses of the ITT
population or subpopulations thereof, or, if necessary, by SAFETY arm for analyses
of the SAFETY population).”
• Section 7.3.2: Instead of including treatment as a variable in the imputation model,
speciﬁed that imputation will be by treatment arm.
• Section 7.3.2: Added the last paragraph to clarify that the principal analysis for the
average symptom level outcome is on the same set of subjects who are included in the
imputation model for this outcome.
• Section 7.3.3: Added to the imputation model for the viral shedding at Day 28 outcome
the following qualiﬁer for the inclusion of a treatment arm indicator: “(if imputation
is not already stratiﬁed by treatment arm)”.
Batch of changes for preliminary version of 07 November 2020
• Section 5.4: Changed text to assume that collected surveys/swabs pertain to the in-
tended day. As such removed text pertaining to assessments/swabs collected on the
same calendar day. (Supersedes changes from 28 July 2020.)
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• Sections 5.4 and 7.3.4: Clariﬁed for the adult household viral acquisition outcome that
it considers swabs from adult household contacts (rather than also considering swabs
from the index subject).
Batch of changes for preliminary version of 11 November 2020
• Section 5.4: Changed text to assume that collected surveys/swabs pertain to the in-
tended day for surveys, but to the participant-reported collection date for swabs. (Su-
persedes changes from 07 November 2020.) Added speciﬁc language about permissible
windows for surveys and for “day 28” swabs.
Batch of changes for preliminary version of 13 November 2020
• Section 5.4: Removed redundant language about swab collection dates being per par-
ticipant report, and corrected one reference to swabs that was supposed to refer to
surveys.
Batch of changes for Version 1 of 18 November 2020
• Updated study name/acronym and latest protocol version number/date.
• Removed all references to the SAP version being preliminary.
• Section 7.5.2: Changed language from closed session of DSMB meetings being “ten-
tatively planned for after approximately 100, 200, 300, and all subjects have been
enrolled” to “tentatively planned for after approximately 100, 300, and all subjects
have been enrolled.” Within the last week, the DSMB meeting scheduled for Novem-
ber 30th was postponed. Nearly 200 were enrolled as of the accompanying October
screen cutoﬀdate that would have been used if the meeting were to take place Novem-
ber 30th. With a new tentative target of mid- to late-January for the next DSMB
meeting, enrollment may be near 300.
Batch of changes for Version 1.1
• Section 5.4: Removed “, with the day 28 wording asking about the past two weeks”
because the day 28 symptom assessment asks about one day, not for the past two
weeks.
• Section 5.4:
Corrected the erroneous statement about the symptom duration ex-
ploratory outcome: “Therefore, the DayA15 assessments asking about symptom levels
over the previous two-week period will be ignored.” It now states, “Therefore, the
DayA28 symptom assessments will be ignored when determining symptom duration.”
• Section 7.5.2: Removed the phrase “(tentatively planned for after approximately 100,
300, and all subjects have been enrolled)” in describing the closed session of DSMB
meetings. The change of 18 November 2020 to remove “200” as a planned frequency
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should not have been made as the meeting postponement was not intended to reduce
the number of meetings, but rather to delay one meeting. The DSMB charter describes
the ability of the DSMB to have ﬂexibility in the frequency of meetings. The removed
text is not necessary for the SAP, regardless.
• Corrected page headers to state “Statistical Analysis Plan” instead of “Provisional
Draft of Statistical Analysis Plan for Internal Review.”
• Cover page: Noted that September 24, 2020 is the eﬀective date (in this case, also
the IRB approval date) for version 1.5 of the protocol. Added prior protocol version
numbers and eﬀective dates. Added the eﬀective date for version 1.0 of the SAP.
Batch of changes for Version 1.2
• Cover page: Added approval date for SAP Version 1.1 and creation date for SAP
Version 1.2.
• Sections 5.4 and 7.3.4: Amended the adult household contact viral acquisition outcomes
to be based on collected swabs through DayD14 for the main analysis. Previously these
outcomes had been deﬁned using all collected swabs. Noted additional exploratory
analyses that modify the revised outcomes to also include the Day 28 swabs, as before.
• Section 5.4.
Changed “will” to “may” in the following excerpt to make the out-
come optional: “Another person-level outcome will may count the number of study-
administered positive swabs from the person and the number of study-administered
swabs with a result . . .”
• Section 5.4: Added a missing closing parenthesis to the deﬁnition of the EQ-5D-5L
VAS.
Batch of changes for Version 1.3
• Cover page: Added approval date for SAP Version 1.2 and creation date for SAP
Version 1.3. Updated the current protocol version to 1.6 and added its eﬀective date.
Noted use of some DCC language and contributions from Cody Olsen.
• Section 2.1.3: Instead of stating the protocol will be amended, noted that the protocol
has been amended to include persistence of viral shedding at Day 28 as a secondary
outcome.
• Edited the wording and deﬁnition of the primary outcome to better align with the
protocol. Changes are noted with strikethrough (deleted text) and italics (new text)
in the following:
– Section 2.1.2: “The primary outcome is duration of viral shedding, as deﬁned
by days from randomization to the ﬁrst of two consecutive negative swabs, mea-
sured on days 1–14 through 14 days after randomization (formally deﬁned in
Section 5.4).”
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– Section 5.4: “Duration of viral shedding (until DayD14 through 14 days after
randomization, i.e., DayR + 14): this is an integer outcome which is deﬁned
as (Date of ﬁrst sustained negative swab (ignoring any swab that was not in
the interval DayR + 1 through DayR + 14, inclusive) - DayR).
The date of
ﬁrst sustained negative swab is the ﬁrst day with a negative swab followed by
the next available day’s swab being negative. The requirement for conﬁrmation
will be waived for patients who are negative for shedding on DayD14 DayR +
14. If no more positive swabs nor negative swabs are available by DayD14 by
DayR + 14 following a negative swab, the date of the negative swab will be
considered conﬁrmed for the primary analysis (using the last-observation-carried-
forward approach). If the ﬁnal swab from on or before DayD14 DayR+14 which
has a positive or negative result is positive and there were not two preceding
consecutive negative swabs, the duration will be considered to be right censored
on the day of the positive swab.”
– Section 7.2: “Due to the nature of the data collected over the DayR–(DayR+14)
DayD14 interval, and uncertainty about the distribution of shedding duration and
the resulting hazard function, our primary analysis will apply the stratiﬁed log-
rank test to compare the distribution of shedding duration between the hydrox-
ychloroquine and control groups, with administrative right censoring at DayD14
DayR + 14.”
– Section 7.2.1: “For example, in the unexpected scenario where the cumulative inci-
dence curves for the ending of shedding actually cross during the DayR–DayD14
(DayR + 1) to (DayR + 14) evaluation period”.
• Section 5.4: Edited the wording and deﬁnition of a secondary outcome to better align
with the new deﬁnition of the primary outcome: “The protocol originally speciﬁed a
secondary outcome of duration of viral shedding for days 1–14 and 28. Because the
primary outcome is viral shedding through Day 14 from DayR+1 through DayR+14,
the secondary outcome of persistence of viral shedding on Day 28 is substituted for
duration through Day 28; there is limited precision between Days 15 and 28. The
deﬁnition of the persistence of viral shedding on Day 28 outcome relies heavily on the
Day 28 swab and is limited to those who have a test result for the Day 28 swab or
who are not known to have died on or before DayR + 30 (there is a ±2 day window
for collecting the Day 28 swab). If the Day 28 swab result is known, the result will be
used to deﬁne the outcome (“yes” if positive, “no” if negative). Otherwise, subjects
with a conﬁrmed cessation of viral shedding by Day 14 when considering daily swab
results from DayR + 1 to DayR + 25, inclusive (with the requirement for conﬁrmation
waived if the latest available daily result in this interval is negative), and a missing Day
28 value will be assumed to be negative on Day 28; otherwise subjects hospitalized on
any of the days DayR+26–DayR+30 with a missing Day 28 value will be assumed to
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be positive on Day 28; otherwise, multiple imputation will be performed as described
in Section 7.3.3.”
• Edited the wording and deﬁnition of another secondary outcome to better align with
the new deﬁnition of the primary outcome.
– Section 5.4: “Adult Household Contact Viral Acquisition This outcome
will be analyzed for households with at least two adults for which no other adult
besides the index study subject is positive for COVID-19 at baseline and for which
the index study subject is in the ITT population. This binary outcome will be
at the household level and will be a “yes” if there is a positive swab by one or
more adult household contacts for any of the study-administered swabs through
DayD14 (i.e., not including Day 28 swabs) from days DayR + 1 to DayR + 14,
inclusive.
If there are no positive swabs but at least one negative swab, the
outcome will be a “no;” otherwise it will be missing. For some additional analyses,
an analogous outcome will be deﬁned at the person level for each non-index adult
from a household for which no other adult besides the index study subject is
positive for COVID-19 at baseline and for which the index study subject is in
the ITT population.
