Effect of Mailing Educational Material to Patients With Atrial Fibrillation and Their Clinicians on Use of Oral Anticoagulants

Key Points Question Does a single educational mailing to a patient with atrial fibrillation and their clinician increase the use of oral anticoagulants for stroke prevention? Findings This randomized clinical trial found no statistically significant increase in initiation of oral anticoagulants among patients with atrial fibrillation after a single educational mailing to patients and their clinicians. Meaning More-intensive interventions are needed to address the public health issue of underuse of anticoagulation for stroke prevention among patients with atrial fibrillation.


Implementation of a Randomized Controlled Trial to Improve Treatment with Oral Anticoagulants in Patients wit h Atrial Fibrillation
(IMPACT-AFib)

I. PROTOCOL SYNOPSIS Protocol Title:
IMplementation of a randomized controlled trial to imProve treatment with oral AntiCoagulanTs in patients with Atrial Fibrillation (IMPACT-AFib)

Research Hypothesis:
Education on stroke prevention in atrial fibrillation (AF) among AF patients and their providers can result in increased use of oral anticoagulants (OAC) for stroke prevention among those AF patients with guideline-based indications for oral anticoagulation (CHA 2 DS 2 -VASc score of 2 or greater)

Study Schema and Length of Trial:
Early patient and provider * education interventions versus usual care (with delayed provider * education intervention at the date on which at least 80% of eligible study participants have at least 12 months of follow-up time). Duration of follow-up for the primary outcome (OAC treatment) will be from the date that the early intervention materials are mailed through the date on which at least 80% of eligible study participants have at least 12 months of follow-up time; secondary outcomes will also be evaluated at this time.

Study Objectives:
Primary: evaluate the effect of the patient and provider education interventions (versus usual care with delayed provider education intervention) on the proportion of patients with evidence of at least one OAC prescription fill (defined as one OAC dispensing or 4 INR tests) over the course of the follow-up through the date on which at least 80% of eligible study participants have at least 12 months of follow-up time.
Secondary: evaluate the impact on outcomes of the patient and provider education interventions over the course of the follow-up through the date on which at least 80% of eligible study participants have at least 12 months of follow-up time: 1. Incident rate of stroke or transient ischemic attack (TIA) hospitalization 2. Incident rate of hospitalization for stroke 3. Time to first OAC prescription fill 4. Proportion of days covered by OAC prescription fills 5. Proportion of patients actively on OAC at 12 months of follow-up 6. Incident rate of hospitalization for any bleeding 7. All-cause in-hospital mortality rates * Where it is possible to identify an individual provider. See Section IX. Method of Assigning Patients to an Intervention for further information. 8. All-cause mortality rates among patients with accurate outof-hospital mortality data (such as Medicare Advantage patients) 9. Health care utilization for AF patients, which would be reported as counts of number of health care utilization events (outpatient visits, days hospitalized, number of emergency department visits, etc.)

Exploratory:
10. Evaluate the effect of the education interventions on the primary and secondary endpoints over the course of the follow-up through the date on which at least 80% of eligible study participants have at least 24 months of follow-up time. 11. Explore the Clinical Trials Transformation Initiative (CTTI) and the FDA supported Sentinel Data Partners' ability to successfully conduct a pragmatic trial to answer important questions to improve public health

Study Design:
Prospective, randomized, open-label education intervention trial. Patients with AF and a CHA 2 DS 2 -VASc score of 2 or greater will be randomized in a 1:1 ratio to (a) the early intervention arm: early patient and provider educational interventions for those patients identified at the time of randomization and (b) the delayed intervention arm: usual care followed by provider education intervention 12 months after at least 80% of early intervention mailing has occurred (eligibility status of these patients will be assessed at time of delayed mailing). All inclusion criteria, exclusion criteria, and outcomes will be determined through claims data. The primary outcome is the proportion of AF patients with evidence of at least one OAC prescription fill over the course of the follow-up through the date on which at least 80% of eligible study participants have at least 12 months of follow-up time. A total of approximately 80,000 patients will be enrolled within multiple major health plans across the United States. Follow-up for the primary outcome and secondary outcomes will be assessed 12 months after the date on which at least 80% of eligible early intervention participants were mailed the early intervention materials. The randomization will be performed by the central coordinating center (Harvard Pilgrim), and statistical analyses will be performed by the Duke Clinical Research Institute. A second exploratory assessment of the primary and secondary endpoints will be performed once at least 80% of participants have at least 24 months of follow-up time to assess the durability and longer-term outcomes of the effect of the education intervention. Because the Sentinel Distributed Database will be used for follow-up information, and this information is refreshed approximately quarterly and this is done on separate timetables for the different health plans, it is likely that when at least the required follow-up time is available for at least 80% of people, there will be more than 12 or 24 months of follow-up for over 80% of people. All possible person-time will be used to assess participants' outcomes (patients will have different duration of follow-up).

Accrual Goal (Total number of participants):
Approximately 80,000 patients across all participating Data Partners (Aetna, Harvard Pilgrim, HealthCore, Humana, and Optum) Accrual Rate (Number of participants expected per month): All patients and providers will be randomized prior to the initiation of the early intervention. The enrollment date for all patients (early and delayed intervention patients) will be the date that the letters are mailed out to early intervention patients and providers by their respective health plans.
Inclusion Criteria: 1. Two or more diagnoses of AF (ICD-9 and/or ICD-10 codes) at least one day apart and with at least one diagnosis within the last 12 months prior to the last date in the current approved data used for cohort identification 2. CHA 2 DS 2 -VASc score of 2 or greater 3. Medical and pharmacy insurance coverage of at least the prior year as identified via administrative claims databases of one of the participating Data Partners as of the date of randomization 4. Age 30 years or greater as of the last date in the current approved data used for cohort identification Exclusion Criteria: 1. Evidence of OAC medication fill during the 12 months prior to randomization (determined at randomization for the early intervention cohort and 12 months postrandomization for the delayed intervention cohort) 2. Conditions other than AF that require anticoagulation, including treatment of deep venous thrombosis, pulmonary embolism, or ever having had a mechanical prosthetic heart valve prior to the last date in the current approved data used for cohort identification 3. Pregnancy within 6 months of the last date in the current approved data used for cohort identification 4. Any known history of intracranial hemorrhage prior to the last date in the current approved data used for cohort identification 5. Hospitalization for any bleeding within the last 6 months of the last date in the current approved data used for cohort identification 6. Patients with recent P2Y12 antagonist use (i.e. clopidogrel, prasugrel, ticlopidine, or ticagrelor) within 90 days of the last date in the current approved data used for cohort identification Criteria for Evaluation (Effectiveness, safety, stopping rules, etc.): The primary outcome is evidence of at least one OAC prescription fill through the date on which at least 80% of eligible study participants have at least 12 months of follow-up time.

Patient-Level Interventions (early intervention arm):
• Letters to patients that (1) explain to the patient that he or she appears to have AF, characterize the risk of stroke, and emphasize that although there may be a medical reason, the patient does not seem to be on an anticoagulant and (2) encourage the patient to discuss this with his or her provider to ask if he or she might benefit from OAC therapy to prevent stroke • Written education materials • Website with the patient-focused information contained in the letters to patients

Provider-Level Interventions (early intervention and delayed intervention arms):
• Letters to providers: o Early intervention letters to providers that explain this project, the nature of the problem, and identify a list of the provider's patients who have been contacted, as the provider and patient letters will be sent at approximately the same time; describe evidence and guidelines regarding oral anticoagulation o Delayed intervention letters to providers that explain this project, the nature of the problem, and identify a list of the provider's patients who are at risk for stroke and have not been treated with an oral anticoagulant; describe evidence and guidelines regarding oral anticoagulation • Response mailer that gives the provider the opportunity to share the rationale for his or her patient ( Primary outcome: proportion of AF patients with evidence of at least one OAC prescription fill through the date on which at least 80% of eligible study participants have at least 12 months of follow-up time Sample size and power determination assumptions: • 33% OAC initiation rate in the delayed intervention arm over the first year of the study • 38% OAC initiation rate in the early intervention arm (a 5% improvement in OAC initiation over the 33% OAC initiation expected in the delayed intervention arm over 1-year follow-up) • 1-year attrition rate: 30% dropout or lost-to-follow-up • Two-sided type I error of 0.05 • Roughly 10,000 patients will yield more than 99% power to detect a 5% absolute difference  1 year stroke or TIA rate in the early intervention group would be 13.82%, i.e., an absolute reduction of 0.55%), the study will have 46% power to detect this 0.55% reduction. However, if 40.5% of early intervention patients have at least 1 fill of OAC (meaning the 1 year stroke or TIA rate in the early intervention group would be 13.54%, i.e., an absolute reduction of 0.83%), the study will have 80% power to detect this 0.83% reduction. • 1-year attrition rate: 30% dropout or lost-to-follow-up • Two-sided type I error of 0.05 • The sample size has 80% power to detect a 0.5% absolute reduction in stroke, assuming a cumulative 1-year incidence of stroke of 4.2% in control (delayed intervention arm) patients and 3.7% in intervention (early intervention arm) patients. The assumption is that patients not on oral anticoagulation have an annual stroke rate of 5%, and stroke will be reduced by 50% (HR=0.5) in the treated (anticoagulated) population. The 80% power requires that 52% of early intervention arm patients are treated at 1year as compared to 33% in the control arm.

