Conditions: Gastroenteritis
Keywords: Lactobacillus rhamnosus GG LGG Probiotic Gastroenteritis acute gastroenteritis child pediatric RCT
Allocation: RANDOMIZED | Intervention model: PARALLEL
Enrollment: 971
Healthy volunteers: no

Brief summary:
The investigators will study the efficacy and side effect profile of LGG, a probiotic, in pediatric patients with acute gastroenteritis.

Detailed description:
Multicenter randomized controlled trial of LGG in patients 3-48 months of age presenting to the Emergency Department with acute gastroenteritis.

Arms:
arm 1: LGG 10\^10 cfu PO bid x 5 days arm 2: micro-crystalline cellulose PO bid x 5 days

Interventions: intervention 1: LGG intervention 2: micro-crystalline cellulose
Intervention descriptions: intervention 1: LGG 10\^10 cfu PO BID X 5 days intervention 2: 1 capsule PO bid x 5 days

Protocol document:
Prot_SAP_000.pdf: 
Lactobacillus Rhamnosus GG vs. Placebo for Pediatric Acute Gastroenteritis 
 
Supplement 
 
This supplement contains the following items: 
 
    1.Original protocol, final protocol, summary of changes. 
 
    2.Original statistical analysis plan, final statistical analysis plan, summary of changes. 
 
 


Impact of Emergency Department Probiotic
Treatment of Pediatric Gastroenteritis
(Probiotics Study)
PECARN Protocol Number 032
Pediatric Emergency Care Applied Research Network
National Institute for Child Health and Human Development
(NICHD)
Protocol Version 1.00
Version Date: January 24, 2014
Printing Date: January 24, 2014


Copyright c⃝2014. University of Utah School of Medicine on behalf of the Principal
Investigator, David Schnadower, M.D. and the Pediatric Emergency Care Applied Re-
search Network (PECARN). All rights reserved.
This protocol is PECARN Protocol Number 032, and has been authored by David
Schnadower, M.D., Washington University, for implementation with the PECARN inves-
tigators. This study is supported by R01-HD071915 awarded to Washington University
(PI:David Schnadower, M.D.) by the Eunice Kennedy Shriver National Institute for Child
Health and Human Development (NICHD).
The PECARN research node centers are Washington University, University of Michigan
at Ann Arbor, Cincinnati Children’s Hospital Medical Center, Columbia University, Uni-
versity of California at Davis Medical Center, Children’s Hospital of Pittsburgh, and Chil-
dren’s National Medical Center are supported by Cooperative Agreements U03-MC00003,
U03-MC22684, U03-MC00007, U03-MC00001, U03MC22685, and U03-MC00006 from the
Emergency Medical Services for Children (EMSC) Program, Maternal and Child Health
Bureau, Health Resources and Services Administration.
This document was prepared by the PECARN EMSC Data Coordinating Center
(DCC) located at the University of Utah School of Medicine, Salt Lake City, Utah. The
document was written and typeset using LATEX2". The DCC at the University of Utah is
supported by Cooperative Agreement U03-MC00008 from the Emergency Medical Services
for Children (EMSC) Program, Maternal and Child Health Bureau, Health Resources
and Services Administration.