Another person-level outcome may count the number of
study-administered positive swabs from the person and the number of study-
administered swabs with a result (e.g., as an oﬀset in a Poisson regression model),
again through DayD14 from days DayR + 1 to DayR + 14, inclusive.
– “As exploratory outcomes, the deﬁnitions in the previous paragraph will also
include the Day 28 swabs (i.e., all study-administered swabs). study-administered
swabs after DayR + 14 through DayR + 30, if available.”
– Section 7.3.4: “The analyses in this paragraph will be conducted twice, once when
using the principal version of the outcomes (i.e., using swabs collected through
DayD14) from DayR + 1 to DayR + 14, inclusive) and once when using the
additional exploratory versions of the outcomes (i.e., using all collected swabs,
and therefore also including Day 28 swabs from DayR + 1 to the Day 28 swabs,
inclusive).”
• Section 4.2.4: Added a restriction to the ITT population: “The Intention-to-Treat
(ITT) population consists of all enrolled subjects who were randomized before being
administered study treatment” and an accompanying footnote: “After enrollment had
ended, study statisticians became aware that due to a participant mix up, an unenrolled
person was administered study treatment meant for somebody else, and that after this
was initially discovered by study staﬀ, the person was consented to the study (even
though ineligible) and randomized to a treatment arm. However, because the treatment
had already been administered, this person is not considered to be in the ITT popula-
tion because there did not seem to have been an intention to follow-through on a post
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hoc randomization. This individual is included in the safety population for the arm
corresponding to the administered treatment.”
• Section 4.2.7: Added a clariﬁcation to the SAFETY population: “The safety pop-
ulation (SAFETY) consists of all ITT subjects who are administered at least one
pill/tablet of the delivered study drug (HCQ or placebo). If the delivered study drug
diﬀers from the randomly assigned study drug, analysis of the safety population by
arm will be according to drug delivered rather than drug assigned. In addition, a post-
hoc decision was made to include one person who was erroneously administered study
treatment before consenting/randomization due to a participant mix up, so although
this individual will be omitted from the study’s ITT-based analysis for the primary
manuscript, the person will still be considered to be in the safety population for the
treatment arm that corresponds to the delivered study treatment.”
• Section 5.4: Resolved an inconsistency in the truncation day for an exploratory out-
come. “Post-randomization hospitalizations on or before day of study drug delivery,
up to 14 days post-randomization (truncated at DayR + 13): this outcome will be
assessed for the entire ITT population. This is ‘yes’ if a hospitalization (or death)
is documented to have occurred after the time of randomization and on orbefore the
earlier of the day of drug delivery (DayD1) or (DayR+14) (DayR + 13). This is
‘no’ otherwise, assuming an absence of documentation of hospitalization/death in the
medical chart is ‘no.’”
• In keeping with the ﬂexibility of DSMB meeting frequency, made the following edit to
Section 6.1: “DSMB meetings to review safety data are scheduled for after approximately
100, 200, 300, and all patients have enrolled as desired by the DSMB, as described in
the DSMB charter.”
• Protocol version 1.6 expanded changed the windows for surveys at Day 28 and at 6
months. Induced changes to the SAP use the union of the windows and SAP edits are
noted:
– Section 5.4: “Note that while 28-day symptom and quality of life assessments
will be considered to be on DayA28, there is an allowed ±2 day −2 day/+2 week
window for when they occur. Likewise, the 6-month symptom and quality of life
assessments for analysis purposes will use have a ±2 week −2 week/+2 month
window... Because swabs are intended to be delivered along with study
drug, the drug delivery date will be assumed to correspond to swab
delivery date, with the ﬁrst swab to be collected on DayD1.
There
is likewise a window permitted for the Day 28 swab, although it is
narrower: DayR + 26 to DayR + 30, inclusive.
– “Participants may complete surveys late (e.g., slow response by email) or dates
may be incorrectly entered that suggest assessments were done early. Additionally,
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surveys may be completed one day late by phone. It will be assumed that answers
to any survey submitted 1 day before or after the intended day for the survey will
be treated as the intended day. For example, if the day 4 and day 5 assessments are
each completed by email four days after DayD1, it will be assumed that the day 4
responses pertain to DayD4 and the day 5 responses pertain to DayD5. However,
surveys submitted more than one day before or after the intended day will not be
analyzed (except for baseline surveys, which have a longer window because they
may be done any day between randomization and the study treatment delivery,
inclusive, and day 28 surveys, which have a ±2day −2 days/+2 weeks window,
and 6 month surveys, with a window of −2 weeks/+2 months). Swabs will be
analyzed based on the collection date reported by the participant, which may not
necessarily match the day on the swab label. If multiple swabs from a participant
have the same participant-reported collection date but diﬀerent results, a positive
result will supersede a negative result, and a negative result will supersede an
invalid or indeterminate result. If collected swab dates are clearly erroneous (e.g.,
before day of randomization), the associated swabs will be ignored. If the “day
28” a swab was collected within ±2 days of day 28 DayR + 28, or on a day
that coincides with any of days 1-14, it will be used regarded as a Day 28 swab;
otherwise, it will be treated as missing. It will also be assumed swab specimens
were collected on the intended day.” (The ﬁnal sentence was deleted because it is
confusing given the preceding language–it is assumed swabs were collected on the
reported day, which is not necessarily the intended day.)
• Section 7.3.4: Deleted the redundancy in “rate of household viral acquisition rates”.
• Section 7.5.2: Corrected subject-verb disagreement to state “Formal statistical analysis
analyses of adverse events is not planned”.
• References: Corrected two instances of an author surname from “Lwe” to “L¨owe”.
Batch of changes for Version 1.4. Other than one inconsequential update on 23 Feb 2022
explicitly noted below, decisions below drafted and preliminarily approved by subset of
statistical team 15–16 Feb 2022, approved by statistical team (BB, CO, RH, TG) on or
before 23 Feb 2022, and then proposed to study PIs on 23 Feb 2022.
• Cover page: Added approval date for SAP Version 1.3 and creation date for SAP
Version 1.4.
• Edited the handling of swabs on a hospitalized day, which aﬀects the primary outcome.
Background: The protocol had assumed swabs would not be collected during hospital-
ization and prescribed last value carried forward (LVCF), explicitly noting that positive
swab results would be assumed during hospitalization if the last pre-hospitalization
swab were positive. The SAP had noted swabs may not be collected during hospi-
talization and also speciﬁed LVCF imputation. Discussion with the statistical team
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after the primary manuscript had been drafted revealed diﬀerences of interpretation
among the statistical team as to the intent of the protocol (and SAP) language, but
with the expectation that results would be qualitatively similar with various reasonable
interpretations because of the small percentage of hospitalized participants and given
the swab data available from these participants. The statistical team decided after
extensive debate that all hospitalized days would be considered as having a positive
swab, even if there were no swab or a negative swab on such a day, and considered this
consistent with the original intent of the protocol and the convention already in the
SAP that on days with mixed swab results, a positive swab would supersede a neg-
ative swab. Thus, a hospitalization’s assumed positive swab results would supersede
any obtained swabs those days. The edits to the SAP are tracked below.
– Section 5.4: Special handling will be required in the primary analysis of shedding
duration for periods in which patients are hospitalized because swabs might not be
obtained during hospitalizations. In the primary analysis, the last-value-carried-
forward imputation approach will be applied during hospitalization, such that
continued viral shedding during hospitalization will be assumed for patients whose
last pre-hospitalization assessment is positive. A sensitivity analysis is described
in Section 7.2.1. The primary outcome was viral-shedding duration over the ﬁrst
two weeks. Because the protocol stipulated that swabs would not be obtained dur-
ing hospitalizations, and that positive results would be carried forward through
hospitalization, swab status was considered positive for all hospital days. Hospi-
talizations or swabs documented after day 15 (i.e., DayR + 14) were not used for
this outcome. Duration was considered to end on the ﬁrst day of two consecutive
negative swabs, allowing days without swab results between two negative swabs,
or on the last available swab result if negative. Without negative conﬁrmation,
the outcome was considered right-censored on the day of their last positive result
or day 15. In a sensitivity analysis, we treated hospitalized patients prior to day
15 without a prior conﬁrmed negative as right-censored on the day of hospital
admission or day 15.
– Section 7.2: The primary analysis of shedding duration will consider every hos-
pitalized day as having a positive swab result. apply a last-observation-carried-
forward imputation approach for missing swabs that would have been obtained
during hospitalization. See section 5.4. [23 Feb 2022 note: The sentence “See
section 5.4.” had been preserved in this description of changes, but removed from
Section 7.2 on 15 Feb 2022. This inconsequential discrepancy was unilaterally
resolved by BB on 23 Feb 2022, after the statistical team had approved of the
other decisions but before sending to the PIs, by adding this sentence back to
Section 7.2.]