II. INTRODUCTION
Atrial fibrillation (AF) is the most common arrhythmia seen in clinical practice, accounting for one-third of rhythm-related hospitalizations. 1 The prevalence of AF in the United States is 1% overall and more than 10% in people over age 80 years, with approximately 70% of cases in patients between 65 and 85 years of age. 2 As Americans age, the number of patients with AF is expected to increase 150% by 2050, with more than 50% of patients being octogenarians or older. [3][4][5][6][7][8] The increasing burden of AF is expected to lead to a higher incidence of stroke, as patients with AF have a five to seven fold greater risk of stroke than the general population. [9][10][11] The incidence of stroke in AF patients is 4 to 5% per year. 12 Patients with a stroke due to AF have worse prognoses than patients with stroke without AF. 13,14 Oral anticoagulants (OACs) are an important therapy for patients with AF as they decrease the rate of stroke by more than two-thirds. 15 The clinical benefit of warfarin is only seen in patients who consistently maintain their international normalized ratio (INR) values within the therapeutic range (2.0-3.0). 16 The median times in the therapeutic range in the ARISTOTLE 17 , ROCKET AF 18 , RE-LY 19 , and ENGAGE 20 trials were 62%, 55%, 64%, and 68%, respectively. As part of quality improvement efforts, there is significant interest in measuring and improving performance of physicians in prescribing anticoagulation for patients with AF. The CHADS 2 and CHA 2 DS 2 -VASC scores have been developed to support providers in identifying patients with AF who are at an increased risk for stroke. 21,22 Paradoxically, anticoagulation use is no higher, or declines, as the risk of stroke, as measured by these scores, increases. 23 This is in large part due to the fact that physicians and patients are concerned about the risk of bleeding in higher-risk populations, and they may underappreciate the net benefit from anticoagulants, including stroke prevention. In any case, approximately 40-60% of patients with AF at risk of stroke are not prescribed anticoagulation therapy. 15,[24][25][26][27][28][29][30] This translates to over 50,000 preventable strokes each year in the United States with a number needed to treat of approximately 25 patients to prevent 1 stroke.
The specific reasons for not using an anticoagulant in eligible AF patients are poorly defined. The AVERROES trial provided some insight into reasons for patients deemed "unsuitable for warfarin" with 42% unable to maintain therapeutic INR, 43% unlikely to monitor INR, and 37% refusing warfarin. 31 The reasons for underuse of oral anticoagulation are likely related to three types of barriers: patient-level barriers (i.e. overestimation of risk of bleeding, underestimation of risk of stroke, misperceptions of adverse events from OACs), provider-level barriers (i.e. overestimation of risk of bleeding, underestimation of risk of stroke, misperceptions of adverse events from OACs, misperceptions about a patient's fall risk, misperceptions of the benefits of aspirin in stroke prevention), and system-level barriers (i.e. lack of time in a clinic visit to discuss stroke prevention, access to care such as an anticoagulation clinic, cost of OACs, feasibility of warfarin monitoring).
Another issue driving under-treatment with oral anticoagulants is poor medication adherence, which may be driven by patient barriers or system-level barriers. Medication non-adherence is defined as a patient's passive failure to follow a prescribed drug regimen. An average of 50% of patients are nonadherent to their prescribed treatment regimens for chronic diseases, such as AF. 32 Non-adherence rates are similar across disease states, treatment regimens, and age groups, with the first several months of therapy characterized by the highest rates of discontinuation. 33 Interventions to support patient management of medications have fallen short, and sustainable adherence rates have not improved. 34,35 The cost to the health care system of hospitalizations due to medication non-adherence for all disease states may be as high as approximately $100 billion annually. 36 Patient-provider communication regarding medication use is poor, and opportunities to document and provide feedback on metrics for medication adherence are not readily available in EMR applications. 37 Meaningful and measurable improvements in adherence require a comprehensive, multifaceted intervention in which all participants, including physicians, play an active part.

III. RESEARCH HYPOTHESIS
Among AF patients with guideline indications for OAC for stroke prevention who have not received any OAC dispensing for at least one year, an education intervention at the patient-level and the providerlevel will increase the proportion of patients started on OAC for stroke prevention.

A. PRIMARY OBJECTIVE
The primary objective is to evaluate the effect of the patient and provider education interventions (versus usual care with delayed provider education intervention) on the proportion of patients with evidence of at least one OAC prescription fill (defined as one OAC dispensing or 4 INR tests) over the course of the follow-up through the date on which at least 80% of eligible study participants have at least 12 months of follow-up time.

B. SECONDARY OBJECTIVE
The secondary objectives are to evaluate the impact on outcomes of the patient and provider education interventions over the course of the follow-up through the date on which at least 80% of eligible study participants have at least 12 months of follow-up time:

C. EXPLORATORY OBJECTIVES
The exploratory objectives are to: 1. Evaluate the effect of the early and delayed education interventions on primary and secondary endpoints over the course of the follow-up through the date on which at least 80% of eligible study participants have at least 24 months of follow-up time. 2. Explore the CTTI and the FDA supported Sentinel Data Partnership's ability to successfully conduct a pragmatic trial to answer important questions to improve public health.

VI. STUDY DESIGN AND DURATION
The study is a prospective, randomized, and open-label education intervention trial. Patients with AF and a CHA 2 DS 2 -VASc score of 2 or greater will be randomized in a 1:1 ratio to an early intervention cohort and a delayed intervention cohort within each participating health plan. The definition for OAC medication fill will be an OAC medication dispensing or at least 4 INR tests in the claims data. 1 The claims records of the patients randomized to the early intervention cohort will then be linked to "fresh" (i.e. about 1-4 months old) pharmacy claims data at the time of randomization. Patients without evidence of an OAC medication fill during the 12 months prior to randomization will be included in the patient-level and provider-level early educational intervention (patients randomized to this early intervention with evidence of an OAC medication fill during the 12 months prior to randomization will be excluded from the trial.). In addition to usual care, these patients and their providers 2 will receive a 1 Not all OAC dispensings are well captured in pharmacy claims, particularly, for warfarin. INR tests are assumed indicative of OAC fills that were not billed through the claims. 4 INR tests or values within a 12-month period will be used as a proxy since that is roughly the number of tests administered in the process of stabilizing dose. 2 See Section IX. Method of Assigning Patients to an Intervention for detail regarding provider identification. In certain circumstances, a member or provider may not receive the one-time mailing.
one-time mailing at trial start. There will be two waves of mailings for the early intervention cohort at most sites due to the practical challenges of claims data: the patients are assigned to wave 1 if they have a provider easily identified in the data (i.e., the provider associated with the most recent AF diagnosis is an individual provider), and they are assigned to wave 2 if it is difficult to identify a provider (e.g., the first identified provider is a facility). Follow-up time will start on the date of the respective wave 1 and wave 2 mailings for the early intervention patients The delayed intervention cohort will receive usual care over the initial study period. After the date on which at least 80% of eligible study participants have at least 12 months of follow-up time, "fresh" pharmacy claims data for the delayed intervention cohort that was generated and locked at the time of randomization will be used to assess trial eligibility, and those patients without evidence of an OAC medication fill during the 12 months prior to randomization will be included in the primary and secondary analyses as the delayed intervention arm. Patients randomized to the delayed intervention arm with evidence of an OAC medication fill during the 12 months prior to randomization will be excluded from the trial and will not be included in analyses. The baseline characteristics of the delayed intervention patients will be examined at the same time point as the early intervention patients, meaning at the time of randomization. The primary outcome is a comparison of the proportion of patients not on OAC during the 12 months prior to randomization, who were started on OAC over the course of the follow-up through the date on which at least 80% of eligible study participants have at least 12 months of follow-up time in the early versus the delayed intervention arm. A total of approximately 80,000 patients (randomized 1:1) across all participating Data Partners (Aetna, Harvard Pilgrim, HealthCore, Humana, and Optum) will be enrolled from participating Data Partners across the United States. Similar to the early intervention cohort, the patients in the delayed intervention cohort will be assigned to wave 1 or wave 2 ("pseudo" wave assignments) depending on the difficulty in identifying the patient's provider (the intent is to handle them the same way as was done for the early intervention arm). The follow-up for the delayed intervention patients will start on the date the wave 1 or 2 mailings take place for a given Data Partner's early intervention cohort. The follow-up time for the primary outcome will be 12 months from the date at which at least 80% of eligible study participates are enrolled (date on which early intervention materials are mailed).
The providers of patients in the delayed cohort who did not receive OAC medication during the course of the 12-month study period and meet our inclusion criteria will receive the delayed intervention: the provider-only education intervention, a one-time mailing administered 12 months after at least 80% of early intervention mailing have occurred (patients will not receive any educational materials unless no provider can be identified for a mailing). We intend to assess the primary and secondary endpoints again once at least 80% of patients have at least 24 months of follow-up time to assess the durability and longer-term outcomes of the effect of the patient-and provider-level education intervention, as well as the use of OAC following the delayed provider-level education intervention. However, as this second assessment is exploratory, we may not conduct these analyses if the results of the primary outcome are null.
Because the Sentinel Distributed Database will be used for follow-up information, and this information is refreshed approximately quarterly and this is done on separate timetables for the different health plans, it is likely that when at least the required follow-up time is available for at least 80% of people, there will be more than 12 or 24 months of follow-up for over 80% of people. All participants' outcomes will be assessed using all possible person-time; patients will have different duration of follow-up and that will be accounted for in the analyses.
A schematic diagram below shows the design of the early intervention period of the study over the course of the follow-up through the date on which at least 80% of eligible study participants have at least 12 months of follow-up time: IMPACT-AFib A schematic diagram below shows the design of the delayed intervention portion of the study:

VII. STUDY POPULATION
All inclusion and exclusion criteria will be determined by claims data. For entry into the study, the following criteria will be met:

A. INCLUSION CRITERIA
1. Two or more diagnoses of AF (ICD-9 and/or ICD-10 codes) at least one day apart and with at least one diagnosis within the last 12 months prior to the last date in the current approved data used for cohort identification 2. CHA 2 DS 2 -VASc score of 2 or greater 3. Medical and pharmacy insurance coverage of at least the prior year as identified via administrative claims databases of one of the participating Data Partners as of the date of randomization 4. Age 30 years or greater as of the last date in the current approved data used for cohort identification

B. EXCLUSION CRITERIA
1. Evidence of OAC medication fill (defined as 1 OAC dispensing or 4 INR tests) during the 12 months prior to randomization (determined at randomization for the early intervention cohort and 12 months post-randomization for the delayed intervention cohort) 2. Conditions other than AF that require anticoagulation, including treatment of deep venous thrombosis, pulmonary embolism, or ever having had a mechanical prosthetic heart valve prior to the last date in the current approved data used for cohort identification 3. Pregnancy within 6 months of the last date in the current approved data used for cohort identification 4. Any known history of intracranial hemorrhage prior to the last date in the current approved data used for cohort identification 5. Hospitalization for any bleeding within the last 6 months of the last date in the current approved data used for cohort identification 6. Patients with recent P2Y12 antagonist use (i.e. clopidogrel, prasugrel, ticlopidine, or ticagrelor within 90 days of the last date in the current approved data used for cohort identification The complete code list for inclusion and exclusion criteria is accessible on the Sentinel website (https://www.sentinelinitiative.org/FDA-catalyst/projects/implementation-randomized-controlled-trialimprove-treatment-oral-anticoagulants-patients).

A. PATIENT-LEVEL INTERVENTIONS (EARLY INTERVENTION ARM)
• Letters to patients that (1) explain to the patient that he or she appears to have AF, characterize the risk of stroke, and emphasize that although there may be a medical reason, the patient does not seem to be on an anticoagulant and (2) encourage the patient to discuss this with his or her provider to ask if he or she might benefit from OAC therapy to prevent stroke. • Written education materials about AF and anticoagulants, including answers to commonly asked questions • Website with the patient-focused information contained in the letters to patients

B. PROVIDER-LEVEL INTERVENTIONS (EARLY INTERVENTION AND DELAYED INTERVENTION ARM)
• Letters to providers: o Early intervention letters to providers that explain this project, the nature of the problem, and identify a list of the provider's patients who have been contacted, as the provider and patient letters will be sent at approximately the same time; describe evidence and guidelines regarding oral anticoagulation o Delayed intervention letters to providers that explain this project, the nature of the problem, and identify a list of the provider's patients who are at risk for stroke and have not been treated with an oral anticoagulant; describe evidence and guidelines regarding oral anticoagulation • Response mailer that gives the provider the opportunity to share the rationale for his or her patient(s) not being on OAC

IX. METHOD OF ASSIGNING PATIENTS TO AN INTERVENTION
An electronic program, developed by the central coordinating center (Harvard Pilgrim), will be used by the participating Data Partners to identify their eligible member-patients who meet the inclusion and exclusion criteria for this trial. The patient billing claims records will not be linked to pharmacy data until after randomization, so the inclusion criterion of no OAC medication fill during the 12 months prior to randomization will not be applied until after randomization. This will be done immediately for the early intervention group, and in the delayed intervention group, not until 12 months after at least 80% of early intervention mailing have occurred. Patients will be randomly assigned in a 1:1 ratio, via the program, to early patient-level and provider-level intervention versus delayed provider-level intervention. A list of eligible member-patients will stay at each Data Partner, and identifiable patientlevel data will not be shared with the central coordinating center (Harvard Pilgrim) or the statistical analysis center (Duke Clinical Research Institute). The Data Partners will remove any individuals who cannot be included in research studies, which includes certain Centers for Medicare and Medicaid Services and Administrative Services Only patients. There are several other reasons that could prevent mailing of the intervention, to members and/or their providers (list may not be exhaustive): • Member is now deceased • Member disenrolls from health plan • Member transitions to a plan that does not allow for inclusion in research • Member has a recent anticoagulant dispensing • Member has an incorrect/missing/bad address • Member is added to a do-not-contact list at the health plan The list of randomized individuals will include the provider on each patient's most recent encounter with an AF diagnosis as of the last date in the current approved data used for cohort identification. When the identified provider is an individual, this provider will receive the provider intervention materials. When the identified provider is a facility, Data Partners will select an alternate provider or conduct a member only mailing based on their health plan policies and the decision of the health plan's leadership. An alternative provider may be a patient's PCP or other recent clinician who provided care. At least one health plan intends to mail letters to the member only when an individual provider is not identified with the most recent AF diagnosis given the large volume of members.
As with the member-patient list, the provider list will be kept by each Data Partner and not shared, as each Data Partner will be mailing the intervention materials to their respective patients and providers.

X. ETHICAL CONSIDERATIONS
This study will be conducted, where appropriate, in accordance with good research practice as outlined by Good Clinical Practice (GCP) and the International Conference on Harmonisation (ICH) and in accordance with the ethical principles underlying the United States Code of Federal Regulations, Title 21, Part 50 (21CFR50). The study will be conducted in compliance with the protocol. The protocol and any amendments will receive Institutional Review Board/Independent Ethics Committee (IRB/IEC) approval/favorable opinion before initiation of the study. Study personnel involved in conducting this study will be qualified by education, training, and experience to perform their respective tasks. This study will not use the services of study personnel where sanctions have been invoked or where there has been scientific misconduct or fraud (e.g., loss of medical licensure; debarment).
Insurance companies do not ordinarily identify their members with AF who might be appropriate candidates for OACs, and they perform no standard outreach to either clinicians or members regarding treatment of AF. Individuals who are identified for this trial will have had their health care providers bill under the diagnosis code of AF at least twice, with at least one billed diagnosis within the last 12 months. Thus, this trial involves no new identification of AF, since the method of ascertainment is through billing by providers based on their diagnosing AF. The current standard of care is for clinicians and their patients with AF to decide together whether anticoagulation for the diagnosed atrial fibrillation is appropriate. All Data Partners collaborating in the IMPACT-AFib trial are insurers (or affiliates of insurers), not care providers, and the clinicians are not employees of the Data Partners.
There is no current evidence that the communications by insurers (like those being assessed in this trial) will have any effect on use of anticoagulation. All eligible patients included in the trial who do not appear to fill an OAC prescription will receive an intervention, as they will either be in the early intervention or the delayed intervention cohort.