Protocol 032 (Schnadower)
Page 3 of 49
PROTOCOL TITLE:
Impact of Emergency Department Probiotic Treatment of Pediatric Gastroenteritis
Short Title: Probiotics Study
PECARN Protocol Number: 032
Lead Investigator and Author:
David Schnadower, M.D.
Washington University
Protocol Version: 1.00
Version Date: January 24, 2014
I conﬁrm that I have read this protocol, I understand it, and I will conduct the study
according to the protocol. I will also work consistently with the ethical principles that have
their origin in the Declaration of Helsinki and will adhere to the Ethical and Regulatory
Considerations as stated. I conﬁrm that if I or any of my sta↵are members of the Insti-
tutional Review Board, we will abstain from voting on this protocol, its future renewals,
and its future amendments.
Principal Investigator Name:
Principal Investigator Signature:
Date:
Probiotics Study Protocol Version 1.00
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Contents
1
Study Summary
9
1.1
Hypotheses
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
9
1.2
Speciﬁc Aims . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
9
1.3
Trial Endpoints . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
10
1.4
Subject Eligibility, Accrual and Study Duration . . . . . . . . . . . . . .
10
2
Rationale and Background
11
2.1
Rationale for Probiotic Eﬃcacy . . . . . . . . . . . . . . . . . . . . . . .
12
2.2
Limitations of Research to Date . . . . . . . . . . . . . . . . . . . . . . .
13
2.3
Validation of the Modiﬁed Vesikari Score . . . . . . . . . . . . . . . . . .
14
3
Study Design and Data Collection
15
3.1
Study Design Overview . . . . . . . . . . . . . . . . . . . . . . . . . . . .
15
3.2
Participant Screening and Consent
. . . . . . . . . . . . . . . . . . . . .
15
3.3
Baseline Data Collection . . . . . . . . . . . . . . . . . . . . . . . . . . .
16
3.4
Follow Up Data Collection . . . . . . . . . . . . . . . . . . . . . . . . . .
16
4
Study Procedures
17
4.1
Randomization (Enrollment) . . . . . . . . . . . . . . . . . . . . . . . . .
17
4.2
Study Drug Administration
. . . . . . . . . . . . . . . . . . . . . . . . .
17
4.3
Discontinuation of Study Drug . . . . . . . . . . . . . . . . . . . . . . . .
18
4.4
Withdrawal from Study
. . . . . . . . . . . . . . . . . . . . . . . . . . .
20
4.5
Stool Sample Testing . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
20
5
Data Analysis
21
5.1
Speciﬁc Aim Analyses
. . . . . . . . . . . . . . . . . . . . . . . . . . . .
21
5.2
Secondary Study Outcomes
. . . . . . . . . . . . . . . . . . . . . . . . .
23
5.3
Sample Size Calculations and Statistical Power . . . . . . . . . . . . . . .
24
5.3.1
Enrichment Design . . . . . . . . . . . . . . . . . . . . . . . . . .
25
5.3.2
Sub-group Analyses . . . . . . . . . . . . . . . . . . . . . . . . . .
25
5.4
Recruitment Estimates and Attrition . . . . . . . . . . . . . . . . . . . .
26
5.4.1
Recruitment . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
26
5.4.2
Potential for Bias . . . . . . . . . . . . . . . . . . . . . . . . . . .
26
5.4.3
Compliance . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
26
5.4.4
Loss to Follow-up . . . . . . . . . . . . . . . . . . . . . . . . . . .
27
5.4.5
Compensation . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
27
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Protocol 032 (Schnadower)
6
Data Management
27
6.1
Clinical Sites
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
27
6.2
PECARN Data Coordinating Center (Utah) . . . . . . . . . . . . . . . .
28
6.3
Data Conﬁdentiality
. . . . . . . . . . . . . . . . . . . . . . . . . . . . .
29
6.4
Data Quality Management and Monitoring . . . . . . . . . . . . . . . . .
29
6.5
Record Access . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
29
7
Protection of Human Subjects
30
7.1
Institutional Review Board (IRB) Approval
. . . . . . . . . . . . . . . .
30
7.2
Informed Consent . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
30
7.3
Potential Risks
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
30
7.4
Protections Against Potential Risks . . . . . . . . . . . . . . . . . . . . .
31
7.5
Potential Beneﬁts . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
31
8
Data and Safety Monitoring Plan
32
8.1
Data Safety Monitoring Board (DSMB) . . . . . . . . . . . . . . . . . . .
32
8.2
Frequency of Interim Analysis: . . . . . . . . . . . . . . . . . . . . . . . .
32
8.3
Adverse Event Reporting . . . . . . . . . . . . . . . . . . . . . . . . . . .
33
8.3.1
Deﬁnitions, Relatedness, Severity and Expectedness . . . . . . . .
33
8.3.2
Time Period for Adverse Events . . . . . . . . . . . . . . . . . . .
35
8.3.3
Data Collection Procedures for Adverse Events
. . . . . . . . . .
35
8.3.4
Unanticipated Problems (UP) . . . . . . . . . . . . . . . . . . . .
36
8.3.5
Monitoring Serious Adverse Events . . . . . . . . . . . . . . . . .
36
8.3.6
Follow-up of Serious, Unexpected and Related Adverse Events . .
37
9
Study Training and Monitoring
37
9.1
Study Training
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
37
9.2
Study Monitoring . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
38
9.2.1
Site Monitoring Plan . . . . . . . . . . . . . . . . . . . . . . . . .
38
9.2.2
Clinical Site Monitoring
. . . . . . . . . . . . . . . . . . . . . . .
38
9.2.3
Remote Monitoring . . . . . . . . . . . . . . . . . . . . . . . . . .
38
9.2.4
Pharmacy Monitoring
. . . . . . . . . . . . . . . . . . . . . . . .
39
10 Regulatory Issues
39
10.1 Food and Drug Administration
. . . . . . . . . . . . . . . . . . . . . . .
39
10.2 Health Insurance Portability and Accountability Act
. . . . . . . . . . .
39
10.3 Inclusion of Women and Minorities . . . . . . . . . . . . . . . . . . . . .
40
10.4 ClinicalTrials.gov Requirements . . . . . . . . . . . . . . . . . . . . . . .
40
10.5 Retention of Records . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
40
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Bibliography
40
List of Tables
1
Modiﬁed Vesikari Score
. . . . . . . . . . . . . . . . . . . . . . . . . . .
15
2
Power Analysis
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
25
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Protocol 032 (Schnadower)
Abstract
Practice guidelines do not endorse routine use of probiotics in pediatric acute
gastroenteritis. However, probiotic manufacturers aggressively purvey probiotics
using health claims that have not been supported by rigorous research, and the
world-wide market for probiotic products is equivalent to $32.6 billion per year. The
Food and Drug Administration and the European Food Safety Authority remain
concerned about probiotic value and safety.1–3 Some institutions now recommend
the routine use of probiotics based on potentially ﬂawed or limited evidence,4 and
parents of patients with acute gastroenteritis often administer probiotics to their
children without guidance from medical professionals.5 Since the use of probiotics
is increasing without adequate evidence to support its use in the United States, the
study described in this protocol was designed and successfully submitted to the
National Institute for Child Health and Human Development (NICHD) for funding.
The overall objective of this randomized, placebo-controlled, double-blind study
is to determine if probiotic administration reduces the severity of acute gastroen-
teritis episodes in children aged 3 to 48 months. The probiotic agent that will be
used in this trial is Lactobacillus rhamnosus GG, ATCC 53103 (LGG).
Participants will be randomized to receive a ﬁve-day course of probiotic or
placebo. The trial is anticipated to enroll 900 children, age 3-48 months, treated
in participating emergency departments for acute gastroenteritis. We deﬁne acute
gastroenteritis as the presence of three or more watery stools in a 24-hour period.
Children with underlying illness that pose potential increased risk from probiotic
therapy (e.g. indwelling vascular access line, structural heart disease, immuno-
suppressive therapy or known immunodeﬁciency, chronic gastrointestinal disease
such as inﬂammatory bowel disease, or household contact with immunodeﬁciency
or immunosuppressive therapy) will be excluded. The age range of 3-48 months
was selected because this age group has the highest incidence of acute gastroen-
teritis and the greatest morbidity. Subjects will be recruited at the time of an
emergency department visit. All eligible subjects who present for treatment when
study personnel are available will be approached for participation. Those agreeing
to participate will be randomized, using block randomization stratiﬁed by study
site, to treatment groups. The study will be conducted at multiple sites within
the Pediatric Emergency Care Applied Research Network (PECARN). We will also
collect and freeze pre- and post-treatment bulk stool specimens at the lead study
site to assess the mechanism of action of the speciﬁc probiotic agent, Lactobacillus
rhamnosus GG, ATCC 53103 (LGG).
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1
Study Summary
This randomized, double-blind, placebo-controlled trial will quantify the beneﬁts and
potential side e↵ects associated with probiotic administration in ambulatory children
presenting to the emergency department with acute gastroenteritis. This will provide the
ﬁrst deﬁnitive evidence in the United States for, or against, using probiotic therapy for this
condition. This study will use the most commonly employed probiotic agent (Lactobacillus
rhamnosus GG, ATCC 53103 (LGG)) approved for use in the United States. The results
of this multicenter study will guide the standard of care: if probiotic administration is
associated with beneﬁt, it o↵ers an inexpensive, safe and easy to administer treatment to
reduce morbidity from acute gastroenteritis. If the trial does not demonstrate probiotic
eﬃcacy, healthcare, caregiver and societal resources may be refocused on alternative
therapeutic interventions.
1.1
Hypotheses
The hypotheses of this study are:
1. In children with acute gastroenteritis, probiotic administration in the emergency
department will be associated with a clinically-important decrease in the proportion
of children su↵ering from moderate-severe disease, deﬁned by a validated Modiﬁed
Vesikari Score ≥9, compared to placebo.
2. In children with acute gastroenteritis, probiotic administration will not be associated
with serious adverse events, and will have a similar rate of side e↵ects (e.g. bloating,
fever, abdominal distention) as compared to placebo-treated children.
1.2
Speciﬁc Aims
This project has the following Speciﬁc Aims:
Speciﬁc Aim 1. Determine the clinical e↵ectiveness of probiotic administration to re-
duce morbidity in children presenting to the emergency department with acute
gastroenteritis.
Speciﬁc Aim 2. Determine the safety and side e↵ect proﬁles of Lactobacillus rhamnosus
GG, ATCC 53103 (LGG) in children presenting to the emergency department with
acute gastroenteritis.
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Protocol 032 (Schnadower)
1.3
Trial Endpoints
Primary Endpoints
• The primary eﬃcacy endpoint of this study is the presence of moderate-severe
acute gastroenteritis, as deﬁned by a total post-enrollment Modiﬁed Vesikari Score
≥9 during the 2-week follow-up period.
• The primary safety endpoint of this study is the occurrence of invasive disease
(including meningitis and bacteremia) from Lactobacillus rhamnosus.
Secondary Endpoints
1. Diarrhea duration: Time from randomization until the appearance of the last
watery stool as reported during daily surveys.
2. Vomiting duration: Time from randomization until the last vomiting episode as
reported during daily surveys. Vomiting duration is only evaluated in children who
vomited ≥3 times during the 24 hours prior to the emergency department visit.
3. Return visits: Return visits for unscheduled care to a healthcare provider related
to vomiting, diarrhea, dehydration, fever, or ﬂuid refusal, within 2 weeks of the
index visit. Scheduled visits (e.g. reassessment, vaccinations, unrelated issues) will
not be included.
4. Missed daycare: Days of daycare missed by subjects who attend daycare.
5. Missed work: Days of work missed by caregivers who work outside of the home.
6. Household transmission rate: A household census will be obtained at the time
of enrollment, and information about household contacts symptoms will be obtained
during daily surveys to determine household transmission rate.
7. Adverse Events: Occurrence of side e↵ects such as bloating, gas, intestinal
rumbling, diarrhea, blood in stool, abdominal pain, abdominal cramps nausea,
vomiting, loss of appetite, abnormal taste, heartburn, constipation, skin rash, fever,
nasal congestion, sore throat, cough, headache, muscle aches, chills, etc..
1.4
Subject Eligibility, Accrual and Study Duration
Eligible participants will be identiﬁed by on-site study sta↵. Inclusion criteria are:
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1. Age 3-48 months (have not yet reached their fourth birthday); AND
2. Presence of 3 or more watery stools within 24 hours of screening; AND
3. Duration of vomiting or diarrhea less than 7 days; AND
4. Symptoms consistent with acute intestinal infectious process.
We will exclude subjects with any of the following:
1. Presence of an indwelling vascular access line; OR
2. Presence of structural heart disease excluding non-pathological heart murmurs; OR
3. Receiving immunosuppressive therapy or history of immunodeﬁciency; OR
4. Hematochezia in the preceding 48 hours; OR
5. Chronic gastrointestinal problems (e.g. short gut syndrome, inﬂammatory bowel
disease); OR
6. Patients with known pancreatitis; OR
7. Critically ill patients; OR
8. Family member with an indwelling vascular access line, or on immunosuppressive
therapy, or with a known immunodeﬁciency; OR
9. Bilious emesis; OR
10. Probiotic use (supplement) in the preceding 2 weeks; OR
11. Previously enrolled in this trial; OR
12. Allergy to lactobacillus or Microcrystalline Cellulose (MCC); OR
13. Allergy to erythromycin, clindamycin, AND β-lactam antibiotics (all); OR
14. Patients who have already been enrolled in the study once; OR
15. Not available for daily follow-up while symptomatic; OR
16. Parent/guardian not speaking English or Spanish.
The trial is anticipated to enroll 900 subjects over four years, which will include four
acute gastroenteritis seasons. An interim safety analysis will be prepared for Data Safety
Monitoring Board (DSMB) review after the ﬁrst 80 subjects (half of whom will be under
1 year of age) have been followed for 1 month. At the time of this review, the DSMB
may alter the subsequent sample size based on overall event rates.
2
Rationale and Background
Acute gastroenteritis is a leading cause of malnutrition and death worldwide and a↵ects
millions of children in the United States each year.6, 7 Acute gastroenteritis exerts high
impact burdens on children and their families: each episode causes on average 6-8 days
of diarrhea, 2-4 days of vomiting, and 2-4 days of fever.8–11 In two prospective studies
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Protocol 032 (Schnadower)
conducted in 11 Canadian and 5 United States pediatric emergency departments, 433/683
(63%) children 3-48 months of age with acute gastroenteritis had moderate to-severe symp-
toms at presentation, resulting in substantial daycare and parental work absenteeism.12, 13
The economic burden associated with such cases is considerable.14 Unfortunately, current
treatment options are limited to rehydration, symptomatic management and supportive
care, prevention of severe dehydration and secondary infection control.15–17
Probiotic agents represent a novel approach to management of pediatric acute gas-
troenteritis. Probiotics are viable microbes that are generally considered to be safe and
are relatively inexpensive, easily administered, and hypothesized to modulate disease
processes.18 They may also reduce symptoms (i.e. diarrhea, vomiting, fever)19–22 and
morbidity, thereby diminishing acute gastroenteritis-associated resource consumption (e.g.
physician visits, hospitalization) and societal costs. Numerous studies report promising
results in children with acute gastroenteritis treated with probiotics, but these studies have
been inadequate to change clinical practice, because of ﬂaws in methodology including
small sample sizes, lack of probiotic quality control, and outcomes that are of minimal
relevance to patients and their families.19 Remarkably, few studies of probiotics have
evaluated outpatients, a group representing >90% of acute gastroenteritis episodes in
the United States.23, 24 Moreover, only a single emergency department study of probiotic
eﬃcacy in acute gastroenteritis has been reported.20
To date, practice guidelines do not endorse routine use of probiotics in pediatric acute
gastroenteritis.5, 19, 25–27 However, current trends provide the motivations for the study
described in this protocol. First, probiotic manufacturers aggressively purvey probiotics
using health claims that have not been supported by rigorous research,28–31 and the
world-wide market for probiotic products is growing rapidly (projected growth 2009-2014
12.6%, now equivalent to $32.6 billion per year).32 Second, the United States Food and
Drug Administration and the European Food Safety Authority remain concerned about
probiotic value and safety.1–3 Third, some institutions now recommend the routine use of
probiotics based on potentially ﬂawed or limited evidence.4 Fourth, parents of patients
with acute gastroenteritis often administer probiotics to their children without guidance
from medical professionals.5
2.1
Rationale for Probiotic Eﬃcacy
Probiotics, deﬁned as viable microbial preparations with beneﬁcial e↵ects on the health
of the host,33 are regarded as safe, and are generally a↵ordable and convenient (i.e., as
over-the-counter food supplements). Probiotics, and Lactobacillus rhamnosus GG, ATCC
53103 (LGG) in particular, promote colonization resistance and modulate immune re-
sponses in the host, and can be directly antimicrobial. Over 100 studies have studied how
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probiotics can improve immune function in humans.34 At the mucosal surface, probiotics:
• compete with pathogenic bacteria for nutrients and adhesion binding sites;35–38
• produce antimicrobial substances;37, 39, 40
• provide nutrients to colonocytes;41
• alter epithelial gene expression;42 and
• reduce intestinal permeability.43
Additional mechanisms of action include enhancing phagocyte44 and natural killer cell
activity,45 and increasing fecal,46 salivary,47and systemic48 IgA levels.
Preliminary probiotic studies in humans, including over 56 trials in children with
gastroenteritis (17 of which used some form of Lactobacillus rhamnosus GG, ATCC
53103 (LGG) , the agent employed in this trial) suggest that probiotics may improve the
course of acute gastroenteritis. Meta-analyses19, 21, 49–51 report reduced mean duration of
diarrhea (by 25 hours), reduced proportion of diarrhea lasting four days (risk ratio 0.41),
and reduced stool frequency on Day 2 (mean di↵erence 0.8).19 This has prompted some
physicians and institutions to recommend probiotics in children with acute gastroenteritis.
Careful examination of the data, however, shows signiﬁcant methodological ﬂaws in these
studies. For these reasons, experts and agencies have continued to recommend large,
unbiased, well designed deﬁnitive trials to inform practice.19, 26
2.2
Limitations of Research to Date
Most trials of probiotics for acute gastroenteritis have been methodologically ﬂawed.19
Published studies have used small sample sizes and non-standardized treatment regi-
mens, probiotic preparations with variable production quality and non-veriﬁed colony
counts. Outcomes have been focused almost exclusively on diarrhea duration, and use
inconsistent (or unreported) deﬁnitions,19, 52 without considering the more global (and
relevant) assessment of the illness (e.g. fever, vomiting, repeat emergency department
visits, hospitalization). Because the outcomes sought are heterogeneous, and/or not
validated, and/or of minimal importance to participants,53 and have not addressed clinical
and socioeconomic eﬃcacy,49, 50 the value of the existing data has been questioned.54
Moreover, few studies address side e↵ects and adverse events systematically.1–3
Although >90% of children with acute gastroenteritis are treated as outpatients,23
hospitalized children have been the main focus of most research in this area. Extrapolation
to outpatients is problematic because hospitalized children are more likely to have
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rotavirus infections,55 severe disease, and to beneﬁt from probiotics.21, 52, 56 Emergency
department patients are ideal for outpatient probiotic trials, as their acute gastroenteritis
disease severity represents the entire spectrum in a normal distribution,13 o↵ering distinct
advantages over primary care populations. Emergency department patients are at risk for
more severe disease, there is a greater potential for beneﬁt because of the disease acuity
and the large sample size, and disease spectrum will enable identiﬁcation of subgroups
most likely to beneﬁt. Emergency departments are also a high venue of presentation
for acute gastroenteritis, enabling uniform trial design and compliance compared to
non-emergency department ambulatory settings.24, 57–59 Only one emergency department
study has been conducted previously, but the study was underpowered and did not explore
side e↵ects.20
2.3
Validation of the Modiﬁed Vesikari Score
The Vesikari Score, a composite measure of seven items ﬁrst described in 1990,60 has been
used in many clinical trials for treating acute gastroenteritis, particularly those evaluating
rotavirus vaccines in infants, and in large international epidemiological studies.8, 61–65 The
score incorporates features of acute gastroenteritis that are important to parents, children
and physicians, including
• diarrhea duration
• diarrhea frequency,
• vomiting duration,
• vomiting frequency,
• maximum daily temperature,
• medical interventions required, and
• degree of dehydration.
In outpatient studies, the degree of dehydration, measured as weight loss, is problematic
because it requires in-person re-evaluations, can vary based on recent voiding, defecation,
and liquid intake, and also might reﬂect inadequate caloric intake or catabolism during
acute illness. In fact, the assessment of dehydration using signs or scales designed based
on the use of post-illness weight as a gold standard has been questioned.66 Because
of these limitations, modiﬁcations to the original Vesikari score have been tested.67, 68
The modiﬁcation replaces percent dehydration with the need for an unscheduled future
healthcare visit within the two week follow-up period (Table 1 on the facing page). This
modiﬁcation is supported by evidence that the demand for professional medical care
correlates with disease severity.67 The Modiﬁed Vesikari Score has been validated in two
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Points
0
1
2
3
Diarrhea duration
0
1-96 hrs
97-120 hrs
≥121 hours
Max # of diarrheal stools/24 hrs
0
1-3
4-5
≥6
Vomiting duration
0
1-24 hrs
25-48 hrs
≥49 hours
Max # of vomiting episodes/24 hrs
0
1
2-4
≥5
Max recorded fever
37◦C
37.1-38.4◦C
38.5-38.9◦C
≥39◦C
Unscheduled healthcare visit
0
—
Primary
Care
Emergency
Department
Treatment
None
Rehydration
Hospital
Admission
—
Table 1: Modiﬁed Vesikari Score
multicenter studies12, 13 conducted during the planning of the current trial described in
this protocol.
3
Study Design and Data Collection
3.1
Study Design Overview
This is a double-blind randomized placebo controlled trial of probiotic therapy for acute
gastroenteritis. Children 3 months of age to 48 months of age who present to a participating
emergency department with acute gastroenteritis will be assessed for eligibility. Children
for whom parents provide permission to participate in the trial will be randomized to
receive probiotic therapy (Lactobacillus rhamnosus GG, ATCC 53103 (LGG)) or placebo.
The trial will be analyzed as an intention-to-treat study.
3.2
Participant Screening and Consent
Potentially eligible patients will be identiﬁed and screened for eligibility. The treating
physician or other study personnel will discuss the details of the study with the patient’s
caregivers to explain the study and obtain parental permission.
For patients who are actively screened in real time and meet all inclusion criteria, data
will be recorded that include yes/no answers to each of the exclusion criteria. If a patient
is ineligible at this point, no further data will be recorded, and the patient’s parents will
not be approached for participation in the study. If a patient is eligible, the parents will
be approached to request permission for their child to participate in the study. If parents
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are not approached for permission, the reason the parents were not approached will be
recorded. If the parents decline permission to participate, the reason for refusal will be
documented (if o↵ered by the parent). The recorded exclusion criteria and reasons for
declining permission will enable the investigators to assess barriers to trial enrollment
and identify potential biases in the study.
3.3
Baseline Data Collection
Trained study sta↵at each site will collect baseline demographic information (e.g. birth-
date, gender, race, ethnicity) and relevant clinical variables, record the data on worksheets,
and enter the data into the electronic data capture system provided by the Data Coordi-
nating Center. Baseline clinical dehydration scale69 and disease severity scores (Modiﬁed
Vesikari Score)13 will be assigned to enable baseline comparisons between treatment arms.
3.4
Follow Up Data Collection
Successful follow up will be maximized by obtaining multiple phone numbers for families
and emergency contacts, scheduling calls and sending phone text reminders, allowing for
electronic completion and centralizing all follow-up procedures at the lead institution
(Washington University). Trained, experienced study sta↵will contact the family daily
(including weekends) until both the diarrhea and vomiting have resolved and the treatment
has been completed on day 5. Additional contact will be made on day 14 for outcome
assessment, and months 1, 3, 6, 9 and 12 for long term safety outcomes. Study sta↵
will use a standardized data collection form, and will inquire about ongoing symptoms,
medical evaluations, treatments, child care, work absenteeism, and side e↵ects. Detailed
questioning will follow positive responses. A study diary will be provided to caregivers to
use as a note-taking tool. Caregivers may also be provided an option of completing the
follow-up collection electronically. Patient compliance with study drug administration
will be assessed on day 5. To maximize compliance, caregivers will be reminded of the
importance and method of administering the study drug. On day 14, the study site sta↵
(not the central sta↵conducting the follow up) will perform a chart review for ﬁnal data
collection and identiﬁcation of recorded adverse events during the 14 day study period.
Adverse event reporting is described in detail in Section 8.3 on page 33.
Every e↵ort will be made complete daily follow-up on the day necessary. However,
if one or two days of follow-up contact is missed, data for those missed days may be
collected on the next contact, if the caregiver used the home diaries or can recall the
information. If all contact is missed but then the parent is contacted on day 14, follow-up
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data for the daily calls will be collected only if the parent diaries were used. For day 5
and 14, contact may be made within + 3 days. For month 1, 3, 6, 9, and 12 follow-up,
contact may be made within ± 2 weeks.
4
Study Procedures
4.1
Randomization (Enrollment)
Randomization will be accomplished through the use of an online randomization service.
Subjects will be randomized to receive either probiotic (Lactobacillus rhamnosus GG,
ATCC 53103 (LGG)) or placebo. Equal allocation randomization tables will be provided
by the Data Coordinating Center to the central research pharmacy. The central research
pharmacy will prepare consecutively numbered study kits according to the randomization
schedule. Study kits will be sent to the clinical sites. Randomization tables will be
created at the Data Coordinating Center using permuted-block randomization stratiﬁed
by clinical site and duration of symptoms. This will ensure that variations (e.g. site
speciﬁc practice patterns, gastrointestinal patterns) are comparably distributed across
treatment arms. The randomization number will be recorded in the database.
4.2
Study Drug Administration
Study Drug Description
Lactobacillus rhamnosus GG, ATCC 53103 (LGG) is supplied in a gelatin capsule con-
taining 1010 colony forming units of Lactobacillus rhamnosus(75 mg). The capsule also
contains 250 mg of microcrystalline cellulose (MCC – puriﬁed partially depolymerized
cellulose), an inert ingredient. Placebo capsules contain only MCC (to a total of 325
mg). Each capsule is wrapped in double foil to protect it against harmful light, air, and
moisture. Blister packs are labeled with the lot number. The probiotic and placebo
capsules have active Drug Master Files at the Food and Drug Administration (BB-MF 2
#13668 and MF2 # 13646).
Initial Study Drug Administration
Clinical sta↵in the emergency department will administer the ﬁrst dose of study drug
by sprinkling the capsule’s contents into 30 mL of room temperature oral replacement
solution (electrolyte solution, e.g. Pedialyte, used to prevent or treat dehydration). Oral
ﬂuid therapy will be encouraged according to sites’ existing clinical guidelines.26 At
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discharge, parents will also be provided with clinical instructions concerning what and
how much ﬂuid to drink, criteria for returning to the emergency department or seeing
their physician, and other standardized discharge instructions for acute gastroenteritis.
Study research coordinators will provide the parents with instructions concerning study
drug administration at home, completion of study forms, and a letter for their pediatrician
that explains the study. The importance of administering all doses dispensed and the
need to communicate with the study team on a daily basis until symptoms resolve will be
stressed.
Home Study Drug Administration
All patients will consume one capsule every 12 hours for 5 days (total of 9 home doses).
Patients will receive the medication at meal time, mixed with 30 mL of a room temperature
non-carbonated liquid and ingested immediately to optimize probiotic viability. One
extra dose/day will be provided (i.e. kits will contain 5 extra doses total of 15 capsules)
to account for vomiting or wastage. The dose may be repeated once if vomiting occurs
within 15 minutes of administration; this rarely happens more than once.70 Oral ﬂuid
therapy will be encouraged according to established guidelines.26
Hospital Study Drug Administration
We estimate that only a small proportion (<5%) of enrolled subjects will be hospitalized.
If that does occur, subjects will continue on the study protocol as described for home study
drug administration, as done in previous studies.71 Future unscheduled hospitalization
at a non-study hospital site is even less common: none of the 274 patients enrolled in
our pilot study were admitted to a di↵erent institution after evaluation.12 To minimize
the impact that such an event could have on this trial, caregivers will be provided with a
letter that they will be instructed to share with their pediatrician and with the admitting
physician. The letter will describe the study, the care-plan, and it will include site
investigator contact information and the importance of adhering to the study protocol.
4.3
Discontinuation of Study Drug
Study drugs are sometimes discontinued because of intolerance or perception of a clinical
adverse event from study drug administration. If any clinical abnormality, laboratory ab-
normality, intercurrent illness, new immunosuppressive therapy, or other condition occurs
such that continued administration of study drug would not be in the best interest of the
subject in the opinion of the investigator, study drug administration may be discontinued.
When this occurs, regardless of the reason, the subject remains in the intention-to-treat
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population, all data collection should proceed, and long term follow up for adverse events
is carried out. Discontinuation of study drug will be documented and will be reported in
the closed session of the next scheduled Data Safety Monitoring Board meeting. Clinical
sta↵and parents should not report the early discontinuation of study drug to research
sta↵who are conducting follow up data collection. The Principal Investigator should not
be contacted by the site investigator, as intentional discontinuation of study drug implies
a safety outcome, and the Principal Investigator should be blind to all study outcomes.
Discontinuation of study drug is not a withdrawal from the study.
If study subjects are hospitalized after discharge to home from the emergency de-
partment, this is not a reason for discontinuation of study drug. We estimate that only
a small proportion (<5%) of enrolled children will be hospitalized after discharge to
home from the emergency department. If that does occur, subjects should continue
on the study protocol unless they have developed an exclusion criterion for study drug
administration (e.g. critical illness, immunosuppression, etc.). To facilitate continuation
of study drug administration during hospitalization, parents are provided with a letter for
their pediatrician. The letter will describe the study, the care-plan, and it will include site
investigator contact information and the importance of adhering to the study protocol.
The parents will be instructed to share this letter with their pediatrician and with the
admitting physician.
Breaking the blinding of the study drug should not be necessary, but an unblinding
procedure will be available. This will require contacting the Medical Monitor (PI of
the Data Coordinating Center), who will have access to the study drug kit numbers.
However, unblinding is almost never necessary. The primary anticipated reason for a
clinician requesting unblinding is the suspected occurrence of invasive infection (bac-
teremia/septicemia or meningitis), and the natural desire to know if the subject was
receiving active Lactobacillus rhamnosus GG, ATCC 53103 (LGG). The initial recommen-
dation from the Medical Monitor will always be that the clinician should assume that the
subject was receiving active drug, and include Lactobacillus rhamnosus in the di↵erential
diagnosis (and treatment coverage) of the suspected invasive infection. Lactobacillus
rhamnosus is readily susceptible to common antibiotics, and the di↵erential diagnosis
of subsequent invasive infection would include organisms other than Lactobacillus rham-
nosus. Thus, future clinical treatment should not be dependent on unblinding information.
If the situation requires unblinding, the Medical Monitor and Data Coordinating
Center sta↵will provide the information, and the unblinding will be documented. Study
drug will be discontinued, but the subject should not be withdrawn from the study! All study
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procedures (except study drug administration) should be continued, as the subsequent
clinical course of the subject is critical to the science of the trial. All unblinding events
will be reported in the closed session of the next scheduled Data Safety Monitoring Board
meeting. Clinical sta↵and parents should not report the unblinding to research sta↵
who are conducting follow up data collection. The Principal Investigator should not be
contacted by the site investigator, as intentional unblinding of a subject implies a safety
outcome, and the Principal Investigator should be blind to all study outcomes.
4.4
Withdrawal from Study
Parents may completely withdraw their child from participation in this study at any
time, including discontinuation of data collection. However, withdrawal from study is a
completely di↵erent issue from discontinuation of study drug, and true withdrawal from
study is an exceedingly rare event. If parents demand withdrawal of their child from the
study, research sta↵will attempt to obtain adverse event information as required by the
Food and Drug Administration (all adverse events for 30 days, monthly follow up for long
term adverse events).
4.5
Stool Sample Testing
Stool sample swabs will be collected for polymerase chain reaction (PCR) analysis. Once
obtained, swabs will be frozen and sent to a central laboratory for analysis. A storage
and shipping protocol will be provided in the study manual of operations. Samples will
be tested with multiplex PCR.
In addition, at the lead site, Washington University, study research personnel will
collect and freeze subjects’ bulk stool specimens in the acute phase (within 24 hours of
presentation) and 14 days after presentation using a previously tested bulk stool specimen
collection protocol. Specimens may be collected in the emergency department or the
families will be given a specimen collection kit, gel packs and a metallic envelope. When
the specimen is ready for collection, a courier will pick up the specimen and cool pack at
the patient’s home and deliver it to a logistics collection center at Washington University
School of Medicine. This service is available 24 hours a day, year round. The stools will
be stored as a part of a future project to assess the potential mechanisms of action of
Lactobacillus rhamnosus GG, ATCC 53103 (LGG) in acute gastroenteritis.
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5
Data Analysis
The hypotheses of this study are:
1. In children with acute gastroenteritis, probiotic administration in the emergency
department will be associated with a clinically-important decrease in the proportion
of children su↵ering from moderate-severe disease, deﬁned by a validated Modiﬁed
Vesikari Score ≥9, compared to placebo.
2. In children with acute gastroenteritis, probiotic administration will not be associated
with serious adverse events, and will have a similar rate of side e↵ects (e.g. bloating,
fever, abdominal distention) as compared to placebo-treated children.
All analyses will be undertaken by the intention-to-treat (ITT) principle, except for
adverse events, which will use the as-treated principle (compare the subjects based on the
treatment regimen that they received). Patients who drop out or inadvertently crossover
will be followed and included in the ITT analysis. All statistical tests of hypotheses will
be two-sided. Baseline characteristics will be analyzed to determine if there is a need to
adjust for di↵erences between groups in exploratory analyses. Sensitivity analyses will
be performed to assess the possibility and consequences of non-random loss to follow-up.
The proportions of children experiencing an unscheduled healthcare visit or any potential
adverse e↵ect, as reported by the caregivers, will be compared between groups using the
Mantel-Haenszel test, stratiﬁed by site. The analysis will evaluate the presence/absence
of pre-speciﬁed side e↵ects, as an aggregate outcome variable. A per-protocol analysis
will be conducted to provide additional insight as non-compliance may result in an
underestimation of the beneﬁts of probiotics in the ITT analysis.72
5.1
Speciﬁc Aim Analyses
Speciﬁc Aim 1. Determine the clinical e↵ectiveness of probiotic administration to re-
duce morbidity in children presenting to the emergency department with acute
gastroenteritis.
The primary eﬃcacy endpoint of this study is the presence of moderate-severe acute
gastroenteritis, as deﬁned by a total post-enrollment Modiﬁed Vesikari Score ≥9 during
the 2-week follow-up period. Each of the 7 items in the score is tabulated individually
(maximum of 20 points); the sum of these individual variables represents the total Modiﬁed
Vesikari Score. At the time of randomization a baseline Modiﬁed Vesikari Score will
be assigned based on symptoms prior to randomization. This baseline score will serve
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as a covariate in a secondary analysis of the primary outcome. The post-enrollment
Modiﬁed Vesikari Score which will be employed to determine the presence/absence of the
primary eﬃcacy outcome, is based only on symptoms that occur between randomization
and day 14, the conclusion of the study period for this outcome. Only symptoms and
outcomes that occur following randomization will be included in the post-enrollment score.
The post-enrollment score is calculated only once, on day 14. At that time, each of the
seven variables will be assigned a score for the entire study period (from randomization
to day 14). Each variable will be scored by 1 of 3 methods:
1. Worst 24 hour period - maximal number of episodes of vomiting in a 24 hour
period, maximal number of episodes of diarrhea in a 24 hour period, and maximal
temperature;
2. Total duration of symptoms, including the number of days on which any gastroenteritis-
related symptom occurred;
3. Occurrence of a treatment outcome or unscheduled subsequent healthcare utilization.
If the patient was admitted directly following their enrollment ED visit and that
admission stay is longer than 48 hours, it will be included as treatment in the post
enrollment MVS. If the patient’s admission stay was less than 48 hours, it will not
be included in any MVS calculation.
The primary eﬃcacy endpoint (the presence of moderate or severe disease, as deﬁned
by a total Modiﬁed Vesikari Score ≥9 during the 2 week follow-up period) will be limited
to symptoms and outcomes that occur after randomization. If a patient’s symptoms
of vomiting and diarrhea stop during the same 24 hours, and then recur, that is not
included in the post-enrollment score since that will be considered a new illness. In the
original score, severe disease was deﬁned as ≥1161, 62, 73–75 and moderate as ≥9.76 In
our derivation and validation pilot studies,12, 13 construct validity was demonstrated and
validated by using scores of ≥9 to deﬁne moderate and ≥11 to deﬁne severe disease.
These cut-points were associated with signiﬁcant increases in other measures of disease
severity such as degree of dehydration, likelihood of admission and daycare (p = 0.01)
and parental work absenteeism (p <0.001).12, 13
The proportion of children with moderate-to-severe disease (i.e. Modiﬁed Vesikari
Score ≥9), the primary outcome, will be analyzed by comparing proportions utilizing a
Mantel-Haenszel test, stratiﬁed by participating center and by duration of symptoms at
enrollment. Signiﬁcance for this primary outcome measure will be set at 0.05. Secondary
analyses of the primary outcome will use logistic regression methods to adjust for covariates
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that may be imbalanced between groups, (e.g. age, pre-enrollment Modiﬁed Vesikari
Score, hydration assessment, need for hospitalization at index visit). We will also analyze
the outcome using Modiﬁed Vesikari Score as a continuous variable through a stratiﬁed