• Section 5.4: Added the following paragraph: “Also of note is that we assumed all
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participants were positive on the day of randomization, even if a negative swab were
available. It was uncommon for a swab to be available on the day of randomization.”
The handling of day-of-randomization swabs had not been particularly emphasized
in the SAP, so this represents the decision that was implemented when obtaining
the already-viewed results. Study swabs were generally unavailable from the day of
randomization, and a study eligibility criterion required a suﬃciently recent positive
test for SARS-CoV-2. It seemed sensible to start all participants as being positive at
the time of randomization.
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Contents
Abbreviations . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
xvii
1
PREFACE
1
1.1
Purpose of SAP . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
1
1.2
Auxiliary/Other Documents . . . . . . . . . . . . . . . . . . . . . . . . . . .
1
2
STUDY OBJECTIVES AND OUTCOMES
2
2.1
Study Objectives . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
2
2.1.1
Primary Objective
. . . . . . . . . . . . . . . . . . . . . . . . . . . .
2
2.1.2
Primary Outcome(s) . . . . . . . . . . . . . . . . . . . . . . . . . . .
2
2.1.3
Secondary Outcome(s) . . . . . . . . . . . . . . . . . . . . . . . . . .
2
2.1.4
Exploratory Outcome(s) . . . . . . . . . . . . . . . . . . . . . . . . .
2
2.1.5
Safety Outcome(s)
. . . . . . . . . . . . . . . . . . . . . . . . . . . .
3
3
STUDY DESIGN AND METHODS
3
3.1
Overall Study Design . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
3
3.2
Method of Treatment Assignment and Randomization . . . . . . . . . . . . .
3
3.2.1
Delivery of Randomization and Emergency Backup . . . . . . . . . .
4
3.2.2
Handling of Incorrect Randomization in Study Analyses and Reports
4
3.3
Treatment Masking (Blinding) . . . . . . . . . . . . . . . . . . . . . . . . . .
4
3.4
Study Intervention Compliance
. . . . . . . . . . . . . . . . . . . . . . . . .
4
4
STUDY SUBJECTS AND ANALYSIS POPULATIONS
4
4.1
Eligibility
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
4
4.2
Populations . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
5
4.2.1
Screening Population . . . . . . . . . . . . . . . . . . . . . . . . . . .
5
4.2.2
Eligible Population . . . . . . . . . . . . . . . . . . . . . . . . . . . .
5
4.2.3
Consented Population
. . . . . . . . . . . . . . . . . . . . . . . . . .
5
4.2.4
Intention-to-Treat Population . . . . . . . . . . . . . . . . . . . . . .
5
4.2.5
Drug-delivered Intention-To-Treat
. . . . . . . . . . . . . . . . . . .
5
4.2.6
Per-Protocol Eﬃcacy Population
. . . . . . . . . . . . . . . . . . . .
6
4.2.7
Safety Populations
. . . . . . . . . . . . . . . . . . . . . . . . . . . .
6
5
GENERAL ISSUES FOR STATISTICAL ANALYSES
6
5.1
Analysis Software . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
6
5.2
Methods for Withdrawals, Missing Data, and Outliers . . . . . . . . . . . . .
6
5.3
Multiple Comparisons and Multiplicity . . . . . . . . . . . . . . . . . . . . .
7
5.4
Derived and Computed Variables
. . . . . . . . . . . . . . . . . . . . . . . .
7
5.5
Independent Review
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
13
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6
INTERIM ANALYSES
13
6.1
Frequency of and Timepoints for Interim Analysis . . . . . . . . . . . . . . .
13
6.2
Stopping Rules for Interim Eﬃcacy Analysis . . . . . . . . . . . . . . . . . .
14
6.3
Blinding in the Interim Analysis . . . . . . . . . . . . . . . . . . . . . . . . .
14
7
PLANNED ANALYSES
14
7.1
Description of Subject Characteristics . . . . . . . . . . . . . . . . . . . . . .
14
7.2
Primary Outcome Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . .
14
7.2.1
Additional Analyses of Primary Outcome . . . . . . . . . . . . . . . .
15
7.3
Secondary Outcome(s) Analyses . . . . . . . . . . . . . . . . . . . . . . . . .
16
7.3.1
14-day Hospitalization . . . . . . . . . . . . . . . . . . . . . . . . . .
16
7.3.2
Average of COVID-19 attributable symptoms
. . . . . . . . . . . . .
16
7.3.3
Persistence of Viral Shedding on Day 28
. . . . . . . . . . . . . . . .
17
7.3.4
Adult Household Contact Viral Acquisition . . . . . . . . . . . . . . .
18
7.4
Exploratory Outcomes Analyses . . . . . . . . . . . . . . . . . . . . . . . . .
18
7.4.1
Duration of COVID-19 attributable symptoms . . . . . . . . . . . . .
19
7.4.2
Six-month mortality
. . . . . . . . . . . . . . . . . . . . . . . . . . .
19
7.4.3
Six-month hospitalization
. . . . . . . . . . . . . . . . . . . . . . . .
19
7.4.4
Hospitalizations before DayD1
. . . . . . . . . . . . . . . . . . . . .
19
7.4.5
Quality of life (EQ-5D-5L Assessment) . . . . . . . . . . . . . . . . .
20
7.4.6
Six-month depression (PHQ-9 Total) . . . . . . . . . . . . . . . . . .
20
7.4.7
Six-month anxiety (GAD-7 Total) . . . . . . . . . . . . . . . . . . . .
20
7.4.8
Post-traumatic stress disorder (PCL-5 Total) . . . . . . . . . . . . . .
20
7.4.9
Additional Analyses for Time-to-event Outcomes
. . . . . . . . . . .
20
7.5
Safety Analyses . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
21
7.5.1
Formal Safety Outcome(s) . . . . . . . . . . . . . . . . . . . . . . . .
21
7.5.2
Adverse Events . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
21
8
SAMPLE SIZE DETERMINATION
22
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Abbreviations
Abbreviation
Deﬁnition
CMH
Cochran-Mantel-Haenszel
CONSENTED
Consented Population
CRF
Case Report Form
DayA1
Study Assessment Day 1
DayD1
Day of study drug delivery
DayR
Day of randomization
DCC
Data Coordinating Center
dITT
Drug-delivered Intention-to-Treat
DSMB
Data and Safety Monitoring Board
ELIGIBLE
Eligible Population
EQ-5D-5L
5-level EuroQol- 5 Dimension
GAD-7
Generalized Anxiety Disorder 7-item
HCQ
hydroxychloroquine
HCQ Trial
Hydroxychloroquine for Outpatients with Conﬁrmed COVID-19 Trial
(original name of trial)
ITT
Intention-To-Treat
LVCF
Last Value Carried Forward
MedDRA
Medical Dictionary for Regulatory Activities
PCL-5
Post-traumatic Stress Disorder Checklist for DSM-5
PHQ-9
Patient Health Questionnaire 9
PP
Per-Protocol
(S)AE
(Serious) Adverse Event
SAFETY
Safety Population
SAP
Statistical Analysis Plan
SCREEN
Screening Population
UTAH One
Understanding Treatment And Health in the Ongoing coroNa Epidemic: A
Hydroxychloroquine Outpatient Study
VAS
Visual Analog Scale (of EQ-5D-5L)
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1
PREFACE
1.1
Purpose of SAP
This Statistical Analysis Plan (SAP) describes the planned analysis and reporting for the pro-
tocol: UTAH One (Understanding Treatment And Health in the Ongoing coroNa Epidemic):
A Hydroxychloroquine Outpatient Study; formerly Hydroxychloroquine for Outpatients with
Conﬁrmed COVID-19 (HCQ Trial).
The structure and content of this SAP provides suﬃcient detail to meet the requirements
and standards set by the Data Coordinating Center (DCC).
1.2
Auxiliary/Other Documents
The following documents were reviewed in preparation of this SAP:
• Protocol: UTAH One (Understanding Treatment And Health in the Ongoing coroNa
Epidemic): A Hydroxychloroquine Outpatient Study.
• Case Report Forms (CRFs) for the UTAH One protocol
The reader of this SAP is encouraged to read the protocol for details on the conduct of this
study, and the operational aspects of clinical assessments.
The purpose of this SAP is to outline the planned analyses to be completed for the UTAH
One
trial. The planned analyses identiﬁed in this SAP will be included in future study
abstracts and manuscripts. Also, exploratory analyses not necessarily identiﬁed in this SAP
may be performed. Any post hoc, or unplanned, analyses not explicitly identiﬁed in this
SAP will be clearly identiﬁed as such in any published reports from this study.