XI. INSTITUTIONAL REVIEW BOARD/INDEPENDENT ETHICS COMMITTEE
Before study initiation, the co-principal investigators must have written and dated approval/favorable opinion from the IRB/IEC for the protocol, and any other written information to be provided to prospective participants.
The investigators should provide the IRB/IEC with reports, updates, and other information (e.g., expedited safety reports, amendments, and administrative letters) according to regulatory requirements or institution procedures.

XII. INFORMED CONSENT
Consent will be waived. The reasons for the waiver include: 1. The contacting of the delayed intervention patients for consent would be an intervention by itself and might affect the results of the trial. 2. The intervention is entirely consistent with a quality improvement initiative that the health plans could initiate on their own. Thus, the intervention is very low risk for harm. 3. The intervention only adds on to the existing care of and programs for patients. There are no restrictions placed on the delayed intervention group, as a result of the trial. 4. It would be impractical to collect informed consent on the patients included in this trial.
The waiver of informed consent is consistent with the approach that has been taken in several similar clinical trials, the first using individual patient randomization, the others cluster randomized:

XIII. INDEPENDENT ADVISORY COMMITTEE
An independent advisory committee (IAC), consisting of members independent from the study team and with expertise in statistics, anticoagulation for atrial fibrillation, engagement, health plan management, and/or in practical clinical trials, will serve to enhance patient safety and trial integrity. The IAC will meet with study leadership at least twice. The first meeting will occur before intervention materials are mailed, and the second will take place two months after all mailings are sent. In addition, other meetings will occur if deemed necessary by the IAC chair, study leads and/or the FDA. The study team will provide the IAC with the study protocol before any intervention materials are mailed and will brief the IAC on any issues (or lack thereof) that have been raised 2 months after the last mailing has occurred. The IAC will advise on concerns that arise. An IAC charter describes the roles, responsibilities, and operations of the IAC.

A. SAMPLE SIZE AND POWER CALCULATIONS
Our target sample size is 80,000 patients. All enrolled patients and/or their providers will be targeted by mailing (early or delayed) provided they are eligible at time of mailing and able to be contacted.

Primary Endpoint
The following assumptions were used to determine the sample size and power for the primary endpoint assessing the proportion of AF patients with evidence of at least one OAC prescription fill through the date on which at least 80% of eligible study participants have at least 12 months of follow-up time: • 33% OAC initiation rate in the delayed intervention arm over the first year of the study o In a Sentinel feasibility assessment of identified health plan members meeting similar inclusion and exclusion criteria as this trial, 33% had evidence of OAC initiation in a 1 year period of follow-up. • 38% OAC initiation rate in the early intervention arm (a 5% absolute improvement in OAC initiation over the 33% OA initiation expected in thedelayed intervention arm over 1-year follow-up) • 1-year attrition rate: 30% dropout or lost-to-follow-up • Two-sided type I error of 0.05 • Roughly 10,000 patients (Table below) will yield more than 99% power to detect a 5% absolute difference 90%  5610  2805  2805  95%  6910  3455  3455  99% 9718 4859 4859

Important Secondary Analysis of Stroke or TIA
A study with approximately 80,000 patients is well powered for the outcome of stroke or TIA over the course of the follow-up through the date on which at least 80% of eligible study participants have at least 12 months of follow-up time, under certain assumptions listed below: • 1-year stroke or TIA rate: 18% among patients not treated with OAC • 1-year stroke or TIA rate: 7% among patients treated with at least 1 OAC fill • Duration of follow-up: 1 year • 33% of delayed intervention patients will have at least 1 fill of OAC, meaning the 1 year stroke or TIA rate in the delayed intervention group would be 14.4% • If 38% of early intervention patients have at least 1 fill of OAC (meaning the 1 year stroke or TIA rate in the early intervention group would be 13.82%, i.e., an absolute reduction of 0.55%), the study will have 46% power to detect this 0.55% reduction. However, if 40.5% of early intervention patients have at least 1 fill of OAC (meaning the 1 year stroke or TIA rate in the early intervention group would be 13.54%, i.e., an absolute reduction of 0.83%), the study will have 80% power to detect this 0.83% reduction.
• 1-year attrition rate: 30% dropout or lost-to-follow-up • Two-sided type I error of 0.05 • The sample size has 80% power to detect a 0.5% absolute reduction in stroke, assuming a cumulative 1-year incidence of stroke of 4.2% in control (delayed intervention arm) patients and 3.7% in intervention (early intervention arm) patients. The assumption is that patients not on oral anticoagulation have an annual stroke rate of 5%, and stroke will be reduced by 50% (HR=0.5) in the treated (anticoagulated) population. The 80% power requires that 52% of early intervention arm patients are treated at 1-year as compared to 33% in the control arm.

B. POPULATIONS FOR ANALYSIS
All analyses will be based on a modified intention-to-treat principle (i.e., all identified early intervention patients who meet eligibility and are mailed the intervention will be included; using "pseudo" wave assignments, all identified delayed intervention patients who meet eligibility at the time of corresponding early mailings will be included in the analysis). The primary endpoint will be calculated based on the proportion of patients with evidence of at least one OAC prescription fill over the course of the follow-up through the date on which at least 80% of eligible study participants have at least 12 months of follow-up time. An as-randomized analysis will be performed for the primary endpoint as a sensitivity analysis. All possible person-time will be used to assess participants' outcomes; patients will have different duration of follow-up and that will be accounted for in the analyses. Patients will be censored from the analysis at the time of death, disenrollment from the health plan, loss of medical or pharmacy coverage, or change in eligibility for inclusion in research based on health plan membership. The statistical analysis plan (SAP) provided more information and outlines in detail how granular aggregate data will be received from each Data Partner in lieu of patient-level data.

XV. OUTCOME DEFINITIONS
All outcome definitions will be based on available claims data. 3. OAC prescription coverage: the proportion of days that AF patients have OAC prescription fills over the duration of the study. The assumption is that a 30-day or 90-day supply will last for the planned period, even in the case of warfarin, when the length of time that a prescription lasts may be less well defined. Patients will only be included in this secondary analysis, if they had a prescription fill for apixaban, dabigatran, edoxaban, rivaroxaban, or warfarin. 4. OAC rates at follow-up: proportion of patients with an active oral anticoagulant dispensing at the end of the one-year follow-up. This will include patients with apixaban, dabigatran, edoxaban, rivaroxaban, or warfarin medication fills that encompass the end of the study period.
If there was no prescription fill for these medications, this will also include patients with 4 or

A. DEMOGRAPHICS AND BASELINE CHARACTERISTICS
Baseline characteristics of eligible early and delayed intervention cohorts will be based on the claims data at the time of randomization. Frequency distribution and summary statistics for demographic and baseline variables will be presented by early intervention group, delayed intervention group, and for the overall study population. Key demographic and baseline variables to be summarized include: geographic region, age, sex, risk factors for stroke, risk factors for bleeding, and select comorbid conditions. Continuous variables will be summarized as mean (±SD) and median (25 th , 75 th percentiles); the comparison between the two groups will be conducted using Wilcoxon rank-sum test. For the continuous variables in combined study population, the mean will be summarized. Categorical variables will be presented as counts (percentages) and will be compared between groups by using Pearson's chisquare or Fisher's exact test, as appropriate.

B. RESPONSES FROM PROVIDERS
As part of the provider intervention materials, providers will have the opportunity to respond to the patient's health plan and give an explanation for why their patients were not being treated with OAC via a postage paid postcard. The data collected from these responses will be aggregated by rationale for non-treatment and reported as counts (percentages) by the coordinating center. Data will not be linked to specific patients or providers.