Wilcoxon rank-sum test and compare the results with the primary analysis.
Speciﬁc Aim 2. Determine the safety and side e↵ect proﬁles of Lactobacillus rhamnosus
GG, ATCC 53103 (LGG) in children presenting to the emergency department with
acute gastroenteritis.
The primary safety endpoint of this study is the occurrence of invasive disease (in-
cluding meningitis and bacteremia) from Lactobacillus rhamnosus. The secondary safety
outcome will be the presence of any adverse events. For more information on adverse
events, see Section 8.3 on page 33. Adverse events (including serious) will be tabulated
by study arm for DSMB reporting and for ﬁnal analysis of the safety of Lactobacillus
rhamnosus GG, ATCC 53103 (LGG) in this setting. Adverse events will also be coded
using the MedDRA vocabulary.
5.2
Secondary Study Outcomes
Secondary outcomes will include three of the individual components of the Modiﬁed
Vesikari Score considered independently and one additional measure of burden of illness.
Speciﬁcally, they are:
1. Diarrhea duration: Time from randomization until the appearance of the last
watery stool as reported during daily surveys.
2. Vomiting duration: Time from randomization until the last vomiting episode as
reported during daily surveys. Vomiting duration is only evaluated in children who
vomited ≥3 times during the 24 hours prior to the emergency department visit.
3. Return visits: Return visits for unscheduled care to a healthcare provider related
to vomiting, diarrhea, dehydration, fever, or ﬂuid refusal, within 2 weeks of the
index visit. Scheduled visits (e.g. reassessment, vaccinations, unrelated issues) will
not be included.
4. Missed daycare: Days of daycare missed by subjects who attend daycare.
5. Missed work: Days of work missed by caregivers who work outside of the home.
6. Household transmission rate: A household census will be obtained at the time
of enrollment, and information about household contacts symptoms will be obtained
during daily surveys to determine household transmission rate.
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7. Adverse Events: Occurrence of side e↵ects such as bloating, gas, intestinal
rumbling, diarrhea, blood in stool, abdominal pain, abdominal cramps nausea,
vomiting, loss of appetite, abnormal taste, heartburn, constipation, skin rash, fever,
nasal congestion, sore throat, cough, headache, muscle aches, chills, etc..
The overall signiﬁcance level for statistical tests on the secondary outcomes will be
set at 0.05. Holm’s method will be used to adjust for multiple comparisons.77 The
continuous variables of duration of diarrhea and duration of vomiting (measured in hours
and analyzed with a Van Elteren test),78 will be stratiﬁed by clinical center. Similarly,
the number of days the child is absent from daycare and the caregiver is absent from work
will be analyzed with a Van Elteren test, stratiﬁed by clinical center and etiology.
Dichotomous outcomes to be evaluated include emergency department acute gastroenteritis-
related revisits, intravenous rehydration, and hospitalization. Additional analyses involving
these outcomes will include linear and logistic regression models that adjust for possible
e↵ects of baseline characteristics.
5.3
Sample Size Calculations and Statistical Power
The primary analysis will be performed on a binary outcome: development of moderate-
to-severe disease. The power of this analysis is based on the proportion of patients with
moderate-to-severe disease. Our pilot data12, 13 indicate that 25% of patients will have
moderate to severe disease during the course of their illness. Furthermore expert surveys
indicated that an absolute risk reduction of 10% would constitute a minimal clinically-
important di↵erence (MCID). Therefore our sample size calculation assumed a 25% event
rate in the control group for which we desire to detect an absolute beneﬁcial treatment
e↵ect of 10% with 90% power. Using a two-sided type I error (↵) of 0.05 and the hypothe-
sized proportions yields a required total sample size of 670 patients.79 Our expected power,
should we ﬁnd di↵erent event rates in our 2 groups, is displayed in Table 2 on the next page.
Based on previous work by our group,70, 71, 80 we assumed a 10% loss to follow up
(670/0.90 = 744), 5% drop out, and 3% drop in (caregivers who buy a probiotic agent
to administer to their child) rate (744/(0.92)2 = 879). Adjustment for O’Brien-Fleming
monitoring boundaries requires a further 2% increase. Thus, the total number randomized
(ﬁnal sample size) will be 897.
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Outcome Control
Outcome Intervention
% Di↵erence
Power
0.30
0.21
9%
0.76
0.30
0.20
10%
0.85
0.25
0.15
10%
0.90
0.25
0.16
9%
0.82
0.25
0.17
8%
0.72
0.20
0.10
10%
0.95
0.20
0.12
8%
0.81
0.20
0.13
7%
0.69
Table 2: Power Analysis
5.3.1
Enrichment Design
The above study design and power analysis are based on the assumption of homogeneous
treatment e↵ect. We may also incorporate an enrichment design81, 82 to restore the
statistical power in case the presence of a subpopulation with a substantially low treatment
e↵ect is identiﬁed.
We are particularly interested in two potential subpopulations:
participants with <2 days of symptoms and those with ≥2 days of symptoms. Based on
our pilot data, each subpopulation accounts for approximately 50% of the total population.
The decision for enrollment modiﬁcation will be made at the ﬁrst interim analysis for
eﬃcacy. Speciﬁcally, three statistics (based on a normal approximation of binomial
distribution, or z-statistics) will be calculated to compare the primary eﬃcacy endpoint
between treatment and control groups for subjects in the total population and the two
subpopulations, respectively. If the z-statistic from a subpopulation is <0.3 and also
smaller than that in the total population, subjects from this subpopulation will no longer
be considered in the subsequent enrollment. All subjects, regardless of symptom duration
will be included in the ﬁnal analyses. Our simulation studies have shown that such
an enrichment design can increase the power considerably when the treatment e↵ects
are di↵erent across subpopulations, while it will have little impact on power when the
treatment e↵ects are similar.
5.3.2
Sub-group Analyses
The presence of a Modiﬁed Vesikari Score ≥9 will be analyzed by age <1 year, duration
of symptoms, breast-feeding status, antibiotic usage, rotavirus and norovirus positivity.
A subgroup e↵ect will be considered signiﬁcant if the interaction between subgroup and
treatment in a logistic regression model is signiﬁcant at a Bonferroni-corrected level.
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5.4
Recruitment Estimates and Attrition
5.4.1
Recruitment
To estimate the number of subjects with acute gastroenteritis of eligible ages that would
meet all inclusion criteria and be enrolled annually, we obtained discharge diagnoses
from all study sites for 2005-2011. In 2011, the study sites evaluated 14,048 potentially
eligible subjects (patients 3-48 months with ICD9 codes for diarrhea) out of 507,039
total emergency department visits (2.8%). In the past 7 years the lowest proportion of
such patients per total emergency department volume was 2.3% (2008). Therefore, using
2011 emergency department volumes and lowest proportion of patients with diarrhea our
conservative estimate for eligible patients would be 11,150 patients 3-48 months with
diarrhea per year (or 30 patients per day network wide). Our best estimate is that 4.5%
of children with acute gastroenteritis aged 3-48 months will be enrolled. We plan to enroll
225 patients/year and 900 subjects over 4 acute gastroenteritis seasons.
5.4.2
Potential for Bias
Reporting bias will be minimized by adhering to CONSORT recommendations including
the use of third-party assignment.83 Placebo capsules and active drug will be provided
by I-Health Inc. The total weight of all capsules is 325 mg. The probiotic and placebo
capsules and powder are identical in appearance, taste, texture, and odor. Participants,
families, healthcare providers, data collectors, outcome adjudicators, and data analysts
will be blinded as to intervention arm, thereby preventing bias in outcome assessment.
Two DCC statisticians will be partially unblinded (with knowledge of group assignments,
but not group identities) in order to present interim results to the DSMB. An intention-
to-treat analysis will be performed to minimize bias associated with poor compliance
and non-random loss of participants.84 Co-interventions (e.g. antiemetic administration,
intravenous rehydration) and other potential sources of confounding will be recorded.
Our use of a published validated score as an outcome measure will protect against the
introduction of bias in the assessment of treatment e↵ects.85
5.4.3
Compliance
Noncompliance with probiotics is rarely reported in previous studies, and not expected
to be problematic in this cohort.86, 87 Participant withdrawal has been related mostly to
the primary illness.19 In the Canadian pilot study, compliance was 91%, We will track
compliance by obtaining from parents unused capsule counts on day 5. If there are any
unused capsules, we will request their return (a pre-stamped, pre-addressed envelope will
be provided).
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5.4.4
Loss to Follow-up
Our previous emergency department pediatric acute gastroenteritis research studies
achieved telephone follow-up rates of 98% on day 3 and 96% on day 7.70 Similar success
has been documented in other PECARN multicenter studies (91%).80 We estimate a 10%
loss to follow-up. If daily contact does not occur, we will collect data from missed days on
subsequent days when caregivers are contacted. The use of patient diaries (paper and/or
electronic) and chart review will supplement parent contact. Based on our pilot trial we
have devised the following strategies to maximize follow-up: all follow-up procedures will
be centralized at the lead institution and conducted by experienced study sta↵; we will
obtain multiple phone numbers from caregivers as well as emergency contacts, and we
will schedule calls and send reminders prior to the call if preferred. Finally, electronic
diary ﬁling and transmission may be available for interested families.
5.4.5
Compensation
Financial compensation may be provided to compensate for parent’s time completing
follow-up. This compensation must be approved by each site’s Institutional Review Board.
6
Data Management
6.1
Clinical Sites
Study data will be recorded on paper work forms, which will be retained at the clinical
site. Data will then be entered into the electronic data capture (EDC) system provided
by the Data Coordinating Center at the University of Utah School of Medicine.
The clinical investigator at each participating site will complete a Form FDA 1572,
Statement of Investigator. That individual is responsible for all aspects of study imple-
mentation, including administration of study drug, collection of accurate study data, and
correct entry of the data into the EDC. These tasks may be speciﬁcally delegated to other
individuals at the clinical site, but the clinical investigator is responsible to supervise all
aspects of the study, and is responsible to assure that all sta↵involved in this study are
adequately trained to perform the delegated tasks. All local research records will remain
in a locked ﬁle in a secure room unless being used by research sta↵, and all computerized
information will be maintained on password protected computers.
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6.2
PECARN Data Coordinating Center (Utah)
In addition to locally secured, identiﬁable information, partially identiﬁable information
for all sites will be maintained at the PECARN Data Coordinating Center, located at
the University of Utah in Salt Lake City, Utah. The Data Coordinating Center has a
state-of-the-art computer infrastructure with a dedicated server room with a ﬁre sup-
pression system, air conditioning, cooling system and separate air ﬁltering. The server
facility is locked separately from the remainder of the Data Coordinating Center and
access to the building is monitored by security personnel year round. The Data Co-
ordinating Center coordinates its network infrastructure and security with the Health
Sciences Campus (HSC) information systems at the University of Utah. This provides
the Data Coordinating Center with e↵ective ﬁrewall hardware, automatic network in-
trusion detection, and the expertise of dedicated security experts working at the University.
Network equipment includes four high-speed switches. User authentication is cen-
tralized with two Windows 2008 domain servers. Communication over public networks
is encrypted with virtual point-to-point sessions using SSL or VPN technologies, both
of which provide at least 128 bit encryption. OpenClinica (Web-based clinical studies
data management system), eRoomTM (Web-based collaborative workspace) and other
web applications use the SSL protocol to transmit data securely over the Internet. Direct
access to Data Coordinating Center machines is only available while physically located
inside the Data Coordinating Center oﬃces, or via a VPN client. All network traﬃc is
monitored for intrusion attempts, security scans are regularly run against our servers, and
IT sta↵are notiﬁed of intrusion alerts.
Production servers running mission critical applications are clustered and conﬁgured
for failover events. Servers are backed up with encryption through a dedicated backup
server that connects across an internal 10 gigabit network to a tape drive. Storage area
networking (SAN) applications, clusters, and switch-to-switch links are also on a 10
gigabit network. Incremental backups occur hourly during the week. Incremental backups
also are performed nightly with full system backups occurring every week. Tapes are
stored in a ﬁreproof safe inside the data center facility, and full backups are taken to an
o↵-site commercial storage facility. Security is maintained with Windows 2008 user/group
domain-level security.
Users are required to change their passwords every 90 days, and workstations time
out after 5 minutes of inactivity. All ﬁles are protected at group and user levels; database
security is handled in a similar manner with group level access to databases, tables, and
views in Microsoft SQL Server. All portable computers are whole-disk-encrypted.
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6.3
Data Conﬁdentiality
The PI and other research personnel have all completed training and received certiﬁcation
in Human Subjects Research Protection and HIPAA. All project sta↵hired will also
successfully complete this training prior to engaging in any research or treatment with
study participants and renew this training as required by their institution.
The investigators and sta↵of the Data Coordinating Center are fully committed to
the security and conﬁdentiality of all data collected for PECARN studies. All Data
Coordinating Center personnel at the University of Utah have signed conﬁdentiality
agreements concerning all data encountered in the center. Violation of these agreements
may result in termination from employment at the University of Utah. In addition, all
personnel involved with data coordinating center data systems have received Human
Subjects Protection and HIPAA education.
The sta↵, reviewers and investigators involved with this study will be required to sign
agreements from the Data Coordinating Center that relate to maintenance of passwords,
information system security, and data conﬁdentiality.
6.4
Data Quality Management and Monitoring
The Data Coordinating Center monitors PECARN studies on behalf of the investigators
and the funding agency. The purposes of monitoring include demonstration of adherence
to human subjects protection requirements and assurance of high quality study data.
Monitoring is usually done remotely and may also involve physical site monitoring visits.
Site monitoring is described in more detail in Section 9.2.
6.5
Record Access
The medical record and study ﬁles (including informed consent, permission, and assent
documents) must be made available to authorized representatives of the Data Coordinating
Center, upon request, for source veriﬁcation of study documentation. In addition, medical
information and data generated by this study must be available for inspection upon request
by representatives of the the National Institutes of Health, Food and Drug Administration,
and the Institutional Review Board (IRB) for each study site.
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7
Protection of Human Subjects
7.1
Institutional Review Board (IRB) Approval
The Data Coordinating Center and each clinical center must obtain approval from their
respective IRB prior to participating in the study.
The Data Coordinating Center
will track IRB approval status at all participating centers and will not permit subject
enrollment without documentation of initial IRB approval and maintenance of that
approval throughout subsequent years of the project.
7.2
Informed Consent
This protocol requires that parents or other legally empowered guardians sign a parental
permission form. The parent or legal guardian will be informed about the objectives of
the study and the potential risks. Parents or legal guardians of eligible children with
symptoms of gastroenteritis will be approached to provide permission for their child’s
participation in the study. Parental or guardian permission will be obtained prior to
initiation of study activities. Documentation of parental permission will be maintained at
the study site. As the maximum eligible age is 48 months, child assent is not applicable.
7.3
Potential Risks
Lactobacilli are ubiquitous in the human diet and are a large part of the over 1 trillion
live bacteria that reside in the gastrointestinal tract of healthy individuals. Overall, Lac-
tobacillus rhamnosus GG, ATCC 53103 (LGG) is well tolerated in the pediatric patient
population. Infections (bacteremia, endocarditis, pneumonia, deep abdominal abscesses)
have been reported in sick neonates, severely debilitated and immune-compromised in-
dividuals given probiotics. The use of probiotics in these individuals continues to be
controversial; however prospective studies have been conducted in adults and children
with HIV as well as preterm neonates, with no reported systemic infections. Finally, there
are 7 case reports of invasive disease after administration of Lactobacillus rhamnosus GG,
ATCC 53103 (LGG). These occurred in patients in intensive care units, in patients with
central venous catheters, or in patients who are on immunosuppressive therapy, have short
gut syndrome, or are at risk for endocarditis. These risk factors are exclusion criteria
from our study population.
The clinical risks of invasive infection from Lactobacillus rhamnosus are related to
receiving Lactobacillus rhamnosus GG, ATCC 53103 (LGG). There are risks associated
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with acute gastroenteritis that are not related to study participation, including dehydra-
tion, electrolyte abnormalities, systemic infection and co-infection, and hospital admission.
All subjects will be clinically treated for acute gastroenteritis in accordance with local
site treatment protocols. There may be other unknown risks of Lactobacillus rhamnosus
GG, ATCC 53103 (LGG) in children with acute gastroenteritis.
Loss of conﬁdentially is always a risk in a study, but safeguards are in place to protect
against this.
7.4
Protections Against Potential Risks
Several steps will be taken to minimize the risks of participation in the study. All of the
participating clinical centers are tertiary pediatric hospitals with highly trained pediatric
sta↵. Subjects will be closely followed after discharge. Families will be contacted daily
until both the diarrhea and vomiting have resolved and the treatment has been completed.
Additional contact will be made on day 14, and months 1, 3, 6, 9 and 12 for long term
safety outcomes. Parents or legally authorized representatives will also receive speciﬁc
instructions as to when to see a health care provider. If an adverse event is reported at
the time of follow-up, research personnel will refer subjects for appropriate medical care,
when applicable.
Loss of conﬁdentiality will be mitigated by the use of the PECARN Data Coordinating
Center which has a highly secure IT infrastructure, and by the existence of trained
research sta↵at participating sites. Data security is described in Section 6.
7.5
Potential Beneﬁts
Subjects participating in the study may beneﬁt directly by experiencing less severe disease,
shorter duration of symptoms, and decreased need for further health care utilization.
There may also be reduced symptoms (i.e. diarrhea, vomiting, fever) and morbidity,
thereby diminishing acute gastroenteritis-associated resource consumption (e.g. physician
visits, hospitalization) and societal costs. Additional beneﬁts in the study include closer
monitoring of symptoms and potentially earlier recognition of any worsening of acute
gastroenteritis due to the frequency of telephone follow up and communication with the
family. The knowledge gained in this study may lead to improved treatment options for
gastroenteritis for other children and lead to new therapeutic options for future patients.
Subjects and their families may therefore beneﬁt indirectly by participating in research
with the potential to provide subsequent beneﬁt to others. Finally, future analysis of bulk
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stool specimens will enable a better understanding of potential mechanisms of action of
Lactobacillus rhamnosus GG, ATCC 53103 (LGG), which will likely provide beneﬁt to
future patients.
8
Data and Safety Monitoring Plan
8.1
Data Safety Monitoring Board (DSMB)
This study will have a Data Safety Monitoring Board (DSMB) appointed in accordance
with instructions from the NICHD program oﬃcer. The DSMB will have a charter, will
approve the protocol prior to implementation, and will review interim analyses for safety
and eﬃcacy.
The purpose of the DSMB is to advise the Federal funding agency (NICHD), the
study Principal Investigator (Dr. Schnadower), and the PECARN Steering Committee
regarding the continuing safety of study subjects and the continuing validity and scientiﬁc
merit of the study. The DSMB is responsible for monitoring accrual of study subjects,
adherence to the study protocol, assessments of data quality, performance of individual
clinical sites, review of serious adverse events and other subject safety issues, and review
of formal interim statistical analyses of treatment eﬃcacy.
The Data Coordinating Center will send reports relating to these topics to DSMB
members prior to each DSMB meeting. The Data Coordinating Center will sta↵DSMB
meetings. The production and approval of DSMB minutes will be done in accordance with
requirements of the NICHD. Each DSMB meeting will have a summary recommendation
that will be provided to each participating clinical site for submission to the local
Institutional Review Board (IRB). More detailed information from the DSMB meetings
will not be routinely provided for local IRB submission.
8.2
Frequency of Interim Analysis:
The Data Safety Monitoring Board (DSMB) will meet after 80 patients (safety end
points for 1 month), approximately 350 patients (end of 2nd year of enrollment) and 620
patients (end of 3rd year of enrollment) to review enrollment, study procedures, loss to
follow-up, drop-in rate, and interim safety and eﬃcacy results. The analyses will test the
hypothesis that the probability of developing moderate-to-severe acute gastroenteritis in
the probiotic arm is equal to that in the placebo arm. An analysis will also be conducted
after 20 subjects under 6 months of age have been enrolled. The DSMB is to review
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interim data and make recommendations regarding continuation or modiﬁcation of the
study based on safety in this age group.
Conservative O’Brien-Fleming monitoring
boundaries, implemented using the Lan-DeMets ↵-spending function approach, will be
used as guidelines for early stopping for eﬃcacy.
8.3
Adverse Event Reporting
8.3.1
Deﬁnitions, Relatedness, Severity and Expectedness
Deﬁnition:
An adverse event (AE) is any untoward medical occurrence experienced by a
subject. An event constitutes a disease, a set of related signs or symptoms, or a single sign
or symptom. On each study day, the site investigators will evaluate adverse events. Study
sta↵will obtain information on symptoms and adverse events on scheduled follow up calls.
Adverse events not previously documented in the study will be recorded on the adverse
event record form. The nature of each experience, date and time (where appropriate) of
onset, outcome, course, and relationship to treatment should be established.
Relatedness:
The suspected relationship between study interventions and any adverse
event will be determined by the site investigator using the following criteria. Relatedness
may not be assessed by a research coordinator, and must be assessed by an investigator.
Not Related: The event is clearly related to other factors, such as the subject’s clinical
state, therapeutic interventions, or concomitant drugs administered to the subject.
Possibly Related: The event follows compatible temporal sequence from the time of
beginning the assigned study intervention, but could have been produced by other
factors such as the subject’s clinical state, therapeutic interventions, or concomitant
drugs administered to the subject.
Probably Related: The event follows a reasonable temporal sequence from the time
of beginning the assigned study intervention, and cannot be reasonably explained
by other factors such as the subject’s clinical state, therapeutic interventions, or
concomitant drugs administered to the subject.
Some toxicities will be diﬃcult to distinguish from abdominal symptoms related to acute
gastroenteritis (such as bloating, abdominal pain, diarrhea, fever and diaper rash), and
only at the time of analysis will we be able to determine whether these signs and symptoms
are di↵erent between the groups.
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Seriousness:
The severity of clinical adverse events and laboratory abnormalities will
be recorded by the site investigator and categorized. A serious adverse event (SAE) is an
adverse event that:
• results in death; or
• is life-threatening (the patient was, in the view of the site investigator, in immediate
danger of death from the event as it occurred); or
• requires inpatient hospitalization or prolongs an existing hospitalization; or
• results in persistent or signiﬁcant disability or incapacity; or
• results in congenital anomaly/birth defect; or
• any other event that, based upon appropriate medical judgment, may jeopardize
the subject’s health and may require medical or surgical intervention to prevent one
of the other outcomes listed in this deﬁnition.
Expectedness of the Event:
All adverse events, including serious adverse events, will
be evaluated as to whether their occurrence was expected or unexpected. An adverse
event is considered expected if it is known to be associated with acute gastroenteritis
(acute gastroenteritis), other underlying medical conditions of the subject, is directly
related to study outcome, or is otherwise mentioned in the protocol, informed consent,
investigator brochure, or other study documents.
Expected complications of acute
gastroenteritis include loss of appetite, abnormal taste, heartburn, constipation, skin rash,
fever, nasal congestion, sore throat, cough, headache, malaise, muscle aches, chills, blood
in stool, bloating, gas, intestinal rumbling, abdominal distention, foul smelling stools,
diarrhea, buttock rash, abdominal pain, abdominal cramps, nausea, vomiting, dehydration,
electrolyte and other laboratory abnormalities, systemic infection and co-infection, seizures
and hospital admission. Other expected adverse events are reactions known to occur
with probiotic administration, speciﬁcally bloating, gas, intestinal rumbling, diarrhea,
blood in stool, bacteremia, abdominal pain, abdominal cramps, nausea, vomiting, foul
smelling stools, loss of appetite, abnormal taste, heartburn, constipation, skin rash, fever,
nasal congestion, sore throat, cough, headache, malaise, muscle aches, other symptoms
associated with viral syndromes.
Treatment or Action Taken:
For each adverse event, the site investigator will record
whether an intervention was required:
• Intervention: Surgery or procedure
• Other Treatment: Medication initiation, change, or discontinuation
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• None: No action taken
Outcome of Event:
Finally, the site investigator will record the clinical outcome of
each adverse event as follows:
• Death
• Recovered and the patient returned to baseline status
• Recovered with permanent sequelae
• Symptoms continue
8.3.2
Time Period for Adverse Events
For purposes of this study, adverse events occur following randomization through 30 days
after the last study drug dose will be recorded. Serious adverse events, unexpected medi-
cally attended events, and new onset chronic illnesses will be recorded from randomization
through twelve months after the last study dose. Speciﬁcally, events that occur following
parental permission to participate in the study, but prior to actual randomization, are
not adverse events. These should be recorded as baseline conditions.
8.3.3
Data Collection Procedures for Adverse Events
After patient randomization, all adverse events (including serious adverse events), whether
anticipated or unanticipated, will be recorded according to the date of ﬁrst occurrence,
severity, and their duration, as well as any treatment prescribed. Any medical condition
present at the time of randomization, recorded in the patient’s baseline history at study
entry, which remains unchanged or improves, will not be recorded as an adverse event at
subsequent evaluations. However, worsening of a medical condition that was present at
the time of randomization will be considered a new adverse event and reported.
Abnormal laboratory values that are clinically signiﬁcant will be recorded as adverse
events and the site investigator will assess the severity and relationship to the study.
Laboratory values that are abnormal at the time of randomization and that do not worsen
will not be recorded as adverse events.
Adverse events will be coded using the MedDRA coding vocabulary. Coding will be
done centrally at the Data Coordinating Center because this requires speciﬁc training.
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8.3.4
Unanticipated Problems (UP)
Unanticipated problems (UP) are deﬁned as incidents, experiences, or outcomes that are
unexpected, related to participation in the study, and suggest that the research places
subjects at a greater risk of harm than was previously known or recognized. The site
investigator will report unanticipated problems to the Data Coordinating Center within 24
hours. A detailed completed report will be required to be sent to the Data Coordinating
Center within 3 working days of the event. After receipt of the complete report, the Data
Coordinating Center will report these unanticipated problems to the NICHD Program
Oﬃcial or Project Oﬃcer in an expedited manner (within 24 hours). In accordance with
local IRB requirements, the site investigator may be required to report such unanticipated
problems to the IRB in addition to notifying the Data Coordinating Center. In the
event that the medical monitor believes that such an event warrants emergent suspension
of enrollment in the trial, and NICHD sta↵cannot be reached expeditiously, the Data
Coordinating Center will notify the study investigator (Dr.Schnadower) and all site
investigators to cease enrollment in the trial. Resumption of enrollment will not occur
without consent of the NICHD sta↵after discussion with the DSMB.
8.3.5
Monitoring Serious Adverse Events
The Principal Investigator of the Data Coordinating Center (Dr. Dean) will act as the
medical monitor for this study. If Dr. Dean is unavailable, a qualiﬁed physician will be
designated to fulﬁll this function. Site investigators and/or research coordinators will
report serious adverse events to the Data Coordinating Center within 24 hours. A detailed
completed report will be required to be sent to the Data Coordinating Center within 3
working days of the event, and the medical monitor will assess all serious adverse events
reported from site investigators.
For each of these serious adverse events, the site investigator will provide suﬃcient
medical history and clinical details for a safety assessment to be made with regard to
continuation of the trial. The medical monitor will sign each SAE report after review.
All SAE reports will be retained at the Data Coordinating Center, and all SAE reports
will be available for review by DSMB members and NICHD sta↵.
In the unlikely event that the medical monitor believes an unexpected and study-
related SAE warrants emergent cessation of enrollment in the trial, NICHD sta↵and the
DSMB chairperson will be immediately consulted. If these individuals concur with the
judgment of the medical monitor, or if the NICHD sta↵and the DSMB chairperson cannot
be reached expeditiously, the Data Coordinating Center will notify the study investigator
(Dr.Schnadower) and all site investigators to cease enrollment in the trial. Resumption of
enrollment will not occur without consent of the NICHD sta↵after discussion with the
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DSMB.
In accordance with local IRB requirements, the site investigator may be required to
report such events to the IRB in addition to notifying the Data Coordinating Center.
After notiﬁcation of the NICHD Program Oﬃcial or Project Oﬃcer, and the DSMB
chairperson, of serious, unexpected, and study-related adverse events or unanticipated
problems (UP), decisions will be made whether to continue the study without change,
and whether to convene the entire DSMB for an emergent meeting. If a decision is made
to suspend enrollment in the trial, this will be reported to the study investigator (Dr.
Schnadower) and all clinical investigators, who will be instructed to report this to their
local IRB.
The DSMB will review all adverse events (not necessarily serious, unexpected, and
study-related) during scheduled DSMB meetings. The Data Coordinating Center will
prepare a Summary Report of Adverse Events for the DSMB meetings, classiﬁed with
the MedDRA coding system.
8.3.6
Follow-up of Serious, Unexpected and Related Adverse Events
All serious, unexpected and related adverse events, that are unresolved at the time of the
patient’s termination from the study or discharge from the hospital, will be followed by
the Clinical Center investigators until the events are resolved, subject is lost to follow-up,
the adverse event is otherwise explained or has stabilized, or 12 months have passed from
the time of last study dose.
9
Study Training and Monitoring
9.1
Study Training
A formal training program for investigators and research sta↵will be held prior to the
start of enrollment. The training program will cover regulatory topics and Good Clinical
Practice. The training will also provide in depth explanations regarding study procedures,
clinical care, adverse event reporting, data entry procedures, quality assurance, site
monitoring, and the informed consent process. A manual of operations will be provided
to each Clinical Center investigator prior to the start of enrollment. The manual will
detail speciﬁc information about the study procedures, regulatory information, safety
reporting, and other necessary information. Updates and revisions to the manual will be
made available electronically. The Data Coordinating Center, in collaboration with the
study investigator (Dr. Schnadower), will be the main contact for study questions.
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9.2
Study Monitoring
The investigators recognize the importance of ensuring data of excellent quality. Site
monitoring is critical to this process. Site monitoring has been a very e↵ective tool for
maintaining data quality in previous PECARN studies, and we will utilize this process
to ensure excellent quality data in the proposed study. Our site monitoring plan is
designed to identify problems with sites and methods for handling problems that arise.
Site monitors must be provided with full access to study materials and the medical records
for study subjects. If the medical records are in electronic form, the clinical investigator
or an authorized individual must provide any assistance necessary to facilitate the site
monitor’s review of data in the electronic medical record.
9.2.1
Site Monitoring Plan
A supplemental study-speciﬁc monitoring plan, separate from the protocol will be com-
pleted which outlines speciﬁc criteria for monitoring. This plan will include the number of
planned site visits, criteria for focused visits, or additional visits, a plan for chart review
and a follow up plan for non-compliant sites. The monitoring plan also describes the type
of monitoring that will take place (e.g. sample of all subjects within a site; key data or all
data), the schedule of visits, how they are reported and a time frame to resolve any issues
found. Remote site monitoring schedules will be determined by the Data Coordinating
Center in coordination with the study principal investigator.
9.2.2
Clinical Site Monitoring
Site monitoring visits will be performed by a trained site monitor during the study
period to ensure regulatory compliance, patient safety, and to monitor the quality of data
collected. Essential document binders, regulatory documents and data collection forms
may be reviewed. Interim visits will take place depending on grant budget, site enrollment,
and compliance issues identiﬁed. The site monitor will provide each site with a written
report, and sites will be required to follow up on any deﬁciencies. It is anticipated that
the study monitoring visits for this protocol will consist of a site initiation visit (prior
to patient enrollment), interim visits, and a close out visit. The site initiation may take
place as group training made up of site investigators and research assistants.
9.2.3
Remote Monitoring
The Data Coordinating Center may supplement on-site monitoring with remote monitoring
activities. Remote monitoring involves detailed review of the data entered by the Clinical
Center and consultations with the Clinical Center investigator and/or research coordinator
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to review safety and data quality. This may require uploading de-identiﬁed copies of
speciﬁc parts of the medical record, patient study ﬁle, regulatory documentation, or other
source documents to the Data Coordinating Center sta↵, who review those materials
against the data recorded in the electronic data capture system. This helps assure protocol
compliance and accurate data collection. The Data Coordinating Center may conduct
more remote monitoring activities early in the trial to assure protocol compliance and
identify any training issues that may exist. Remote monitoring the documents will be
retained in accordance with federal requirements. Safety of subjects will be monitored
and ensured in accordance with the Data and Safety Monitoring Board (DSMB) plan.
9.2.4
Pharmacy Monitoring
The Clinical Center pharmacy must maintain adequate records of all dispensed study
drug. Each pharmacy will be monitored and may be requested to send copies of these
documents to the Data Coordinating Center. Since this study will use a central pharmacy,
that pharmacy must also maintain adequate records and will also be monitored.
10
Regulatory Issues
10.1
Food and Drug Administration
This trial is being conducted under an Investigational New Drug application approved by
the Food and Drug Administration (Investigational New Drug application #15371). The
clinical investigator at each participating site will complete a Form FDA 1572, “Statement
of Investigator.”
10.2
Health Insurance Portability and Accountability Act
The abstracted data will include limited identiﬁers as deﬁned by the Health Insurance
Portability and Accountability Act, and speciﬁc contact information will be provided to
research sta↵conducting follow up with parents. Abstracted data will be retained and
archived at the Data Coordinating Center in accordance with record retention requires
of the Food and Drug Administration and the NIH. Contact information will not be
provided to the Data Coordinating Center (it will be provided directly to the central
follow up research sta↵). For data analysis outside the Data Coordinating Center (e.g.,
when a public access database is made available), the Data Coordinating Center will
create a completely de-identiﬁed analytical database for use by the study investigators,
and for ﬁnal archiving. All study sites have been or will be o↵ered Business Associate
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Agreements with the University of Utah. Copies of signed Business Associate Agreements
are maintained at the Data Coordinating Center.
10.3
Inclusion of Women and Minorities
The gender, ethnic and racial composition of patients enrolled in all PECARN studies is
a function of the underlying referral population at each PECARN site participating in
this trial. There will be no exclusion of patients based on gender, race, or ethnicity.
10.4
ClinicalTrials.gov Requirements
This trial has been registered at ClinicalTrials.gov (NCT #01773967). The title is “Impact
of Emergency Department Probiotic (LGG) Treatment of Pediatric Gastroenteritis.”
10.5
Retention of Records
For federally funded studies subject to the Common Rule, records relating to the research
conducted shall be retained for at least 3 years after completion of the research. Completion
of the research for this protocol should be anticipated to include planned primary and
secondary analyses, as well as subsequent derivative analyses. Completion of the research
also entails completion of all publications relating to the research. All records shall be
accessible for inspection and copying by authorized representatives of the regulatory
authorities at reasonable times and in a reasonable manner [45 CFR §46.115(b)].
Bibliography
[1] P. Coppens, M. F. da Silva, and S. Pettman. European regulations on nutraceuticals,
dietary supplements and functional foods: a framework based on safety. Toxicology,
221(1):59–74, 2006.
[2] L. G. Saldanha. US Food and Drug Administration regulations governing label
claims for food products, including probiotics. Clin Infect Dis, 46 Suppl 2:S119–21;
discussion S144–51, 2008.
[3] A. von Wright. Regulating the safety of probiotics–the European approach. Curr
Pharm Des, 11(1):17–23, 2005.
[4] Cincinnati Children’s Hospital. Use of Lactobacillus GG in children with acute
gastroenteritis, 2011.
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Impact of Emergency Department Probiotic
Treatment of Pediatric Gastroenteritis
(Probiotics Study)
PECARN Protocol Number 032
Pediatric Emergency Care Applied Research Network
National Institute for Child Health and Human Development
(NICHD)
Protocol Version 3.00
Version Date: February 13, 2017
Printing Date: February 13, 2017


