Objectives
This is a protocol for a Cochrane review (intervention). The objectives are as follows:
To assess the benefits and harms of oral anticoagulant monotherapy compared with oral anticoagulant plus antiplatelet therapy in adults with stable coronary artery disease requiring long‐term anticoagulation.
Background
Description of the condition
Stable coronary artery disease (CAD) is a chronic manifestation of atherosclerotic cardiovascular disease characterised by a history of myocardial infarction, prior coronary revascularisation, or angiographically documented coronary stenosis in the absence of acute coronary syndrome [1]. Ischaemic heart disease affects an estimated 240 to 254 million people worldwide [2, 3], with prevalence increasing substantially with age, from approximately 4% to 7% among adults aged 40 to 79 years to more than 10% among those aged ≥ 80 years [4].
Despite advances in secondary prevention, people with stable CAD remain at substantial long‐term risk of recurrent ischaemic events and death. In the international CLARIFY registry, five‐year all‐cause mortality was approximately 8%, while cardiovascular death or non‐fatal myocardial infarction occurred in 8.0% of participants, despite high use of evidence‐based secondary prevention therapy [5].
Antithrombotic management becomes particularly complex when stable CAD coexists with an indication for long‐term oral anticoagulation. Atrial fibrillation is present in approximately 5% to 10% of people with CAD, whereas venous thromboembolism and mechanical heart valve indications are less common but remain clinically important [6, 7]. In these populations, antithrombotic management requires consideration of net clinical benefit, balancing the prevention of thromboembolic and recurrent coronary ischaemic events against the risk of major bleeding.
Description of the intervention and how it might work
Antiplatelet agents, such as aspirin and P2Y12 inhibitors, reduce platelet activation and aggregation, thereby targeting atherothrombotic processes [8]. They have been the cornerstone of secondary prevention in CAD, with lifelong single antiplatelet therapy – most commonly aspirin – traditionally recommended to reduce the risk of myocardial infarction, stroke, and cardiovascular death in people with established disease [1, 9].
Oral anticoagulants, including vitamin K antagonists (VKAs) and direct oral anticoagulants (DOACs), inhibit components of the coagulation cascade and are highly effective in preventing cardioembolic events [10, 11, 12, 13, 14]. In conditions such as atrial fibrillation and venous thromboembolism, oral anticoagulation is the cornerstone of therapy, supported by robust evidence for the prevention of stroke, systemic embolism, and recurrent venous thromboembolism [13, 15].
Traditionally, combination antithrombotic therapy consisting of an oral anticoagulant (OAC) plus an antiplatelet agent has been used to address both thromboembolic and atherothrombotic risks. The potential benefit of targeting both pathways was further supported by the COMPASS trial, in which very low‐dose rivaroxaban combined with aspirin reduced major cardiovascular events compared with aspirin alone in people with stable atherosclerotic vascular disease, albeit at the cost of increased major bleeding [16].
However, stable CAD represents a phase in which coronary thrombotic risk is lower than in the acute setting, and the incremental benefit of continued antiplatelet therapy beyond the early post‐event or post‐intervention period has become increasingly uncertain [1].
Why it is important to do this review
Several randomised controlled trials have directly compared OAC monotherapy with OAC plus single antiplatelet therapy in people with stable CAD requiring long‐term anticoagulation. These include OAC‐ALONE, AFIRE, PRAEDO‐AF, EPIC‐CAD, ADAPT AF‐DES, and AQUATIC [17, 18, 19, 20, 21, 22]. Collectively, these trials generally suggest that OAC monotherapy reduces bleeding without a clear increase in ischaemic events.
Several systematic reviews and meta‐analyses have already synthesised evidence in this area [23, 24, 25]. Most recently, Gargiulo and colleagues published a brief‐report meta‐analysis incorporating six randomised trials, including EPIC‐CAD, ADAPT AF‐DES, and AQUATIC, and provided an important updated synthesis of the available evidence [26]. Although these recent analyses provide important information, a comprehensive Cochrane review remains valuable to provide a rigorous and transparent assessment of the benefits and harms, detailed risk of bias assessment using the Cochrane RoB 2 tool, and formal evaluation of the certainty of evidence using the GRADE approach.