C. EFFECTIVENESS ANALYSES
The proportion of patients with evidence of at least one OAC medication fill over the course of the follow-up, the primary endpoint, will be summarized and compared between the early intervention and delayed intervention arms. The definition for OAC medication fill will be an OAC medication billing in the pharmacy claims or at least 4 INR tests billed in the laboratory claims (indicative of OAC use that was not billed through the pharmacy claims data). To evaluate whether the comprehensive evaluation and customized multilevel (patient-level and provider-level) educational interventions increases the rate of use of oral anticoagulants at one year post intervention, we will evaluate the odds ratio (i.e. the odds of an average patient in the early intervention group taking OAC at 1 year compared to the odds of an average patient in the delayed intervention group taking OAC at 1 year) using logistic regression to account for the effect of Data Ppartner and adjust for other potential baseline risk factors. 38 We will present the odds ratio, 95% confidence interval, and p-value to show whether there is a difference in rate of use of OAC at one year post intervention between the early intervention and delayed intervention groups. Similarly, we will analyze the proportion of days covered with an OAC prescription fill over the course of the follow-up. Patients will only be included in this analysis, if they had a prescription fill for apixaban, dabigatran, edoxaban, rivaroxaban, or warfarin.
Event rates for the following secondary outcomes will be summarized by treatment group, as defined by claims data: • Stroke or TIA • Ischemic stroke or unknown stroke • Hemorrhagic stroke • Hospitalization for any bleeding • Composite of ischemic or hemorrhagic stroke • Composite of ischemic stroke, hemorrhagic stroke, and hospitalization for any bleeding For time-to-event outcomes, Kaplan-Meier cumulative incidence estimates and log-rank test will be utilized. 39 In addition, Cox proportional hazards model with early intervention vs. delayed intervention as main effect will be used to assess the clinical outcomes, after adjusting for baseline risk factors. 40 A robust sandwich covariance estimate or a frailty model will be used to account for effect of Data Partner. The hazard ratio, 95% confidence interval and p-value will be presented to summarize the difference in the risk of clinical outcome between early intervention and delayed intervention group. Inhospital death or medically attended death will be collected through claims data. Analyses will be performed using SAS software version 9.4 or higher (SAS Institute, Inc., Cary, NC).
More details on the statistical methods and analyses will be provided in the SAP. The SAP will be finalized prior to study database lock, 12 months after at least 80% of the early intervention mailings. Of note, all patient-level data will be maintained by the Data Partners, so analyses are expected to be conducted via a distributed SAS programming code developed by the coordinating center and results are expected to be returned, by Data Partner, in aggregate to the coordinating center. Analyses will be examined by Data Partner and across Data Partners.

XVII. DISSEMINATION PLAN OVERVIEW
A manuscript describing the study design will be published. A manuscript will also be written describing the results on the primary and secondary endpoints based on the date on which at least 80% of eligible study participants have at least 12 months of follow-up time, and separately once at least 80% of members have at least 24 months of follow-up time (if 24-month aanalysis is conducted). Finally, Data Partner-specific results will be shared with each Data Partner at both time points.
centers and countries as measured by time in therapeutic range.

I. OVERVIEW
This is the statistical analysis plan (SAP) for IMplementation of a randomized controlled trial to imProve treatment with oral AntiCoagulanTs in patients with Atrial Fibrillation (IMPACT-AFib) study. The purpose of this document is to provide an overview of the study design and study objectives, outline the types of analyses and data presentations relevant to the study objectives, and to provide a detailed description of the methods in which the statistical analyses will be conducted to meet protocol objectives. This plan is a supplement to the materials provided in the IMPACT-AFib protocol. This SAP does not contain all the protocol details and is intended to be read in conjunction with the full protocol. Only analytic decisions are documented here.

A. PRIMARY ENDPOINT
IMPACT-AFib is a prospective randomized controlled clinical trial that will evaluate whether a patient and provider education intervention increases the proportion of patients with atrial fibrillation (AF) who fill at least one oral anticoagulant (OAC) over the course of follow-up. Follow up is through the date on which at least 80% of eligible study participants have at least 12 months of follow-up time. As described in the protocol, there is an "early intervention" arm (who receive patient and provider mailings) and a "delayed intervention" arm (who receive provider mailings only, ~12 months after the early intervention mailings occur).

B. SECONDARY ENDPOINTS
We will evaluate the impact of the patient and provider education intervention on the endpoints listed below at the end of follow-up (i.e., the date on which at least 80% of eligible study participants have at least 12 months of follow-up time): The incidence rate of stroke or transient ischemic attack (TIA) hospitalizations The incidence rate of stroke hospitalizations The time to first OAC prescription fill The proportion of days covered by OAC prescription fills Proportion of patients actively on OAC at 12 months of follow-up The incidence rate of hospitalization for any bleeding All-cause in-hospital mortality rates All-cause mortality rates among patients with accurate out-of-hospital mortality data, if data are available (such as Medicare Advantage patients) Health care utilization, reported as counts of number of health care utilization events (outpatient visits, days hospitalized, number of emergency department visits, etc.) Depending on the review of preliminary data, the primary endpoint and some secondary endpoints may be examined separately by warfarin and novel OAC. This will be descriptive only and will not include formal statistical testing.

C. EXPLORATORY ENDPOINTS
We will evaluate the effect of the early and delayed education interventions on the primary and secondary endpoints once at least 80% of eligible study participants have at least 24 months of followup time (the early intervention includes mailing to the patient and provider while the delayed intervention, at ~12 months follow-up, only includes a provider mailing). Note that we may not conduct these analyses if the results of the primary outcome are null in the earlier assessment. Therefore, this statistical analysis plan does not include the details of analyses for a 24 months assessment.

D. DATA SOURCE
The data used for the study are claims data from the five participating sites, transformed into the Sentinel Common Data Model. At the time of analysis, the data available in the Sentinel Distributed Database (i.e., those approved and in use for Sentinel routine surveillance activities) will be used to assess the primary and secondary endpoints.
As background, the identification and creation of the study cohort was based on the claims data in the Sentinel Distributed Database plus linked "fresh" data (i.e., about 1 month old) for pharmacy claims and enrollment information. The target population for the study was those members enrolled in the sites who did not have evidence of an OAC medication dispensing in the 12 months prior to randomization; the fresh and production data ensured we identified those eligible for the trial. The data used for routine Sentinel activities are several months old -hence the need for certain "fresh" data -and the date of the last available claims varies by site.

E. PATIENT INCLUSION CRITERIA
All inclusion and exclusion criteria were determined by claims data. For entry into the study, the following criteria MUST be met at the date of randomization: 1. Two or more diagnoses of AF (ICD-10-CM codes I48.0, 148.1, 148.2, 148.4, or I48.91; ICD-9-CM codes 427.3 or 427.31) at least one day apart and with at least one diagnosis within the last 12 months prior to the last date in the current approved data used for cohort identification 2. CHA 2 DS 2 -VASc score of 2 or greater at the time of the randomization (i.e., as of the last date in the current approved data used for cohort identification). The ICD-9/10-CM coding for CHA 2 DS 2 -VASc is shown in Table 1. The complete code list for inclusion and exclusion criteria is accessible on the Sentinel website (https://www.sentinelinitiative.org/FDAcatalyst/projects/implementation-randomized-controlled-trial-improve-treatment-oralanticoagulants-patients). 3. Medical and pharmacy insurance coverage as identified via administrative claims data as of the date of randomization 4. Age 30 years or greater as of the last date in the current approved data used for cohort identification   Patients are excluded if they meet any of the following criteria: 1. Evidence of OAC medication fill during the 12 months prior to randomization (the delayed intervention group's treatment status will be assessed at the end of the 12 month follow-up period) 2. Conditions other than AF that require anticoagulation such as ever having mechanical prosthetic valve, deep venous thrombosis, or pulmonary embolism prior to the last date in the current approved data used for cohort identification ("ever" is operationalized as -6000 days from the index AF code) 3. Pregnancy identified within 6 months of the last date in the current approved data used for cohort identification 4. Any known history of intracranial hemorrhage prior to the last date in the current approved data used for cohort identification 5. Hospitalization for any bleeding within the last 6 months of the last date in the current approved data used for cohort identification 6. Patients with recent P2Y12 antagonist use (i.e., clopidogrel, prasugrel, or ticagrelor within 90 days of prior to randomization)