It is possible that, due to updates or identiﬁcation of errors in speciﬁc statistical software
discussed in this SAP, the exact technical speciﬁcations for carrying out a given analysis may
be modiﬁed. This is considered acceptable as long as the original, prespeciﬁed statistical
analytic approach is completely followed in the revised technical speciﬁcations.
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2
STUDY OBJECTIVES AND OUTCOMES
2.1
Study Objectives
2.1.1
Primary Objective
The primary objective of the UTAH One is to assess the eﬃcacy and safety of hydroxy-
chloroquine (HCQ) for reduction of viral shedding and hospitalization in outpatients with
conﬁrmed COVID-19.
2.1.2
Primary Outcome(s)
The primary outcome is duration of viral shedding, as deﬁned by days from randomization
to the ﬁrst of two consecutive negative swabs, measured through 14 days after randomization
(formally deﬁned in Section 5.4).
2.1.3
Secondary Outcome(s)
Secondary outcomes are:
• Average level of COVID-19-attributable symptoms
• Hospitalization within 14 days of enrollment
• Persistence of viral shedding on day 28
• Adult household contact viral acquisition
The secondary outcomes according to the original protocol included duration of COVID-
19-attributable symptoms rather than average level of COVID-19-attributable symptoms.
Reﬂecting the study PIs’ desires, it was decided by May 21, 2020 to change this duration
outcome to an exploratory outcome and include the average level as a new secondary out-
come.
Another secondary outcome in the original protocol was duration of viral shedding, measured
on days 1-14 and 28. Because of how similar this is to the primary outcome, this secondary
outcome has been changed in the SAP(and since amended in the protocol) to persistence of
viral shedding on day 28.
2.1.4
Exploratory Outcome(s)
Exploratory outcomes include, but are not limited to, the following:
• Duration of COVID-19 Symptoms
• Patient-reported instrument measures at baseline, 28 days, and 6 months
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– Patient Health Questionnaire 9 (PHQ-9) Total
– Generalized Anxiety Disorder 7-item (GAD 7) Total
– Post-traumatic Stress Disorder Checklist for DSM-5 (PCL-5) Total
– 5-level EuroQol- 5 Dimension (EQ-5D-5L) Visual Analog Scale (VAS) and index
measure
• Viral shedding numerical measurements
• Viral shedding at 28 days
• Hospital admissions within 14 days of randomization but prior to day of study drug
delivery
• Cumulative mortality at 6 months
• Hospital admission by 6 months
2.1.5
Safety Outcome(s)
In addition to the following list, it should be noted that some of the secondary and ex-
ploratory outcomes also pertain to safety but are not necessarily restated here.
• Adverse event(s) by 14 days
• Mortality by 28 days
• Hospital admission by 28 days
3
STUDY DESIGN AND METHODS
3.1
Overall Study Design
The UTAH One Trial is a prospective, placebo-controlled, randomized controlled trial to
evaluate the eﬃcacy and safety of hydroxychloroquine for subjects with COVID-19. Indi-
viduals are randomized to either the hydroxychloroquine (HCQ) arm or placebo arm. Doses
are scheduled for ﬁve days. Follow-up is most frequent through Day 15 but also is to occur
at Day 28 and at 6 months.
3.2
Method of Treatment Assignment and Randomization
Randomization is stratiﬁed by age group and balanced between the two arms using random
permuted blocks of size 2 or 4 (block size varies randomly after the initial block). A DCC
faculty statistician has generated the sequence using R version 3.6.0 statistical software. The
treatment assignments for study subjects are made available via a REDCap database.
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3.2.1
Delivery of Randomization and Emergency Backup
Treatment assignment will be provided via a REDCap database. There are no emergency
backup plans.
3.2.2
Handling of Incorrect Randomization in Study Analyses and Reports
It is possible that a patient may be randomized into the incorrect age stratum, due to incor-
rect birthdate information or improper speciﬁcation of the age group. Assuming that any
such occurrences are very occasional, legitimate errors, any such patients will be analyzed in
their corrected stratum (i.e., the stratum deﬁned by their true age) rather than in the incor-
rectly initially assigned stratum in all analyses in all reports. Restated, corrected stratum
rather than initially incorrectly assigned randomization stratum is to be used for analyses
in this document.
3.3
Treatment Masking (Blinding)
Because of the expedited timeline for implementing this study, it is infeasible to prepare
a placebo in such a way that it is indistinguishable from the HCQ doses. However, study
staﬀare not to inform the subject which treatment arm has been assigned to the subject
to make this as nearly single-blinded as possible. For the same reason, it is not practical
to implement blinding of research coordinators because they may be involved in preparing
the kit (containing, among other study materials, study drug) that is delivered to study
participants.
3.4
Study Intervention Compliance
Beginning the day after study medication is delivered, subjects are asked to indicate on ﬁve
days whether or not study medication was administered the previous day and how many
pills remain. The number of pills administered is thereby ascertained.
4
STUDY SUBJECTS AND ANALYSIS POPULA-
TIONS
4.1
Eligibility
The inclusion/exclusion criteria for this study are described in the protocol.
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4.2
Populations
4.2.1
Screening Population
The screening population (SCREEN) includes all subjects meeting all inclusion criteria who
were entered on site screening logs provided to the DCC.
4.2.2
Eligible Population
The eligible population (ELIGIBLE) includes subjects meeting all inclusion criteria and none
of the exclusion criteria.
4.2.3
Consented Population
The consented population (CONSENTED) includes all eligible subjects who consent to study
participation.
4.2.4
Intention-to-Treat Population
The Intention-to-Treat (ITT) population consists of all enrolled subjects who were random-
ized before being administered study treatment1. Subjects are not considered enrolled until
they are randomized to a treatment arm, so the day of randomization and day of enrollment
are equivalent. Subjects are considered to be in the treatment arm to which they were ran-
domized, regardless of whether or not they received any doses for the assigned arm. This
will be the primary population for eﬃcacy analyses.
4.2.5
Drug-delivered Intention-To-Treat
The drug-delivered Intention-To-Treat (dITT) population includes all ITT subjects who
had the assigned study drug, HCQ or placebo, delivered to them. Eﬃcacy analyses may be
repeated on this subpopulation as sensitivity analyses.
1After enrollment had ended, study statisticians became aware that due to a participant mix up, an
unenrolled person was administered study treatment meant for somebody else, and that after this was initially
discovered by study staﬀ, the person was consented to the study (even though ineligible) and randomized to a
treatment arm. However, because the treatment had already been administered, this person is not considered
to be in the ITT population because there did not seem to have been an intention to follow-through on a
post hoc randomization. This individual is included in the safety population for the arm corresponding to
the administered treatment.
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4.2.6
Per-Protocol Eﬃcacy Population
The Per-Protocol (PP) eﬃcacy population includes all subjects in the dITT population who
receive at least 80% of the assigned treatment’s pills/tablets. Eﬃcacy analyses will also be
repeated on this subpopulation as sensitivity analyses.
4.2.7
Safety Populations
The safety population (SAFETY) consists of all ITT subjects who are administered at least
one pill/tablet of the delivered study drug (HCQ or placebo). If the delivered study drug
diﬀers from the randomly assigned study drug, analysis of the safety population by arm will
be according to drug delivered rather than drug assigned. In addition, a post-hoc decision
was made to include one person who was erroneously administered study treatment before
consenting/randomization due to a participant mix up, so although this individual will be
omitted from the study’s ITT-based analysis for the primary manuscript, the person will
still be considered to be in the safety population for the treatment arm that corresponds
to the delivered study treatment. The principal safety analyses for outcomes will be on the
ITT population, while the principal analyses for adverse events will be on the SAFETY
population. Adverse event summaries will also be prepared for the ITT population or as
requested by the DSMB.
5
GENERAL ISSUES FOR STATISTICAL ANALY-
SES
5.1
Analysis Software
Analysis will be performed using SAS R⃝Software version 9.4 or later whenever possible.
Other software packages, including R and StatXact R⃝, may be used for particular specialized
procedures. Because of its specialized options for sequential regression imputation, IVEware
is preferred for generating multiple imputations.
5.2
Methods for Withdrawals, Missing Data, and Outliers
Subjects with incomplete data for a variable needed in an analysis may, for example, be
omitted from that analysis or have the last observation carried forward. Which technique is
used depends on the analysis, as described later in the SAP.
Rates of missingness in the primary outcome will be compared between treatment arms for
the ITT, dITT, and PP populations. If a substantial number of subjects have incomplete
data for this outcome, analyses will be conducted to determine factors signiﬁcantly related
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to missingness. The factors assessed would include, at a minimum, assigned treatment arm
and true age stratum.
When multiple imputation is employed, it will be performed separately within each treatment
arm if possible (by ITT arm for analyses of the ITT population or subpopulations thereof,
or, if necessary, by SAFETY arm for analyses of the SAFETY population).