A Cochrane protocol published in 2021 also addressed long‐term antithrombotic therapy in people with atrial fibrillation and stable CAD [27]. However, that protocol was restricted to people with atrial fibrillation and considered several different antithrombotic comparisons. In contrast, the present review focuses specifically on the clinical decision of whether a single antiplatelet agent should be continued in addition to therapeutic oral anticoagulation in people with stable CAD requiring long‐term anticoagulation.
Contemporary US and European guidelines generally favour OAC monotherapy during the chronic phase, although the strength and scope of these recommendations vary. The 2023 American College of Cardiology/American Heart Association (ACC/AHA) atrial fibrillation guideline recommends OAC monotherapy over OAC plus single antiplatelet therapy in people with atrial fibrillation and chronic CAD beyond one year after revascularisation, or with CAD not requiring revascularisation, in the absence of prior stent thrombosis (Class 1, Level B‐R) [13]. The 2023 AHA/ACC chronic coronary disease guideline also supports transition towards DOAC monotherapy after percutaneous coronary intervention (PCI), although the recommendation for discontinuing aspirin and continuing DOAC alone at one year in people at low atherothrombotic risk is weaker (Class 2b, Level B‐R) [1]. European guidance is directionally similar, with the 2024 European Society of Cardiology (ESC) chronic coronary syndrome and atrial fibrillation guidelines supporting de‐escalation of combination antithrombotic therapy after the period of highest coronary thrombotic risk [28, 29]. However, uncertainty remains regarding how broadly these recommendations can be applied across the full spectrum of people with stable CAD requiring long‐term anticoagulation.
Most randomised evidence has been generated in East Asian populations, including OAC‐ALONE, AFIRE, PRAEDO‐AF, EPIC‐CAD, and ADAPT AF‐DES [17, 18, 19, 21, 22]. East Asian populations have been reported to experience a different ischaemic‐bleeding risk balance during antithrombotic therapy, with generally lower rates of ischaemic events but higher bleeding susceptibility compared with Western populations [30, 31]. This so‐called 'East Asian paradox' may affect the generalisability of treatment effects across populations. AQUATIC provides important randomised evidence from a European population and therefore broadens the geographical evidence base [20]. Generalisability is also uncertain with respect to the indication for anticoagulation: although most trial participants have required anticoagulation for atrial fibrillation, the same clinical dilemma arises in people requiring long‐term anticoagulation for other indications.
From the perspective of people receiving treatment, reducing bleeding risk is highly relevant, as bleeding complications adversely affect quality of life and increase healthcare utilisation. From a clinical and policy standpoint, robust evidence is needed to determine whether simplified strategies such as OAC monotherapy can be safely adopted as the standard long‐term approach.
The present review will therefore complement existing meta‐analyses by providing a focused Cochrane assessment of this specific clinical comparison. We will use prespecified patient‐important outcomes, RoB 2, and GRADE to evaluate both ischaemic and bleeding outcomes and the certainty of the evidence. We will also assess the applicability of the findings according to factors including indication for anticoagulation, anticoagulant class, time from the index coronary event or revascularisation, and geographic region.
Objectives
To assess the benefits and harms of oral anticoagulant monotherapy compared with oral anticoagulant plus antiplatelet therapy in adults with stable coronary artery disease requiring long‐term anticoagulation.
Methods
Criteria for considering studies for this review
Types of studies
We will include randomised clinical trials (RCTs), irrespective of publication status, publication date, outcomes measured and reported, or language. We will include parallel‐group, cross‐over (first period only), and cluster‐RCTs that compare OAC monotherapy with OAC plus antiplatelet therapy.
We will exclude quasi‐randomised studies, as allocation in such studies is not truly random.
Types of participants
We will include adults aged 18 years or older with stable CAD who require long‐term oral anticoagulation, most commonly for atrial fibrillation or venous thromboembolism. Stable CAD will include previous myocardial infarction, previous percutaneous coronary intervention (PCI), previous coronary artery bypass grafting (CABG), or angiographically documented CAD not requiring revascularisation, provided that participants are outside the acute coronary syndrome (ACS) or early post‐revascularisation period.
We will exclude studies in which participants were enrolled during ACS or during the early post‐PCI or post‐CABG period. The early post‐revascularisation period will generally be defined as less than 6 months after PCI or CABG, or less than 12 months after ACS‐related revascularisation, unless the trial used a more conservative definition of stable CAD. Studies enrolling mixed populations will be eligible if data for participants meeting the stable CAD definition can be extracted separately, or if the vast majority of participants meet this definition.