F. STUDY DESIGN AND DURATION
As described in detail in the protocol, the study is a prospective, randomized, and open-label educational intervention trial. Patients with AF and a CHA 2 DS 2 -VASc score of 2 or greater were randomized in a 1:1 ratio to an early intervention cohort and a delayed intervention cohort within each participating health plan. The definition for OAC medication fill was an OAC medication dispensing or at least 4 INR tests in the claims data. 2 The claims records of the patients randomized to the early intervention cohort were then linked to "fresh" (i.e., about 1 month old) pharmacy claims data at the time of randomization. Patients without evidence of an OAC medication fill during the 12 months prior to randomization were included in the patient-level and provider-level early educational intervention (patients randomized to this early intervention with evidence of an OAC medication fill during the 12 months prior to randomization were excluded from the trial). In addition to usual care, these patients and their providers received a one-time mailing at trial start. There were two waves of mailing for the early intervention cohort at most sites due to the practical challenges of claims data: the patients were assigned to wave 1 if they had a provider easily identified in the data (i.e., the provider associated with the most recent AF diagnosis is indeed an individual provider), and they were assigned to wave 2 if it was difficult to identify a provider (e.g., the first identified provider is actually a facility). Follow-up time started on the date of the respective wave 1 and wave 2 mailings for the early intervention patients.
The delayed intervention cohort will have received usual care over the initial study period. After the date on which at least 80% of all eligible study participants have at least 12 months of follow-up time, the treatment status of the delayed intervention group will be assessed via the Sentinel data available at that time, in addition to "fresh" pharmacy claims data. The providers of patients in the delayed cohort who did not receive OAC medication during the course of follow-up and still meet all inclusion criteria will receive the provider-only education intervention (patients will not receive the educational materials unless no provider can be identified for a mailing).
Details on the analyses are provided in Section II. Here we describe the data sources for the modified intention-to-treat (primary) and as-randomized (sensitivity) analyses. Similar to early intervention cohort, the patients in the delayed intervention cohort will be assigned to wave 1 or wave 2 ("pseudo" wave assignments) depending on the difficulty in identifying the patient's provider (the intent is to handle them the same way as was done for the early intervention arm, for the modified intention-totreat analysis). The follow-up for the delayed intervention patients will start on the date the wave 1 or 2 mailings took place for a given Data Partner's early intervention cohort. For both early and delayed intervention cohorts, any patients who die, are disenrolled, or get started on OAC between the randomization and early intervention mailing will be excluded from the analysis at each Data Partner. For both the early and delayed arms, exclusion criteria that are based on member medical history were assessed at the time of randomization. For the early intervention cohort, enrollment and treatment status were assessed at randomization for all and re-assessed at the wave 2 time point at some of the sites (this was at site discretion, in response to the lag between wave 1 and 2 mailings). The enrollment and treatment status of the delayed intervention cohort will be examined for eligibility at the same time point as the early intervention patients, meaning at the time of mailing per Data Partner, via the locked data (using the wave 1 and 2 dates).
Because the Sentinel Distributed Database will be used for analyses, and this information is refreshed approximately quarterly on different timetables for the different health plans, it is likely that when the required follow-up time is available for at least 80% of patients, there will be more than 12 months of follow-up for over 80% of patients. All participants' outcomes will be assessed using all possible persontime; patients will have different duration of follow-up and that will be accounted for in the analyses. Note that if the 24 month analysis is conducted, we will do that when at least 80% of members have at least 24 months of follow-up time.
A schematic diagram below shows the design of the early intervention period of the study: over the course of the follow-up, through the date on which at least 80% of eligible study participants have at least 12 months of follow-up time (see the protocol for the full study design and details):

Figure 1. Design of the early intervention period portion of the study IMPACT-AFib
A schematic diagram below shows the design of the delayed intervention portion of the study:

Primary Endpoint
The following assumptions were used to determine the sample size and power for the primary endpoint assessing the proportion of AF patients with evidence of at least one OAC prescription fill through the date on which at least 80% of eligible study participants have at least 12 months of follow-up time: 1. 33% OAC initiation rate in the delayed intervention arm 2. 38% OAC initiation rate in the early intervention arm (5% absolute improvement in OAC initiation over the 33% OAC initiation expected in the delayed intervention arm over 1-year follow-up) 3. 1-year attrition rate: 30% dropout or lost-to-follow-up 4. Two-sided type I error rate of 0.05 5. Roughly 10,000 patients who meet the inclusion/exclusion criteria will yield more than 99% power to detect a 5% absolute difference

Important Secondary Outcome of Stroke or TIA
A study with approximately 80,000 patients could provide reasonable power for stroke or TIA outcome under certain assumptions listed below: 1. 1-year stroke or TIA rate: 18% among patients not treated with OAC 2. 1-year stroke or TIA rate: 7% among patients treated with at least 1 OAC fill 3. Duration of follow-up: 1 year 4. 33% of delayed intervention patients will have at least 1 fill of OAC, meaning the 1 year stroke or TIA rate in the delayed intervention group would be 14.4% 5. 1-year attrition rate: 30% dropout or lost-to-follow-up 6. Two-sided type I error of 0.05 7. If 38% of early intervention patients have at least 1 fill of OAC (meaning the 1 year stroke or TIA rate in the early intervention group would be 13.82%, i.e., an absolute reduction of 0.55%), the study will have 46% power to detect this 0.55% reduction. However, if 40.5% of early intervention patients have at least 1 fill of OAC (meaning the 1 year stroke or TIA rate in the early intervention group would be 13.54%, i.e., an absolute reduction of 0.83%), the study will have 80% power to detect this 0.83% reduction. 8. The sample size has 80% power to detect a 0.5% absolute reduction in stroke, assuming a cumulative 1-year incidence of stroke of 4.2% in control (delayed intervention arm) patients and 3.7% in intervention (early intervention arm) patients. The assumption is that patients not on oral anticoagulation have an annual stroke rate of 5%, and stroke will be reduced by 50% (HR=0.5) in the treated (anticoagulated) population. The 80% power requires that 52% of early intervention arm patients are treated at 1-year as compared to 33% in the control arm.

II. STATISTICAL ANALYSIS
All primary analyses will be based on modified intention-to-treat (mITT) principle (i.e., all identified early intervention patients who met eligibility and were mailed the intervention will be included; using "pseudo" wave assignments, all identified delayed intervention patients who met eligibility at the time of corresponding early mailings will be included). Since the additional exclusions after randomization will be applied in the same way, using the same time points for both the early and delayed intervention groups, we expect there will be no effect from these additional exclusions on the randomization. The mITT analysis will include the following: Early intervention members who were mailed a letter, with follow-up beginning on the date of mailing (up to two dates per site and the dates varied by site).
Delayed intervention members who were not on treatment at the date of mailing (wave assignments were made for the delayed as described earlier in section I.F) with follow-up beginning on that date.
An as-randomized analysis will be performed for the primary endpoint as a sensitivity analysis. Randomization occurred prior to treatment status assessment per the study design. Therefore, the asrandomized analysis will include people who were on treatment as well as others who were not truly eligible for the study (i.e., people who disenrolled, were transitioned to a plan that does not permit their inclusion, had incomplete or invalid addresses, died, or had a "do not contact" status).
Potential sensitivity analysis for mITT analysis: There may be differential loss to follow up between the early and delayed intervention groups because some members did not have valid mailing addresses, though we did not assess the addresses of the members in the delayed intervention arm at the time of early intervention mailings. It is not possible to retrospectively ascertain the address status of the delayed intervention group as of the date on which mailing would have occurred for that group. We can estimate the magnitude by referring to the early intervention group, and in the early intervention group, we can compare the baseline characteristics and experience of the individuals who had no valid address to those who do.
All possible person-time will be used to assess participants' outcomes. For the time-to-event analysis, patients will be censored from the analysis at the time of death, disenrollment from the health plan, loss of medical or pharmacy coverage, or change in eligibility for inclusion in research based on health plan membership.
Providers may have more than 1 patient in the study -either within the same arm or in both the early and delayed intervention arms. The frequency of this, when provider overlap can be identified, will be reported descriptively and it is expected to be a low proportion of whole population. Depending on the number of patients in this scenario, a sensitivity analysis may be considered to examine the effect.
There were a few variations in the implementation of the early intervention across the Data Partners due to pragmatic issues. The intervention per the protocol is targeted at both member and provider (i.e., the provider who gave most recent AF diagnosis). If the AF provider was a facility in the source data, the educational intervention was applied to the member only, unless the site chose an alternate provider. In the latter case, the intervention was sent to both the member and the alternate provider. The number of patients in each of these variations to the intended intervention will be reported.
A detailed Consort flow diagram will be provided showing the number of patients randomized to the early and delayed intervention groups, the numbers of subjects lost to follow up or excluded from analyses, and the number of subjects evaluable for the key study endpoints (Figure 1). 1 All analyses will be conducted using SAS version 9.4 or higher software (SAS Institute Inc., Cary, NC). However, version and modules to be used could vary from one Data Partner to another. All tests will be two-sided and a p-value of <0.05 will be considered statistically significant. No multiplicity adjustment will be made.