5.3
Multiple Comparisons and Multiplicity
Explicit adjustments for multiple testing will not be applied. The secondary outcome of viral
shedding from 1–14, 28 days will be regarded as exploratory unless the primary analysis of
the primary outcome is signiﬁcant.
5.4
Derived and Computed Variables
Deﬁnitions of Days
For each subject, the day of randomization to treatment arm will be
referred to as DayR. The day on which study drug is delivered is DayD1, with the next day
being DayD2 and so forth. The day 1 daily study assessment is referred to as occurring on
DayA1; the next calendar day is DayA2, and so forth through DayA15 = DayA1+14. Note
that if the baseline study assessment were to occur on the same calendar day as DayA1, the
form name in the database will be used to distinguish in such instances which values are used
for baseline values and which are used for DayA1 values so that both sets of measurements
can still be utilized. It is expected that for most subjects study drug will be delivered one
day after randomization, i.e., that DayD1 = DayR+1. It is also expected that for most sub-
jects DayD1 = DayA1. However, because these relationships are not guaranteed, separate
nomenclature is sometimes used to deﬁne outcomes (typically based on intervals beginning
at DayR) and study assessments (often based on days since drug delivery or assessment
day). Note that while 28-day symptom and quality of life assessments will be considered to
be on DayA28, there is an allowed −2 day/+2 week window for when they occur. Likewise,
the 6-month symptom and quality of life assessments for analysis purposes will use a −2
week/+2 month window. If a randomized subject never provides a daily assessment, such
that the anchoring event for deﬁning DayA1 is unavailable, the convention will be taken to
assume DayA1 = DayR + 1. Likewise, if study drug delivery date is not available, then it
will be assumed that DayD1 = DayR+1. Because swabs are intended to be delivered
along with study drug, the drug delivery date will be assumed to correspond to
swab delivery date, with the ﬁrst swab to be collected on DayD1. There is like-
wise a window permitted for the Day 28 swab, although it is narrower: DayR+26
to DayR + 30, inclusive.
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Participants may complete surveys late (e.g., slow response by email) or dates may be in-
correctly entered that suggest assessments were done early. Additionally, surveys may be
completed one day late by phone. It will be assumed that answers to any survey submit-
ted 1 day before or after the intended day for the survey will be treated as the intended
day. For example, if the day 4 and day 5 assessments are each completed by email four
days after DayD1, it will be assumed that the day 4 responses pertain to DayD4 and the
day 5 responses pertain to DayD5. However, surveys submitted more than one day before
or after the intended day will not be analyzed (except for baseline surveys, which have a
longer window because they may be done any day between randomization and the study
treatment delivery, inclusive, day 28 surveys, which have a −2 days/+2 weeks window, and
6 month surveys, with a window of −2 weeks/+2 months). Swabs will be analyzed based
on the collection date reported by the participant, which may not necessarily match the day
on the swab label. If multiple swabs from a participant have the same participant-reported
collection date but diﬀerent results, a positive result will supersede a negative result, and a
negative result will supersede an invalid or indeterminate result. If collected swab dates are
clearly erroneous (e.g., before day of randomization), the associated swabs will be ignored.
If a swab was collected within ±2 days of DayR + 28, it will be regarded as a Day 28 swab.
Primary Outcome
Duration of viral shedding (through 14 days after randomization, i.e.,
DayR + 14): this is an integer outcome which is deﬁned as (Date of ﬁrst sustained negative
swab (ignoring any swab that was not in the interval DayR+1 through DayR+14, inclusive)
- DayR). The date of ﬁrst sustained negative swab is the ﬁrst day with a negative swab
followed by the next available day’s swab being negative. The requirement for conﬁrmation
will be waived for patients who are negative for shedding on DayR + 14. If no more pos-
itive swabs nor negative swabs are available by DayR + 14 following a negative swab, the
date of the negative swab will be considered conﬁrmed for the primary analysis (using the
last-observation-carried-forward approach). If the ﬁnal swab from on or before DayR + 14
which has a positive or negative result is positive and there were not two preceding consec-
utive negative swabs, the duration will be considered to be right censored on the day of the
positive swab.
The primary outcome was viral-shedding duration over the ﬁrst two weeks. Because the pro-
tocol stipulated that swabs would not be obtained during hospitalizations, and that positive
results would be carried forward through hospitalization, swab status was considered positive
for all hospital days. Hospitalizations or swabs documented after day 15 (i.e., DayR + 14)
were not used for this outcome. Duration was considered to end on the ﬁrst day of two
consecutive negative swabs, allowing days without swab results between two negative swabs,
or on the last available swab result if negative. Without negative conﬁrmation, the outcome
was considered right-censored on the day of their last positive result or day 15. In a sen-
sitivity analysis, we treated hospitalized patients prior to day 15 without a prior conﬁrmed
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negative as right-censored on the day of hospital admission or day 15.
Also of note is that we assumed all participants were positive on the day of randomization,
even if a negative swab were available. It was uncommon for a swab to be available on the
day of randomization.
Hospitalization within 14 days of enrollment
Hospitalization within 14 days: this is
a binary outcome which is “yes” if (a) medical chart review (e.g., performed on DayD28)
reveals a hospitalization from DayR to DayR+13 (inclusive) or (b) a study assessment
reports a hospitalization occurring in this span or (c) the subject is known to have died
during this span. If a subjects meets none of these criteria, the outcome will assumed to be
“no”. If a subject meets none of these criteria but was lost to follow-up before DayR+13 and
chart review is not permitted because of study withdrawal, the outcome will be considered
missing.
Persistence of viral shedding on Day 28
The protocol originally speciﬁed a secondary
outcome of duration of viral shedding for days 1–14 and 28. Because the primary outcome
is viral shedding from DayR + 1 through DayR + 14, the secondary outcome of persistence
of viral shedding on Day 28 is substituted for duration through Day 28; there is limited
precision between Days 15 and 28. The deﬁnition of the persistence of viral shedding on Day
28 outcome relies heavily on the Day 28 swab and is limited to those who have a test result
for the Day 28 swab or who are not known to have died on or before DayR + 30 (there is
a ±2 day window for collecting the Day 28 swab). If the Day 28 swab result is known, the
result will be used to deﬁne the outcome (“yes” if positive, “no” if negative). Otherwise,
subjects with a conﬁrmed cessation of viral shedding when considering daily swab results
from DayR + 1 to DayR + 25, inclusive (with the requirement for conﬁrmation waived if
the latest available daily result in this interval is negative), and a missing Day 28 value will
be assumed to be negative on Day 28; otherwise subjects hospitalized on any of the days
DayR + 26–DayR + 30 with a missing Day 28 value will be assumed to be positive on Day
28; otherwise, multiple imputation will be performed as described in Section 7.3.3.
Average of Core COVID-19 symptoms
There are seven core symptoms: fever, chills,
cough, tiredness, shortness of breath, diarrhea, and muscle aches. Symptoms are measured
on a 6-point ordinal scale (not experiencing=0, extremely mild=1, mild=2, moderate=3,
severe=4, extremely severe=5) at baseline, days 1-15, and day 28.If at most one of the core
symptoms is missing for an assessment, the mean of the non-missing core symptoms’ levels
for that assessment will be calculated to obtain a symptom burden score. If two or more core
symptoms are missing from the assessment, the average symptom level for that assessment
will be considered missing.
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Adult Household Contact Viral Acquisition
This outcome will be analyzed for house-
holds with at least two adults for which no other adult besides the index study subject is
positive for COVID-19 at baseline and for which the index study subject is in the ITT pop-
ulation. This binary outcome will be at the household level and will be a “yes” if there is
a positive swab by one or more adult household contacts for any of the study-administered
swabs from days DayR + 1 to DayR + 14, inclusive. If there are no positive swabs but
at least one negative swab, the outcome will be a “no;” otherwise it will be missing. For
some additional analyses, an analogous outcome will be deﬁned at the person level for each
non-index adult from a household for which no other adult besides the index study subject
is positive for COVID-19 at baseline and for which the index study subject is in the ITT
population. Another person-level outcome may count the number of study-administered pos-
itive swabs from the person and the number of study-administered swabs with a result (e.g.,
as an oﬀset in a Poisson regression model), again from days DayR+1 to DayR+14, inclusive.
As exploratory outcomes, the deﬁnitions in the previous paragraph will also include study-
administered swabs after DayR + 14 through DayR + 30, if available).
Exploratory/Safety Outcomes
Duration of COVID-19 symptoms (through DayA15):
this is an integer-valued outcome which is deﬁned as (Date of ﬁrst sustained asymptomatic
day - Start date). To determine the end date, ﬁrst each symptom assessment from baseline
through DayA15, inclusive, will be classiﬁed as symptomatic, asymptomatic, or unknown.