We will exclude studies primarily designed to evaluate antithrombotic treatment during the peri‐PCI or early post‐ACS period, including trials of dual or triple antithrombotic therapy duration immediately after PCI.
We will not restrict eligibility according to non‐antithrombotic concomitant medications. Antiplatelet therapy will be considered part of the intervention or comparator when it defines the randomised comparison.
Both treatment strategies represent long‐term secondary prevention with respect to coronary events because all eligible participants have established CAD. However, the indication for oral anticoagulation may represent either primary or secondary prevention of systemic thromboembolism depending on the underlying condition and the participant's clinical history.
Types of interventions
Experimental intervention
Oral anticoagulant monotherapy, administered orally, including either a DOAC or a VKA, at any approved dose, intensity, and duration defined by the trial, without concomitant antiplatelet therapy.
Control intervention
Oral anticoagulant therapy, administered orally, including either a DOAC or VKA, plus a single antiplatelet agent, such as aspirin or a P2Y12 inhibitor, with the dose, regimen, and duration defined by the trial.
We will exclude regimens involving dual antiplatelet therapy.
Outcome measures
Outcomes were selected based on established cardiovascular outcome frameworks, including the principles of the International Consortium for Health Outcomes Measurement (ICHOM) Standardized Outcome Measurement for Coronary Artery Disease, and prioritised according to patient importance and the anticipated balance between thrombotic and bleeding risks [32].
We will preferentially extract outcomes at the longest available follow‐up for each trial, as this reflects the clinically relevant long‐term effects of antithrombotic therapy. Where multiple time points are reported, we will use time points closest to 12 months for sensitivity analyses to assess consistency.
We will limit the summary of findings table to the three critical outcomes: all‐cause mortality, major bleeding, and composite ischaemic outcome.
Critical outcomes
All‐cause mortality (death).
Major bleeding (International Society on Thrombosis and Haemostasis (ISTH), Thrombolysis in Myocardial Infarction (TIMI), or Bleeding Academic Research Consortium (BARC) definitions). We will define major bleeding according to the criteria used by the trialists, preferentially using ISTH definitions, followed by BARC type 3 to 5 or TIMI major bleeding where applicable [33]. This outcome captures clinically significant bleeding events, including fatal bleeding, bleeding in critical organs, or bleeding requiring transfusion or causing substantial haemoglobin decline, and reflects the principal safety concern associated with intensified antithrombotic therapy. If multiple definitions are reported, we will extract data according to a predefined hierarchy: ISTH > BARC 3 to 5 > TIMI major bleeding.
Composite ischaemic outcome (cardiovascular death, myocardial infarction, ischaemic stroke, or stent thrombosis). This outcome will include cardiovascular death, non‐fatal myocardial infarction, ischaemic stroke, or stent thrombosis, as defined by the individual trials. This composite endpoint captures the overall burden of thrombotic events and reflects the principal efficacy domain in antithrombotic trials. We will interpret composite outcomes with caution, particularly when component events differ in clinical importance or frequency.
Important outcomes
Individual components of composite ischaemic outcomes, including cardiovascular death, myocardial infarction, ischaemic stroke, and stent thrombosis, will be analysed separately to allow interpretation of the relative contribution and direction of effect of each component.
Clinically relevant non‐major bleeding. This will be defined according to trialist definitions, typically aligned with ISTH criteria, and includes bleeding events that do not meet major bleeding thresholds but require medical attention, lead to treatment interruption, or affect daily functioning [34].
Cardiovascular hospitalisation. This will be defined as admission to hospital due to cardiovascular causes, including ACS, heart failure, arrhythmia, or other cardiac conditions, as reported by the trialists.
Health‐related quality of life (HRQoL), assessed using validated patient‐reported outcome measures, such as EQ‐5D or similar instruments, as reported in the included trials.
Search methods for identification of studies
To minimise bias in our search results, we will follow the guidance in Chapter 4 of the Cochrane Handbook for Systematic Reviews of Interventions [35] and PRISMA‐S [36] on planning and describing the search process for the review. The Cochrane Japan Information Specialist will develop the final search strategies and perform the electronic searches. We will not impose restrictions on language of publication, date, or publication status.