A. METHODS FOR ANALYSIS IN DISTRIBUTED DATA NETWORKS
Patient-level data will be maintained by the Data Partners for all or most analyses. Therefore, analyses specified in this document will be conducted via a distributed SAS programming code developed by the Duke statistical team in collaboration with the study coordinating center at HPHCI as specified in the study table and figure shells. These SAS programs will be shared with HPHCI trial coordinating center for validation, beta testing, and software version compatibility as specified by each Data Partner. Results are expected to be returned by Data Partner to HPHCI and shared with the data coordinating center (DCC) at Duke to conduct an overall statistical analysis across all Data Partners' results. The Duke DCC will have a data use agreement with each Data Partner as necessary in order to receive/access aggregate summary data, which are housed at HPHCI. No Data Partner-specific tables will be shared beyond the coordinating center and Duke DCC, if agreed upon by Data Partners, the analytic team; only data aggregated across sites will be published or made public.
There are several analytic approaches that can be used to perform analysis in a distributed database without requiring patient-level information. 2 3 4 5 6 7 8 Each of these methods requires different types of summary-level information from the participating sites but they generally provide comparable results. We describe these approaches in Appendix D: 1) meta-analysis, 2) case-centered logistic regression, 3) distributed regression. The analysis of primary and secondary outcomes in this study will require using both logistic regression and time-to-event approach. The heterogeneity across Data Partners will need to be assessed. A fixed-effects meta-analysis approach will be the primary statistical method for integrating the findings from each Data Partner. Because case-centered logistic regression and distributed regression methods require a more granular level of data as compared to meta-analysis approach, these methods could be explored as sensitivity analyses depending on the level of data provided by the five Data Partners.
Hereafter, the statistical analysis details will be described based on patient-level data with the understanding that each Data Partner will run these analyses separately and return the results to the HPHCI coordinating center for further analyses.

B. DEMOGRAPHICS AND BASELINE CHARACTERISTICS
Baseline characteristics of the early intervention and delayed intervention cohorts will be based on the claims data at the time of randomization (among those eligible for inclusion in the analysis). Frequency distribution and summary statistics for demographic and baseline variables will be presented by early intervention group, delayed intervention group, and for the overall study population ( Table 1 in Appendix A). Key demographic and baseline variables to be summarized include: geographic region, age, sex, risk factors for stroke, risk factors for bleeding, and selected comorbid conditions. Depending on the data availability and effort required by Data Partners, a sensitivity analysis may be conducted to examine the number of patients associated with different provider types (examination of outcomes by provider type may also be considered). Categorical variables will be presented as counts (percentages) and will be compared between groups by using Pearson's chi-square or Fisher's exact test if the count in any cell is less than 5. Continuous variables will be summarized as mean (±SD) and median (25 th , 75 th percentiles); the comparison between the two groups will be conducted using Wilcoxon rank-sum test for the data within each Data Partner. For the continuous variables in combined study population, only the mean will be summarized. Each Data Partner will run the SAS program(s) distributed by HPHCI, developed with the statistical team at Duke, to generate a summary table for their cohort of patients shown in Tables 1a -1e in Appendix A (one for each Data Partner) and return the summary table to HPHCI. The same summary table will be generated for entire study population by HPHCI, as shown in Table 1 in Appendix A.
As part of the provider intervention materials, providers had the opportunity to respond and provide an explanation for why their patients were not being treated with OAC. The data collected from these responses will be aggregated by rationale for non-treatment and reported as counts (percentages) by the coordinating center.

C. PRIMARY ENDPOINT DATA ANALYSES
The proportion of patients with evidence of at least one OAC medication fill over the course of the follow-up (through the date on which at least 80% of eligible study participants have at least 12 months of follow-up time) is the primary endpoint. The definition for OAC medication fill will be an OAC medication billing in the outpatient pharmacy claims or at least 4 INR tests or results in the laboratory claims (indicative of OAC use that was not billed through the pharmacy claims data). The primary endpoint will be summarized and compared between the early intervention and delayed intervention arms. Both unadjusted and adjusted (based on available baseline risk factors) analyses will be conducted for the difference in the primary endpoint between the early intervention and delayed intervention arms using the data shown in Table 3. The adjusted analysis will be considered the primary analysis.

Adjusted Analysis Model
The logistic regression model will be used for analyzing primary endpoint. Let binary indicator variable T denotes randomized treatment groups, i.e. T=1 indicates early intervention; T=0 indicates delayed intervention. Let denotes the probability that a patient filling at least at least one OAC medication over the course of the 12-months post intervention. The primary analysis model has the form where is the intercept parameter, is the vector of baseline covariates to be adjusted in the model, listed in Appendix A Table 2. The same set of covariates will be used in the analysis performed by each data partner on their cohort of patients. is the vector of slope parameters. is the odds of a patient filling at least one OAC medication prescription over the course of the follow-up through the date on which at least 80% of eligible study participants have at least 12 months of followup time. This model assumes observations are correlated within each Data Partner "cluster" but not across Data Partners, a "working" correlation structure will be used via generalized estimating equation (GEE). 10

Analysis Results Interpretation
The estimate of β 0 in the model in section C.1 is the logarithm of odds ratio of treatment groups (i.e., the odds of an average patient in the early intervention group filling at least one OAC medication prescription as compared to the odds of an average patient in the delayed intervention group filling at least one OAC prescription over the course of the follow-up through the date on which at least 80% of eligible study participants have at least 12 months of follow-up time). To evaluate whether the early patient-level and provider-level educational interventions increases the proportion of patients with evidence of at least one OAC medication fill over the course of the 12-months post intervention, we will calculate the odds ratio using logistic regression model adjusted for baseline risk factors listed in Appendix A Table 2, with GEE to account for the correlation of responses among the patients from a same service provider. The odds ratio, 95% confidence interval (CI), and p-value will be presented to show whether there is a statistically significant difference in the proportion of patients who fill at least one OAC prescription over the course of the follow-up through the date on which at least 80% of eligible study participants have at least 12 months of follow-up time between the early intervention and delayed intervention groups. Each Data Partner will run the SAS program(s) distributed by HPHCI, developed with the statistical team at Duke DCC, to perform logistic regression on their cohort of patients and return the parameter estimate (standard error [SE]), estimated of odds ratio, 95% CI, and p-value, shown in Table 3a -3e in Appendix A (one for each Data Partner), to HPHCI. Meta-analysis methods with inverse-variance weighting on log scale will be used to integrate the results and obtain the estimate of the overall odds ratio, 95% CI and p-value for entire study population, as shown in Table 3 in Appendix A.
There are patients for whom a provider was not identified, and therefore the provider letters were not mailed out. The primary endpoint will be summarized and compared between the patients with provider letter and the patients without provider letter. Each Data Partner will return the descriptive data, shown in Table 4a -4e in Appendix A to HPHCI. Similar summary table will be generated for entire intervention arm by HPHCI, as shown in Table 4 in Appendix A. To evaluate whether the intervention effect is different between the patients with provider letter and the patients without provider letter, an interaction term between treatment and provider status (an indicator variable of Yes/No for the provider letter received) will be tested in the above multivariable model. Each Data Partner will return the p-value of interaction term to HPHCI. Fisher's method as described below will be used to combine the p-values of test for the interaction term from each Data Partner and generate the p-value for the interaction term for entire cohort.
Where is the p-value from ith Data Partner.

OAC Initiation
The time to first OAC initiation, is defined by the first fill date for apixaban, dabigatran, edoxaban, rivaroxaban, or warfarin. If there was no prescription fill for these medications, but the patient had 4 or more INR tests or results documented over the study period, the date of the first INR measurement would be used for initiation of OAC. A Cox proportional hazards 11 model with early intervention vs. delayed intervention as the main effect will be used to model the time to first OAC initiation, after adjusting for baseline risk factors listed in Appendix A Table 2. A robust sandwich covariance estimate or a frailty model will be used to account for the correlation of responses among the patients from a same service provider. The hazard ratio, 95% CI and p-value will be summarized for apixaban, dabigatran, edoxaban, rivaroxaban, or warfarin. Each Data Partner will run the SAS program(s) distributed by HPHCI, developed with the statistical team at Duke DCC, to perform Cox regression model 11 on their cohort of patients and return the estimated hazard ratio, 95% CI and p-value, shown in Table 5a -5e in Appendix A (one for each Data Partner), to HPHCI. Meta-analysis methods with inverse-variance weighting on log scale will be used to integrate the results and obtain the overall estimate of the hazard ratio, 95% CI and p-value for the entire study population, as shown in Table 5 in Appendix A.

OAC Adherence
OAC adherence will be assessed by the proportion of days covered by OAC prescription fills over the duration of the study, or the proportion of days covered. The assumption is that a 30-day or 90-day supply will last for the planned period, even in the case of warfarin, when the length of time that a prescription lasts may be less well defined. Overlapped prescription days will be counted only once, and the days prescribed beyond censor date will be censored accordingly in calculating the total days covered by OAC. Patients will only be included in this secondary analysis if they had a prescription fill for apixaban, dabigatran, edoxaban, rivaroxaban, or warfarin. Proportion of days covered will be summarized as mean (±SD), and median (25 th , 75 th percentiles) by early vs. delayed intervention, the comparison between the two groups will be conducted using Wilcoxon rank-sum test, as shown in Table  6 in Appendix A. Each Data Partner will run the SAS program(s) distributed by HPHCI, developed with the statistical team at Duke, to generate a summary table for their cohort of patients shown in Tables 6a -6e in Appendix A (one for each Data Partner) and return the summary table to HPHCI. For entire study population, the mean of two groups will be generated using meta-analysis methods. Fisher's method as described in Section C will be used to combine the p-values of Wilcoxon rank-sum test from each Data Partner and generate the p-value for entire cohort.