Copyright c⃝2014. University of Utah School of Medicine on behalf of the Principal
Investigator, David Schnadower, M.D. and the Pediatric Emergency Care Applied Re-
search Network (PECARN). All rights reserved.
This protocol is PECARN Protocol Number 032, and has been authored by David
Schnadower, M.D., Washington University, for implementation with the PECARN inves-
tigators. This study is supported by R01-HD071915 awarded to Washington University
(PI:David Schnadower, M.D.) by the Eunice Kennedy Shriver National Institute for Child
Health and Human Development (NICHD).
The PECARN research node centers are Washington University, University of Michi-
gan at Ann Arbor, Cincinnati Children’s Hospital Medical Center, Columbia University,
University of California at Davis Medical Center, Children’s Hospital of Pittsburgh,
and Children’s National Medical Center and are supported by Cooperative Agreements
U03-MC00003, U03-MC22684, U03-MC00007, U03-MC00001, U03MC22685, and U03-
MC00006 from the Emergency Medical Services for Children (EMSC) Program, Maternal
and Child Health Bureau, Health Resources and Services Administration.
This document was prepared by the PECARN EMSC Data Coordinating Center
(DCC) located at the University of Utah School of Medicine, Salt Lake City, Utah. The
document was written and typeset using LATEX2". The DCC at the University of Utah is
supported by Cooperative Agreement U03-MC00008 from the Emergency Medical Services
for Children (EMSC) Program, Maternal and Child Health Bureau, Health Resources
and Services Administration.


Protocol 032 (Schnadower)
Page 3 of 49
PROTOCOL TITLE:
Impact of Emergency Department Probiotic Treatment of Pediatric Gastroenteritis
Short Title: Probiotics Study
PECARN Protocol Number: 032
Lead Investigator and Author:
David Schnadower, M.D.
Washington University
Protocol Version: 3.00
Version Date: February 13, 2017
I conﬁrm that I have read this protocol, I understand it, and I will conduct the study
according to the protocol. I will also work consistently with the ethical principles that have
their origin in the Declaration of Helsinki and will adhere to the Ethical and Regulatory
Considerations as stated. I conﬁrm that if I or any of my sta↵are members of the Insti-
tutional Review Board, we will abstain from voting on this protocol, its future renewals,
and its future amendments.
Principal Investigator Name:
Principal Investigator Signature:
Date:
Probiotics Study Protocol Version 3.00
Protocol Version Date: February 13, 2017
The EMSC Pediatric Emergency Care Applied Research Network


Page 4 of 49
Protocol 032 (Schnadower)
THIS PAGE IS INTENTIONALLY BLANK.
Probiotics Study Protocol Version 3.00
Protocol Version Date: February 13, 2017
The EMSC Pediatric Emergency Care Applied Research Network