A symptomatic day is one in which at least one of the core symptoms (and the average of
the non-baseline symptom levels for that symptom that day, if multiple non-baseline, non-
missing symptom levels were provided for that symptom that day) is observed to exceed the
permissible threshold: not experiencing for fever and chills; extremely mild for shortness of
breath, diarrhea, and muscle aches; mild for cough and tiredness. If at most one symptom
level is missing on a given day and all observed core symptoms’ levels are at or below the
permissible threshold, the day will be classiﬁed as asymptomatic. Otherwise (i.e., if at most
ﬁve of the core symptoms have a reported symptom level and none of the reported symptom
levels exceeded the threshold), the day will be considered unknown.
The analysis of this outcome is limited to participants whose status on the day of the base-
line assessment is symptomatic, per the deﬁnition above. The start date is the date of the
baseline assessment. The end date (i.e., date of the ﬁrst sustained asymptomatic day) is the
ﬁrst asymptomatic day which is followed by the next known day being asymptomatic. The
requirement for conﬁrmation will be waived for subjects whose last available status as of
DayA15 was asymptomatic, provided they were not subsequently hospitalized or deceased
on or before DayA15; the date of the asymptomatic status will be considered conﬁrmed. If
the ﬁnal day with known status from baseline through DayA15 is symptomatic and there
were not two preceding consecutive asymptomatic days, the duration will be considered to
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be right censored on the ﬁnal symptomatic day (up through and including DayA15).
If a subject dies on or before DayA15 before a conﬁrmed asymptomatic day, the end date
will be censored on DayA15. If a subject is hospitalized on or before DayA15 before a
conﬁrmed asymptomatic day, the subject will be regarded as symptomatic through the date
of discharge or DayA15, whichever comes ﬁrst, which may push the date of censoring back.
Although the protocol mentioned analysis of the symptom duration through Day 28, daily
symptom level assessment ceases on DayA15. Therefore, the DayA28 symptom assessments
will be ignored when determining symptom duration.
• EQ-5D-5L measures (administered at baseline, 28 days, and 6 months)[1, 2]
– Visual Analog Scale: 0 to 100 scale. If the value is missing because the individual
is known to be deceased when the assessment was to have occurred, the VAS
change since baseline will be post-processed to -101 (i.e., worse than possible for
any survivor) after multiple imputation (see Section 7.4.5).
– Index measure: The index measure will use coeﬃcients from the cTTO Model
(Model 1 in Table 2 of [2]) to provide a univariable summary of the ﬁve component
dimensions. If the value is missing because the individual is known to be deceased
when the assessment was to have occurred, the index measure will be set to 0.
Otherwise, if any of the ﬁve dimensions are missing, the index measure will be
regarded as missing.
• PCL-5 Total (baseline, 28 days, and 6 months): The 20 items are scored as 0–4 each,
producing a total from 0–80.[3] The cited reference does not provide speciﬁc guidance
on what percentage of missing values may be imputed with the mean of the corre-
sponding non-missing values. In the absence of such a recommendation, if no more
than 4 (i.e., 20%) of the relevant items are missing for an individual’s total, then the
average of the individual’s observed item scores from the total will be substituted for
the missing items to impute the total. If more than 4 items are missing, the total will
be regarded as missing. In addition, subtotals of potential interest may be considered:
cluster B (items 1–5), cluster C (6–7), cluster D (8–14), and cluster E (15–20); see
[3]. Up to 20% of missing values within a cluster would be imputed with the average
of the observed scores in the cluster for determining these subtotals. If the value is
missing because the individual is known to be deceased when the assessment was to
have occurred, the PCL-5 change since baseline will be post-processed as 81 (i.e., worse
than possible for any survivor) after multiple imputation; similar adjustments will be
made for cluster subtotals.
• GAD 7 Total (baseline, 28 days, and 6 months): The 7 items are scored as 0–3 each,
producing a total from 0–21.[4] The cited reference does not provide speciﬁc guidance
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on what percentage of missing values may be imputed with the mean of the correspond-
ing non-missing values. In the absence of such a recommendation from this source, if
no more than one of the relevant items are missing for an individual’s total, then the
average of the individual’s observed item scores from the total will be substituted for
the missing items to impute the total. If more than one item is missing, the total will
be regarded as missing. If the value is missing because the individual is known to be
deceased when the assessment was to have occurred, the GAD-7 change since baseline
will be post-processed to 22 (i.e., worse than possible for any survivor) after multiple
imputation.
• PHQ-9 Total (baseline, 28 days, and 6 months): The 9 items are scored as 0-3 each,
producing a total from 0–27.[5] Several scoring approaches are noted, such as treat-
ing missing item scores as 0 to be “diagnostically conservative” or mean-imputing up
to 20% of item scores.[5] Another validation article allowed 2 of the 9 items to be
mean-imputed.[6] The latter approach will be used such that up to 2 items may be
mean-imputed. If the value is missing because the individual is known to be deceased
when the assessment was to have occurred, the PHQ-9 change in total since baseline
will be post-processed to 28 (i.e., worse than possible for any survivor) after multiple
imputation.
• Hospital admission by 6 months: this is a binary outcome which is “yes” if (a) the
secondary 14-day hospitalization outcome is yes, or (b) any hospitalization, for any
cause, is found in either the 28-day or 6-month chart review or from subject self-report,
or (c) the subject is known to have died by the time of the 6-month chart review. This
is “no” otherwise, assuming an absence of documentation of hospitalization in the
medical chart is “no.”
• Mortality by 14 days: all-cause mortality at DayR+13
• Mortality by 28 days: all-cause mortality at DayR+27
• Hospital admission by 28 days: this is a binary outcome which is “yes” if (a) the subject
self-reported a hospitalization beginning between DayR and DayR+27 inclusive, or
(b) 28-day chart review discovered a hospitalization in this interval, or (c) the subject
is known to have died during this interval.
• Post-randomization hospitalizations on or before day of study drug delivery (truncated
at DayR + 13): this outcome will be assessed for the entire ITT population. This is
“yes” if a hospitalization (or death) is documented to have occurred after the time
of randomization and on or before the earlier of the day of drug delivery (DayD1)
or (DayR + 13). This is “no” otherwise, assuming an absence of documentation of
hospitalization/death in the medical chart is “no.”
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Subgroup Variables
Age group will be determined based on the individual’s age at ran-
domization. The age groups will be 18–44, 45–59, 60–74, 75+.
Presence/absence of comorbidity
The analysis and/or imputation models of some out-
comes utilizes a dichotomous comorbidity variable. Presence/absence of comorbidities will
be deﬁned as “Yes” if any of the following are indicated on the medical history form (and
“No” otherwise, including if status is not available):
• Diabetes mellitus
• Hypertension
• Chronic pulmonary disease
• Immunocompromised status
• Cardiovascular disease
• Congestive heart failure
• Chronic kidney disease
• Active malignancy
• Cerebrovascular disease
• Chronic liver disease
• Morbid obesity
• Chronic neurological disease
5.5
Independent Review
All statistical analyses for primary reporting of trial results will be independently veriﬁed
through dual programming. Two statisticians will each program all datasets and analyses
for the DSMB reports and the primary manuscript(s) and the results will be compared.
6
INTERIM ANALYSES
6.1
Frequency of and Timepoints for Interim Analysis
DSMB meetings to review safety data are as desired by the DSMB, as described in the
DSMB charter. No interim eﬃcacy analyses are planned for this trial.
In addition to the indicated interim safety analyses, the DSMB may request additional safety
and eﬃcacy analyses at their discretion.
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6.2
Stopping Rules for Interim Eﬃcacy Analysis
We do not anticipate applying formal stopping rules for either eﬃcacy or futility in this
trial. However, we will include feasibility evaluations to allow us to determine when the ﬁrst
wave of COVID-19 has resolved, such that further enrollment in the trial is unlikely. Given
the totality of the evidence and enrollment in the trial to date, a decision may be made to
suspend or terminate the trial if there is clear evidence that the ﬁrst wave is over in Utah.
6.3
Blinding in the Interim Analysis
The closed-session DSMB reports will present generic treatment designations (e.g., “A” and
“B”) to promote objective decisions regarding study procedures and analyses. Nonetheless,
the DSMB retains the prerogative to request precise treatment designations rather than
generic labels.
7
PLANNED ANALYSES
7.1
Description of Subject Characteristics
The primary results will include key baseline characteristics for the ITT population, overall
and by assigned arm. A partial list of these characteristics includes
• age
• sex
• race
• ethnicity.
The primary results will also include a CONSORT-like diagram describing patient ﬂow. This
diagram or its footnotes will depict, at minimum, counts in the SCREEN, ELIGIBLE, CON-
SENTED, ITT, dITT, SAFETY, and PP populations along with frequencies for categories
describing why unretained patients were not part of subsequent subsets.
