Types of studies

We included RCTs that compared early intervention versus delayed revascularization in people with recently symptomatic carotid artery stenosis (up to 14 days from onset of symptoms). We included studies only if data on clinically significant endpoints, such as ischemic stroke, hemorrhagic stroke, or death, were available.

Types of participants

We included people who had suffered a recent neurologic (TIA or stroke) event ipsilateral to stenosis of 50% to 99% in the carotid artery. We defined a stroke as any cerebrovascular or retinal event with symptoms lasting longer than 24 hours (Rerkasem 2011; Rothwell 2003), and a TIA as a focal neurologic deficit lasting 24 hours (Ferrero 2014; Giles 2007). We defined a nondisabling stroke as a stroke that resulted in no disability of functional significance (modified Rankin score < 3; Brott 2011; Rerkasem 2011; Rothwell 2003).

Brain imaging that demonstrated a new lesion involving a different anatomic site or vascular territory from the index event could be used to support the diagnosis of perioperative stroke. We classified strokes as disabling or nondisabling (as defined by trial authors), fatal or nonfatal, or contralateral, ipsilateral, hemorrhagic, or ischemic.

Types of interventions

All techniques aimed at revascularization in symptomatic carotid artery stenosis, including but not confined to:

• percutaneous transluminal balloon angioplasty and stenting;

• carotid endarterectomy; and

• carotid eversion.

We included randomized studies comparing early intervention (within two days) versus delayed treatment (after two days).

Types of outcome measures

Electronic searches

We searched the Cochrane Stroke Group's Trials Register (strokecenter.org/trials) and the following electronic databases and trials registers:

• The Cochrane Central Register of Controlled Trials (CENTRAL; The Cochrane Library 2016, Issue 1; Appendix 1);

• MEDLINE (Ovid; 1948 to 26 January 2016; Appendix 2);

• EMBASE (Ovid; 1948 to 26 January 2016; Appendix 3);

• Literatura Latino‐Americana e do Caribe em Ciências da Saúde (LILACS; 1948 to 26 January 2016; Appendix 4);

• ClinicalTrials.gov (clinicaltrials.gov)

• Current Controlled Trials (controlled‐trials.com)

• European Union (EU) Clinical Trials Register (clinicaltrialsregister.eu)

• World Health Organization (WHO) International Clinical Trials Registry Platform (apps.who.int/trialsearch)

We developed the MEDLINE search strategy with the help of the Cochrane Stroke Group Information Specialist and modified it for use with the other databases.

Searching other resources

In an effort to identify further published, unpublished, and ongoing trials, we:

• searched the reference lists of identified studies and reviews;

• contacted study authors and experts in the field;

• contacted relevant pharmaceutical companies; and

• used Science Citation Index Cited Reference Search for forward tracking of important articles.

Selection of studies

Two review authors (VV and NC) independently screened titles and abstracts of the references obtained as a result of our searching activities and excluded obviously irrelevant reports. We retrieved full‐text articles for the remaining references, and two review authors (VV and NC) independently screened the full‐text articles, identified studies for inclusion, and identified and recorded reasons for exclusion of ineligible studies. We resolved disagreements through discussion; if required, we consulted a third review author (JCCBS) for resolution. We collated multiple reports on the same study, so that each study, not each reference, was the unit of interest in the review. We recorded the selection process and completed a PRISMA (Preferred Reporting Items for Systematic Reviews and Meta‐Analyses) flow diagram (Figure 1).

Figure 1

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Study flow diagram.

Data extraction and management

Two review authors (VV and NC) independently extracted the following data from eligible studies and recorded this information on standard data extraction forms:

• Participants: sample size, age, sex, number of participants originally allocated to each treatment group, diagnostic criteria used for carotid stenosis, number of participants in each group with early or delayed intervention.

• Intervention: time interval from onset of symptoms of TIA or stroke to randomization, and from randomization to surgery, type of anesthesia, technique of carotid endarterectomy, technique of carotid artery stenting, any other major vascular surgery.

• Outcomes: number of participants in each group with outcome events, including stroke, myocardial infarction, and death.

• Withdrawals and adverse effects.

• Length of follow‐up.

• Additional important information.

We resolved disagreements between review authors by discussion.