Protocol 032 (Schnadower)
Page 5 of 49
Contents
1
Study Summary
9
1.1
Hypotheses
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
9
1.2
Speciﬁc Aims . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
9
1.3
Trial Endpoints . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
10
1.4
Subject Eligibility, Accrual and Study Duration . . . . . . . . . . . . . .
10
2
Rationale and Background
11
2.1
Rationale for Probiotic Eﬃcacy . . . . . . . . . . . . . . . . . . . . . . .
12
2.2
Limitations of Research to Date . . . . . . . . . . . . . . . . . . . . . . .
13
2.3
Validation of the Modiﬁed Vesikari Score . . . . . . . . . . . . . . . . . .
14
3
Study Design and Data Collection
15
3.1
Study Design Overview . . . . . . . . . . . . . . . . . . . . . . . . . . . .
15
3.2
Participant Screening and Consent
. . . . . . . . . . . . . . . . . . . . .
15
3.3
Baseline Data Collection . . . . . . . . . . . . . . . . . . . . . . . . . . .
16
3.4
Follow Up Data Collection . . . . . . . . . . . . . . . . . . . . . . . . . .
16
4
Study Procedures
17
4.1
Randomization (Enrollment) . . . . . . . . . . . . . . . . . . . . . . . . .
17
4.2
Study Drug Administration
. . . . . . . . . . . . . . . . . . . . . . . . .
17
4.3
Discontinuation of Study Drug . . . . . . . . . . . . . . . . . . . . . . . .
19
4.4
Withdrawal from Study
. . . . . . . . . . . . . . . . . . . . . . . . . . .
20
4.5
Stool Sample Testing . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
20
5
Data Analysis
21
5.1
Speciﬁc Aim Analyses
. . . . . . . . . . . . . . . . . . . . . . . . . . . .
21
5.2
Secondary Study Outcomes
. . . . . . . . . . . . . . . . . . . . . . . . .
23
5.3
Sample Size Calculations and Statistical Power . . . . . . . . . . . . . . .
24
5.3.1
Enrichment Design . . . . . . . . . . . . . . . . . . . . . . . . . .
25
5.3.2
Sub-group Analyses . . . . . . . . . . . . . . . . . . . . . . . . . .
26
5.4
Recruitment Estimates and Attrition . . . . . . . . . . . . . . . . . . . .
26
5.4.1
Recruitment . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
26
5.4.2
Potential for Bias . . . . . . . . . . . . . . . . . . . . . . . . . . .
26
5.4.3
Compliance . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
27
5.4.4
Loss to Follow-up . . . . . . . . . . . . . . . . . . . . . . . . . . .
27
5.4.5
Compensation . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
27
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6
Data Management
27
6.1
Clinical Sites
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
27
6.2
PECARN Data Coordinating Center (Utah) . . . . . . . . . . . . . . . .
28
6.3
Data Conﬁdentiality
. . . . . . . . . . . . . . . . . . . . . . . . . . . . .
29
6.4
Data Quality Management and Monitoring . . . . . . . . . . . . . . . . .
29
6.5
Record Access . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
30
7
Protection of Human Subjects
30
7.1
Institutional Review Board (IRB) Approval
. . . . . . . . . . . . . . . .
30
7.2
Informed Consent . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
30
7.3
Potential Risks
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
30
7.4
Protections Against Potential Risks . . . . . . . . . . . . . . . . . . . . .
31
7.5
Potential Beneﬁts . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
31
8
Data and Safety Monitoring Plan
32
8.1
Data Safety Monitoring Board (DSMB) . . . . . . . . . . . . . . . . . . .
32
8.2
Frequency of Interim Analysis: . . . . . . . . . . . . . . . . . . . . . . . .
33
8.3
Adverse Event Reporting . . . . . . . . . . . . . . . . . . . . . . . . . . .
33
8.3.1
Deﬁnitions, Relatedness, Severity and Expectedness . . . . . . . .
33
8.3.2
Time Period for Adverse Events . . . . . . . . . . . . . . . . . . .
35
8.3.3
Data Collection Procedures for Adverse Events
. . . . . . . . . .
35
8.3.4
Unanticipated Problems (UP) . . . . . . . . . . . . . . . . . . . .
36
8.3.5
Monitoring Serious Adverse Events . . . . . . . . . . . . . . . . .
36
8.3.6
Follow-up of Serious, Unexpected and Related Adverse Events . .
37
9
Study Training and Monitoring
37
9.1
Study Training
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
37
9.2
Study Monitoring . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
38
9.2.1
Site Monitoring Plan . . . . . . . . . . . . . . . . . . . . . . . . .
38
9.2.2
Clinical Site Monitoring
. . . . . . . . . . . . . . . . . . . . . . .
38
9.2.3
Remote Monitoring . . . . . . . . . . . . . . . . . . . . . . . . . .
39
9.2.4
Pharmacy Monitoring
. . . . . . . . . . . . . . . . . . . . . . . .
39
10 Regulatory Issues
39
10.1 Food and Drug Administration
. . . . . . . . . . . . . . . . . . . . . . .
39
10.2 Health Insurance Portability and Accountability Act
. . . . . . . . . . .
39
10.3 Inclusion of Women and Minorities . . . . . . . . . . . . . . . . . . . . .
40
10.4 ClinicalTrials.gov Requirements . . . . . . . . . . . . . . . . . . . . . . .
40
10.5 Retention of Records . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
40
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Bibliography
40
List of Tables
1
Modiﬁed Vesikari Score
. . . . . . . . . . . . . . . . . . . . . . . . . . .
15
2
Power Analysis
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
25
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Abstract
Practice guidelines do not endorse routine use of probiotics in pediatric acute
gastroenteritis. However, probiotic manufacturers aggressively purvey probiotics
using health claims that have not been supported by rigorous research, and the
world-wide market for probiotic products is equivalent to $32.6 billion per year. The
Food and Drug Administration and the European Food Safety Authority remain
concerned about probiotic value and safety.1–3 Some institutions now recommend
the routine use of probiotics based on potentially ﬂawed or limited evidence,4 and
parents of patients with acute gastroenteritis often administer probiotics to their
children without guidance from medical professionals.5 Since the use of probiotics
is increasing without adequate evidence to support its use in the United States, the
study described in this protocol was designed and successfully submitted to the
National Institute for Child Health and Human Development (NICHD) for funding.
The overall objective of this randomized, placebo-controlled, double-blind study
is to determine if probiotic administration reduces the severity of acute gastroen-
teritis episodes in children aged 3 to 48 months. The probiotic agent that will be
used in this trial is Lactobacillus rhamnosus GG, ATCC 53103 (LGG).
Participants will be randomized to receive a ﬁve-day course of probiotic or
placebo. The trial is anticipated to enroll 970 children, age 3-48 months, treated
in participating emergency departments for acute gastroenteritis. We deﬁne acute
gastroenteritis as the presence of three or more watery stools in a 24-hour period.
Children with underlying illness that pose potential increased risk from probiotic
therapy (e.g. indwelling vascular access line, structural heart disease, immuno-
suppressive therapy or known immunodeﬁciency, chronic gastrointestinal disease
such as inﬂammatory bowel disease, or household contact with immunodeﬁciency
or immunosuppressive therapy) will be excluded. The age range of 3-48 months
was selected because this age group has the highest incidence of acute gastroen-
teritis and the greatest morbidity. Subjects will be recruited at the time of an
emergency department visit. All eligible subjects who present for treatment when
study personnel are available will be approached for participation. Those agreeing
to participate will be randomized, using block randomization stratiﬁed by study
site, to treatment groups. The study will be conducted at multiple sites within
the Pediatric Emergency Care Applied Research Network (PECARN). We will also
collect and freeze pre- and post-treatment bulk stool specimens at the lead study
site to assess the mechanism of action of the speciﬁc probiotic agent, Lactobacillus
rhamnosus GG, ATCC 53103 (LGG).
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1
Study Summary
This randomized, double-blind, placebo-controlled trial will quantify the beneﬁts and
potential side e↵ects associated with probiotic administration in ambulatory children
presenting to the emergency department with acute gastroenteritis. This will provide
the ﬁrst deﬁnitive evidence in the United States for, or against, using probiotic therapy
for this condition. This study will use the most commonly employed probiotic agent
(Lactobacillus rhamnosus GG, ATCC 53103 (LGG)) approved for use in the United
States. The results of this multicenter study will guide the standard of care: if probiotic
administration is associated with beneﬁt, it o↵ers an inexpensive, safe and easy way to
administer treatment to reduce morbidity from acute gastroenteritis. If the trial does
not demonstrate probiotic eﬃcacy, healthcare, caregiver and societal resources may be
refocused on alternative therapeutic interventions.
1.1
Hypotheses
The hypotheses of this study are:
1. In children with acute gastroenteritis, probiotic administration in the emergency
department will be associated with a clinically-important decrease in the proportion
of children su↵ering from moderate-severe disease, deﬁned by a validated Modiﬁed
Vesikari Score ≥9, compared to placebo.
2. In children with acute gastroenteritis, probiotic administration will not be associated
with serious adverse events, and will have a similar rate of side e↵ects (e.g. bloating,
fever) as compared to placebo-treated children.
1.2
Speciﬁc Aims
This project has the following Speciﬁc Aims:
Speciﬁc Aim 1. Determine the clinical e↵ectiveness of probiotic administration to re-
duce morbidity in children presenting to the emergency department with acute
gastroenteritis.
Speciﬁc Aim 2. Determine the safety and side e↵ect proﬁles of Lactobacillus rhamnosus
GG, ATCC 53103 (LGG) in children presenting to the emergency department with
acute gastroenteritis.
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1.3
Trial Endpoints
Primary Endpoints
• The primary eﬃcacy endpoint of this study is the presence of moderate-severe
acute gastroenteritis, as deﬁned by a total post-enrollment Modiﬁed Vesikari Score
≥9 during the 2-week follow-up period.
• The primary safety endpoint of this study is the occurrence of invasive disease
(including meningitis and bacteremia) from Lactobacillus rhamnosus.
Secondary Endpoints
1. Diarrhea duration: Time from randomization until the appearance of the last
watery stool as reported during daily surveys.
2. Vomiting duration: Time from randomization until the last vomiting episode as
reported during daily surveys. Vomiting duration is only evaluated in children who
vomited ≥3 times during the 24 hours prior to the emergency department visit.
3. Return visits: Return visits for unscheduled care to a healthcare provider related
to vomiting, diarrhea, dehydration, fever, or ﬂuid refusal, within 2 weeks of the
index visit. Scheduled visits (e.g. reassessment, vaccinations, unrelated issues) will
not be included.
4. Missed daycare: Days of daycare missed by subjects who attend daycare.
5. Missed work: Days of work missed by caregivers who work outside of the home.
6. Household transmission rate: A household census will be obtained at the time
of enrollment, and information about household contacts symptoms will be obtained
during daily surveys to determine household transmission rate.
7. Side E↵ects: Occurrence of side e↵ects such as weakness, bloating, gas, intestinal
rumbling, diarrhea, blood in stool, abdominal pain, abdominal cramps, nausea,
vomiting, loss of appetite, heartburn, constipation, skin rash, fever, nasal congestion,
sore throat, cough, headache, muscle aches, chills, and diaper rash.
1.4
Subject Eligibility, Accrual and Study Duration
Eligible participants will be identiﬁed by on-site study sta↵. Inclusion criteria are:
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1. Age 3-48 months (have not yet reached their fourth birthday); AND
2. Presence of 3 or more watery stools within 24 hours of screening; AND
3. Duration of vomiting or diarrhea less than 7 days; AND
4. Symptoms consistent with acute intestinal infectious process.
We will exclude subjects with any of the following:
1. Presence of an indwelling vascular access line; OR
2. Presence of structural heart disease excluding non-pathological heart murmurs; OR
3. Receiving immunosuppressive therapy or history of immunodeﬁciency; OR
4. Hematochezia in the preceding 48 hours; OR
5. Chronic gastrointestinal problems (e.g. short gut syndrome, inﬂammatory bowel
disease); OR
6. Patients with known pancreatitis; OR
7. History of abdominal surgery; OR
8. Critically ill patients; OR
9. Family member with an indwelling vascular access line, or on immunosuppressive
therapy, or with a known immunodeﬁciency; OR
10. Bilious emesis; OR
11. Probiotic use (supplement) in the preceding 2 weeks; OR
12. Oral or intravenous steroid use in the preceding six months; OR
13. Previously enrolled in this trial; OR
14. Allergy to lactobacillus or Microcrystalline Cellulose (MCC); OR
15. Allergy to erythromycin, clindamycin, AND β-lactam antibiotics (all); OR
16. Not available for daily follow-up while symptomatic; OR
17. Parent/guardian not speaking English or Spanish; OR
18. Under 6 months old AND premature (<37 weeks).
The trial is anticipated to enroll 970 subjects over four years, which will include four
acute gastroenteritis seasons. An interim safety analysis will be prepared for Data Safety
Monitoring Board (DSMB) review after the ﬁrst 80 subjects (half of whom will be under
1 year of age) have been followed for 1 month. At the time of this review, the DSMB
may alter the subsequent sample size based on overall event rates.
2
Rationale and Background
Acute gastroenteritis is a leading cause of malnutrition and death worldwide and a↵ects
millions of children in the United States each year.6, 7 Acute gastroenteritis exerts high
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impact burdens on children and their families: each episode causes on average 6-8 days
of diarrhea, 2-4 days of vomiting, and 2-4 days of fever.8–11 In two prospective studies
conducted in 11 Canadian and 5 United States pediatric emergency departments, 433/683
(63%) children 3-48 months of age with acute gastroenteritis had moderate to-severe symp-
toms at presentation, resulting in substantial daycare and parental work absenteeism.12, 13
The economic burden associated with such cases is considerable.14 Unfortunately, current
treatment options are limited to rehydration, symptomatic management and supportive
care, prevention of severe dehydration and secondary infection control.15–17
Probiotic agents represent a novel approach to management of pediatric acute gas-
troenteritis. Probiotics are viable microbes that are generally considered to be safe and
are relatively inexpensive, easily administered, and hypothesized to modulate disease
processes.18 They may also reduce symptoms (i.e. diarrhea, vomiting, fever)19–22 and
morbidity, thereby diminishing acute gastroenteritis-associated resource consumption (e.g.
physician visits, hospitalization) and societal costs. Numerous studies report promising
results in children with acute gastroenteritis treated with probiotics, but these studies have
been inadequate to change clinical practice, because of ﬂaws in methodology including
small sample sizes, lack of probiotic quality control, and outcomes that are of minimal
relevance to patients and their families.19 Remarkably, few studies of probiotics have
evaluated outpatients, a group representing >90% of acute gastroenteritis episodes in
the United States.23, 24 Moreover, only a single emergency department study of probiotic
eﬃcacy in acute gastroenteritis has been reported.20
To date, practice guidelines do not endorse routine use of probiotics in pediatric acute
gastroenteritis.5, 19, 25–27 However, current trends provide the motivations for the study
described in this protocol. First, probiotic manufacturers aggressively purvey probiotics
using health claims that have not been supported by rigorous research,28–31 and the
world-wide market for probiotic products is growing rapidly (projected growth 2009-2014
12.6%, now equivalent to $32.6 billion per year).32 Second, the United States Food and
Drug Administration and the European Food Safety Authority remain concerned about
probiotic value and safety.1–3 Third, some institutions now recommend the routine use of
probiotics based on potentially ﬂawed or limited evidence.4 Fourth, parents of patients
with acute gastroenteritis often administer probiotics to their children without guidance
from medical professionals.5
2.1
Rationale for Probiotic Eﬃcacy
Probiotics, deﬁned as viable microbial preparations with beneﬁcial e↵ects on the health
of the host,33 are regarded as safe, and are generally a↵ordable and convenient (i.e., as
over-the-counter food supplements). Probiotics, and Lactobacillus rhamnosus GG, ATCC
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53103 (LGG) in particular, promote colonization resistance and modulate immune re-
sponses in the host, and can be directly antimicrobial. Over 100 studies have studied how
probiotics can improve immune function in humans.34 At the mucosal surface, probiotics:
• compete with pathogenic bacteria for nutrients and adhesion binding sites;35–38
• produce antimicrobial substances;37, 39, 40
• provide nutrients to colonocytes;41
• alter epithelial gene expression;42 and
• reduce intestinal permeability.43
Additional mechanisms of action include enhancing phagocyte44 and natural killer cell
activity,45 and increasing fecal,46 salivary,47and systemic48 IgA levels.
Preliminary probiotic studies in humans, including over 56 trials in children with
gastroenteritis (17 of which used some form of Lactobacillus rhamnosus GG, ATCC
53103 (LGG) , the agent employed in this trial) suggest that probiotics may improve the
course of acute gastroenteritis. Meta-analyses19, 21, 49–51 report reduced mean duration of
diarrhea (by 25 hours), reduced proportion of diarrhea lasting four days (risk ratio 0.41),
and reduced stool frequency on Day 2 (mean di↵erence 0.8).19 This has prompted some
physicians and institutions to recommend probiotics in children with acute gastroenteritis.
Careful examination of the data, however, shows signiﬁcant methodological ﬂaws in these
studies. For these reasons, experts and agencies have continued to recommend large,
unbiased, well designed deﬁnitive trials to inform practice.19, 26
2.2
Limitations of Research to Date
Most trials of probiotics for acute gastroenteritis have been methodologically ﬂawed.19
Published studies have used small sample sizes and non-standardized treatment regi-
mens, probiotic preparations with variable production quality and non-veriﬁed colony
counts. Outcomes have been focused almost exclusively on diarrhea duration, and use
inconsistent (or unreported) deﬁnitions,19, 52 without considering the more global (and
relevant) assessment of the illness (e.g. fever, vomiting, repeat emergency department
visits, hospitalization). Because the outcomes sought are heterogeneous, and/or not
validated, and/or of minimal importance to participants,53 and have not addressed clinical
and socioeconomic eﬃcacy,49, 50 the value of the existing data has been questioned.54
Moreover, few studies address side e↵ects and adverse events systematically.1–3
Although >90% of children with acute gastroenteritis are treated as outpatients,23
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hospitalized children have been the main focus of most research in this area. Extrapolation
to outpatients is problematic because hospitalized children are more likely to have
rotavirus infections,55 severe disease, and to beneﬁt from probiotics.21, 52, 56 Emergency
department patients are ideal for outpatient probiotic trials, as their acute gastroenteritis
disease severity represents the entire spectrum in a normal distribution,13 o↵ering distinct
advantages over primary care populations. Emergency department patients are at risk for
more severe disease, there is a greater potential for beneﬁt because of the disease acuity
and the large sample size, and disease spectrum will enable identiﬁcation of subgroups
most likely to beneﬁt. Emergency departments are also a high venue of presentation
for acute gastroenteritis, enabling uniform trial design and compliance compared to
non-emergency department ambulatory settings.24, 57–59 Only one emergency department
study has been conducted previously, but the study was underpowered and did not explore
side e↵ects.20
2.3
Validation of the Modiﬁed Vesikari Score
The Vesikari Score, a composite measure of seven items ﬁrst described in 1990,60 has been
used in many clinical trials for treating acute gastroenteritis, particularly those evaluating
rotavirus vaccines in infants, and in large international epidemiological studies.8, 61–65 The
score incorporates features of acute gastroenteritis that are important to parents, children
and physicians, including
• diarrhea duration
• diarrhea frequency,
• vomiting duration,
• vomiting frequency,
• maximum daily temperature,
• medical interventions required, and
• degree of dehydration.
In outpatient studies, the degree of dehydration, measured as weight loss, is problematic
because it requires in-person re-evaluations, can vary based on recent voiding, defecation,
and liquid intake, and also might reﬂect inadequate caloric intake or catabolism during
acute illness. In fact, the assessment of dehydration using signs or scales designed based
on the use of post-illness weight as a gold standard has been questioned.66 Because
of these limitations, modiﬁcations to the original Vesikari score have been tested.67, 68
The modiﬁcation replaces percent dehydration with the need for an unscheduled future
healthcare visit within the two week follow-up period (Table 1 on the facing page). This
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Points
0
1
2
3
Diarrhea duration
0
1-96 hrs
97-120 hrs
≥121 hours
Max # of diarrheal stools/24 hrs
0
1-3
4-5
≥6
Vomiting duration
0
1-24 hrs
25-48 hrs
≥49 hours
Max # of vomiting episodes/24 hrs
0
1
2-4
≥5
Max recorded fever
37◦C
37.1-38.4◦C
38.5-38.9◦C
≥39◦C
Unscheduled healthcare visit
0
—
Primary
Care
Emergency
Department
Treatment
None
Rehydration
Hospital
Admission
—
Table 1: Modiﬁed Vesikari Score
modiﬁcation is supported by evidence that the demand for professional medical care
correlates with disease severity.67 The Modiﬁed Vesikari Score has been validated in two
multicenter studies12, 13 conducted during the planning of the current trial described in
this protocol.
3
Study Design and Data Collection
3.1
Study Design Overview
This is a double-blind randomized placebo controlled trial of probiotic therapy for acute
gastroenteritis. Children 3 months of age to 48 months of age who present to a participating
emergency department with acute gastroenteritis will be assessed for eligibility. Children
for whom parents provide permission to participate in the trial will be randomized to
receive probiotic therapy (Lactobacillus rhamnosus GG, ATCC 53103 (LGG)) or placebo.
The trial will be analyzed as an intention-to-treat study.
3.2
Participant Screening and Consent
Potentially eligible patients will be identiﬁed and screened for eligibility. The treating
physician or other study personnel will discuss the details of the study with the patient’s
caregivers to explain the study and obtain parental permission.
For patients who are actively screened in real time and meet all inclusion criteria, data
will be recorded that include yes/no answers to each of the exclusion criteria. If a patient
is ineligible at this point, no further data will be recorded, and the patient’s parents will
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not be approached for participation in the study. If a patient is eligible, the parents will
be approached to request permission for their child to participate in the study. If parents
are not approached for permission, the reason the parents were not approached will be
recorded. If the parents decline permission to participate, the reason for refusal will be
documented (if o↵ered by the parent). For all eligible patients who are not randomized,
study personnel will record whether the patient was prescribed probiotics. The recorded
exclusion criteria, reasons for declining permission, and o↵-study probiotic use will enable
the investigators to assess barriers to trial enrollment and identify potential biases in the
study.
3.3
Baseline Data Collection
Trained study sta↵at each site will collect baseline demographic information (e.g. birth-
date, gender, race, ethnicity) and relevant clinical variables, record the data on worksheets,
and enter the data into the electronic data capture system provided by the Data Coordi-
nating Center. Baseline clinical dehydration scale69 and disease severity scores (Modiﬁed
Vesikari Score)13 will be assigned to enable baseline comparisons between treatment arms.
3.4
Follow Up Data Collection
Successful follow up will be maximized by obtaining multiple phone numbers for families
and emergency contacts, scheduling calls and sending phone text reminders, allowing for
electronic completion and centralizing all follow-up procedures at the lead institution
(Washington University). Trained, experienced study sta↵will contact the family daily
(including weekends) until both the diarrhea and vomiting have resolved and the treatment
has been completed on day 5. Additional contact will be made on day 14 for outcome
assessment, and months 1, 3, 6, 9 and 12 for long term safety outcomes. Study sta↵
will use a standardized data collection form, and will inquire about ongoing symptoms,
medical evaluations, treatments, child care, work absenteeism, and side e↵ects. Detailed
questioning will follow positive responses. A study diary will be provided to caregivers to
use as a note-taking tool. Caregivers may also be provided an option of completing the
follow-up collection electronically. Patient compliance with study drug administration
will be assessed on day 5. To maximize compliance, caregivers will be reminded of the
importance and method of administering the study drug. On day 14, the study site sta↵
(not the central sta↵conducting the follow up) will perform a chart review for ﬁnal data
collection and identiﬁcation of recorded adverse events during the 14 day study period.
Adverse event reporting is described in detail in Section 8.3 on page 33.
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Every e↵ort will be made complete daily follow-up on the day necessary. However,
if one or two days of follow-up contact is missed, data for those missed days may be
collected on the next contact, if the caregiver used the home diaries or can recall the
information. If all contact is missed but then the parent is contacted on day 14, follow-up
data for the daily calls will be collected only if the parent diaries were used. For day 5
and 14, contact may be made within + 3 days. For month 1, 3, 6, 9, and 12 follow-up,
contact may be made within ± 2 weeks.
4
Study Procedures
4.1
Randomization (Enrollment)
Randomization will be accomplished through the use of an online randomization service.
Subjects will be randomized to receive either probiotic (Lactobacillus rhamnosus GG,
ATCC 53103 (LGG)) or placebo. Equal allocation randomization tables will be provided
by the Data Coordinating Center to the central research pharmacy. The central research
pharmacy will prepare consecutively numbered study kits according to the randomization
schedule. Study kits will be sent to the clinical sites. Randomization tables will be
created at the Data Coordinating Center using permuted-block randomization stratiﬁed
by clinical site and duration of symptoms. This will ensure that variations (e.g. site
speciﬁc practice patterns, gastrointestinal patterns) are comparably distributed across
treatment arms. The randomization number will be recorded in the database.
4.2
Study Drug Administration
Study Drug Description
Lactobacillus rhamnosus GG, ATCC 53103 (LGG) is supplied in a gelatin capsule con-
taining 1010 colony forming units of Lactobacillus rhamnosus(75 mg). The capsule also
contains 250 mg of microcrystalline cellulose (MCC – puriﬁed partially depolymerized
cellulose), an inert ingredient. Placebo capsules contain only MCC (to a total of 325
mg). Each capsule is wrapped in double foil to protect it against harmful light, air, and
moisture. Blister packs are labeled with the lot number. The probiotic and placebo
capsules have active Drug Master Files at the Food and Drug Administration (BB-MF 2
#13668 and MF2 # 13646).
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Initial Study Drug Administration
Clinical sta↵in the emergency department will administer the ﬁrst dose of study drug
by sprinkling the capsule’s contents into 20-30 mL of room temperature non-carbonated
liquid. Capsule contents may also be sprinkled into 1 tablespoon of applesauce as an
alternative to liquid. Oral ﬂuid therapy will be encouraged according to sites’ existing
clinical guidelines.26 At discharge, parents will also be provided with clinical instructions
concerning what and how much ﬂuid to drink, criteria for returning to the emergency
department or seeing their physician, and other standardized discharge instructions
for acute gastroenteritis. Study research coordinators will provide the parents with
instructions concerning study drug administration at home, completion of study forms,
and a letter for their pediatrician that explains the study. The importance of administering
all doses dispensed and the need to communicate with the study team on a daily basis
until symptoms resolve will be stressed.
Home Study Drug Administration
All patients will consume one capsule twice a day for 5 days (total of 9 home doses).
Patients will receive the medication mixed with 20-30 mL of a room temperature non-
carbonated liquid (or 1 tablespoon of applesauce as an alternative to liquid) and ingested
immediately to optimize probiotic viability. One extra dose/day will be provided (i.e.
kits will contain 5 extra doses total of 15 capsules) to account for vomiting or wastage.
The dose may be repeated once if vomiting occurs within 15 minutes of administration;
this rarely happens more than once.70 Oral ﬂuid therapy will be encouraged according to
established guidelines.26
Hospital Study Drug Administration
We estimate that only a small proportion (<5%) of enrolled subjects will be hospitalized.
If that does occur, subjects will continue on the study protocol as described for home study
drug administration, as done in previous studies.71 Future unscheduled hospitalization
at a non-study hospital site is even less common: none of the 274 patients enrolled in
our pilot study were admitted to a di↵erent institution after evaluation.12 To minimize
the impact that such an event could have on this trial, caregivers will be provided with a
letter that they will be instructed to share with their pediatrician and with the admitting
physician. The letter will describe the study, the care-plan, and it will include site
investigator contact information and the importance of adhering to the study protocol.
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4.3
Discontinuation of Study Drug
Study drugs are sometimes discontinued because of intolerance or perception of a clinical
adverse event from study drug administration. If any clinical abnormality, laboratory ab-
normality, intercurrent illness, new immunosuppressive therapy, or other condition occurs
such that continued administration of study drug would not be in the best interest of the
subject in the opinion of the investigator, study drug administration may be discontinued.
When this occurs, regardless of the reason, the subject remains in the intention-to-treat
population, all data collection should proceed, and long term follow up for adverse events
is carried out. Discontinuation of study drug will be documented and will be reported in
the closed session of the next scheduled Data Safety Monitoring Board meeting. Clinical
sta↵and parents should not report the early discontinuation of study drug to research
sta↵who are conducting follow up data collection. The Principal Investigator should not
be contacted by the site investigator, as intentional discontinuation of study drug implies
a safety outcome, and the Principal Investigator should be blind to all study outcomes.
Discontinuation of study drug is not a withdrawal from the study.
If study subjects are hospitalized after discharge to home from the emergency de-
partment, this is not a reason for discontinuation of study drug. We estimate that only
a small proportion (<5%) of enrolled children will be hospitalized after discharge to
home from the emergency department. If that does occur, subjects should continue
on the study protocol unless they have developed an exclusion criterion for study drug
administration (e.g. critical illness, immunosuppression, etc.). To facilitate continuation
of study drug administration during hospitalization, parents are provided with a letter for
their pediatrician. The letter will describe the study, the care-plan, and it will include site
investigator contact information and the importance of adhering to the study protocol.
The parents will be instructed to share this letter with their pediatrician and with the
admitting physician.
Breaking the blinding of the study drug should not be necessary, but an unblinding
procedure will be available. This will require contacting the Medical Monitor at the
Data Coordinating Center. However, unblinding is almost never necessary. The primary
anticipated reason for a clinician requesting unblinding is the suspected occurrence of
invasive infection (bacteremia/septicemia or meningitis), and the natural desire to know
if the subject was receiving active Lactobacillus rhamnosus GG, ATCC 53103 (LGG).
The initial recommendation from the Medical Monitor will always be that the clinician
should assume that the subject was receiving active drug, and include Lactobacillus
rhamnosus in the di↵erential diagnosis (and treatment coverage) of the suspected invasive
infection. Lactobacillus rhamnosus is readily susceptible to common antibiotics, and the
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di↵erential diagnosis of subsequent invasive infection would include organisms other than
Lactobacillus rhamnosus. Thus, future clinical treatment should not be dependent on
unblinding information.
If the situation requires unblinding, the Medical Monitor and Data Coordinating
Center sta↵will provide the information, and the unblinding will be documented. Study
drug will be discontinued, but the subject should not be withdrawn from the study! All study
procedures (except study drug administration) should be continued, as the subsequent
clinical course of the subject is critical to the science of the trial. All unblinding events
will be reported in the closed session of the next scheduled Data Safety Monitoring Board
meeting. Clinical sta↵and parents should not report the unblinding to research sta↵
who are conducting follow up data collection. The Principal Investigator should not be
contacted by the site investigator, as intentional unblinding of a subject implies a safety
outcome, and the Principal Investigator should be blind to all study outcomes.
4.4
Withdrawal from Study
Parents may completely withdraw their child from participation in this study at any
time, including discontinuation of data collection. However, withdrawal from study is a
completely di↵erent issue from discontinuation of study drug, and true withdrawal from
study is an exceedingly rare event. If parents demand withdrawal of their child from the
study, research sta↵will attempt to obtain adverse event information as required by the
Food and Drug Administration (all adverse events for 30 days, monthly follow up for long
term adverse events).
4.5
Stool Sample Testing
Stool sample swabs will be collected from all study subjects, if possible, for polymerase
chain reaction (PCR) analysis. Once obtained, swabs will be frozen and sent to a central
laboratory for analysis. A storage and shipping protocol will be provided in the study
manual of operations. Samples will be tested with multiplex PCR. Sites will also be asked
to collect an optional bulk sample of stool if one is available at the time of enrollment (i.e.
fresh diaper, etc). This will be used for future studies.
In addition, at the lead site, Washington University, study research personnel will
collect and freeze subjects’ bulk stool specimens in the acute phase (within 24 hours of
presentation) and 14 days after presentation using a previously tested bulk stool specimen
collection protocol. Specimens may be collected in the emergency department or the
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families will be given a specimen collection kit, gel packs and a metallic envelope. When
the specimen is ready for collection, a courier will pick up the specimen and cool pack at
the patient’s home and deliver it to a logistics collection center at Washington University
School of Medicine. This service is available 24 hours a day, year round. The stools will
be stored as a part of a future project to assess the potential mechanisms of action of
Lactobacillus rhamnosus GG, ATCC 53103 (LGG) in acute gastroenteritis.
5
Data Analysis
The hypotheses of this study are:
1. In children with acute gastroenteritis, probiotic administration in the emergency
department will be associated with a clinically-important decrease in the proportion
of children su↵ering from moderate-severe disease, deﬁned by a validated Modiﬁed
Vesikari Score ≥9, compared to placebo.
2. In children with acute gastroenteritis, probiotic administration will not be associated
with serious adverse events, and will have a similar rate of side e↵ects (e.g. bloating,
fever) as compared to placebo-treated children.
All analyses will be undertaken by the intention-to-treat (ITT) principle, except for
adverse events, which will use the as-treated principle (compare the subjects based on the
treatment regimen that they received). Patients who drop out or inadvertently crossover
will be followed and included in the ITT analysis. All statistical tests of hypotheses will
be two-sided. Baseline characteristics will be analyzed to determine if there is a need to
adjust for di↵erences between groups in exploratory analyses. Sensitivity analyses will
be performed to assess the possibility and consequences of non-random loss to follow-up.
The proportions of children experiencing an unscheduled healthcare visit or any potential
adverse e↵ect, as reported by the caregivers, will be compared between groups using the
Mantel-Haenszel test, stratiﬁed by site. The analysis will evaluate the presence/absence
of pre-speciﬁed side e↵ects, as an aggregate outcome variable. A per-protocol analysis
will be conducted to provide additional insight as non-compliance may result in an
underestimation of the beneﬁts of probiotics in the ITT analysis.72
5.1
Speciﬁc Aim Analyses
Speciﬁc Aim 1. Determine the clinical e↵ectiveness of probiotic administration to re-
duce morbidity in children presenting to the emergency department with acute
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gastroenteritis.
The primary eﬃcacy endpoint of this study is the presence of moderate-severe acute
gastroenteritis, as deﬁned by a total post-enrollment Modiﬁed Vesikari Score ≥9 during
the 2-week follow-up period. Each of the 7 items in the score is tabulated individually
(maximum of 20 points); the sum of these individual variables represents the total Modiﬁed
Vesikari Score. At the time of randomization a baseline Modiﬁed Vesikari Score will
be assigned based on symptoms prior to randomization. This baseline score will serve
as a covariate in a secondary analysis of the primary outcome. The post-enrollment
Modiﬁed Vesikari Score which will be employed to determine the presence/absence of the
primary eﬃcacy outcome, is based only on symptoms that occur between randomization
and day 14, the conclusion of the study period for this outcome. Only symptoms and
outcomes that occur following randomization will be included in the post-enrollment score.
The post-enrollment score is calculated only once, on day 14. At that time, each of the
seven variables will be assigned a score for the entire study period (from randomization
to day 14). Each variable will be scored by 1 of 3 methods:
1. Worst 24 hour period - maximal number of episodes of vomiting in a 24 hour
period, maximal number of episodes of diarrhea in a 24 hour period, and maximal
temperature;
2. Total duration of symptoms, including the number of days on which any gastroenteritis-
related symptom occurred;
3. Occurrence of a treatment outcome or unscheduled subsequent healthcare utilization.
If the patient was admitted directly following their enrollment ED visit and that
admission stay is longer than 48 hours, it will be included as treatment in the post
enrollment MVS. If the patient’s admission stay was less than 48 hours, it will not
be included in any MVS calculation.
The primary eﬃcacy endpoint (the presence of moderate or severe disease, as deﬁned
by a total Modiﬁed Vesikari Score ≥9 during the 2 week follow-up period) will be limited
to symptoms and outcomes that occur after randomization. If a patient’s symptoms
of vomiting and diarrhea stop during the same 24 hours, and then recur, that is not
included in the post-enrollment score since that will be considered a new illness. In the
original score, severe disease was deﬁned as ≥1161, 62, 73–75 and moderate as ≥9.76 In
our derivation and validation pilot studies,12, 13 construct validity was demonstrated and
validated by using scores of ≥9 to deﬁne moderate and ≥11 to deﬁne severe disease.
These cut-points were associated with signiﬁcant increases in other measures of disease
severity such as degree of dehydration, likelihood of admission and daycare (p = 0.01)
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and parental work absenteeism (p <0.001).12, 13
The proportion of children with moderate-to-severe disease (i.e. Modiﬁed Vesikari
Score ≥9), the primary outcome, will be analyzed by comparing proportions utilizing a
Mantel-Haenszel test, stratiﬁed by participating center and by duration of symptoms at
enrollment. Signiﬁcance for this primary outcome measure will be set at 0.05. Secondary
analyses of the primary outcome will use logistic regression methods to adjust for covariates
that may be imbalanced between groups, (e.g. age, pre-enrollment Modiﬁed Vesikari
Score, hydration assessment, need for hospitalization at index visit). We will also analyze
the outcome using Modiﬁed Vesikari Score as a continuous variable through a stratiﬁed
Wilcoxon rank-sum test and compare the results with the primary analysis.
Speciﬁc Aim 2. Determine the safety and side e↵ect proﬁles of Lactobacillus rhamnosus
GG, ATCC 53103 (LGG) in children presenting to the emergency department with
acute gastroenteritis.
The primary safety endpoint of this study is the occurrence of invasive disease (in-
cluding meningitis and bacteremia) from Lactobacillus rhamnosus. The secondary safety
outcome will be the presence of any adverse events. For more information on adverse
events, see Section 8.3 on page 33. Adverse events (including serious) will be tabulated
by study arm for DSMB reporting and for ﬁnal analysis of the safety of Lactobacillus
rhamnosus GG, ATCC 53103 (LGG) in this setting. Adverse events will also be coded
using the MedDRA vocabulary.
Side E↵ects: Occurrence of side e↵ects such as weakness, bloating, gas, intestinal
rumbling, diarrhea, blood in stool, abdominal pain, abdominal cramps, nausea, vomiting,
loss of appetite, heartburn, constipation, skin rash, fever, nasal congestion, sore throat,
cough, headache, muscle aches, chills, and diaper rash. These will be tabulated and
compared by study arm.
5.2
Secondary Study Outcomes
Secondary outcomes will include three of the individual components of the Modiﬁed
Vesikari Score considered independently and one additional measure of burden of illness.
Speciﬁcally, they are:
1. Diarrhea duration: Time from randomization until the appearance of the last
watery stool as reported during daily surveys.
2. Vomiting duration: Time from randomization until the last vomiting episode as
reported during daily surveys. Vomiting duration is only evaluated in children who
vomited ≥3 times during the 24 hours prior to the emergency department visit.
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3. Return visits: Return visits for unscheduled care to a healthcare provider related
to vomiting, diarrhea, dehydration, fever, or ﬂuid refusal, within 2 weeks of the
index visit. Scheduled visits (e.g. reassessment, vaccinations, unrelated issues) will
not be included.
4. Missed daycare: Days of daycare missed by subjects who attend daycare.
5. Missed work: Days of work missed by caregivers who work outside of the home.
6. Household transmission rate: A household census will be obtained at the time
of enrollment, and information about household contacts symptoms will be obtained
during daily surveys to determine household transmission rate.
The overall signiﬁcance level for statistical tests on the secondary outcomes will be
set at 0.05. Holm’s method will be used to adjust for multiple comparisons.77 The
continuous variables of duration of diarrhea and duration of vomiting (measured in hours
and analyzed with a Van Elteren test),78 will be stratiﬁed by clinical center. Similarly,
the number of days the child is absent from daycare and the caregiver is absent from work
will be analyzed with a Van Elteren test, stratiﬁed by clinical center and etiology.
Dichotomous outcomes to be evaluated include emergency department acute gastroenteritis-
related revisits, intravenous rehydration, and hospitalization. Additional analyses involving
these outcomes will include linear and logistic regression models that adjust for possible
e↵ects of baseline characteristics.
5.3
Sample Size Calculations and Statistical Power
The primary analysis will be performed on a binary outcome: development of moderate-
to-severe disease. The power of this analysis is based on the proportion of patients with
moderate-to-severe disease. Our pilot data12, 13 indicate that 25% of patients will have
moderate to severe disease during the course of their illness. Furthermore expert surveys
indicated that an absolute risk reduction of 10% would constitute a minimal clinically-
important di↵erence (MCID). Therefore our sample size calculation assumed a 25% event
rate in the control group for which we desire to detect an absolute beneﬁcial treatment
e↵ect of 10% with 90% power. Using a two-sided type I error (↵) of 0.05 and the hypothe-
sized proportions yields a required total sample size of 670 patients.79 Our expected power,
should we ﬁnd di↵erent event rates in our 2 groups, is displayed in Table 2 on the next page.
Based on previous work by our group,70, 71, 80 we assumed a 10% loss to follow up
(670/0.90 = 744), 5% drop out, and 3% drop in (caregivers who buy a probiotic agent
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Outcome Control
Outcome Intervention
% Di↵erence
Power
0.30
0.21
9%
0.76
0.30
0.20
10%
0.85
0.25
0.15
10%
0.90
0.25
0.16
9%
0.82
0.25
0.17
8%
0.72
0.20
0.10
10%
0.95
0.20
0.12
8%
0.81
0.20
0.13
7%
0.69
Table 2: Power Analysis
to administer to their child) rate (744/(0.92)2 = 879). Adjustment for O’Brien-Fleming
monitoring boundaries requires a further 2% increase. Thus, the total number randomized
(ﬁnal sample size) will be 897.
5.3.1
Enrichment Design
The above study design and power analysis are based on the assumption of homogeneous
treatment e↵ect. We may also incorporate an enrichment design81, 82 to restore the
statistical power in case the presence of a subpopulation with a substantially low treatment
e↵ect is identiﬁed.
We are particularly interested in two potential subpopulations:
participants with <2 days of symptoms and those with ≥2 days of symptoms. Based on
our pilot data, each subpopulation accounts for approximately 50% of the total population.
The decision for enrollment modiﬁcation will be made at the ﬁrst interim analysis for
eﬃcacy. Speciﬁcally, three statistics (based on a normal approximation of binomial
distribution, or z-statistics) will be calculated to compare the primary eﬃcacy endpoint
between treatment and control groups for subjects in the total population and the two
subpopulations, respectively. If the z-statistic from a subpopulation is <0.3 and also
smaller than that in the total population, subjects from this subpopulation will no longer
be considered in the subsequent enrollment. All subjects, regardless of symptom duration
will be included in the ﬁnal analyses. Our simulation studies have shown that such
an enrichment design can increase the power considerably when the treatment e↵ects
are di↵erent across subpopulations, while it will have little impact on power when the
treatment e↵ects are similar.
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5.3.2
Sub-group Analyses
The presence of a Modiﬁed Vesikari Score ≥9 will be analyzed by age <1 year, duration
of symptoms, breast-feeding status, antibiotic usage, rotavirus and norovirus positivity.
A subgroup e↵ect will be considered signiﬁcant if the interaction between subgroup and
treatment in a logistic regression model is signiﬁcant at a Bonferroni-corrected level.
5.4
Recruitment Estimates and Attrition
5.4.1
Recruitment
To estimate the number of subjects with acute gastroenteritis of eligible ages that would
meet all inclusion criteria and be enrolled annually, we obtained discharge diagnoses
from all study sites for 2005-2011. In 2011, the study sites evaluated 14,048 potentially
eligible subjects (patients 3-48 months with ICD9 codes for diarrhea) out of 507,039
total emergency department visits (2.8%). In the past 7 years the lowest proportion of
such patients per total emergency department volume was 2.3% (2008). Therefore, using
2011 emergency department volumes and lowest proportion of patients with diarrhea our
conservative estimate for eligible patients would be 11,150 patients 3-48 months with
diarrhea per year (or 30 patients per day network wide). Our best estimate is that 4.5%
of children with acute gastroenteritis aged 3-48 months will be enrolled. We plan to enroll
225 patients/year and 970 subjects over 4 acute gastroenteritis seasons.
5.4.2
Potential for Bias
Reporting bias will be minimized by adhering to CONSORT recommendations including
the use of third-party assignment.83 Placebo capsules and active drug will be provided
by I-Health Inc. The total weight of all capsules is 325 mg. The probiotic and placebo
capsules and powder are identical in appearance, taste, texture, and odor. Participants,
families, healthcare providers, data collectors, outcome adjudicators, and data analysts
will be blinded as to intervention arm, thereby preventing bias in outcome assessment.
Two DCC statisticians will be partially unblinded (with knowledge of group assignments,
but not group identities) in order to present interim results to the DSMB. An intention-
to-treat analysis will be performed to minimize bias associated with poor compliance
and non-random loss of participants.84 Co-interventions (e.g. antiemetic administration,
intravenous rehydration) and other potential sources of confounding will be recorded.
Our use of a published validated score as an outcome measure will protect against the
introduction of bias in the assessment of treatment e↵ects.85
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5.4.3
Compliance
Noncompliance with probiotics is rarely reported in previous studies, and not expected
to be problematic in this cohort.86, 87 Participant withdrawal has been related mostly to
the primary illness.19 In the Canadian pilot study, compliance was 91%. We will track
compliance by obtaining information from parents during the day 5 follow-up contact. If
there are any unused capsules, we will request their return (a pre-stamped, pre-addressed
envelope will be provided).
5.4.4
Loss to Follow-up
Our previous emergency department pediatric acute gastroenteritis research studies
achieved telephone follow-up rates of 98% on day 3 and 96% on day 7.70 Similar success
has been documented in other PECARN multicenter studies (91%).80 We estimate a 10%
loss to follow-up. If daily contact does not occur, we will collect data from missed days on
subsequent days when caregivers are contacted. The use of patient diaries (paper and/or
electronic) and chart review will supplement parent contact. Based on our pilot trial we
have devised the following strategies to maximize follow-up: all follow-up procedures will
be centralized at the lead institution and conducted by experienced study sta↵; we will
obtain multiple phone numbers from caregivers as well as emergency contacts, and we
will schedule calls and send reminders prior to the call if preferred. Finally, electronic
diary ﬁling and transmission may be available for interested families.
5.4.5
Compensation
Financial compensation may be provided to compensate for parent’s time completing
follow-up. This compensation must be approved by each site’s Institutional Review Board.
6
Data Management
6.1
Clinical Sites
Study data will be recorded on paper work forms or by direct data entry into an electronic
data capture (EDC) system. If paper work forms are used they will be retained at the
clinical site. The data from the work forms will then be entered into the EDC system
provided by the Data Coordinating Center at the University of Utah School of Medicine.
The clinical investigator at each participating site will complete a Form FDA 1572,
Statement of Investigator. That individual is responsible for all aspects of study imple-
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mentation, including administration of study drug, collection of accurate study data, and
correct entry of the data into the EDC. These tasks may be speciﬁcally delegated to other
individuals at the clinical site, but the clinical investigator is responsible to supervise all
aspects of the study, and is responsible to assure that all sta↵involved in this study are
adequately trained to perform the delegated tasks. All local research records will remain
in a locked ﬁle in a secure room unless being used by research sta↵, and all computerized
information will be maintained on password protected computers.
6.2
PECARN Data Coordinating Center (Utah)
In addition to locally secured, identiﬁable information, partially identiﬁable information
for all sites will be maintained at the PECARN Data Coordinating Center, located at
the University of Utah in Salt Lake City, Utah. The Data Coordinating Center has a
state-of-the-art computer infrastructure with a dedicated server room with a ﬁre sup-
pression system, air conditioning, cooling system and separate air ﬁltering. The server
facility is locked separately from the remainder of the Data Coordinating Center and
access to the building is monitored by security personnel year round. The Data Co-
ordinating Center coordinates its network infrastructure and security with the Health
Sciences Campus (HSC) information systems at the University of Utah. This provides
the Data Coordinating Center with e↵ective ﬁrewall hardware, automatic network in-
trusion detection, and the expertise of dedicated security experts working at the University.
Network equipment includes four high-speed switches. User authentication is cen-
tralized with two Windows 2008 domain servers. Communication over public networks
is encrypted with virtual point-to-point sessions using SSL or VPN technologies, both
of which provide at least 128 bit encryption. OpenClinica (Web-based clinical studies
data management system), eRoomTM (Web-based collaborative workspace) and other
web applications use the SSL protocol to transmit data securely over the Internet. Direct
access to Data Coordinating Center machines is only available while physically located
inside the Data Coordinating Center oﬃces, or via a VPN client. All network traﬃc is
monitored for intrusion attempts, security scans are regularly run against our servers, and
IT sta↵are notiﬁed of intrusion alerts.
Production servers running mission critical applications are clustered and conﬁgured
for failover events. Servers are backed up with encryption through a dedicated backup
server that connects across an internal 10 gigabit network to a tape drive. Storage area
networking (SAN) applications, clusters, and switch-to-switch links are also on a 10
gigabit network. Incremental backups occur hourly during the week. Incremental backups
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also are performed nightly with full system backups occurring every week. Tapes are
stored in a ﬁreproof safe inside the data center facility, and full backups are taken to an
o↵-site commercial storage facility. Security is maintained with Windows 2008 user/group
domain-level security.
Users are required to change their passwords every 90 days, and workstations time
out after 5 minutes of inactivity. All ﬁles are protected at group and user levels; database
security is handled in a similar manner with group level access to databases, tables, and
views in Microsoft SQL Server. All portable computers are whole-disk-encrypted.
6.3
Data Conﬁdentiality
The PI and other research personnel have all completed training and received certiﬁcation
in Human Subjects Research Protection and HIPAA. All project sta↵hired will also
successfully complete this training prior to engaging in any research or treatment with
study participants and renew this training as required by their institution.
The investigators and sta↵of the Data Coordinating Center are fully committed to
the security and conﬁdentiality of all data collected for PECARN studies. All Data
Coordinating Center personnel at the University of Utah have signed conﬁdentiality
agreements concerning all data encountered in the center. Violation of these agreements
may result in termination from employment at the University of Utah. In addition, all
personnel involved with data coordinating center data systems have received Human
Subjects Protection and HIPAA education.
The sta↵, reviewers and investigators involved with this study will be required to sign
agreements from the Data Coordinating Center that relate to maintenance of passwords,
information system security, and data conﬁdentiality.
6.4
Data Quality Management and Monitoring
The Data Coordinating Center monitors PECARN studies on behalf of the investigators
and the funding agency. The purposes of monitoring include demonstration of adherence
to human subjects protection requirements and assurance of high quality study data.
Monitoring is usually done remotely and may also involve physical site monitoring visits.
Site monitoring is described in more detail in Section 9.2.
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6.5
Record Access
The medical record and study ﬁles (including informed consent, permission, and assent
documents) must be made available to authorized representatives of the Data Coordinating
Center, upon request, for source veriﬁcation of study documentation. In addition, medical
information and data generated by this study must be available for inspection upon request
by representatives of the the National Institutes of Health, Food and Drug Administration,
and the Institutional Review Board (IRB) for each study site.
7
Protection of Human Subjects
7.1
Institutional Review Board (IRB) Approval
The Data Coordinating Center and each clinical center must obtain approval from their
respective IRB prior to participating in the study.
The Data Coordinating Center
will track IRB approval status at all participating centers and will not permit subject
enrollment without documentation of initial IRB approval and maintenance of that
approval throughout subsequent years of the project.
7.2
Informed Consent
This protocol requires that parents or other legally empowered guardians sign a parental
permission form. The parent or legal guardian will be informed about the objectives of
the study and the potential risks. Parents or legal guardians of eligible children with
symptoms of gastroenteritis will be approached to provide permission for their child’s
participation in the study. Parental or guardian permission will be obtained prior to
initiation of study activities. Documentation of parental permission will be maintained at
the study site. As the maximum eligible age is 48 months, child assent is not applicable.
7.3
Potential Risks
Lactobacilli are ubiquitous in the human diet and are a large part of the over 1 trillion
live bacteria that reside in the gastrointestinal tract of healthy individuals. Overall, Lac-
tobacillus rhamnosus GG, ATCC 53103 (LGG) is well tolerated in the pediatric patient
population. Infections (bacteremia, endocarditis, pneumonia, deep abdominal abscesses)
have been reported in sick neonates, severely debilitated and immune-compromised in-
dividuals given probiotics. The use of probiotics in these individuals continues to be
controversial; however prospective studies have been conducted in adults and children
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with HIV as well as preterm neonates, with no reported systemic infections. Finally, there
are 7 case reports of invasive disease after administration of Lactobacillus rhamnosus GG,
ATCC 53103 (LGG). These occurred in patients in intensive care units, in patients with
central venous catheters, or in patients who are on immunosuppressive therapy, have short
gut syndrome, or are at risk for endocarditis. These risk factors are exclusion criteria
from our study population.
The clinical risks of invasive infection from Lactobacillus rhamnosus are related to
receiving Lactobacillus rhamnosus GG, ATCC 53103 (LGG). There are risks associated
with acute gastroenteritis that are not related to study participation, including dehydra-
tion, electrolyte abnormalities, systemic infection and co-infection, and hospital admission.
All subjects will be clinically treated for acute gastroenteritis in accordance with local
site treatment protocols. There may be other unknown risks of Lactobacillus rhamnosus
GG, ATCC 53103 (LGG) in children with acute gastroenteritis.
Loss of conﬁdentially is always a risk in a study, but safeguards are in place to protect
against this.
7.4
Protections Against Potential Risks
Several steps will be taken to minimize the risks of participation in the study. All of the
participating clinical centers are tertiary pediatric hospitals with highly trained pediatric
sta↵. Subjects will be closely followed after discharge. Families will be contacted daily
until both the diarrhea and vomiting have resolved and the treatment has been completed.
Additional contact will be made on day 14, and months 1, 3, 6, 9 and 12 for long term
safety outcomes. Parents or legally authorized representatives will also receive speciﬁc
instructions as to when to see a health care provider. If an adverse event is reported at
the time of follow-up, research personnel will refer subjects for appropriate medical care,
when applicable.
Loss of conﬁdentiality will be mitigated by the use of the PECARN Data Coordinating
Center which has a highly secure IT infrastructure, and by the existence of trained
research sta↵at participating sites. Data security is described in Section 6.
7.5
Potential Beneﬁts
Subjects participating in the study may beneﬁt directly by experiencing less severe disease,
shorter duration of symptoms, and decreased need for further health care utilization.
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There may also be reduced symptoms (i.e. diarrhea, vomiting, fever) and morbidity,
thereby diminishing acute gastroenteritis-associated resource consumption (e.g. physician
visits, hospitalization) and societal costs. Additional beneﬁts in the study include closer
monitoring of symptoms and potentially earlier recognition of any worsening of acute
gastroenteritis due to the frequency of telephone follow up and communication with the
family. The knowledge gained in this study may lead to improved treatment options for
gastroenteritis for other children and lead to new therapeutic options for future patients.
Subjects and their families may therefore beneﬁt indirectly by participating in research
with the potential to provide subsequent beneﬁt to others. Finally, future analysis of bulk
stool specimens will enable a better understanding of potential mechanisms of action of
Lactobacillus rhamnosus GG, ATCC 53103 (LGG), which will likely provide beneﬁt to
future patients.
8
Data and Safety Monitoring Plan
8.1
Data Safety Monitoring Board (DSMB)
This study will have a Data Safety Monitoring Board (DSMB) appointed in accordance
with instructions from the NICHD program oﬃcer. The DSMB will have a charter, will
approve the protocol prior to implementation, and will review interim analyses for safety
and eﬃcacy.
The purpose of the DSMB is to advise the Federal funding agency (NICHD), the
study Principal Investigator (Dr. Schnadower), and the PECARN Steering Committee
regarding the continuing safety of study subjects and the continuing validity and scientiﬁc
merit of the study. The DSMB is responsible for monitoring accrual of study subjects,
adherence to the study protocol, assessments of data quality, performance of individual
clinical sites, review of serious adverse events and other subject safety issues, and review
of formal interim statistical analyses of treatment eﬃcacy.
The Data Coordinating Center will send reports relating to these topics to DSMB
members prior to each DSMB meeting. The Data Coordinating Center will sta↵DSMB
meetings. The production and approval of DSMB minutes will be done in accordance with
requirements of the NICHD. Each DSMB meeting will have a summary recommendation
that will be provided to each participating clinical site for submission to the local
Institutional Review Board (IRB). More detailed information from the DSMB meetings
will not be routinely provided for local IRB submission.
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8.2
Frequency of Interim Analysis:
The Data Safety Monitoring Board (DSMB) will meet after 80 patients (safety end
points for 1 month), approximately 350 patients (end of 2nd year of enrollment) and 620
patients (end of 3rd year of enrollment) to review enrollment, study procedures, loss to
follow-up, drop-in rate, and interim safety and eﬃcacy results. The analyses will test the
hypothesis that the probability of developing moderate-to-severe acute gastroenteritis in
the probiotic arm is equal to that in the placebo arm. An analysis will also be conducted
after 20 subjects under 6 months of age have been enrolled. The DSMB is to review
interim data and make recommendations regarding continuation or modiﬁcation of the
study based on safety in this age group.
Conservative O’Brien-Fleming monitoring
boundaries, implemented using the Lan-DeMets ↵-spending function approach, will be
used as guidelines for early stopping for eﬃcacy.
8.3
Adverse Event Reporting
8.3.1
Deﬁnitions, Relatedness, Severity and Expectedness
Deﬁnition:
An adverse event (AE) is any untoward medical occurrence experienced by a
subject. An event constitutes a disease, a set of related signs or symptoms, or a single sign
or symptom. On each study day, the site investigators will evaluate adverse events. Study
sta↵will obtain information on symptoms and adverse events on scheduled follow up calls.
Adverse events not previously documented in the study will be recorded on the adverse
event record form. The nature of each experience, date and time (where appropriate) of
onset, outcome, course, and relationship to treatment should be established.
Side E↵ects: Occurrence of side e↵ects such as weakness, bloating, gas, intestinal
rumbling, diarrhea, blood in stool, abdominal pain, abdominal cramps, nausea, vomiting,
loss of appetite, heartburn, constipation, skin rash, fever, nasal congestion, sore throat,
cough, headache, muscle aches, chills, and diaper rash. Study sta↵will obtain information
about side e↵ects on scheduled follow up contacts.
Relatedness:
The suspected relationship between study interventions and any adverse
event will be determined by the site investigator using the following criteria. Relatedness
may not be assessed by a research coordinator, and must be assessed by an investigator.
Not Related: The event is clearly related to other factors, such as the subject’s clinical
state, therapeutic interventions, or concomitant drugs administered to the subject.
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Possibly Related: The event follows compatible temporal sequence from the time of
beginning the assigned study intervention, but could have been produced by other
factors such as the subject’s clinical state, therapeutic interventions, or concomitant
drugs administered to the subject.
Probably Related: The event follows a reasonable temporal sequence from the time
of beginning the assigned study intervention, and cannot be reasonably explained
by other factors such as the subject’s clinical state, therapeutic interventions, or
concomitant drugs administered to the subject.
Some toxicities will be diﬃcult to distinguish from abdominal symptoms related to acute
gastroenteritis (such as bloating, abdominal pain, diarrhea, fever and diaper rash), and
only at the time of analysis will we be able to determine whether these signs and symptoms
are di↵erent between the groups.
Seriousness:
The severity of clinical adverse events and laboratory abnormalities will
be recorded by the site investigator and categorized. A serious adverse event (SAE) is an
adverse event that:
• results in death; or
• is life-threatening (the patient was, in the view of the site investigator, in immediate
danger of death from the event as it occurred); or
• requires inpatient hospitalization or prolongs an existing hospitalization; or
• results in persistent or signiﬁcant disability or incapacity; or
• results in congenital anomaly/birth defect; or
• any other event that, based upon appropriate medical judgment, may jeopardize
the subject’s health and may require medical or surgical intervention to prevent one
of the other outcomes listed in this deﬁnition.
Expectedness of the Event:
All adverse events, including serious adverse events, will
be evaluated as to whether their occurrence was expected or unexpected. An adverse event
is considered expected if it is known to be associated with acute gastroenteritis (acute
gastroenteritis), other underlying medical conditions of the subject, is directly related to
study outcome, or is otherwise mentioned in the protocol, informed consent, investigator
brochure, or other study documents. Expected complications of acute gastroenteritis
include abnormal taste, malaise, abdominal distention, foul smelling stools, dehydration,
electrolyte and other laboratory abnormalities, other symptoms associated with viral
syndromes, systemic infection and co-infection, seizures, and hospital admission.
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Treatment or Action Taken:
For each adverse event, the site investigator will record
whether an intervention was required:
• Intervention: Surgery or procedure
• Other Treatment: Medication initiation, change, or discontinuation
• None: No action taken
Outcome of Event:
Finally, the site investigator will record the clinical outcome of
each adverse event as follows:
• Death
• Recovered and the patient returned to baseline status
• Recovered with permanent sequelae
• Symptoms continue
8.3.2
Time Period for Adverse Events
For purposes of this study, adverse events occur following randomization through 30 days
after the last study drug dose will be recorded. Serious adverse events, unexpected medi-
cally attended events, and new onset chronic illnesses will be recorded from randomization
through twelve months after the last study dose. Speciﬁcally, events that occur following
parental permission to participate in the study, but prior to actual randomization, are
not adverse events. These should be recorded as baseline conditions.
8.3.3
Data Collection Procedures for Adverse Events
After patient randomization, all adverse events (including serious adverse events), whether
anticipated or unanticipated, will be recorded according to the date of ﬁrst occurrence,
severity, and their duration, as well as any treatment prescribed. Any medical condition
present at the time of randomization, recorded in the patient’s baseline history at study
entry, which remains unchanged or improves, will not be recorded as an adverse event at
subsequent evaluations. However, worsening of a medical condition that was present at
the time of randomization will be considered a new adverse event and reported.
Abnormal laboratory values that are clinically signiﬁcant will be recorded as adverse
events and the site investigator will assess the severity and relationship to the study.
Laboratory values that are abnormal at the time of randomization and that do not worsen
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will not be recorded as adverse events.
Adverse events will be coded using the MedDRA coding vocabulary. Coding will be
done centrally at the Data Coordinating Center because this requires speciﬁc training.
8.3.4
Unanticipated Problems (UP)
Unanticipated problems (UP) are deﬁned as incidents, experiences, or outcomes that are
unexpected, related to participation in the study, and suggest that the research places
subjects at a greater risk of harm than was previously known or recognized. The site
investigator will report unanticipated problems to the Data Coordinating Center within 24
hours. A detailed completed report will be required to be sent to the Data Coordinating
Center within 3 working days of the event. After receipt of the complete report, the Data
Coordinating Center will report these unanticipated problems to the NICHD Program
Oﬃcial or Project Oﬃcer in an expedited manner (within 24 hours). In accordance with
local IRB requirements, the site investigator may be required to report such unanticipated
problems to the IRB in addition to notifying the Data Coordinating Center. In the
event that the medical monitor believes that such an event warrants emergent suspension
of enrollment in the trial, and NICHD sta↵cannot be reached expeditiously, the Data
Coordinating Center will notify the study investigator (Dr.Schnadower) and all site
investigators to cease enrollment in the trial. Resumption of enrollment will not occur
without consent of the NICHD sta↵after discussion with the DSMB.
8.3.5
Monitoring Serious Adverse Events
The Principal Investigator of the Data Coordinating Center (Dr. Dean) will act as the
medical monitor for this study. If Dr. Dean is unavailable, a qualiﬁed physician will be
designated to fulﬁll this function. Site investigators and/or research coordinators will
report serious adverse events to the Data Coordinating Center within 24 hours. A detailed
completed report will be required to be sent to the Data Coordinating Center within 3
working days of the event, and the medical monitor will assess all serious adverse events
reported from site investigators.
For each of these serious adverse events, the site investigator will provide suﬃcient
medical history and clinical details for a safety assessment to be made with regard to
continuation of the trial. The medical monitor will sign each SAE report after review.
All SAE reports will be retained at the Data Coordinating Center, and all SAE reports
will be available for review by DSMB members and NICHD sta↵.
In the unlikely event that the medical monitor believes an unexpected and study-
related SAE warrants emergent cessation of enrollment in the trial, NICHD sta↵and the
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DSMB chairperson will be immediately consulted. If these individuals concur with the
judgment of the medical monitor, or if the NICHD sta↵and the DSMB chairperson cannot
be reached expeditiously, the Data Coordinating Center will notify the study investigator
(Dr.Schnadower) and all site investigators to cease enrollment in the trial. Resumption of
enrollment will not occur without consent of the NICHD sta↵after discussion with the
DSMB.
In accordance with local IRB requirements, the site investigator may be required to
report such events to the IRB in addition to notifying the Data Coordinating Center.
After notiﬁcation of the NICHD Program Oﬃcial or Project Oﬃcer, and the DSMB
chairperson, of serious, unexpected, and study-related adverse events or unanticipated
problems (UP), decisions will be made whether to continue the study without change,
and whether to convene the entire DSMB for an emergent meeting. If a decision is made
to suspend enrollment in the trial, this will be reported to the study investigator (Dr.
Schnadower) and all clinical investigators, who will be instructed to report this to their
local IRB.
The DSMB will review all adverse events (not necessarily serious, unexpected, and
study-related) during scheduled DSMB meetings. The Data Coordinating Center will
prepare a Summary Report of Adverse Events for the DSMB meetings, classiﬁed with
the MedDRA coding system.
8.3.6
Follow-up of Serious, Unexpected and Related Adverse Events
All serious, unexpected and related adverse events, that are unresolved at the time of the
patient’s termination from the study or discharge from the hospital, will be followed by
the Clinical Center investigators until the events are resolved, subject is lost to follow-up,
the adverse event is otherwise explained or has stabilized, or 12 months have passed from
the time of last study dose.
9
Study Training and Monitoring
9.1
Study Training
A formal training program for investigators and research sta↵will be held prior to the
start of enrollment. The training program will cover regulatory topics and Good Clinical
Practice. The training will also provide in depth explanations regarding study procedures,
clinical care, adverse event reporting, data entry procedures, quality assurance, site
monitoring, and the informed consent process. A manual of operations will be provided
to each Clinical Center investigator prior to the start of enrollment. The manual will
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detail speciﬁc information about the study procedures, regulatory information, safety
reporting, and other necessary information. Updates and revisions to the manual will be
made available electronically. The Data Coordinating Center, in collaboration with the
study investigator (Dr. Schnadower), will be the main contact for study questions.
9.2
Study Monitoring
The investigators recognize the importance of ensuring data of excellent quality. Site
monitoring is critical to this process. Site monitoring has been a very e↵ective tool for
maintaining data quality in previous PECARN studies, and we will utilize this process
to ensure excellent quality data in the proposed study. Our site monitoring plan is
designed to identify problems with sites and methods for handling problems that arise.
Site monitors must be provided with full access to study materials and the medical records
for study subjects. If the medical records are in electronic form, the clinical investigator
or an authorized individual must provide any assistance necessary to facilitate the site
monitor’s review of data in the electronic medical record.
9.2.1
Site Monitoring Plan
A supplemental study-speciﬁc monitoring plan, separate from the protocol will be com-
pleted which outlines speciﬁc criteria for monitoring. This plan will include the number of
planned site visits, criteria for focused visits, or additional visits, a plan for chart review
and a follow up plan for non-compliant sites. The monitoring plan also describes the type
of monitoring that will take place (e.g. sample of all subjects within a site; key data or all
data), the schedule of visits, how they are reported and a time frame to resolve any issues
found. Remote site monitoring schedules will be determined by the Data Coordinating
Center in coordination with the study principal investigator.
9.2.2
Clinical Site Monitoring
Site monitoring visits will be performed by a trained site monitor during the study
period to ensure regulatory compliance, patient safety, and to monitor the quality of data
collected. Essential document binders, regulatory documents and data collection forms
may be reviewed. Interim visits will take place depending on grant budget, site enrollment,
and compliance issues identiﬁed. The site monitor will provide each site with a written
report, and sites will be required to follow up on any deﬁciencies. It is anticipated that
the study monitoring visits for this protocol will consist of a site initiation visit (prior
to patient enrollment), interim visits, and a close out visit. The site initiation may take
place as group training made up of site investigators and research assistants.
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9.2.3
Remote Monitoring
The Data Coordinating Center may supplement on-site monitoring with remote monitoring
activities. Remote monitoring involves detailed review of the data entered by the Clinical
Center and consultations with the Clinical Center investigator and/or research coordinator
to review safety and data quality. This may require uploading de-identiﬁed copies of
speciﬁc parts of the medical record, patient study ﬁle, regulatory documentation, or other
source documents to the Data Coordinating Center sta↵, who review those materials
against the data recorded in the electronic data capture system. This helps assure protocol
compliance and accurate data collection. The Data Coordinating Center may conduct
more remote monitoring activities early in the trial to assure protocol compliance and
identify any training issues that may exist. Remote monitoring the documents will be
retained in accordance with federal requirements. Safety of subjects will be monitored
and ensured in accordance with the Data and Safety Monitoring Board (DSMB) plan.
9.2.4
Pharmacy Monitoring
The Clinical Center pharmacy must maintain adequate records of all dispensed study drug.
Each pharmacy may be monitored, either in person or remotely, and may be requested to
send copies of these documents to the Data Coordinating Center. Since this study will
use a central pharmacy, that pharmacy must also maintain adequate records and may
also be monitored.
10
Regulatory Issues
10.1
Food and Drug Administration
This trial is being conducted under an Investigational New Drug application approved by
the Food and Drug Administration (Investigational New Drug application #15371). The
clinical investigator at each participating site will complete a Form FDA 1572, “Statement
of Investigator.”
10.2
Health Insurance Portability and Accountability Act
The abstracted data will include limited identiﬁers as deﬁned by the Health Insurance
Portability and Accountability Act, and speciﬁc contact information will be provided to
research sta↵conducting follow up with parents. Abstracted data will be retained and
archived at the Data Coordinating Center in accordance with record retention requires
of the Food and Drug Administration and the NIH. Contact information will not be
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provided to the Data Coordinating Center (it will be provided directly to the central
follow up research sta↵). For data analysis outside the Data Coordinating Center (e.g.,
when a public access database is made available), the Data Coordinating Center will
create a completely de-identiﬁed analytical database for use by the study investigators,
and for ﬁnal archiving. All study sites have been or will be o↵ered Business Associate
Agreements with the University of Utah. Copies of signed Business Associate Agreements
are maintained at the Data Coordinating Center.
10.3
Inclusion of Women and Minorities
The gender, ethnic and racial composition of patients enrolled in all PECARN studies is
a function of the underlying referral population at each PECARN site participating in
this trial. There will be no exclusion of patients based on gender, race, or ethnicity.
10.4
ClinicalTrials.gov Requirements
This trial has been registered at ClinicalTrials.gov (NCT #01773967). The title is “Impact
of Emergency Department Probiotic (LGG) Treatment of Pediatric Gastroenteritis.”
10.5
Retention of Records
For federally funded studies subject to the Common Rule, records relating to the research
conducted shall be retained for at least 3 years after completion of the research. Completion
of the research for this protocol should be anticipated to include planned primary and
secondary analyses, as well as subsequent derivative analyses. Completion of the research
also entails completion of all publications relating to the research. All records shall be
accessible for inspection and copying by authorized representatives of the regulatory
authorities at reasonable times and in a reasonable manner [45 CFR §46.115(b)].
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Probiotics Study Protocol Version 3.00
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The EMSC Pediatric Emergency Care Applied Research Network