Electronic searches
We will search the following electronic databases to identify relevant RCTs:
Cochrane Central Register of Controlled Trials (CENTRAL) via the Cochrane Library (inception onwards);
Ovid MEDLINE (1946 onwards);
Embase via Ovid (1947 onwards);
CINAHL via EBSCOhost (Cumulative Index to Nursing and Allied Health Literature) (1937 onwards).
We will use the Cochrane Highly Sensitive Search Strategies for identifying randomised trials in MEDLINE and Embase, modified to include relevant search terms for identifying retraction statements and errata, as recommended in Chapter 4 of the Cochrane Handbook for Systematic Reviews of Interventions [35].
Supplementary material 1 shows the preliminary search strategies with the expected date range of the searches. We will provide the actual date of the electronic searches at the review stage.
Searching other resources
We will check the reference lists of all included studies and relevant systematic reviews to identify additional eligible trials. We will also examine retraction statements, errata, and expressions of concern related to included or potentially eligible studies.
We will contact study authors to obtain missing data, unpublished results, or information about ongoing studies. We will also search ClinicalTrials.gov (clinicaltrials.gov/) and the World Health Organization International Clinical Trials Registry Platform (trialsearch.who.int/) for relevant ongoing or completed but unpublished studies.
We will provide the search terms used for these resources and the dates of search at the review stage.
When necessary, we will contact experts in the field to identify ongoing or unpublished trials. To detect post‐publication amendments, we will search the Retraction Watch Database and the websites of journals in which the included studies were published.
We will use relevant sections of the PRISMA‐S checklist to ensure complete reporting of the search strategy [36]. We will search for grey literature using Google Scholar.
Data collection and analysis
We will follow the guidelines provided in the Cochrane Handbook for Systematic Reviews of Interventions [37].
Selection of studies
Two review authors will independently screen the titles and abstracts identified through the search strategy for potential relevance using Rayyan [38]. We will retrieve the full‐text reports of records considered potentially eligible and import them into Covidence [39]. Two review authors will independently assess the full‐text reports against the eligibility criteria. Another review author (SK) will resolve any disagreements regarding eligibility through discussion with the review team.
We will list studies that do not meet the eligibility criteria as excluded and provide the main reasons for exclusion in the 'Characteristics of excluded studies' table. We will document the study selection process in sufficient detail to complete a PRISMA 2020 flow diagram for new systematic reviews, including searches of databases, registers, and other sources [40, 41].
When unanticipated issues arise, the review authors will make post hoc decisions about study eligibility as necessary and will transparently document and justify these decisions in the review.
Data extraction and management
We will develop a standardised data extraction form using Covidence to systematically collect and manage data on study characteristics [39]. Extracted information will include details on interventions and comparisons, participant characteristics, co‐interventions, randomisation methods, outcome definitions, and information relevant to the risk of bias assessment.
One review author (SK) will perform primary data extraction for all included trials. Secondary data extraction will be conducted independently by other review authors, with the included trials distributed among them. Any discrepancies will be resolved through discussion to achieve consensus.
The data extraction form will be piloted on a sample of included studies and refined as needed to ensure consistency and clarity before full data extraction. For studies published in languages other than English, translation support will be sought where necessary.
Risk of bias assessment in included studies
We will assess the effect of assignment to the interventions, based on the intention‐to‐treat principle, which includes all randomised participants regardless of the interventions actually received. We will assess risk of bias in the included studies using the Cochrane RoB 2 tool [42].
For cluster‐randomised trials, we will use the RoB 2 variant for cluster‐randomised trials. For cross‐over trials, because only data from the first intervention period will be included, we will use the standard RoB 2 tool for parallel‐group randomised trials. We will also consider whether selective reporting of first‐period data may have introduced bias.
We will assess the following risk of bias domains.
Bias arising from the randomisation process
Bias due to deviations from the intended interventions
Bias due to missing outcome data
Bias in measurement of the outcome
Bias in selection of the reported result
We will assess risk of bias for outcomes included in the main analyses (i.e. all‐cause mortality, major bleeding, and composite ischaemic outcomes). Where additional clinically important outcomes are included in analyses, we will assess risk of bias for those outcomes as appropriate.
One review author (SK) will oversee the risk of bias assessment, and a second review author (HH) will independently evaluate each domain. We will assess risk of bias as 'low risk of bias', 'some concerns', or 'high risk of bias', according to the RoB 2 algorithms and signalling questions. We will use the RoB 2 Excel tool (available at www.riskofbias.info/) to implement and manage the assessments.