Proportion of Patients Actively on OAC at the End of Follow-up
The proportion of patients actively on OAC at the end of follow-up will be summarized and compared between the early intervention and delayed intervention arms. Last Observation Carry Forward will be used if the patient is censored. To evaluate whether the early patient-level and provider-level educational intervention increases the proportion of patients being actively on OAC at the end of followup, we will calculate the odds ratio (i.e., the odds of an average patient in the early intervention group being actively on OAC at the end of follow-up as compared to the odds of an average patient in the delayed intervention group being actively on OAC at the end of follow-up) using logistic regression model adjusted for baseline risk factors listed in Appendix A Table 2, with GEE to account for the correlation of responses among the patients from a same service provider. The odds ratio, 95% confidence interval (CI) and p-value will be presented to show whether there is a statistically significant difference in the proportion of patients who are actively on OAC at the end of follow-up between the early intervention and delayed intervention groups. Each Data Partner will run the SAS program(s) distributed by HPHCI, developed with the statistical team at Duke DCC, to perform logistic regression analysis on their cohort of patients and return the parameter estimate (SE), estimated odds ratio, 95% confidence interval (CI) and p-value, shown in Table 7a -7e in Appendix A (one for each Data Partner), to HPHCI. Meta-analysis methods with inverse-variance weighting on log scale will be used to integrate the results and obtain the estimate of the overall odds ratio, 95% confidence interval and p-value for entire study population, as shown in Table 7 in Appendix A.

Clinical Outcomes
Claims data (ICD-10-CM codes used for defining these outcomes are listed in Appendix C) will be used to define the following clinical outcomes: Hospitalization for ischemic stroke or unknown stroke Hospitalization for hemorrhagic stroke Hospitalization for any bleeding Composite of ischemic or hemorrhagic stroke Composite of ischemic stroke, hemorrhagic stroke, and hospitalization for any bleeding All-cause in-hospital death For each of these outcomes, time-to-event methodology will be implemented. Kaplan-Meier estimator 12 will be used to estimate the probability of occurrence at 12 months of follow-up and the log-rank test 13 will be used to compare the survival curves. The Cox proportional hazards model with early intervention vs. delayed intervention as main effect will be used to model the time to event, after adjusting for baseline risk factors listed in Appendix A Table 2. The hazard ratio, 95% CI and p-value will be presented to summarize the difference in the risk of clinical outcome between early intervention and delayed intervention groups. In-hospital death or medically attended death will be collected through claims data.
Depending on number of patients and events, the comparison of the stroke rate between early and delayed intervention may be examined separately in patients who have 1 OAC fill and multiple OAC fills. This will be descriptive only and will not include formal statistical testing.
Each Data Partner will run SAS program(s) distributed by HPHCI, developed with the statistical team at Duke DCC, to perform analysis on their cohort of patients and return the results to HPHCI. For the comparison of probability of occurrence, each Data Partner will return the estimate of probability of occurrence, standard error, 95% CI by early intervention vs. delayed intervention, and p-value, as shown in Table 8a -8e in Appendix A (one for each Data Partner). For the comparison of risk, each Data Partner will return the parameter estimate (SE), hazard ratio, 95% CI and p-value, as shown in in Appendix A Table 9a -9e (one for each Data Partner). The statistical team will use meta-analysis methods to integrate the results and obtain the results for entire study population, as shown in Tables 8 and 9 in Appendix A.

Health Care Utilization
The total counts of health care utilization (number of outpatient visits, emergency department visits, hospital admissions, and days hospitalized) at the end of follow-up time, including AF and non-AF related care, will be summarized by early intervention and delayed intervention group, as shown in Table 10 in Appendix A.

A. TABLES
For all tables below, the study coordinating center at HPHCI will receive Data Partner-specific tables. The coordinating center will generate aggregated tables across Data Partners (shown below), using metaanalysis methods where appropriate (for continuous variables in aggregated tables, only mean will be generated); these will be shared with the Duke DCC statistical team. Duke DCC will have a data-use agreement with each Data Partner as necessary in order to receive/access aggregate summary data, which are housed at HPHCI. No Data Partner-specific tables will be shared beyond the coordinating center and Duke DCC, if agreed upon by Data Partners, the analytic team; only data aggregated across sites will be published or made public. Scientific background and explanation of rationale 2b Specific objectives or hypotheses

Methods
Trial design 3a Description of trial design (such as parallel, factorial) including allocation ratio 3b Important changes to methods after trial commencement (such as eligibility criteria), with reasons Participants 4a Eligibility criteria for participants 4b Settings and locations where the data were collected Interventions 5 The interventions for each group with sufficient details to allow replication, including how and when they were actually administered Outcomes 6a Completely defined pre-specified primary and secondary outcome measures, including how and when they were assessed 6b Any changes to trial outcomes after the trial commenced, with reasons Sample size 7a How sample size was determined 7b When applicable, explanation of any interim analyses and stopping guidelines Randomisation: Sequence generation 8a Method used to generate the random allocation sequence 8b Type of randomization; details of any restriction (such as blocking and block size) Allocation concealment mechanism 9 Mechanism used to implement the random allocation sequence (such as sequentially numbered containers), describing any steps taken to conceal the sequence until interventions were assigned Implementation 10 Who generated the random allocation sequence, who enrolled participants, and who assigned participants to interventions Blinding 11a If done, who was blinded after assignment to interventions (for example, participants, care providers, those assessing outcomes) and how 11b If relevant, description of the similarity of interventions For each group, the numbers of participants who were randomly assigned, received intended treatment, and were analyzed for the primary outcome 13b For each group, losses and exclusions after randomization, together with reasons Recruitment 14a Dates defining the periods of recruitment and follow-up 14b Why the trial ended or was stopped Baseline data 15 A table showing baseline demographic and clinical  characteristics for each group  Numbers analysed  16 For each group, number of participants (denominator) included in each analysis and whether the analysis was by original assigned groups Outcomes and estimation 17a For each primary and secondary outcome, results for each group, and the estimated effect size and its precision (such as 95% confidence interval) 17b For binary outcomes, presentation of both absolute and relative effect sizes is recommended Ancillary analyses 18 Results of any other analyses performed, including subgroup analyses and adjusted analyses, distinguishing pre-specified from exploratory

Meta-analysis
In meta-analysis, each Data Partner estimates the effect and their variance (or other information needed to calculate the weight) using pre-specified models on their own individual-level data and send these to the coordinating center. Then, the overall estimated effect and 95% confidence interval is derived by pooling site-specific estimates. A commonly used weight is inverse of variance on the log scale of the estimate. Meta-analysis method requires the least amount of data sharing and is flexible with respect the types of study design and analysis. However, it is the least flexible with respect to the subgroup and sensitivity analyses and requires greatest degree of programing/analysis ability at each participating site.

Case-centered Logistic Regression
In this method, each Data Partner transfers an aggregated dataset to the coordinating center that includes 1 record per risk set. Each risk set is anchored by a case (patient with the outcome of interest) and comprised of the cases and comparable individuals at risk of the outcome at the time the case occurs. Each record includes a binary variable indicating whether the patient diagnosed with the outcome is exposed to the treatment and the log odds of the site-specific proportion of exposed patients in the risk set. Confounding adjustment will be conducted through stratification. Specifically, if the number of imbalanced covariates is small, we will create strata that are defined by these covariates within each site; the risk set for a given case will be at-risk individuals who are within the same covariate stratum as the case. If the number of imbalanced covariates is large, we will create propensity score (PS) strata. The PS will be estimated within each site, and the risk set for a given case will be at -risk individuals who are within the same propensity score stratum as the case. The statistical team fits a logistic regression model with indicator variable as the dependent variable and log odds as the independent variable. It is shown that this method maximized the same likelihood as a stratified Cox model using patient-level data. Thus, it is appropriate for study designs that needs to be analyzed using Cox proportional hazards model.

Distributed Regression
Distributed regression is a suite of methods that enable researchers to conduct multi-database multivariable-adjusted regression analysis without the need to centrally combine all individual-level data from participating sites. It performs the same numeric algorithm as standard ordinary least squares regression but uses only summary statistics for computation. By following the same computation process, distributed regression and pooled individual-level data analysis produce statistically equivalent results. With distributed regression, we can adjust for imbalanced covariates directly in the outcome regression models.