Lactobacillus Rhamnosus GG vs. Placebo for Pediatric Acute Gastroenteritis 
 
Summary of Protocol Changes (from version 1.0- January 2014- to V2.0 – April 2014- to V 3.0 – 
February 2017) 
A) Changes made in April 2014 (V1.0 to V2.0) 
1. Added and clarified exclusion criteria (history of abdominal surgery, oral or intravenous 
steroid use in the past 6 months, under 6 months and premature (page 11) 
2. Clarification of adverse events section separating adverse from side effects (page 10 and 
42) and added list of side effects (pages 26 and 39) 
3. Added question about whether non-randomized eligible patients were prescribed 
probiotics (page 16)  
4. Clarification of product preparation and administration (pages 19-20) 
5. Clarification of wording related to PI and Medical Monitor at the Data Coordinating 
Center (page 21) 
6. Clarification regarding stool sample collection (page 22) 
7. Clarified how compliance questions should be asked (page 31) 
8. Clarification of data collection methods to include direct data capture (page 32) 
9. Clarification of wording related to pharmacy monitoring (page 47) 
 
B) Changes made in February 2017 (V2.0 to V3.0) 
1. Increased sample size from 900 to 970 following discovery that up to 36 patients 
were potentially exposed to lower probiotic dosing (pages 8, 11 and 26) 


Statistical Analysis Plan
Protocol Title (Number): Impact of Emergency Department Probiotic Treatment of Pedi-
atric Gastroenteritis (Probiotics Study) (PECARN Protocol # 032)
Protocol Version and Date: 1.00; January 24, 2014
SAP Author: T. Charles Casper, Ph.D.
SAP Version and Date: 1.0; January 16, 2015
Changes from last version:
SAP Version 1 Date: January 16, 2015
CONFIDENTIAL
i


PECARN Protocol # 032: Statistical Analysis Plan
Page ii
Approvals:
Approved By:
Name
Title
Date
Name
Title
Date
January 16, 2015
CONFIDENTIAL


PECARN Protocol # 032: Statistical Analysis Plan
Page iii
Contents
Abbreviations
v
1
Preface
1
1.1
Purpose of SAP . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
1
1.2
Auxiliary/Other Documents . . . . . . . . . . . . . . . . . . . . . . . . . . .
1
2
Study Objectives and Outcomes
1
2.1
Study Objectives . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
1
2.1.1
Primary Objectives . . . . . . . . . . . . . . . . . . . . . . . . . . . .
1
2.2
Study Outcomes
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
2
2.2.1
Primary Outcome . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
2
2.2.2
Safety Outcomes
. . . . . . . . . . . . . . . . . . . . . . . . . . . . .
2
2.2.3
Secondary Outcomes . . . . . . . . . . . . . . . . . . . . . . . . . . .
2
2.2.4
Tertiary Outcomes . . . . . . . . . . . . . . . . . . . . . . . . . . . .
3
2.3
Covariates . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
3
3
Study Design and Methods
4
3.1
Overall Study Design . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
4
3.2
Randomization and Blinding . . . . . . . . . . . . . . . . . . . . . . . . . . .
4
3.2.1
Method of Treatment Assignment . . . . . . . . . . . . . . . . . . . .
4
3.2.2
Blinding . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
4
3.3
Sample Size and Power Determination
. . . . . . . . . . . . . . . . . . . . .
5
4
Study Subjects and Analysis Populations
6
4.1
Analysis Populations . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
6
4.1.1
Screening Population . . . . . . . . . . . . . . . . . . . . . . . . . . .
6
4.1.2
Intention-to-Treat Population . . . . . . . . . . . . . . . . . . . . . .
6
4.1.3
Per-Protocol Eﬃcacy Population
. . . . . . . . . . . . . . . . . . . .
6
4.1.4
Safety Population . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
6
4.2
Study Subjects
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
6
4.2.1
Inclusion and Exclusion Criteria . . . . . . . . . . . . . . . . . . . . .
6
4.3
Enrichment Design . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
8
5
General Analysis Issues
9
5.1
Analysis Software . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
9
5.2
Methods for Withdrawals, Missing Data, and Outliers . . . . . . . . . . . . .
9
5.3
Multicenter Studies . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
9
5.4
Multiple Comparisons
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
10
5.5
Planned Subgroups, Interactions, and Covariates . . . . . . . . . . . . . . . .
10
January 16, 2015
CONFIDENTIAL