7.2
Primary Outcome Analysis
Due to the nature of the data collected over the DayR–(DayR+14) interval, and uncertainty
about the distribution of shedding duration and the resulting hazard function, our primary
analysis will apply the stratiﬁed log-rank test to compare the distribution of shedding dura-
tion between the hydroxychloroquine and control groups, with administrative right censoring
at DayR+14. The primary analysis will be conducted using a 2-sided α=0.05. The log-rank
test will be stratiﬁed by the age group randomization stratum. The Efron approach will be
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used to account for tied shedding duration times. Kaplan-Meier curves will summarize the
shedding time distributions in the two randomized groups.
The primary analysis of shedding duration will consider every hospitalized day as having a
positive swab result. See section 5.4.
7.2.1
Additional Analyses of Primary Outcome
A sensitivity analysis will right-censor follow-up on the day of hospital admission. These two
analyses (primary and sensitivity) represent the range of plausible scenarios for shedding dur-
ing hospitalization under the assumption that any association between hospitalization and
shedding must be positive; i.e., conditional on past history, the risk of viral shedding on any
given day is at least as large for hospitalized as for non-hospitalized subjects. It is expected
that a relatively modest proportion of subjects will be hospitalized, limiting the impact of as-
sumptions concerning shedding during hospitalizations on the primary analysis. Additional
sensitivity analyses, including analyses in which the end date of shedding is modeled as a
latent variable will be considered.
Quantiﬁcation of the magnitude of “treatment eﬀect,” and indeed the interpretation of the
trial results, will depend on the speciﬁc patterns of the shedding duration distribution. For
example, in the unexpected scenario where the cumulative incidence curves for the ending
of shedding actually cross during the (DayR + 1) to (DayR + 14) evaluation period, the
treatment arm with lower 14-day shedding rate would likely be preferred regardless of any
shorter-term beneﬁt observed in the other arm. Assuming, however, that the assumption
of proportional hazards is found to be consistent with the data, the eﬀect of the treatment
will be expressed as a hazard ratio with 95% conﬁdence interval. We will also report the
randomization age-group-stratiﬁed diﬀerences between the randomized groups in truncated
mean shedding duration to 14 days and in median shedding duration with 95% conﬁdence
intervals based on estimates derived from Kaplan-Meier curves. The conﬁdence intervals for
each diﬀerence will be derived by ﬁrst sampling with replacement the participant-level data
from among the participants with at least some viral-shedding information, then ﬁtting the
stratiﬁed Kaplan-Meier curves, and ﬁnally estimating stratum-speciﬁc and overall median
shedding durations and truncated mean durations. This will be repeated for a minimum
of 500 bootstrap replicates. The 2.5th and 97.5th percentiles of each diﬀerence between
treatments, overall and by age group randomization stratum, will be used as the conﬁdence
interval endpoints. The conﬁdence interval construction is similar to the approach taken in
Calkins et al.[7] for overall and stratiﬁed conﬁdence intervals of the restricted mean duration,
with a key diﬀerence being that no weights will be applied because treatment groups were
randomly assigned.
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As an additional exploratory analysis of the primary outcome, the primary analysis will be
repeated when stratifying by duration of pre-randomization symptoms rather than by age
group.
7.3
Secondary Outcome(s) Analyses
For each secondary outcome except the adult household contact viral acquisition, the popu-
lation of interest is the ITT population, with assigned treatment arm used, even if it diﬀers
from administered treatment arm. The viral acquisition outcome is further restricted to
households with at least two adults for which no other adult besides the index study subject
is positive for COVID-19 at baseline.
7.3.1
14-day Hospitalization
The comparison of proportion of patients hospitalized by DayR+13 between the randomized
hydroxychloroquine and placebo groups will be performed with a two-sided Cochran-Mantel-
Haenszel (CMH) test stratifying by the age categories as used for randomization, with 2-
sided α=0.05. As noted in Section 5.4, in the unlikely event that some patients die within 14
days after randomization without being hospitalized, these patients will be assigned to the
hospitalization category in the analysis. Results will be presented as relative risks with 95%
conﬁdence intervals within each age stratum, and then pooled across strata. The pooled
estimator is the estimator for the principal analysis.
7.3.2
Average of COVID-19 attributable symptoms
As noted in Section 2.1.3 of this SAP, the average symptom level of COVID-19-attributable
symptoms was not originally an outcome in the protocol, but the PIs agreed to make this a
secondary outcome and change the symptom duration outcome to be an exploratory outcome.
The average symptom level of the core symptoms will be analyzed as an average level for
the 15 daily assessments, DayA1–DayA15. Missingness in outcomes is particularly acute
because the univariate outcome is the average of 15 assessments. The following approach,
which combines multiple imputation and the last value carried forward (LVCF), will therefore
be taken.
1. Restrict the data to individuals who did not die on or before DayA1 and who have at
least one nonmissing daily average from among the following collection of assessments:
Baseline, DayA1, DayA2, . . ., DayA15.
2. For each participant, determine which of DayA1–DayA15 meet all of the following
conditions: (a) the participant was hospitalized on at least some portion of the day,
AND (b) the participant is not known to have died that day, AND (c) the participant’s
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daily symptom average is missing, as described in Section 5.4. If there are any such
days, then
• Beginning at the earliest such day, determine if the immediately preceding period
(i.e., baseline if for DayA1, DayA1 if for DayA2, etc.) had a nonmissing value.
If so, assign the previous symptom average score to be the missing day’s average
and move to the next such day to determine if it will propagate a value forward
or not. If not, leave the day as missing and proceed to the next such day to
determine it if will propagate a value forward or not.
3. Impute any remaining missing values (whether hospitalized, dead, or not), separately
for each ITT treatment arm, using chained equations with the following variables:
daily core average from the baseline assessment and assessment days 1–15, comorbid-
ity presence, age group, sex, ethnicity, and race. The imputation will be conducted in
IVEware and will use an R-squared entry criterion of 0.01 for each variable’s imputa-
tion; a minimum of 10 imputed data sets will be generated.
4. Post-process values that had been imputed during hospitalization by applying LVCF;
the value to carry forward is from the most-recent period that (a) has an observed
average score AND was earlier in the same hospitalization, if any, or otherwise (b) was
the (possibly imputed) assessment period immediately before hospitalization. If there is
no previous assessment because the hospitalization was before the baseline assessment,
carry forward the imputed baseline value while the hospitalization is ongoing or through
the period immediately before a nonmissing average was observed, whichever occurs
ﬁrst.
5. Calculate the average value for DayA1–DayA15. If the individual died on or before
DayA15, average only the values from DayA1 to the day before death, inclusive.
The outcome will be modeled with linear regression while adjusting for the baseline average,
age group, comorbidity presence, treatment, sex, race, ethnicity, and age group × comor-
bidity interaction eﬀects. Rubin’s rules will be used to make ﬁnal inference, with interest on
the two-sided p-value for the treatment eﬀect, which will be declared statistically signiﬁcant
if < 0.05.
As with the imputation model, the main analysis model for the average symptom level will
be restricted to ITT subjects who had at least one observed symptom average from among
the baseline or DayA1–DayA15 measurements.
7.3.3
Persistence of Viral Shedding on Day 28
This analysis will omit subjects known to have died on or before DayR + 30 without having
a Day 28 swab result. (The Day 28 swab may be in a ±2 day window, so a participant may
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have a “Day 28” swab even if the subject died on DayD28.) Some missing data will be
assumed positive or negative, as described for this day 28 shedding outcome in Section 5.4.
Then, multiple imputation will be employed for subjects with still-missing values for the
Day 28 viral shedding outcome. There will be a minimum of m = 10 imputed datasets, and
variables used to impute the outcome will include variables such as prior hospitalizations
while on study, treatment arm (if imputation is not already stratiﬁed by treatment arm),
age group, and viral shedding history.
Comparison of the proportion of index subjects with Day 28 viral shedding between the
randomized hydroxychloroquine and placebo groups will be performed. This will be based
on the Cochran-Mantel-Haenszel test statistic when stratifying by the age categories as used
for randomization. It is desired to employ a test statistic that is approximately normally
distributed under the null hypothesis of no treatment eﬀect so that Rubin’s rules may be
used to make inference across imputations. Therefore, the signed square root of the CMH
test statistic will be calculated for each imputation (negative if and only if the CMH odds
ratio for the imputed data set is < 1). The two-sided test will use α=0.05.