We will resolve disagreements through discussion to reach consensus. If further information is required, we will contact the corresponding authors or co‐authors of the included trials.
For each assessed result within each trial, we will judge the overall risk of bias as low risk, some concerns, or high risk according to the RoB 2 algorithm. These assessments will subsequently inform the risk of bias domain of the GRADE assessment for each outcome.
Measures of treatment effect
For event outcomes, we will use the effect measure appropriate to the form of the available data. We will report fixed‐time point dichotomous data using risk ratios (RRs) with 95% confidence intervals (CIs).
For outcomes reported as time‐to‐event data, we will preferentially use hazard ratios (HRs) with 95% CIs, as these account for censoring and variable follow‐up durations. If HRs are not reported directly, we will attempt to derive log HRs and their standard errors from available summary information using the methods described by Tierney and colleagues, where sufficient information is available [43]. If an HR cannot be obtained or reliably estimated, we will analyse appropriate fixed‐time point event data using RRs in separate analyses. We will not combine HRs and RRs in the same meta‐analysis.
We will report continuous outcomes using mean differences (MDs) with 95% CIs when outcomes are measured using the same scale, and standardised mean differences (SMDs) when different scales are used to measure the same construct. Where SMDs are used, we will interpret values of approximately 0.2, 0.5, and 0.8 as representing small, moderate, and large effects, respectively, while taking account of the clinical context and direction of the measurement scales. Where feasible, we will facilitate interpretation by relating the SMD to a familiar measurement scale.
Where appropriate, we will present absolute effects based on the pooled relative effect and an appropriate assumed control risk, as recommended in Chapter 15 of the Cochrane Handbook for Systematic Reviews of Interventions [44].
Unit of analysis issues
In all cases, we will consider the randomised participant as the unit of analysis.
For trials with more than two relevant arms, we will avoid double‐counting participants by combining relevant intervention or comparator groups where appropriate. If combining groups is not appropriate, we will use another suitable approach, such as splitting a shared comparator group, in accordance with the guidance in the Cochrane Handbook for Systematic Reviews of Interventions [45].
For outcomes reported at multiple time points, we will use the data reported at the longest follow‐up for each trial for the primary analysis.
For cluster‐randomised trials, we will account for clustering using the methods described in Section 23.1 of the Cochrane Handbook [45]. If a trial does not report results adjusted for clustering, we will adjust standard errors using the intracluster correlation coefficient, if available, or an appropriate external estimate.
For cross‐over trials, we will use data from the first intervention period only, before cross‐over, to avoid potential carryover effects [45].
Dealing with missing data
If relevant outcome data are missing or unclear, we will contact the corresponding trial authors where feasible. We will preferentially use analyses based on the intention‐to‐treat principle.
We will not impute missing outcome data in the primary analysis unless an appropriate imputation has been performed by the trial investigators and is consistent with the estimand of interest.
Where appropriate, we will explore the potential impact of missing outcome data in sensitivity analyses, including best‐worst‐case and worst‐best‐case scenarios for dichotomous outcomes.
Reporting bias assessment
We will assess reporting biases according to the recommendations described in Section 13.3.5 of the Cochrane Handbook for Systematic Reviews of Interventions [46]. If at least 10 trials are included in a given meta‐analysis, we will assess small‐study effects and potential publication bias using funnel plots and visual inspection.
Synthesis methods
We will use RevMan to perform the meta‐analyses [47].
We will meta‐analyse outcome data when we judge that the participants, interventions, comparisons, and outcomes are sufficiently similar for a pooled estimate to be clinically meaningful.
We will use a random‐effects model because we anticipate clinical diversity across trials. We will use the Restricted Maximum Likelihood (REML) method to estimate between‐trial variance [48].
We will use the Hartung‐Knapp‐Sidik‐Jonkman method to calculate CIs for the meta‐analysis effect estimate when there are at least three trials and the estimated heterogeneity is greater than zero [49]. In pooled analyses of two trials, or when estimated heterogeneity is zero, we will use the Wald‐type method [49].
We will generate forest plots in RevMan to illustrate the effect estimates. If meta‐analysis is not feasible, we will present the findings using structured synthesis methods consistent with the Synthesis Without Meta‐analysis (SWiM) guideline [50].