PECARN Protocol # 032: Statistical Analysis Plan
Page iv
5.6
Derived and Computed Variables
. . . . . . . . . . . . . . . . . . . . . . . .
10
5.7
Independent Review
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
10
6
Overview of Planned Analyses
11
6.1
Schedule of Interim Analyses . . . . . . . . . . . . . . . . . . . . . . . . . . .
11
6.2
Stopping Rules for Interim Analyses . . . . . . . . . . . . . . . . . . . . . . .
11
6.3
Blinding in the Interim Analyses . . . . . . . . . . . . . . . . . . . . . . . . .
11
6.4
Schedule of Final Analyses . . . . . . . . . . . . . . . . . . . . . . . . . . . .
12
7
Planned Analyses with Procedures for Completion
12
7.1
Analysis of Demographic and Other Pre-Treatment Characteristics
. . . . .
12
7.2
Analysis of Primary Outcome . . . . . . . . . . . . . . . . . . . . . . . . . .
12
7.2.1
Multiple Imputation
. . . . . . . . . . . . . . . . . . . . . . . . . . .
14
7.2.2
Additional Analyses of Primary Outcome . . . . . . . . . . . . . . . .
15
7.3
Analysis of Secondary Outcomes . . . . . . . . . . . . . . . . . . . . . . . . .
16
7.3.1
Duration of Symptoms, Missed Daycare and Missed Work
. . . . . .
16
7.3.2
Return Visits . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
16
7.4
Safety Outcomes
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
16
7.4.1
Side-Eﬀects . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
16
7.4.2
Adverse Events . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
17
7.5
Analysis of Tertiary Outcomes . . . . . . . . . . . . . . . . . . . . . . . . . .
17
7.6
Analysis of Subgroups
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
17
References
19
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PECARN Protocol # 032: Statistical Analysis Plan
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Abbreviations
Abbreviation
Deﬁnition
DCC
Data Coordinating Center
CRF
Case Report Form
DSMB
Data and Safety Monitoring Board
ITT
Intent-To-Treat
MCID
Minimal Clinically-Important Diﬀerence
MVS
Modiﬁed Vesikari Score
PECARN
Pediatric Emergency Care Applied Research Network
PP
Per-Protocol
(S)AE
(Serious) Adverse Event
SAFETY
Safety Population
SAP
Statistical Analysis Plan
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PECARN Protocol # 032: Statistical Analysis Plan
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1
Preface
1.1
Purpose of SAP
This Statistical Analysis Plan (SAP) describes the planned analysis and reporting for the
PECARN Protocol: Impact of Emergency Department Probiotic Treatment of Pediatric
Gastroenteritis (Probiotics Study).
The purpose of this study is to determine if probiotic administration reduces the severity
of acute gastroenteritis episodes in children aged 3 to 48 months. The study is a randomized,
placebo-controlled trial with a parallel-group design.
The structure and content of this SAP provides suﬃcient detail to meet the requirements
and standards set by the PECARN Data Coordinating Center (DCC). All work planned and
reported for this SAP will follow guidelines for statistical practice published by the American
Statistical Association [2].
1.2
Auxiliary/Other Documents
The following documents were reviewed in preparation of this SAP:
• PECARN Protocol: Impact of Emergency Department Probiotic Treatment of Pedi-
atric Gastroenteritis (Probiotics Study).
• Case Report Forms (CRFs) for the Probiotics 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
Probiotics 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
analysis approach is completely followed in the revised technical speciﬁcations.
2
Study Objectives and Outcomes
2.1
Study Objectives
2.1.1
Primary Objectives
The primary objectives of the Probiotics trial are:
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PECARN Protocol # 032: Statistical Analysis Plan
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1. to test the hypothesis that, in children with acute gastroenteritis, probiotic administra-
tion in the emergency department will decrease the likelihood of moderate-severe dis-
ease, deﬁned by a validated Modiﬁed Vesikari Score (MVS) ≥9, compared to placebo.
2. to test the hypothesis that, in children with acute gastroenteritis, probiotic administra-
tion will not be associated with serious adverse events, and will have a similar rate of
side eﬀects (e.g., bloating, fever, abdominal distention) as compared to placebo-treated
children.
2.2
Study Outcomes
2.2.1
Primary Outcome
The primary outcome is the presence of moderate-severe acute gastroenteritis, as deﬁned
by a total post-enrollment Modiﬁed Vesikari Score (MVS) ≥9 during the 2-week follow-up
period.
2.2.2
Safety Outcomes
Safety outcomes are:
1. The occurrence of invasive disease (including meningitis and bacteremia) from Lacto-
bacillus rhamnosus.
2. Occurrence of side eﬀects: bloating, gas, intestinal rumbling, diarrhea, blood in stool,
abdominal pain, abdominal cramps, nausea, vomiting, loss of appetite, heartburn,
constipation, skin rash, diaper rash, fever, nasal congestion, runny nose, sore throat,
cough, headache, muscle aches, chills, weakness.
2.2.3
Secondary Outcomes
Secondary outcomes are:
1. Time to last watery stool as reported during daily surveys.
2. Time to last vomiting episode. Vomiting duration is only evaluated in children who
vomited ≥3 times during the 24 hours prior to the emergency department visit.
3. Return visits for unscheduled care to a healthcare provider related to vomiting, diar-
rhea, dehydration, fever, or ﬂuid refusal, within 2 weeks of the index visit.
4. Days of daycare missed by subjects who attend daycare.
5. Days of work missed by caregivers who work outside of the home.
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PECARN Protocol # 032: Statistical Analysis Plan
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6. Household transmission rate.
In addition to the primary analysis, MVS will be analyzed in secondary analyses for
conﬁrmatory purposes as:
1. a numeric variable (i.e., actual MVS, rather than dichotomized)
2.2.4
Tertiary Outcomes
Tertiary outcomes are:
1. Emergency department acute gastroenteritis-related visits
2. Intravenous rehydration
3. Hospitalization
4. Total number of diarrheal stools
5. Total number of vomiting episodes
6. Adherence to oral medication (deﬁned as ≥7 out of 10 doses)
In the event that eﬃcacy of the probiotic is demonstrated, cost will also be analyzed
(cost-eﬀectiveness).
2.3
Covariates
Although randomization should result in approximate balance between treatment groups
with respect to critical baseline variables aﬀecting the outcomes, additional exploratory
analyses will be conducted to assess the eﬀects of treatment after adjusting for baseline
covariates in models for each outcome. The covariates considered are:
• baseline MVS (actual score),
• duration of symptoms prior to enrollment (<48 hours vs. 48 hours or more),
• age,
• gender,
• clinical center,
• breast-feeding status,
• antibiotic useage during the 14 days prior to ED visit,
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PECARN Protocol # 032: Statistical Analysis Plan
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• infective agent at baseline (e.g., norovirus, rotavirus),
• hydration assessment (Gorelick dehydration score),
• need for hospitalization from initial ED visit,
3
Study Design and Methods
3.1
Overall Study Design
The Probiotics trial has a parallel group design with a placebo control. We will not describe
speciﬁcs about the active agent or placebo here, as these are contained in the protocol. We
will refer to the two trial arms as Active and Placebo. Study participants will be randomized
to Active or Placebo, each having equal allocation. Treatment with the assigned therapy is
to commence immediately following randomization. The primary analysis will be performed
on an intention-to-treat basis. We will also use an enrichment design, possibly modifying
the eligibility criteria of the trial based on interim results.
3.2
Randomization and Blinding
3.2.1
Method of Treatment Assignment
Randomization will be balanced among the study arms. Randomization will be stratiﬁed by
clinical center and by duration of symptoms. Permuted blocks of lengths 2, 4, and 6 will be
used for randomization. This trial will use a web-based system for randomization provided
by randomize.net. Randomization/kit numbers will be provided in a scrambled order and
separated into arms (A and B).
Delivery of Randomization
Randomizations will be delivered to the clinical centers
using a web-based system administered by randomize.net. This system will use each enrolled
patient’s clinical center and duration of symptoms (<48 hours vs. 48 hours or more) to deliver
the next assigned treatment.
In this trial, there will be no “emergency backup” randomization, as we expect to be able
to capture a suﬃcient number of patients.
3.2.2
Blinding
The Probiotics trial will be performed in a double-blind fashion. All study personnel, includ-
ing investigators and research coordinators, shall be blinded to assigned treatment arm for
each enrolled subject. Of necessity, biostatisticians involved in presenting interim analyses
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PECARN Protocol # 032: Statistical Analysis Plan
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to the DSMB will be aware which subjects have received “Treatment A” and which have
received “Treatment B”, but they will not be aware of the identity of the two arms.
Unblinded personnel in this study will include: the central research pharmacist and,
possibly, a pharmacy monitor contracted by the DCC expressly for the purpose of ensuring
assigned treatments have been correctly prepared and delivered in this study. The DSMB
may request to be unblinded to treatment assignment at any time.
3.3
Sample Size and Power Determination
The primary outcome is binary: whether total post-enrollment Modiﬁed Vesikari Score
(MVS) is ≥9 during the 2-week follow-up period.
The diﬀerence between arms will be
tested at a 0.05 level. The null and alternative hypotheses are, respectively,
H0 : pA = pP
and
H1 : pA ̸= pP,
where pA and pP are, respectively, the true probabilities of MVS≥9 on the Active drug and
on Placebo.
Our pilot data indicate that 25% of patients will have moderate to severe disease (MVS≥9)
during the course of their illness. Furthermore, expert surveys indicated that an absolute
risk reduction of 10% would constitute a minimal clinically-important diﬀerence (MCID).
Therefore, our sample size calculation assumed a 25% event rate in the control group for
which we desire to detect an absolute beneﬁcial treatment eﬀect of 10% with 90% power
(0.1 Type II error rate). Using a two-sided type I error (α) of 0.05 and the hypothesized
proportions yields a required total sample size of 670 patients. Our expected power, should
we ﬁnd diﬀerent event rates in our 2 groups, is displayed in the following table.
Placebo
Active
% Diﬀerence
Power
0.30
0.21
9%
0.76
0.30
0.20
10%
0.85
0.25
0.15
10%
0.90
0.25
0.16
9%
0.82
0.25
0.17
8%
0.72
0.20
0.10
10%
0.95
0.20
0.12
8%
0.81
0.20
0.13
7%
0.69
Based on previous work by our group, we assumed 10% loss to follow-up (670/0.90 = 744),
5% drop-out, and 3% drop-in (caregivers who buy a probiotic agent to administer to their
child) rate (744/(0.92)2 = 879). Adjustment for O’Brien-Fleming monitoring boundaries
requires a further 2% increase. Thus, the total number randomized (ﬁnal target sample size)
will be 900.
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PECARN Protocol # 032: Statistical Analysis Plan
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4
Study Subjects and Analysis Populations
4.1
Analysis Populations
4.1.1
Screening Population
The screening population (SCREEN) includes all patients who are screened for eligibility
into the trial, regardless of randomization into the trial or treatment status. This population
represents all patients who meet inclusion criteria outlined in the study protocol and who
are screened in real-time by study staﬀat the site. This population will be used for reporting
of study ﬂow per CONSORT guidelines.
4.1.2
Intention-to-Treat Population
The Intention-to-Treat (ITT) population includes all subjects who are randomized into the
trial, regardless of adherence to the protocol, including, for example, subjects who receive
no study drug. The ITT population will be used for the primary eﬃcacy analyses in the
study, as well as for main eﬃcacy analyses of secondary and tertiary outcomes. All analyses
using the ITT population will be based on each subject’s assigned treatment arm, regardless
of treatment actually received.
4.1.3
Per-Protocol Eﬃcacy Population
The Per-Protocol (PP) eﬃcacy population includes all subjects in the ITT population who
are veriﬁed to meet all study inclusion and exclusion criteria, who receive study drug accord-
ing to their assigned study arm (deﬁned as ≥7 out of 10 doses). This population will be
used to examine whether results seen in the ITT population are maintained in the population
adhering to the protocol.
4.1.4
Safety Population
The safety population (SAFETY) includes all subjects who receive any study drug. Report-
ing of results based on this population will be summarized according to treatment received.
This population will be used for analysis of adverse events and (in addition to ITT) to
examine safety outcomes.
4.2
Study Subjects
4.2.1
Inclusion and Exclusion Criteria
To be included in the study, patients:
• are between 3 and 48 months of age; AND
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PECARN Protocol # 032: Statistical Analysis Plan
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• have had 3 or more watery stools within 24 hours prior to screening; AND
• have had vomiting or diarrhea less than 7 days; AND
• have symptoms consistent with acute intestinal infectious process.
The following patients will be excluded from the study:
• patients with an indwelling vascular access line; OR
• patients with structural heart disease excluding non-pathological heart murmurs; OR
• patients receiving immunosuppressive therapy or having history of immunodeﬁciency;
OR
• patients with hematochezia in the preceding 48 hours; OR
• patients with chronic gastrointestinal problems (e.g., short gut syndrome, inﬂammatory
bowel disease); OR
• patients with known pancreatitis; OR
• critically ill patients; OR
• patients having a family member with an indwelling vascular access line, or on im-
munosuppressive therapy, or with a known immunodeﬁciency; OR
• patients with bilious emesis; OR
• patients who have used probiotics (supplement) in the preceding 2 weeks; OR
• patients previously enrolled in this trial; OR
• patients who are allergic to lactobacillus or Microcrystalline Cellulose (MCC); OR
• patients who are allergic to erythromycin, clindamycin, AND β-lactam antibiotics (all);
OR
• patients who will not be available for daily follow-up while symptomatic; OR
• patients whose parent/guardian do not speak English or Spanish; OR
• patients under 6 months of age AND premature (<37 weeks).
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PECARN Protocol # 032: Statistical Analysis Plan
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4.3
Enrichment Design
The study design and power analysis described are based on the assumption of homogeneous
treatment eﬀect. We may also incorporate an enrichment design to restore the statistical
power in case the presence of a subpopulation with a substantially low treatment eﬀect is
identiﬁed [1]. We are particularly interested in two potential subpopulations: participants
with <48 hours of symptoms prior to presentation and those with 48 hours or more of
symptoms. Based on pilot data, each subpopulation accounts for approximately 50% of the
total population. The decision for enrollment modiﬁcation will be made at the ﬁrst interim
analysis for eﬃcacy.
Speciﬁcally, three Mantel-Haenszel z-statistics will be calculated to
compare the primary eﬃcacy outcome between Active and Placebo groups for subjects in
the total population and the two subpopulations, respectively.
Denote these z-statistics
as Z0,1, Z<48,1, and Z>48,1. Note that a positive z-statistic sign will be used to indicate
superiority of probiotic relative to placebo.
First, Z0,1 will be compared to the O’Brien-Fleming boundary to determine whether the
trial should be discontinued for eﬃcacy (as described in Section 6.2). If the boundary is
not crossed, or if the DSMB will otherwise recommend continuation of the trial, all three
z-statistics will be considered. If Z0,1 is larger than both Z<48,1 and Z>48,1, or if both Z<48,1
and Z>48,1 are >0.3, accrual will continue as before.
Otherwise, future patients will be
recruited only from the subpopulation with the larger z-statistic. All subjects, regardless of
symptom duration will be included in the ﬁnal analyses. At the second interim analysis and
the ﬁnal analysis (or any additional unplanned interim analysis), the following method will
be used to test for eﬃcacy.
Let Z2 be the Mantel-Haenszel z-statistic that is based only on subjects enrolled since
the ﬁrst interim analysis. Then, the ﬁnal test statistic to be used is a weighted sum of the
statistics from each stage:
Z =
!
n1
n1 + n2
"
Z0,1 +
!
n2
n1 + n2
"
Z2,
where n1 and n2 are, respectively, the number of subects enrolled prior to and following
the ﬁrst interim analysis. Note that, if no enrichment is performed (i.e., accrual from the
full population), Z is asymptotically equivalent to the usual z-statistic ignoring the stages.
This ﬁnal Z value will be compared to the quantiles of the standard normal distribution
corresponding to the interim or ﬁnal boundaries described in Section 6.2.
A signiﬁcant
result will indicate eﬃcacy in the population that was enrolled following the ﬁrst interim
analysis.
Simulations were performed to evaluate the performance of this design. Additional as-
sumptions/considerations:
• The (untreated) outcome rate in the subpopulation with greater than 2 days of symp-
toms is 20%, while it is 30% in the other subpopulation.
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PECARN Protocol # 032: Statistical Analysis Plan
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• Each subpopulation accounts for 50% of the overall population.
• The normal approximation to the binomial distribution was used, rather than a chi-
square or Mantel-Haenszel test.
• The interim analyses occur at 35% and 70% of target patient enrollment.
Several diﬀerent treatment eﬀect scenarios were simulated. The results show that the en-
richment design will increase power when the treatment eﬀect diﬀers by subpopulation, but
will have little impact on power if the treatment eﬀect is the same in both subpopulations.
One slight disadvantage is that, depending on outcome rates, the enrichment design will only
accrue a subpopulation after the ﬁrst interim analysis with probability 0.05–0.35 when, in
fact, there is a homogeneous treatment eﬀect.
5
General Analysis Issues
5.1
Analysis Software
Analysis will be performed using SAS R⃝Software version 9.3 or later whenever possible.
Other software packages, including R and StatXact R⃝, may be used for particular specialized
procedures.
5.2
Methods for Withdrawals, Missing Data, and Outliers
Per the intention-to-treat principle, subjects who withdraw from the study or are lost to
follow-up will have all available data used in the analysis. In the event that a substantial
number of subjects are withdrawn or lost to follow-up, baseline characteristics and available
information on hospital course will be reviewed and compared to subjects not withdrawn or
lost, to assess empirically if these subjects diﬀer from those remaining in the study for the
scheduled treatment and follow-up time.
Data from the follow-up surveys will be collected in such a way that data for a particular
day should be complete. Information may be missing, however, if an entire day is not com-
pleted. For cases where the information needed to derive the primary outcome is incomplete,
multiple imputation methods will be used. This is described in more detail in Section 7.2.
Outliers will be reviewed for validity. Outliers that are valid, for example, high number
of vomiting episodes, will be included in all primary reports from this trial.
5.3
Multicenter Studies
The randomization sequences will be stratiﬁed by clinical center, to assure approximate
balance of sites between study arms at all times. The primary analysis, and other analyses
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PECARN Protocol # 032: Statistical Analysis Plan
Page 10
will be stratiﬁed by clinical center in order to account for possible baseline diﬀerences between
centers.
5.4
Multiple Comparisons
The secondary outcomes will be subject to adjustment of signiﬁcance level for multiple com-
parisons. Diarrhea duration, vomiting duration, return visits, missed daycare, missed work,
and household transmission rate will be subject to Holm’s stepdown procedure. Speciﬁcally,
the smallest of the six p-values will be compared to a signiﬁcance level of 0.05/6. If sig-
niﬁcance is reached, the next-smallest p-value will be compared to 0.05/5, and so on. The
ﬁnal p-value of the six will be compared to 0.05, assuming that all others are signiﬁcant.
Conﬁrmatory and tertiary outcome results will not be adjusted for multiple comparisons, as
these are more exploratory in nature.
5.5
Planned Subgroups, Interactions, and Covariates
There are three subgroup factors prespeciﬁed for formal analysis in this trial:
1. Age (under 1 year versus 1 and older)
2. Antibiotic useage during the 14 days prior to ED visit,
3. Infectious agent: virus, bacteria, parasite, or other/unidentiﬁed.
We will also consider the factor used to randomize, duration of symptoms (<48 hours vs. 48
hours or more), in subgroup analyses.
5.6
Derived and Computed Variables
All derived and computed variables will be outlined in the analysis dataset speciﬁcations for
this study. These datasets are independently programmed by two statisticians. The SAS
COMPARE procedure will be used to verify that the dual programmed analysis datasets are
identical for each variable and each observation.
5.7
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. This
process will begin at the analysis design stage and will continue through writing of abstracts
and manuscripts.
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PECARN Protocol # 032: Statistical Analysis Plan
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6
Overview of Planned Analyses
6.1
Schedule of Interim Analyses
This study has two planned formal interim analyses.
There will be additional meetings
for review of the protocol, safety of the ﬁrst 80 patients, and other meetings, as necessary.
Formal interim analyses will examine treatment eﬃcacy as well as patient safety. These
analyses will be reviewed by the DSMB. The DSMB will, at their discretion, be able to
request analyses additional to those described in this SAP.
The total target enrollment for this study is 900 subjects. We estimate that this will take
4 years. The ﬁrst analysis (safety) will take place after enrollment of 80 subjects (40 of these
<1 year old and 40 ≥1). The ﬁrst formal eﬃcacy interim analysis will take place after the
second year of enrollment, after approximately 350 subjects have been enrolled. The second
formal eﬃcacy interim analysis will be performed after approximately 620 subjects have
been enrolled. The DSMB is to review interim data and make recommendations regarding
continuation or modiﬁcation of the study.
6.2
Stopping Rules for Interim Analyses
Two-sided O’Brien-Fleming boundaries, implemented using the alpha-spending function ap-
proach will be used. Speciﬁcally, if the analyses are performed exactly when planned, the
signiﬁcance levels that will be used at interim analyses are 0.00065 and 0.0136. If the trial
reaches the anticipated total sample size, a signiﬁcance level of 0.0457 will be used for the
ﬁnal test. These boundaries assure that the total Type I error rate will be less than or equal
to 0.05.
6.3
Blinding in the Interim Analyses
Data center biostatisticians involved in this study will be partially blinded, aware of results
by treatment arm, but not of arm identities. Other data center personnel will be blinded to
treatment assignments, but data center study team for this trial will have access to individual
safety and eﬃcacy data. Personnel at the clinical centers will be blinded to aggregate safety
and eﬃcacy data until the time of ﬁnal analysis or until the decision is made to unblind all
investigators to study results.
All by-treatment interim analyses will refer to arms as “A” and “B” throughout the report
presented to the DSMB. The DSMB will have the option of being unblinded to treatment
arm identity at any time.
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PECARN Protocol # 032: Statistical Analysis Plan
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6.4
Schedule of Final Analyses
All ﬁnal, planned analyses identiﬁed in the protocol and in this SAP will be performed only
after all randomized patients have completed the protocol and the results of all signiﬁcant
queries have been resolved. Any post hoc, exploratory analyses completed to support planned
study analyses, which were not identiﬁed in this SAP, will be documented and reported as
such in all study publications.
7
Planned Analyses with Procedures for Completion
7.1
Analysis of Demographic and Other Pre-Treatment Charac-
teristics
Publication of the primary results will include reporting of key baseline characteristics overall,
and by assigned treatment arm. These will include, but are not limited to
• gender
• race
• age
• baseline MVS
• duration of symptoms prior to enrollment (<48 hours vs. 48 hours or more)
• breast-feeding status
• antibiotic useage during the 14 days prior to ED visit
• infective agent at baseline (e.g., norovirus, rotavirus)
• hydration assessment (Gorelick dehydration score)
• need for hospitalization from initial ED visit
7.2
Analysis of Primary Outcome
The primary outcome for the study is a post-enrollment (2-week) modiﬁed Vesikari Score
(MVS), deﬁned as MVS ≥9. The scientiﬁc hypotheses regarding the primary outcome are
described in Section 3.3.
The post-enrollment score is calculated based on the elements of the score collected Day
1 through Day 14, or when symptoms resolve. Resolution of symptoms is deﬁned as the ﬁrst
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PECARN Protocol # 032: Statistical Analysis Plan
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Points
0
1
2
3
Diarrhea duration
0
1–96 hrs
97–120 hrs
≥121 hrs
Max # of diarrheal stools/24 hrs
0
1–3
4–5
≥6
Vomiting duration
0
1–24 hrs
25–48 hrs
≥49 hrs
Max # of vomiting episodes/24 hrs
0
1
2–4
≥5
Max recorded fever
≤37◦C
37.1–38.4◦C
38.5–38.9◦C
≥39◦C
Unscheduled healthcare visit
0
—
Primary
Emergency
Care
Department
Treatment
None
Rehydration
Hospital
—
Admission
Table 1: Modiﬁed Vesikari Score
daily survey with absence of both diarrhea and vomiting. Each of the seven components will
be assigned a score for the entire study period (from randomization to day 14). Scoring of
each component is described in Table 1.
The components will be calculated by the following rules:
1. Maximum number of episodes of vomiting in a 24-hour period. The number
of episodes of vomiting is not collected precisely in 24-hour blocks.
However, this
component will be deﬁned as the maximum number of vomiting episodes reported on
a single daily follow-up survey.
2. Maximum number of episodes of diarrhea in a 24-hour period. This will use
the same procedure as the previous component.
3. Maximum temperature. This will also use the same procedure as the two above.
4. Diarrhea duration. The start time for this component is randomization time. If
diarrhea is recorded only on consecutive daily surveys, the end time is the time of the
last recorded diarrhea episode. On the other hand, if diarrhea is absent on any daily
survey and then present on a later daily survey (but vomiting must be present on the
daily surveys between, otherwise it will not be considered the same disease), then the
component will be calculated as time from randomization through the last diarrhea
episode prior to the break in diarrhea plus the time from the start (noon) of the next
daily survey where diarrhea is reported until the time of the last diarrhea episode. If
there is yet another break in diarrhea, the procedure is repeated. If multiple end times
are recorded for a subject, the ﬁrst valid time will be used.
5. Vomiting duration. This component will be calculated using exactly the same pro-
cedure described for diarrhea when vomiting is present at randomization. If vomiting
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PECARN Protocol # 032: Statistical Analysis Plan
Page 14
is not present at randomization and never occurs, vomiting duration will be 0. If vom-
iting starts after randomization, the start time will be the start time (noon) of the ﬁrst
daily survey where vomiting is present.
6. Unscheduled healthcare visit. Presence of an unscheduled healthcare visit will be
collected on the survey and will be classiﬁed as “none”, “primary care”, or “emergency
department”.
7. Treatment. Treatment will be classiﬁed as “none”, “rehydration”, or “hospital ad-
mission”. If the patient is admitted directly following their enrollment ED visit and
that admission stay is longer than 48 hours, it will be counted as treatment in the post
enrollment MVS. If the patient’s enrollment admission stay was less than 48 hours,
it will not be counted as “treatment”. The same logic will be used for “rehydration”
during the enrollment ED visit (and admission stay, if admitted).
This outcome will be tabulated by treatment for each stratum (clinical center and du-
ration of symptoms). A Mantel-Haenszel statistic, assessing the eﬀect of treatment on the
primary outcome controlling for strata, will be calculated to test the primary hypothesis.
Summary statistics for the eﬀect sizes will be given. For dichotomous outomes, Mantel-
Haenszel risk ratios will be reported to the DSMB at interim analyses.
Choice of ﬁnal
summary statistic reported (e.g., risk diﬀerence, risk ratio, or odds ratio) will be based, in
part, by which statistic is least variable across subgroups (i.e., shows the smallest degree of
interaction across subgroups).
It is expected that, for both the ﬁnal analyses as well as interim analyses, the asymptotic
version of the Mantel-Haenszel test will be appropriate. This analysis will be performed
using SAS PROC FREQ. In the case of low outcome counts, which may occur within strata
at early interim analyses, the Mantel-Fleiss criterion will be assessed. If the criterion has a
value less than 5, the exact version of the Mantel-Haenszel test will be used and the two-sided
p-value will be deﬁned as the sum of all probabilities of test statistics with point probabilities
less than or equal to that of the observed value.
In the event any patients were randomized within an incorrect stratum (i.e., wrong dura-
tion of symptoms) due to misspeciﬁcation at time of randomization, the actual rather than
assigned category will be used in the above analysis.
7.2.1
Multiple Imputation
When the primary outcome is unable to be derived due to missing data, multiple imputation
will be used. This method will be applied to the components of the overall MVS: Diarrhea
duration, Maximum number of diarrheal stools/24 hours, Vomiting duration, Maximum
number of vomiting episodes/24 hours, Maximum fever, Unscheduled ED visit, Unscheduled
Primary Care Visit, Rehydration, and Hospital Admission.
In the case where no MVS
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PECARN Protocol # 032: Statistical Analysis Plan
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outcome data are available, the subject will not be included in imputations and the outcomes
will remain missing.
Sequential Regression Multivariate Imputation Models
We will use logistic regres-
sion methods to model unscheduled ED visit, Unscheduled Primary Care Visit, Rehydration,
and Hospital Admission. We will use Poisson or linear regression methods to model Diar-
rhea duration, Maximum number of diarrheal stools/24 hours, Vomiting duration, Maximum
number of vomiting episodes/24 hours, and Maximum fever. For all models, we will use for-
ward stepwise variable selection to select predictors.
Variables to include in imputation models
Stratum: Stratify models using treatment
assigned
Minimum and maximum possible values will be computed and used as bounds for imput-
ing MVS components: Diarrhea duration, Maximum number of diarrheal stools/24 hours,
Vomiting duration, Maximum number of vomiting episodes/24 hours, Maximum fever
General model variables: age, gender, breast-feeding status, hospital/site
Baseline model variables: duration of symptoms prior to enrollment, diarrhea duration,
maximum number of diarrheal stools/24 hours, vomiting duration, maximum number of
vomiting episodes/24 hours, maximum fever, dehydration status, antibiotics use, Number in
household, number infected in household
Post-randomization model variables: Time to symptom resolution, ED disposition, primary
care visits, Emergency department visits, hospital admissions, daycare days missed, work
days missed, antibiotic use, invasive LGG disease, bloating, gas, intestinal rumbling, blood
in stool, abdominal cramps, nausea, loss of appetite, heartburn, constipation, skin rash,
muscle aches, sore throat, cough, headache, chills, weakness, runny nose, number infected in
household
Minimum and maximum possible values will also be used for imputing the following: Daycare
Days Missed, Work Days Missed, number infected in household
Number of imputations
We will impute and analyze 10 datasets. We will increase that
number if the eﬃciency of the imputed datasets is less than 0.99.
7.2.2
Additional Analyses of Primary Outcome
A secondary analysis of the primary outcome will test for treatment eﬀect on the primary
outcome using a logistic regression model with baseline MVS as a covariate. We will also
analyze the MVS outcome as a continuous variable. For this analysis, treatment groups will
be compared using a Van Elteren test, stratiﬁed by center and duration of symptoms.
We will perform further analyses of the MVS score outcomes by assessing the treatment
eﬀect after adjustment for covariates. The covariates that will be included have been de-
January 16, 2015
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PECARN Protocol # 032: Statistical Analysis Plan
Page 16
scribed previously. A logistic regression model will be used for the indicator outcome of
moderate-severe disease (MVS ≥9). Linear models will be used for the continuous MVS
score. These models will be evaluated and adjustments will be made if any assumptions ap-
pear to be seriously violated. For example, a distribution other than the normal distribution
may be used for the MVS score.
7.3
Analysis of Secondary Outcomes
7.3.1
Duration of Symptoms, Missed Daycare and Missed Work
Duration of diarrhea, duration of vomiting (components of the MVS), days of missed daycare,
and hours of missed work will be analyzed in a similar manner. Groups will be compared
using the Van Elteren test, stratiﬁed by center and duration of symptoms (pre-enrollment).
Analysis of duration of vomiting, missed daycare, and days of missed work will be restricted
to the populations in which the measures are applicable. Additional analyses involving these
outcomes will include linear regression models that adjust for possible eﬀects of baseline
characteristics.
7.3.2
Return Visits
Return visits will be assessed as to whether or not they are related to vomiting, diarrhea,
dehydration, fever, or ﬂuid refusal. If any such visit occurs within 2 weeks of the index visit,
it will be counted for this outcome. The outcome will be compared between treatment groups
using the Mantel-Haenszel test, stratiﬁed by clinical center and duration of symptoms.
7.4
Safety Outcomes
7.4.1
Side-Eﬀects
The occurence of any side-eﬀect (listed previously) will be analyzed as a dichotomous variable
for two time windows: the initial disease window (through day 14, or until resolution of
symptoms) and through day 35 (which includes the initial window). The ﬁrst of these two
windows will not count diarrhea, vomiting, or fever, as these will likely be experienced by
a vast majority of subjects and are part of the primary and secondary outcomes.
The
latter window will only count diarrhea, vomiting, or fever that occur after the initial disease
window.
The outcome will be compared between treatment groups using a Mantel-Haenszel test,
stratiﬁed by center and duration of symptoms prior to randomization.
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PECARN Protocol # 032: Statistical Analysis Plan
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7.4.2
Adverse Events
Adverse events (AEs) will be recorded from the time of randomization through 35 days.
Symptoms/side-eﬀects described previously will generally not be counted as AEs, as they
will be reported separately. Serious adverse events (SAEs), unexpected medically attended
events, and new chronic illnesses will be reported from randomization through one year after
last study dose. Adverse events will be coded using the Medical Dictionary for Regulatory
Activities (MedDRA), version 14.0.
All Adverse Events
Summaries of incidence rates (frequencies and percentages), inten-
sity, and relationship to study of individual AEs by System Organ Class and Preferred Term
(MedDRA) will be prepared. All AEs beginning after randomization but before discharge
will be included. Basic summaries by assigned groups will be prepared. The DSMB may
request to see more detailed tables. The occurrence of any adverse event will be considered
as a dichotomous outcome and will be compared between groups using a Mantel-Haenszel
test, stratiﬁed by clinical center and duration of symptoms.
Serious Adverse Events/Deaths
SAEs/Deaths will be reported separately in a similar
fashion to the more general AE reports. In addition, narratives will be available for each
event.
7.5
Analysis of Tertiary Outcomes
Tertiary outcomes will be analyzed in a manner similar to the primary and secondary out-
comes. Dichotomous outcomes will be compared between groups using the Mantel-Haenszel
test, while continuous outcomes will be compared using the Van Elteren test. Both types
of tests will be stratiﬁed by the randomization stratiﬁcation factors: clinical center and
duration of symptoms.
7.6
Analysis of Subgroups
There are 3 subgroup factors prespeciﬁed for formal analysis in this trial:
1. Age (under 1 year versus 1 and older)
2. Antibiotic useage during the 14 days prior to ED visit,
3. Infectious agent: virus, bacteria, parasite, or other/unidentiﬁed.
Rates of the primary study outcome will be reported by treatment arm for all prespeciﬁed
subgroups. Secondary outcomes will also be reported by arm for all subgroups.
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PECARN Protocol # 032: Statistical Analysis Plan
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A “subgroup” eﬀect will be declared to be signiﬁcant only if the interaction between
assigned treatment and the subgroup factor is signiﬁcant in the appropriate statistical model
testing for each particular interaction, at a signiﬁcance level of 0.05/3 = 0.017. These results
must still be viewed with caution, given the number of outcomes. For the primary outcome,
and other binary outcomes, logistic regression models will be used with a main eﬀect for
treatment, a main eﬀect for the subgroup variable of interest, and an interaction between
the subgroup variable of interest and the treatment. Interactions for continuous outcomes
will be evaluated in a similar manner, using linear regression models.
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PECARN Protocol # 032: Statistical Analysis Plan
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References
[1] M Rosenblum and MJ Van Der Laan. Optimizing randomized trial designs to distinguish
which subpopulations beneﬁt from treatment. Biometrika, 98:845–860, 2011.
[2] The American Statistical Association, Committee on Professional Ethics. Ethical guide-
lines for statistical practice, August 1999.
January 16, 2015
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Statistical Analysis Plan
Protocol Title (Number): Impact of Emergency Department Probiotic Treatment of Pedi-
atric Gastroenteritis (Probiotics Study) (PECARN Protocol # 032)
Protocol Version and Date: 1.00; January 24, 2014
SAP Author: T. Charles Casper, Ph.D.
SAP Version and Date: 1.2; April 6, 2017
Changes from last version:
• Section 7.2: A sensitivity analysis was added. This will look at the primary results
after excluding subjects with daily surveys that were completed more than 14 days
after the corresponding survey day.
SAP Version 1 Date: January 16, 2015
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PECARN Protocol # 032: Statistical Analysis Plan
Page ii
Approvals:
Approved By:
Name
Title
Date
Name
Title
Date
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PECARN Protocol # 032: Statistical Analysis Plan
Page iii
Contents
Abbreviations
v
1
Preface
1
1.1
Purpose of SAP . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
1
1.2
Auxiliary/Other Documents . . . . . . . . . . . . . . . . . . . . . . . . . . .
1
2
Study Objectives and Outcomes
1
2.1
Study Objectives . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
1
2.1.1
Primary Objectives . . . . . . . . . . . . . . . . . . . . . . . . . . . .
1
2.2
Study Outcomes
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
2
2.2.1
Primary Outcome . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
2
2.2.2
Safety Outcomes
. . . . . . . . . . . . . . . . . . . . . . . . . . . . .
2
2.2.3
Secondary Outcomes . . . . . . . . . . . . . . . . . . . . . . . . . . .
2
2.2.4
Tertiary Outcomes . . . . . . . . . . . . . . . . . . . . . . . . . . . .
3
2.3
Covariates . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
3
3
Study Design and Methods
4
3.1
Overall Study Design . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
4
3.2
Randomization and Blinding . . . . . . . . . . . . . . . . . . . . . . . . . . .
4
3.2.1
Method of Treatment Assignment . . . . . . . . . . . . . . . . . . . .
4
3.2.2
Blinding . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
4
3.3
Sample Size and Power Determination
. . . . . . . . . . . . . . . . . . . . .
5
4
Study Subjects and Analysis Populations
6
4.1
Analysis Populations . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
6
4.1.1
Screening Population . . . . . . . . . . . . . . . . . . . . . . . . . . .
6
4.1.2
Intention-to-Treat Population . . . . . . . . . . . . . . . . . . . . . .
6
4.1.3
Per-Protocol Eﬃcacy Population
. . . . . . . . . . . . . . . . . . . .
6
4.1.4
Safety Population . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
6
4.2
Study Subjects
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
6
4.2.1
Inclusion and Exclusion Criteria . . . . . . . . . . . . . . . . . . . . .
6
4.3
Enrichment Design . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
8
5
General Analysis Issues
9
5.1
Analysis Software . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
9
5.2
Methods for Withdrawals, Missing Data, and Outliers . . . . . . . . . . . . .
9
5.3
Multicenter Studies . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
9
5.4
Multiple Comparisons
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
10
5.5
Planned Subgroups, Interactions, and Covariates . . . . . . . . . . . . . . . .
10
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PECARN Protocol # 032: Statistical Analysis Plan