7.3.4
Adult Household Contact Viral Acquisition
The principal analysis of adult household contact viral acquisition will be restricted to house-
holds with at least two adults for which no other adult besides the index study subject is
positive for COVID-19 at baseline. We will evaluate the eﬀect of the hydroxychloroquine
intervention on the risk of adult household viral acquisition by applying a Cochran-Mantel-
Haenszel test stratifying by the randomization age categories and total number of adults
within the household (with this total number being regardless of whether or not the adults
contributed to the study’s swab collection). Results will be presented as relative risks with
95% conﬁdence intervals within each stratum, and then pooled across strata. A secondary
analysis will assess the eﬀect of treatment arm on household viral acquisition rates aver-
aged across all non-index adults within the household by using a modiﬁed Poisson regression
model incorporating correlation between participants in the same household, and controlling
for age category and number of household members. The analyses in this paragraph will be
conducted twice, once when using the principal version of the outcomes (i.e., using swabs
collected from DayR + 1 to DayR + 14, inclusive) and once when using the additional ex-
ploratory versions of the outcomes (i.e., using all collected swabsfrom DayR + 1 to the Day
28 swabs, inclusive).
7.4
Exploratory Outcomes Analyses
The original protocol mentioned an analysis of viral shedding numerical measurements. Such
an analysis may or may not be conducted; if conducted, the analysis will be described
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elsewhere and regarded as an exploratory analysis.
7.4.1
Duration of COVID-19 attributable symptoms
As noted in Section 5.4 of this SAP, we will analyze symptom duration through DayA15,
rather than Day 28, which is a departure from what was described in the protocol.
The duration of COVID-19-attributable symptoms will be summarized graphically using
Kaplan-Meier curves, and compared between randomized groups by applying the Gehan
test with stratiﬁcation by the age group.
As a sensitivity analysis, the duration of symptoms will be recalculated without any restric-
tions for having conﬁrmation. That is, the ﬁrst asymptomatic day in the window will be
regarded as the end date, even if the next available symptom assessment indicates a symp-
tomatic day. The symptom duration analysis will be repeated on this modiﬁed version of
the outcome.
7.4.2
Six-month mortality
Subjects for whom this outcome cannot be ascertained will be excluded from analysis of this
exploratory outcome.
The frequency and percentage of ITT subjects known to have died by six months will be
calculated, overall and by treatment arm. In addition, the estimated relative risk within each
stratum will be reported along with a 95% conﬁdence interval, and the Cochran-Mantel-
Haenszel estimate of a common relative risk will be reported along with a 95% conﬁdence
interval.
7.4.3
Six-month hospitalization
Subjects for whom this outcome cannot be ascertained will be excluded from analysis of this
exploratory outcome.
Analysis will be conducted as for the six-month mortality outcome.
7.4.4
Hospitalizations before DayD1
For this outcome, the frequency and percentage of ITT subjects who are hospitalized or
die on or before the earlier of the day before study drug delivery and DayR + 13 will be
calculated, overall and by treatment arm.
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7.4.5
Quality of life (EQ-5D-5L Assessment)
The EQ-5D-5L quality of life assessment is administered at baseline, 28 days, and 6 months
and we will analyze the VAS and an index measure, as described in Section 5.4. Multi-
ple imputation of missing values will be implemented prior to analysis to improve inference
given the expectation that missingness may depend on other characteristics. Imputation will
include a death indicator for subjects who were known to have died before the assessment
was to have occurred. After imputation, diﬀerences between day 28 (6 months) and baseline
values of the VAS will be calculated. Any subjects whose measurement at day 28 (6 months)
is missing because the individual died will then be post-processed to have a value worse than
the worst possible diﬀerence among survivors (i.e., -101). Mean diﬀerences between day 28
(month 6) values and baseline will be compared between arms using a suitable approach
(e.g., Van Elteren test), while adjusting for age stratum.
A similar analytical approach will be taken for the EQ-5D-5L index measure, except that the
index measure will be set to 0 for individuals who were missing the assessment because they
were deceased. No other missing index measure values will be imputed. Note that survivors
may have a lower value for this index measure (i.e., <0) than those who are deceased.
7.4.6
Six-month depression (PHQ-9 Total)
Analysis of the PHQ-9 Total will be conducted in the manner analogous to that of the 28-day
and six-month EQ-5D-5L VAS.
7.4.7
Six-month anxiety (GAD-7 Total)
Analysis of the GAD-7 Total will be conducted in the manner analogous to that of the 28-day
and six-month EQ-5D-5L VAS.
7.4.8
Post-traumatic stress disorder (PCL-5 Total)
Analysis of the PCL-5 Total will be conducted in the manner analogous to that of the 28-day
and six-month EQ-5D-5L VAS.
7.4.9
Additional Analyses for Time-to-event Outcomes
Kaplan-Meier incidence curves will also be created by treatment group for the following:
• Time to death
• Time to ﬁrst hospitalization and death out of the hospital (as competing risks)
• Time to no symptoms and death (as competing risks)
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For all but the ﬁrst, the cumulative incidence curves for the composite outcome including
death would be depicted along with cumulative incidence curves for death and for the other
outcome overlaid on the plot.
7.5
Safety Analyses
7.5.1
Formal Safety Outcome(s)
In addition to outcomes described earlier in this section, additional exploratory safety out-
comes for this trial include:
• Mortality by 14 days
• Mortality by 28 days
• Hospital admission by 28 days
The analysis of each of these additional safety outcomes will be conducted in analogous fash-
ion to the six-month mortality and six-month hospitalization endpoints (see Sections 7.4.2
and 7.4.3). For these exploratory outcomes, the analysis will be conducted on the ITT and
SAFETY populations, with emphasis on the former.
7.5.2
Adverse Events
Per the protocol, AEs will be recorded through the earlier of hospitalization and Day 14.
Collected adverse events
The protocol identiﬁes adverse events (AEs) to be collected
in AE report forms of the database. These include
• Serious adverse events (SAEs)
• Non-serious AEs judged by investigator as related to study drug or study procedures
or of uncertain relationship
• AEs resulting in permanent discontinuation of study drug
Summaries
Formal statistical analysis of adverse events is not planned, other than what
has been noted previously in this SAP for adverse events that are used to deﬁne trial out-
comes. However, descriptive summaries of adverse events will be created to assist the DSMB
in monitoring safety.
For the closed session of DSMB meetings the overall number and percentage of patients
with AEs and SAEs will be summarized, overall and by Medical Dictionary for Regulatory
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Activities (MedDRA) coding. AEs will be classiﬁed by relatedness, expectedness, serious-
ness, intensity, action taken, outcome, and modiﬁcation to study treatment. AEs will be
summarized by seriousness, relatedness, and expectedness, and SAEs will be summarized by
relatedness and expectedness. This will be done by treatment arm for the SAFETY pop-
ulation (principal focus) and for the ITT population. Generic treatment designations are
preferred for interim DSMB meetings unless the DSMB requests otherwise.
8
SAMPLE SIZE DETERMINATION
The protocol contains a detailed sample size justiﬁcation.
References
[1] EuroQol Research Foundation. EQ-5D-5L User Guide, 2019. Available from: https:
//euroqol.org/publications/user-guides.
[2] A. Simon Pickard, Ernest H. Law, Ruixuan Jiang, Eleanor Pullenayegum, James W.
Shaw, Feng Xie, Mark Oppe, Kristina S. Boye, Richard H. Chapman, Cynthia L. Gong,
Alan Balch, Jan J.V. Busschbach. United States Valuation of EQ-5D-5L Health States
Using an International Protocol, Value in Health, 22(8), 2019, 931–941. https://doi.
org/10.1016/j.jval.2019.02.009.
[3] U.S.
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[4] Spitzer, R.L., Kroenke, K., Williams, J.B.W., L¨owe, B. A Brief Measure for Assessing
Generalized Anxiety Disorder: The GAD-7. Archives of Internal Medicine, 166(10), May
2006, 1092–1097.
[5] Kroenke, K., Spitzer, R.L., Williams, J.B.W., L¨owe, B. The Patient Health Questionnaire
Somatic, Anxiety, and Depressive Symptom Scales: a systematic review. General Hospital
Psychiatry, 32(4), 2010, 345–359. doi: https://doi.org/10.1016/j.genhosppsych.
2010.03.006.
[6] Arrieta, J., Aguerrebere, M., Raviola, G., Flores, H., Elliott, P., Espinosa, A., Reyes,
A., Ortiz-Panozo, E., Rodriguez-Gutierrez, E.G., Mukherjee, J., Palazuelos, D., Franke,
M.F. Validity and Utility of the Patient Health Questionnaire (PHQ)-2 and PHQ-9 for
Screening and Diagnosis of Depression in Rural Chiapas, Mexico: A Cross-Sectional
Study. J. Clin. Psychol., 73, 2017, 1076–1090.
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[7] Calkins, K.L., Canan, C.E., Moore, R.D., Lesko, C.R., Lau, B. An application of re-
stricted mean survival time in a competing risks setting: comparing time to ART ini-
tiation by injection drug use. BMC Med Res Methodol 18, Article 27, 2018. https:
//doi.org/10.1186/s12874-018-0484-z.
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