Investigation of heterogeneity and subgroup analysis
We will assess statistical heterogeneity through the visual inspection of forest plots and by considering the Chi² test and I² statistic. We will use P < 0.10 for the Chi² test as an indication of statistical heterogeneity.
We will interpret I² approximately as follows:
0% to 40%: may not be important;
30% to 60%: may represent moderate heterogeneity;
50% to 90%: may represent substantial heterogeneity;
75% to 100%: considerable heterogeneity.
We will interpret these ranges in the context of the magnitude and direction of effects and the strength of evidence for heterogeneity.
Where important heterogeneity is present, we will explore possible clinical and methodological sources by examining study characteristics and forest plots. If heterogeneity cannot be adequately explained, and the effect estimates differ substantially in direction or magnitude, we may refrain from pooling the results and instead present a structured synthesis.
We will consider performing subgroup analyses for the critical outcomes only, based on the following prespecified factors.
Indication for oral anticoagulation. We will compare trials enrolling predominantly participants with atrial fibrillation with those enrolling participants anticoagulated for other indications, such as venous thromboembolism or mechanical heart valves, because the balance between thromboembolic and coronary risks may differ across these populations.
Type of OAC. We will compare trials evaluating DOACs with those evaluating VKAs because the efficacy and safety balance of monotherapy versus combination therapy may differ according to anticoagulant class.
Time from index coronary event or PCI. Where data permit, we will compare trials or trial populations according to time elapsed since the index coronary event or PCI because the incremental benefit of antiplatelet therapy may diminish over time in stable CAD.
Geographic region. We will compare trials conducted predominantly in Asian populations with those conducted predominantly in non‐Asian populations because baseline risks of bleeding and ischaemic events, as well as clinical practice patterns, may differ across regions.
Baseline bleeding risk. Where reported, we will compare trials or populations at higher versus lower baseline bleeding risk according to trial‐defined criteria or recognised bleeding risk tools because treatment effects may differ according to underlying bleeding susceptibility.
We will assess subgroup differences using the formal test for interaction implemented in RevMan. We will interpret subgroup findings cautiously as exploratory analyses.
Within‐study subgroup estimates will be considered only when the subgroup‐defining factor was used for stratified randomisation and when a formal test for interaction was prespecified and reported. Such within‐study subgroup results will be treated as exploratory evidence and will not be pooled with trial‐level subgroup estimates to avoid double‐counting participants.
Meta‐regression analyses will be considered only when at least 10 studies are available for a given outcome, and results will be interpreted cautiously given the observational nature of such analyses [49].
Sensitivity analysis
We will perform sensitivity analyses for the critical outcomes of all‐cause mortality, major bleeding, and composite ischaemic outcome to assess the robustness of the findings.
These analyses will include restricting analyses to trials at low risk of bias and examining the impact of missing outcome data using best‐worst‐case and worst‐best‐case scenarios, where feasible [49].
We will also conduct a sensitivity analysis using outcome measurements closest to 12 months, where sufficient data are available, to assess whether findings are consistent with analyses based on the longest available follow‐up.
Certainty of the evidence assessment
We will assess the certainty of the evidence using the GRADE approach and present the results in a single summary of findings table [51] for the comparison of OAC monotherapy versus OAC plus a single antiplatelet agent in adults with stable CAD requiring long‐term anticoagulation. We will present the results and the certainty of evidence for the critical outcomes of all‐cause mortality, major bleeding, and composite ischaemic outcome.
Randomised clinical trials will initially be considered high‐certainty evidence and may be downgraded for risk of bias, inconsistency, imprecision, indirectness, or publication bias.
Two review authors (SK and HH) will independently assess the certainty of the evidence using the GRADE approach [52]. We will resolve any disagreements through discussion to reach consensus.
For dichotomous outcomes, we will consider whether the 95% CI crosses prespecified thresholds for important benefit or important harm when assessing imprecision. We will use a relative risk reduction or increase of 25% as the threshold for important benefit or harm. We chose this threshold because moderate relative effects may be clinically important in long‐term antithrombotic therapy, particularly for major bleeding and major ischaemic events.
In our assessment of indirectness, we will pay particular attention to the extent to which included trial populations reflect the target population of this review, especially if most of the available evidence is derived from participants with atrial fibrillation rather than the full spectrum of people requiring long‐term oral anticoagulation.
We will use GRADEpro GDT software to prepare the summary of findings table and associated footnotes [53].