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5.6
Derived and Computed Variables
. . . . . . . . . . . . . . . . . . . . . . . .
10
5.7
Independent Review
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
10
6
Overview of Planned Analyses
11
6.1
Schedule of Interim Analyses . . . . . . . . . . . . . . . . . . . . . . . . . . .
11
6.2
Stopping Rules for Interim Analyses . . . . . . . . . . . . . . . . . . . . . . .
11
6.3
Blinding in the Interim Analyses . . . . . . . . . . . . . . . . . . . . . . . . .
11
6.4
Schedule of Final Analyses . . . . . . . . . . . . . . . . . . . . . . . . . . . .
12
7
Planned Analyses with Procedures for Completion
12
7.1
Analysis of Demographic and Other Pre-Treatment Characteristics
. . . . .
12
7.2
Analysis of Primary Outcome . . . . . . . . . . . . . . . . . . . . . . . . . .
12
7.2.1
Multiple Imputation
. . . . . . . . . . . . . . . . . . . . . . . . . . .
15
7.2.2
Additional Analyses of Primary Outcome . . . . . . . . . . . . . . . .
16
7.2.3
Sensitivity Analysis of Primary Outcome . . . . . . . . . . . . . . . .
16
7.3
Analysis of Secondary Outcomes . . . . . . . . . . . . . . . . . . . . . . . . .
17
7.3.1
Duration of Symptoms, Missed Daycare and Missed Work
. . . . . .
17
7.3.2
Return Visits . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
17
7.4
Safety Outcomes
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
17
7.4.1
Side-Eﬀects . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
17
7.4.2
Adverse Events . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
17
7.5
Analysis of Tertiary Outcomes . . . . . . . . . . . . . . . . . . . . . . . . . .
18
7.6
Analysis of Subgroups
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
18
References
19
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PECARN Protocol # 032: Statistical Analysis Plan
Page v
Abbreviations
Abbreviation
Deﬁnition
DCC
Data Coordinating Center
CRF
Case Report Form
DSMB
Data and Safety Monitoring Board
ITT
Intent-To-Treat
MCID
Minimal Clinically-Important Diﬀerence
MVS
Modiﬁed Vesikari Score
PECARN
Pediatric Emergency Care Applied Research Network
PP
Per-Protocol
(S)AE
(Serious) Adverse Event
SAFETY
Safety Population
SAP
Statistical Analysis Plan
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PECARN Protocol # 032: Statistical Analysis Plan
Page 1
1
Preface
1.1
Purpose of SAP
This Statistical Analysis Plan (SAP) describes the planned analysis and reporting for the
PECARN Protocol: Impact of Emergency Department Probiotic Treatment of Pediatric
Gastroenteritis (Probiotics Study).
The purpose of this study is to determine if probiotic administration reduces the severity
of acute gastroenteritis episodes in children aged 3 to 48 months. The study is a randomized,
placebo-controlled trial with a parallel-group design.
The structure and content of this SAP provides suﬃcient detail to meet the requirements
and standards set by the PECARN Data Coordinating Center (DCC). All work planned and
reported for this SAP will follow guidelines for statistical practice published by the American
Statistical Association [2].
1.2
Auxiliary/Other Documents
The following documents were reviewed in preparation of this SAP:
• PECARN Protocol: Impact of Emergency Department Probiotic Treatment of Pedi-
atric Gastroenteritis (Probiotics Study).
• Case Report Forms (CRFs) for the Probiotics 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
Probiotics 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
analysis approach is completely followed in the revised technical speciﬁcations.
2
Study Objectives and Outcomes
2.1
Study Objectives
2.1.1
Primary Objectives
The primary objectives of the Probiotics trial are:
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PECARN Protocol # 032: Statistical Analysis Plan
Page 2
1. to test the hypothesis that, in children with acute gastroenteritis, probiotic administra-
tion in the emergency department will decrease the likelihood of moderate-severe dis-
ease, deﬁned by a validated Modiﬁed Vesikari Score (MVS) ≥9, compared to placebo.
2. to test the hypothesis that, in children with acute gastroenteritis, probiotic administra-
tion will not be associated with serious adverse events, and will have a similar rate of
side eﬀects (e.g., bloating, fever, abdominal distention) as compared to placebo-treated
children.
2.2
Study Outcomes
2.2.1
Primary Outcome
The primary outcome is the presence of moderate-severe acute gastroenteritis, as deﬁned
by a total post-enrollment Modiﬁed Vesikari Score (MVS) ≥9 during the 2-week follow-up
period.
2.2.2
Safety Outcomes
Safety outcomes are:
1. The occurrence of invasive disease (including meningitis and bacteremia) from Lacto-
bacillus rhamnosus.
2. Occurrence of side eﬀects: bloating, gas, intestinal rumbling, diarrhea, blood in stool,
abdominal pain, abdominal cramps, nausea, vomiting, loss of appetite, heartburn,
constipation, skin rash, diaper rash, fever, nasal congestion, runny nose, sore throat,
cough, headache, muscle aches, chills, weakness.
2.2.3
Secondary Outcomes
Secondary outcomes are:
1. Time to last watery stool as reported during daily surveys.
2. Time to last vomiting episode. Vomiting duration is only evaluated in children who
vomited ≥3 times during the 24 hours prior to the emergency department visit.
3. Return visits for unscheduled care to a healthcare provider related to vomiting, diar-
rhea, dehydration, fever, or ﬂuid refusal, within 2 weeks of the index visit.
4. Days of daycare missed by subjects who attend daycare.
5. Days of work missed by caregivers who work outside of the home.
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PECARN Protocol # 032: Statistical Analysis Plan
Page 3
6. Household transmission rate.
In addition to the primary analysis, MVS will be analyzed in secondary analyses for
conﬁrmatory purposes as:
1. a numeric variable (i.e., actual MVS, rather than dichotomized)
2.2.4
Tertiary Outcomes
Tertiary outcomes are:
1. Emergency department acute gastroenteritis-related visits
2. Intravenous rehydration
3. Hospitalization
4. Total number of diarrheal stools
5. Total number of vomiting episodes
6. Adherence to oral medication (deﬁned as ≥7 out of 10 doses)
In the event that eﬃcacy of the probiotic is demonstrated, cost will also be analyzed
(cost-eﬀectiveness).
2.3
Covariates
Although randomization should result in approximate balance between treatment groups
with respect to critical baseline variables aﬀecting the outcomes, additional exploratory
analyses will be conducted to assess the eﬀects of treatment after adjusting for baseline
covariates in models for each outcome. The covariates considered are:
• baseline MVS (actual score),
• duration of symptoms prior to enrollment (<48 hours vs. 48 hours or more),
• age,
• gender,
• clinical center,
• breast-feeding status,
• antibiotic useage during the 14 days prior to ED visit,
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PECARN Protocol # 032: Statistical Analysis Plan
Page 4
• infective agent at baseline (e.g., norovirus, rotavirus),
• hydration assessment (Gorelick dehydration score),
• need for hospitalization from initial ED visit,
3
Study Design and Methods
3.1
Overall Study Design
The Probiotics trial has a parallel group design with a placebo control. We will not describe
speciﬁcs about the active agent or placebo here, as these are contained in the protocol. We
will refer to the two trial arms as Active and Placebo. Study participants will be randomized
to Active or Placebo, each having equal allocation. Treatment with the assigned therapy is
to commence immediately following randomization. The primary analysis will be performed
on an intention-to-treat basis. We will also use an enrichment design, possibly modifying
the eligibility criteria of the trial based on interim results.
3.2
Randomization and Blinding
3.2.1
Method of Treatment Assignment
Randomization will be balanced among the study arms. Randomization will be stratiﬁed by
clinical center and by duration of symptoms. Permuted blocks of lengths 2, 4, and 6 will be
used for randomization. This trial will use a web-based system for randomization provided
by randomize.net. Randomization/kit numbers will be provided in a scrambled order and
separated into arms (A and B).
Delivery of Randomization
Randomizations will be delivered to the clinical centers
using a web-based system administered by randomize.net. This system will use each enrolled
patient’s clinical center and duration of symptoms (<48 hours vs. 48 hours or more) to deliver
the next assigned treatment.
In this trial, there will be no “emergency backup” randomization, as we expect to be able
to capture a suﬃcient number of patients.
3.2.2
Blinding
The Probiotics trial will be performed in a double-blind fashion. All study personnel, includ-
ing investigators and research coordinators, shall be blinded to assigned treatment arm for
each enrolled subject. Of necessity, biostatisticians involved in presenting interim analyses
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PECARN Protocol # 032: Statistical Analysis Plan
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to the DSMB will be aware which subjects have received “Treatment A” and which have
received “Treatment B”, but they will not be aware of the identity of the two arms.
Unblinded personnel in this study will include: the central research pharmacist and,
possibly, a pharmacy monitor contracted by the DCC expressly for the purpose of ensuring
assigned treatments have been correctly prepared and delivered in this study. The DSMB
may request to be unblinded to treatment assignment at any time.
3.3
Sample Size and Power Determination
The primary outcome is binary: whether total post-enrollment Modiﬁed Vesikari Score
(MVS) is ≥9 during the 2-week follow-up period.
The diﬀerence between arms will be
tested at a 0.05 level. The null and alternative hypotheses are, respectively,
H0 : pA = pP
and
H1 : pA ̸= pP,
where pA and pP are, respectively, the true probabilities of MVS≥9 on the Active drug and
on Placebo.
Our pilot data indicate that 25% of patients will have moderate to severe disease (MVS≥9)
during the course of their illness. Furthermore, expert surveys indicated that an absolute
risk reduction of 10% would constitute a minimal clinically-important diﬀerence (MCID).
Therefore, our sample size calculation assumed a 25% event rate in the control group for
which we desire to detect an absolute beneﬁcial treatment eﬀect of 10% with 90% power
(0.1 Type II error rate). Using a two-sided type I error (α) of 0.05 and the hypothesized
proportions yields a required total sample size of 670 patients. Our expected power, should
we ﬁnd diﬀerent event rates in our 2 groups, is displayed in the following table.
Placebo
Active
% Diﬀerence
Power
0.30
0.21
9%
0.76
0.30
0.20
10%
0.85
0.25
0.15
10%
0.90
0.25
0.16
9%
0.82
0.25
0.17
8%
0.72
0.20
0.10
10%
0.95
0.20
0.12
8%
0.81
0.20
0.13
7%
0.69
Based on previous work by our group, we assumed 10% loss to follow-up (670/0.90 = 744),
5% drop-out, and 3% drop-in (caregivers who buy a probiotic agent to administer to their
child) rate (744/(0.92)2 = 879). Adjustment for O’Brien-Fleming monitoring boundaries
requires a further 2% increase. Thus, the total number randomized (ﬁnal target sample size)
will be 900.
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PECARN Protocol # 032: Statistical Analysis Plan
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4
Study Subjects and Analysis Populations
4.1
Analysis Populations
4.1.1
Screening Population
The screening population (SCREEN) includes all patients who are screened for eligibility
into the trial, regardless of randomization into the trial or treatment status. This population
represents all patients who meet inclusion criteria outlined in the study protocol and who
are screened in real-time by study staﬀat the site. This population will be used for reporting
of study ﬂow per CONSORT guidelines.
4.1.2
Intention-to-Treat Population
The Intention-to-Treat (ITT) population includes all subjects who are randomized into the
trial, regardless of adherence to the protocol, including, for example, subjects who receive
no study drug. The ITT population will be used for the primary eﬃcacy analyses in the
study, as well as for main eﬃcacy analyses of secondary and tertiary outcomes. All analyses
using the ITT population will be based on each subject’s assigned treatment arm, regardless
of treatment actually received.
4.1.3
Per-Protocol Eﬃcacy Population
The Per-Protocol (PP) eﬃcacy population includes all subjects in the ITT population who
are veriﬁed to meet all study inclusion and exclusion criteria, who receive study drug accord-
ing to their assigned study arm (deﬁned as ≥7 out of 10 doses). This population will be
used to examine whether results seen in the ITT population are maintained in the population
adhering to the protocol.
4.1.4
Safety Population
The safety population (SAFETY) includes all subjects who receive any study drug. Report-
ing of results based on this population will be summarized according to treatment received.
This population will be used for analysis of adverse events and (in addition to ITT) to
examine safety outcomes.
4.2
Study Subjects
4.2.1
Inclusion and Exclusion Criteria
To be included in the study, patients:
• are between 3 and 48 months of age; AND
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PECARN Protocol # 032: Statistical Analysis Plan
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• have had 3 or more watery stools within 24 hours prior to screening; AND
• have had vomiting or diarrhea less than 7 days; AND
• have symptoms consistent with acute intestinal infectious process.
The following patients will be excluded from the study:
• patients with an indwelling vascular access line; OR
• patients with structural heart disease excluding non-pathological heart murmurs; OR
• patients receiving immunosuppressive therapy or having history of immunodeﬁciency;
OR
• patients with hematochezia in the preceding 48 hours; OR
• patients with chronic gastrointestinal problems (e.g., short gut syndrome, inﬂammatory
bowel disease); OR
• patients with known pancreatitis; OR
• critically ill patients; OR
• patients having a family member with an indwelling vascular access line, or on im-
munosuppressive therapy, or with a known immunodeﬁciency; OR
• patients with bilious emesis; OR
• patients who have used probiotics (supplement) in the preceding 2 weeks; OR
• patients previously enrolled in this trial; OR
• patients who are allergic to lactobacillus or Microcrystalline Cellulose (MCC); OR
• patients who are allergic to erythromycin, clindamycin, AND β-lactam antibiotics (all);
OR
• patients who will not be available for daily follow-up while symptomatic; OR
• patients whose parent/guardian do not speak English or Spanish; OR
• patients under 6 months of age AND premature (<37 weeks).
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PECARN Protocol # 032: Statistical Analysis Plan
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4.3
Enrichment Design
The study design and power analysis described are based on the assumption of homogeneous
treatment eﬀect. We may also incorporate an enrichment design to restore the statistical
power in case the presence of a subpopulation with a substantially low treatment eﬀect is
identiﬁed [1]. We are particularly interested in two potential subpopulations: participants
with <48 hours of symptoms prior to presentation and those with 48 hours or more of
symptoms. Based on pilot data, each subpopulation accounts for approximately 50% of the
total population. The decision for enrollment modiﬁcation will be made at the ﬁrst interim
analysis for eﬃcacy.
Speciﬁcally, three Mantel-Haenszel z-statistics will be calculated to
compare the primary eﬃcacy outcome between Active and Placebo groups for subjects in
the total population and the two subpopulations, respectively.
Denote these z-statistics
as Z0,1, Z<48,1, and Z>48,1. Note that a positive z-statistic sign will be used to indicate
superiority of probiotic relative to placebo.
First, Z0,1 will be compared to the O’Brien-Fleming boundary to determine whether the
trial should be discontinued for eﬃcacy (as described in Section 6.2). If the boundary is
not crossed, or if the DSMB will otherwise recommend continuation of the trial, all three
z-statistics will be considered. If Z0,1 is larger than both Z<48,1 and Z>48,1, or if both Z<48,1
and Z>48,1 are >0.3, accrual will continue as before.
Otherwise, future patients will be
recruited only from the subpopulation with the larger z-statistic. All subjects, regardless of
symptom duration will be included in the ﬁnal analyses. At the second interim analysis and
the ﬁnal analysis (or any additional unplanned interim analysis), the following method will
be used to test for eﬃcacy.
Let Z2 be the Mantel-Haenszel z-statistic that is based only on subjects enrolled since
the ﬁrst interim analysis. Then, the ﬁnal test statistic to be used is a weighted sum of the
statistics from each stage:
Z =
!
n1
n1 + n2
"
Z0,1 +
!
n2
n1 + n2
"
Z2,
where n1 and n2 are, respectively, the number of subects enrolled prior to and following
the ﬁrst interim analysis. Note that, if no enrichment is performed (i.e., accrual from the
full population), Z is asymptotically equivalent to the usual z-statistic ignoring the stages.
This ﬁnal Z value will be compared to the quantiles of the standard normal distribution
corresponding to the interim or ﬁnal boundaries described in Section 6.2.
A signiﬁcant
result will indicate eﬃcacy in the population that was enrolled following the ﬁrst interim
analysis.
Simulations were performed to evaluate the performance of this design. Additional as-
sumptions/considerations:
• The (untreated) outcome rate in the subpopulation with greater than 2 days of symp-
toms is 20%, while it is 30% in the other subpopulation.
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PECARN Protocol # 032: Statistical Analysis Plan
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• Each subpopulation accounts for 50% of the overall population.
• The normal approximation to the binomial distribution was used, rather than a chi-
square or Mantel-Haenszel test.
• The interim analyses occur at 35% and 70% of target patient enrollment.
Several diﬀerent treatment eﬀect scenarios were simulated. The results show that the en-
richment design will increase power when the treatment eﬀect diﬀers by subpopulation, but
will have little impact on power if the treatment eﬀect is the same in both subpopulations.
One slight disadvantage is that, depending on outcome rates, the enrichment design will only
accrue a subpopulation after the ﬁrst interim analysis with probability 0.05–0.35 when, in
fact, there is a homogeneous treatment eﬀect.
5
General Analysis Issues
5.1
Analysis Software
Analysis will be performed using SAS R⃝Software version 9.3 or later whenever possible.
Other software packages, including R and StatXact R⃝, may be used for particular specialized
procedures.
5.2
Methods for Withdrawals, Missing Data, and Outliers
Per the intention-to-treat principle, subjects who withdraw from the study or are lost to
follow-up will have all available data used in the analysis. In the event that a substantial
number of subjects are withdrawn or lost to follow-up, baseline characteristics and available
information on hospital course will be reviewed and compared to subjects not withdrawn or
lost, to assess empirically if these subjects diﬀer from those remaining in the study for the
scheduled treatment and follow-up time.
Data from the follow-up surveys will be collected in such a way that data for a particular
day should be complete. Information may be missing, however, if an entire day is not com-
pleted. For cases where the information needed to derive the primary outcome is incomplete,
multiple imputation methods will be used. This is described in more detail in Section 7.2.
Outliers will be reviewed for validity. Outliers that are valid, for example, high number
of vomiting episodes, will be included in all primary reports from this trial.
5.3
Multicenter Studies
The randomization sequences will be stratiﬁed by clinical center, to assure approximate
balance of sites between study arms at all times. The primary analysis, and other analyses
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PECARN Protocol # 032: Statistical Analysis Plan
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will be stratiﬁed by clinical center in order to account for possible baseline diﬀerences between
centers.
5.4
Multiple Comparisons
The secondary outcomes will be subject to adjustment of signiﬁcance level for multiple com-
parisons. Diarrhea duration, vomiting duration, return visits, missed daycare, missed work,
and household transmission rate will be subject to Holm’s stepdown procedure. Speciﬁcally,
the smallest of the six p-values will be compared to a signiﬁcance level of 0.05/6. If sig-
niﬁcance is reached, the next-smallest p-value will be compared to 0.05/5, and so on. The
ﬁnal p-value of the six will be compared to 0.05, assuming that all others are signiﬁcant.
Conﬁrmatory and tertiary outcome results will not be adjusted for multiple comparisons, as
these are more exploratory in nature.
5.5
Planned Subgroups, Interactions, and Covariates
There are three subgroup factors prespeciﬁed for formal analysis in this trial:
1. Age (under 1 year versus 1 and older)
2. Antibiotic useage during the 14 days prior to ED visit,
3. Infectious agent: virus, bacteria, parasite, or other/unidentiﬁed.
We will also consider the factor used to randomize, duration of symptoms (<48 hours vs. 48
hours or more), in subgroup analyses.
5.6
Derived and Computed Variables
All derived and computed variables will be outlined in the analysis dataset speciﬁcations for
this study. These datasets are independently programmed by two statisticians. The SAS
COMPARE procedure will be used to verify that the dual programmed analysis datasets are
identical for each variable and each observation.
5.7
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. This
process will begin at the analysis design stage and will continue through writing of abstracts
and manuscripts.
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PECARN Protocol # 032: Statistical Analysis Plan
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6
Overview of Planned Analyses
6.1
Schedule of Interim Analyses
This study has two planned formal interim analyses.
There will be additional meetings
for review of the protocol, safety of the ﬁrst 80 patients, and other meetings, as necessary.
Formal interim analyses will examine treatment eﬃcacy as well as patient safety. These
analyses will be reviewed by the DSMB. The DSMB will, at their discretion, be able to
request analyses additional to those described in this SAP.
The total target enrollment for this study is 900 subjects. We estimate that this will take
4 years. The ﬁrst analysis (safety) will take place after enrollment of 80 subjects (40 of these
<1 year old and 40 ≥1). The ﬁrst formal eﬃcacy interim analysis will take place after the
second year of enrollment, after approximately 350 subjects have been enrolled. The second
formal eﬃcacy interim analysis will be performed after approximately 620 subjects have
been enrolled. The DSMB is to review interim data and make recommendations regarding
continuation or modiﬁcation of the study.
6.2
Stopping Rules for Interim Analyses
Two-sided O’Brien-Fleming boundaries, implemented using the alpha-spending function ap-
proach will be used. Speciﬁcally, if the analyses are performed exactly when planned, the
signiﬁcance levels that will be used at interim analyses are 0.00065 and 0.0136. If the trial
reaches the anticipated total sample size, a signiﬁcance level of 0.0457 will be used for the
ﬁnal test. These boundaries assure that the total Type I error rate will be less than or equal
to 0.05.
6.3
Blinding in the Interim Analyses
Data center biostatisticians involved in this study will be partially blinded, aware of results
by treatment arm, but not of arm identities. Other data center personnel will be blinded to
treatment assignments, but data center study team for this trial will have access to individual
safety and eﬃcacy data. Personnel at the clinical centers will be blinded to aggregate safety
and eﬃcacy data until the time of ﬁnal analysis or until the decision is made to unblind all
investigators to study results.
All by-treatment interim analyses will refer to arms as “A” and “B” throughout the report
presented to the DSMB. The DSMB will have the option of being unblinded to treatment
arm identity at any time.
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PECARN Protocol # 032: Statistical Analysis Plan
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6.4
Schedule of Final Analyses
All ﬁnal, planned analyses identiﬁed in the protocol and in this SAP will be performed only
after all randomized patients have completed the protocol and the results of all signiﬁcant
queries have been resolved. Any post hoc, exploratory analyses completed to support planned
study analyses, which were not identiﬁed in this SAP, will be documented and reported as
such in all study publications.
7
Planned Analyses with Procedures for Completion
7.1
Analysis of Demographic and Other Pre-Treatment Charac-
teristics
Publication of the primary results will include reporting of key baseline characteristics overall,
and by assigned treatment arm. These will include, but are not limited to
• gender
• race
• age
• baseline MVS
• duration of symptoms prior to enrollment (<48 hours vs. 48 hours or more)
• breast-feeding status
• antibiotic useage during the 14 days prior to ED visit
• infective agent at baseline (e.g., norovirus, rotavirus)
• hydration assessment (Gorelick dehydration score)
• need for hospitalization from initial ED visit
7.2
Analysis of Primary Outcome
The primary outcome for the study is a post-enrollment (2-week) modiﬁed Vesikari Score
(MVS), deﬁned as MVS ≥9. The scientiﬁc hypotheses regarding the primary outcome are
described in Section 3.3.
The post-enrollment score is calculated based on the elements of the score collected Day
1 through Day 14, or when symptoms resolve. Resolution of symptoms is deﬁned as the ﬁrst
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PECARN Protocol # 032: Statistical Analysis Plan
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Points
0
1
2
3
Diarrhea duration
0
1–96 hrs
97–120 hrs
≥121 hrs
Max # of diarrheal stools/24 hrs
0
1–3
4–5
≥6
Vomiting duration
0
1–24 hrs
25–48 hrs
≥49 hrs
Max # of vomiting episodes/24 hrs
0
1
2–4
≥5
Max recorded fever
≤37◦C
37.1–38.4◦C
38.5–38.9◦C
≥39◦C
Unscheduled healthcare visit
0
—
Primary
Emergency
Care
Department
Treatment
None
Rehydration
Hospital
—
Admission
Table 1: Modiﬁed Vesikari Score
daily survey with absence of both diarrhea and vomiting. Each of the seven components will
be assigned a score for the entire study period (from randomization to day 14). Scoring of
each component is described in Table 1.
The components will be calculated by the following rules:
1. Maximum number of episodes of vomiting in a 24-hour period. The number
of episodes of vomiting is not collected precisely in 24-hour blocks.
However, this
component will be deﬁned as the maximum number of vomiting episodes reported on
a single daily follow-up survey.
2. Maximum number of episodes of diarrhea in a 24-hour period. This will use
the same procedure as the previous component.
3. Maximum temperature. This will also use the same procedure as the two above.
4. Diarrhea duration. This is calculated as the time between randomization and the
last diarrhea episode.
When diarrhea is reported to have stopped on one survey,
and started again on a later survey, but prior to all symptoms (i.e., vomiting in this
case) stopping, the durations of diarrhea episodes are summed.
The ﬁrst diarrhea
episode would be calculated from randomization date/time until the ﬁrst diarrhea
stop date/time. Subsequent episodes would be calculated from the beginning (noon)
of the survey day on which diarrhea reportedly returned until the next diarrhea stop
date/time. In cases where diarrhea stop date/times are not in sync with the expected
survey dates, we assume the date/times to be correct as long as a daily duration is no
more than 84 hours (i.e., more than 3.5 days) late. Otherwise, we assume the dates are
erroneous, and use the expected dates instead of the reported dates. For example, if
the stop date on survey 5 should be Jan 5, but is reportedly Feb 5, we would use Jan 5.
If the reported date was Jan 8, we would assume that some surveys were skipped, and
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PECARN Protocol # 032: Statistical Analysis Plan
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use Jan 8. If any duration is less than 0, we use 0 hours. This will happen if diarrhea
stops at any time prior to randomization.
5. Vomiting duration. This component will be calculated using exactly the same pro-
cedure described for diarrhea when vomiting is present at randomization. If vomiting
is not present at randomization and never occurs, vomiting duration will be 0. If vom-
iting starts after randomization, the start time will be the start time (noon) of the ﬁrst
daily survey where vomiting is present.
6. Unscheduled healthcare visit. Presence of an unscheduled healthcare visit will be
collected on the survey and will be classiﬁed as “none”, “primary care”, or “emergency
department”.
7. Treatment. Treatment will be classiﬁed as “none”, “rehydration”, or “hospital ad-
mission”. If the patient is admitted directly following their enrollment ED visit and
that admission stay is longer than 48 hours, it will be counted as treatment in the post
enrollment MVS. If the patient’s enrollment admission stay was less than 48 hours,
it will not be counted as “treatment”. The same logic will be used for “rehydration”
during the enrollment ED visit (and admission stay, if admitted).
This outcome will be tabulated by treatment for each stratum (clinical center and du-
ration of symptoms). A Mantel-Haenszel statistic, assessing the eﬀect of treatment on the
primary outcome controlling for strata, will be calculated to test the primary hypothesis.
Summary statistics for the eﬀect sizes will be given. For dichotomous outomes, Mantel-
Haenszel risk ratios will be reported to the DSMB at interim analyses.
Choice of ﬁnal
summary statistic reported (e.g., risk diﬀerence, risk ratio, or odds ratio) will be based, in
part, by which statistic is least variable across subgroups (i.e., shows the smallest degree of
interaction across subgroups).
It is expected that, for both the ﬁnal analyses as well as interim analyses, the asymptotic
version of the Mantel-Haenszel test will be appropriate. This analysis will be performed
using SAS PROC FREQ. In the case of low outcome counts, which may occur within strata
at early interim analyses, the Mantel-Fleiss criterion will be assessed. If the criterion has a
value less than 5, the exact version of the Mantel-Haenszel test will be used and the two-sided
p-value will be deﬁned as the sum of all probabilities of test statistics with point probabilities
less than or equal to that of the observed value.
In the event any patients were randomized within an incorrect stratum (i.e., wrong dura-
tion of symptoms) due to misspeciﬁcation at time of randomization, the actual rather than
assigned category will be used in the above analysis.
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PECARN Protocol # 032: Statistical Analysis Plan
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7.2.1
Multiple Imputation
When the primary outcome is unable to be derived due to missing data, multiple imputation
will be used. This method will be applied to the components of the overall MVS: Diarrhea
duration, Maximum number of diarrheal stools/24 hours, Vomiting duration, Maximum
number of vomiting episodes/24 hours, Maximum fever, Unscheduled ED visit, Unscheduled
Primary Care Visit, Rehydration, and Hospital Admission.
In the case where no MVS
outcome data are available, the subject will not be included in imputations and the outcomes
will remain missing.
Sequential Regression Multivariate Imputation Models
We will use logistic regres-
sion methods to model unscheduled ED visit, Unscheduled Primary Care Visit, Rehydration,
and Hospital Admission. We will use Poisson or linear regression methods to model Diar-
rhea duration, Maximum number of diarrheal stools/24 hours, Vomiting duration, Maximum
number of vomiting episodes/24 hours, and Maximum fever. For all models, we will use for-
ward stepwise variable selection to select predictors.
Variables to include in imputation models
Stratum: Stratify models using treatment
assigned
Minimum and maximum possible values will be computed and used as bounds for imput-
ing MVS components: Diarrhea duration, Maximum number of diarrheal stools/24 hours,
Vomiting duration, Maximum number of vomiting episodes/24 hours, Maximum fever
General model variables: age, gender, breast-feeding status, hospital/site
Baseline model variables: duration of symptoms prior to enrollment, diarrhea duration,
maximum number of diarrheal stools/24 hours, vomiting duration, maximum number of
vomiting episodes/24 hours, maximum fever, dehydration status, antibiotics use, Number in
household, number infected in household
Post-randomization model variables: Time to symptom resolution, ED disposition, primary
care visits, Emergency department visits, hospital admissions, daycare days missed, work
days missed, antibiotic use, invasive LGG disease, bloating, gas, intestinal rumbling, blood
in stool, abdominal cramps, nausea, loss of appetite, heartburn, constipation, skin rash,
muscle aches, sore throat, cough, headache, chills, weakness, runny nose, number infected in
household
Minimum and maximum possible values will also be used for imputing the following: Daycare
Days Missed, Work Days Missed, number infected in household
Combining results from imputed datasets for nonparametric tests
For the main
analysis of the primary outcome (Mantel-Haenszel test), the chi-square test statistic (S) will
be calculated for each imputed dataset. We will also calculate the MH odds ratio (MHOR),
deﬁned so that MHOR<1 suggests that Arm A has a lower rate of the outcome. If MHOR<1,
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PECARN Protocol # 032: Statistical Analysis Plan
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then let z = −
√
S. Otherwise, z =
√
S. The standard error of z is 1. If the calculated zs
are the same among all of the imputations, then the ﬁnal p-value is that common p-value,
and the z-statistic is the common z.
If the calculated zs diﬀer, then the z-statistic will
be estimated and the corresponding p-value (testing z = 0) will be calculated using the
imputation-speciﬁc zs and standard errors using SAS PROC MIANALYZE.
For the analysis of continuous outcomes using the Van Elteren test, a similar approach
will be used. Instead of odds ratios, the mean in each group will be used to determine the
direction of the diﬀerence. For example, if the mean of Arm A is less than that of B, then
z = −
√
S, where S is the Van Elteren chi-square statistic.
Number of imputations
We will impute and analyze 10 datasets. We will increase that
number if the eﬃciency of the imputed datasets is less than 0.99.
7.2.2
Additional Analyses of Primary Outcome
A secondary analysis of the primary outcome will test for treatment eﬀect on the primary
outcome using a logistic regression model with baseline MVS as a covariate. We will also
analyze the MVS outcome as a continuous variable. For this analysis, treatment groups will
be compared using a Van Elteren test, stratiﬁed by center and duration of symptoms.
We will perform further analyses of the MVS score outcomes by assessing the treatment
eﬀect after adjustment for covariates. The covariates that will be included have been de-
scribed previously. A logistic regression model will be used for the indicator outcome of
moderate-severe disease (MVS ≥9). Linear models will be used for the continuous MVS
score. These models will be evaluated and adjustments will be made if any assumptions ap-
pear to be seriously violated. For example, a distribution other than the normal distribution
may be used for the MVS score.
7.2.3
Sensitivity Analysis of Primary Outcome
The daily surveys are intended to be completed on or very shortly after the corresponding
study day.
In some cases, a family may be contacted long after the events in question
occurred. In theory, this information should have been recorded real-time in a diary. Also,
there is little reason to believe the delayed information would diﬀer in quality by treatment
arm. However, we will perform a sensitivity analysis to ascertain whether the primary results
hold when information collected after long delay is excluded. For this analysis, we will exclude
any patient with a daily survey collected more than 14 days after the day corresponding to
the survey and we will repeat the primary analysis.
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PECARN Protocol # 032: Statistical Analysis Plan
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7.3
Analysis of Secondary Outcomes
7.3.1
Duration of Symptoms, Missed Daycare and Missed Work
Duration of diarrhea, duration of vomiting (components of the MVS), days of missed daycare,
and hours of missed work will be analyzed in a similar manner. Groups will be compared
using the Van Elteren test, stratiﬁed by center and duration of symptoms (pre-enrollment).
Analysis of duration of vomiting, missed daycare, and days of missed work will be restricted
to the populations in which the measures are applicable. Additional analyses involving these
outcomes will include linear regression models that adjust for possible eﬀects of baseline
characteristics.
7.3.2
Return Visits
Return visits will be assessed as to whether or not they are related to vomiting, diarrhea,
dehydration, fever, or ﬂuid refusal. If any such visit occurs within 2 weeks of the index visit,
it will be counted for this outcome. The outcome will be compared between treatment groups
using the Mantel-Haenszel test, stratiﬁed by clinical center and duration of symptoms.
7.4
Safety Outcomes
7.4.1
Side-Eﬀects
The occurence of any side-eﬀect (listed previously) will be analyzed as a dichotomous variable
for two time windows: the initial disease window (through day 14, or until resolution of
symptoms) and through day 35 (which includes the initial window).
The ﬁrst of these
two windows will not count diarrhea, vomiting, fever, or diaper rash as these will likely be
experienced by a vast majority of subjects and are part (with the exception of diaper rash) of
the primary and secondary outcomes. The latter window will only count diarrhea, vomiting,
fever, or diaper rash that occur after the initial disease window.
The outcome will be compared between treatment groups using a Mantel-Haenszel test,
stratiﬁed by center and duration of symptoms prior to randomization.
7.4.2
Adverse Events
Adverse events (AEs) will be recorded from the time of randomization through 35 days.
Symptoms/side-eﬀects described previously will generally not be counted as AEs, as they
will be reported separately. Serious adverse events (SAEs), unexpected medically attended
events, and new chronic illnesses will be reported from randomization through one year after
last study dose. Adverse events will be coded using the Medical Dictionary for Regulatory
Activities (MedDRA), version 14.0.
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PECARN Protocol # 032: Statistical Analysis Plan
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All Adverse Events
Summaries of incidence rates (frequencies and percentages), inten-
sity, and relationship to study of individual AEs by System Organ Class and Preferred Term
(MedDRA) will be prepared. All AEs beginning after randomization but before discharge
will be included. Basic summaries by assigned groups will be prepared. The DSMB may
request to see more detailed tables. The occurrence of any adverse event will be considered
as a dichotomous outcome and will be compared between groups using a Mantel-Haenszel
test, stratiﬁed by clinical center and duration of symptoms.
Serious Adverse Events/Deaths
SAEs/Deaths will be reported separately in a similar
fashion to the more general AE reports. In addition, narratives will be available for each
event.
7.5
Analysis of Tertiary Outcomes
Tertiary outcomes will be analyzed in a manner similar to the primary and secondary out-
comes. Dichotomous outcomes will be compared between groups using the Mantel-Haenszel
test, while continuous outcomes will be compared using the Van Elteren test. Both types
of tests will be stratiﬁed by the randomization stratiﬁcation factors: clinical center and
duration of symptoms.
7.6
Analysis of Subgroups
There are 3 subgroup factors prespeciﬁed for formal analysis in this trial:
1. Age (under 1 year versus 1 and older)
2. Antibiotic useage during the 14 days prior to ED visit,
3. Infectious agent: virus, bacteria, parasite, or other/unidentiﬁed.
Rates of the primary study outcome will be reported by treatment arm for all prespeciﬁed
subgroups. Secondary outcomes will also be reported by arm for all subgroups.
A “subgroup” eﬀect will be declared to be signiﬁcant only if the interaction between
assigned treatment and the subgroup factor is signiﬁcant in the appropriate statistical model
testing for each particular interaction, at a signiﬁcance level of 0.05/3 = 0.017.
These
results must still be viewed with caution, given the number of outcomes. For the primary
outcome, and other binary outcomes, logistic regression models will be used with a main
eﬀect for treatment, a main eﬀect for the subgroup variable of interest, and an interaction
between the subgroup variable of interest and the treatment. Interactions for continuous
outcomes will be evaluated in a similar manner, using linear regression models. Interactions
for count outcomes (missed days of daycare and work) will be evaluated using negative
binomial regression models.
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References
[1] M Rosenblum and MJ Van Der Laan. Optimizing randomized trial designs to distinguish
which subpopulations beneﬁt from treatment. Biometrika, 98:845–860, 2011.
[2] The American Statistical Association, Committee on Professional Ethics. Ethical guide-
lines for statistical practice, August 1999.
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Lactobacillus Rhamnosus GG vs. Placebo for Pediatric Acute Gastroenteritis 
 
Summary of SAP changes (from version 1.1- January 2015- to V1.2 April 2017)  
 
1. Section 7.2: The definitions of duration of diarrhea and vomiting were changed to 
incorporate additional details about handling potentially erroneous dates and times. 
(Pages 13 and 14) 
2. Section 7.2.1: Detail was added on the approach for combining results from 
nonparametric tests across imputed datasets. (Page 15) 
3. Section 7.2: A sensitivity analysis was added. This will look at the primary results after 
excluding subjects with daily surveys that were completed more than 14 days after the 
corresponding survey day. (page 16) 
4. Section 7.4: Diaper rash was added as one of the symptoms not counted in the initial “side 
effects” window due to an expected high prevalence at baseline and early follow-up. 
(Page17) 
5. Section 7.6: Detail was given on the analysis of subgroup effects related to count 
outcomes (negative binomial regression). (page 18)