Equity considerations
We will report participant characteristics, where available, using the PROGRESS‐Plus framework, including place of residence, race/ethnicity/culture/language, occupation, gender/sex, religion, education, socioeconomic status, social capital, age, and other relevant factors associated with disadvantage [54].
Where data permit, we will consider whether the effects of OAC monotherapy versus combination therapy differ across population subgroups that may be associated with health inequities, paying particular attention to sex, age, geographic region, and baseline bleeding risk. We will interpret any such findings cautiously as these analyses are expected to be limited by incomplete reporting and small numbers of studies.
Consumer involvement
This review will not involve direct consumer participation in the development or conduct of the research.
Supporting Information
Supplementary materials are available with the online version of this article: 10.1002/14651858.CD016399.
Supplementary materials are published alongside the article and contain additional data and information that support or enhance the article. Supplementary materials may not be subject to the same editorial scrutiny as the content of the article and Cochrane has not copyedited, typeset or proofread these materials. The material in these sections has been supplied by the author(s) for publication under a Licence for Publication and the author(s) are solely responsible for the material. Cochrane accordingly gives no representations or warranties of any kind in relation to, and accepts no liability for any reliance on or use of, such material.
Supplementary material 1 Search strategies
New
Additional information
Acknowledgements
Cochrane Japan supported the authors in the development of this review. Special thanks to Takaaki Suzuki for his assistance in developing the search strategies and conducting the electronic searches. We are grateful to all the authors who contributed to the development of the review protocol.
Editorial and peer‐reviewer contributions
The following people conducted the editorial process for this article:
Sign‐off Editor (final editorial decision): Rupa Sarkar, Editor‐in‐Chief, Cochrane;
Managing Editor (selected peer reviewers, provided editorial guidance to authors, edited the article): Alan Thomas, Cochrane Central Editorial Service;
Editorial Assistant (conducted editorial policy checks, collated peer‐reviewer comments, and supported the editorial team): Lisa Wydrzynski, Cochrane Central Editorial Service;
Copy Editor (copy editing and production): Lisa Winer, Cochrane Central Production Service;
Peer reviewers (provided comments and recommended an editorial decision): Dr Kerry Dwan, University of York (methods review), Jo Platt, Central Editorial Information Specialist (search review). One additional peer reviewer provided patient and public peer review but chose not to be publicly acknowledged.
Contributions of authors
Saehyeon Kim: conceptualisation; methodology; project administration; writing – original draft; writing – review and editing.
Hiroki Harada: methodology; risk of bias methodology; writing – review and editing.
Kazuteru Murakoshi: methodology; writing – review and editing.
Masataka Ono: methodology; writing – review and editing.
Ken Goda: methodology; writing – review and editing.
Paniz Parvar: writing – review and editing.
Zeyad Abdelaziz: writing – review and editing.
Norio Watanabe: methodology; supervision; writing – review and editing.
All authors approved the final version of the protocol.
Declarations of interest
The authors declare that the performance of this review is free from any real or perceived bias introduced by the receipt of any financial or non‐financial benefit from any source that may have, or be perceived to have, an interest in the outcomes of the review.
Saehyeon Kim: no known conflict of interest
Hiroki Harada: no known conflict of interest
Kazuteru Murakoshi: no known conflict of interest
Masataka Ono: no known conflict of interest
Ken Goda: no known conflict of interest
Paniz Parvar: no known conflict of interest
Zeyad Abdelaziz: no known conflict of interest
Norio Watanabe: no known conflict of interest
Sources of support
Internal sources
-
Cochrane Japan, Japan
This protocol was conducted during work hours.
External sources
No sources of support provided
Registration and protocol
Cochrane approved the proposal for this review in April 2026.
Data, code and other materials
No data, code, or other materials were generated or analysed for this protocol.
Disclosure of artificial intelligence use
The authors used ChatGPT‐5 (OpenAI, San Francisco, CA; accessed May 2026) for grammar review and linguistic refinement. No content generation or data interpretation was performed by the tool.
Notes
Published notes in RevMan are for editor use only. Authors should leave this section blank.
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Associated Data
This section collects any data citations, data availability statements, or supplementary materials included in this article.
Supplementary Materials
Supplementary material 1 Search strategies
Data Availability Statement
No data, code, or other materials were generated or analysed for this protocol.