Assessment of risk of bias in included studies

Two review authors (VV and NC) independently assessed risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We resolved disagreements by discussion or by involving another review author (JCCBS). We assessed the following domains as 'Yes' (low risk of bias), 'Unclear' (uncertain risk of bias) or 'No' (high risk of bias):

• Random sequence generation: was the sequence generation adequate?

• Allocation concealment: was allocation adequately concealed?

• Blinding of participants and personnel: were participants and personnel blinded to the allocated interventions?

• Blinding of outcome assessment: were the outcome assessors blinded to the allocated interventions?

• Incomplete outcome data: were incomplete outcome data adequately addressed and similar across intervention groups?

• Selective outcome reporting: are reports of the study free of the suggestion of selective outcome reporting?

• Other bias: was the study apparently free of other problems that could put it at a risk of bias?

We graded the risk of bias for each domain as high, low, or unclear and provided information from the study report together with a justification for our judgment in the 'Risk of bias' tables.

Measures of treatment effect

For dichotomous variables, we calculated risk ratios (RRs) and 95% confidence intervals (CIs). For continuous data, we would have calculated mean differences (MDs) and 95% CIs between treatment groups if studies reported exactly the same outcomes. If similar outcomes were reported on different scales, we would have calculated the standardized mean difference (SMD) and the 95% CI. The most appropriate way of summarizing time‐to‐event data would have been to use methods of survival analysis while expressing the intervention effect as a hazard ratio; we extracted these data directly from the results of studies (Higgins 2011).

Unit of analysis issues

We based the unit of analysis on the individual participant (unit randomized for interventions to be compared; i.e. the number of observations in the analysis should have matched the number of individuals randomly assigned).

Dealing with missing data

For missing or unavailable data, we contacted study authors to request additional information. If we received no response, regardless of the type of data, we had planned to report dropout rates in the 'Characteristics of included studies' tables of the review, and use intention‐to‐treat analysis (Higgins 2011). Therefore, we included all randomized participants in the groups to which they were allocated.

Assessment of heterogeneity

We would have assessed clinical and methodological diversity in terms of participants, interventions, outcomes, and study characteristics for the included studies in order to determine whether a meta‐analysis was appropriate. We would have conducted this by observing these data from the data extraction tables. We would have assessed statistical heterogeneity by visual inspection of the forest plot for obvious differences in results between the studies, and by using the I² and Chi² statistical tests.

We would have qualified inconsistency among pooled estimates by using the I² statistic: ((Q ‐ df)/Q) × 100% test, where Q was the Chi² statistic and df represented the degree of freedom). This would have examined the percentage of total variation across studies due to heterogeneity rather than to chance (Higgins 2003; Higgins 2011).

We would have used these thresholds for interpretation of I²:

• 0% to 25%: low heterogeneity.

• 25% to 75%: moderate heterogeneity.

• Greater than 75%: significant heterogeneity (Higgins 2003).

Assessment of reporting biases

Given the limited number of eligible trials available, we did not create funnel plots to assess reporting biases. In future updates of this review, we will interpret any funnel plot asymmetry with caution.

Data synthesis

Methods of synthesizing studies depend on quality, design, and heterogeneity. We would have explored both clinical and statistical heterogeneity. Where we considered studies to be sufficiently similar, we would have conducted a meta‐analysis by pooling appropriate data using RevMan (RevMan 2014).

We assessed the quality of the evidence using the Grading of Recommendations Assessment, Development and Evaluation (GRADE 2015) approach and constructed 'summary of findings Table for the main comparison for the outcomes.

Subgroup analysis and investigation of heterogeneity

If we had found sources of heterogeneity, and when data were sufficient, we had planned to conduct meta‐analyses by subgroups. If we had identified an adequate number of studies, we had planned to performed subgroup analyses according to participant age, participant sex, type of revascularization, degree of stenosis, and initial neurologic severity.

If we had identified no significant heterogeneity, we had planned to compute pooled estimates of the treatment effect for each outcome using a fixed‐effect model. When we detected significant heterogeneity despite subgroup analyses, we would have calculated the pooled estimate of treatment effects using random‐effects models.

Sensitivity analysis

If an adequate number of studies had been identified, we had planned to perform sensitivity analyses based on separation of studies according to risk of bias. We would have done this by excluding trials that were most susceptible to bias, based on our risk of bias assessment: those with inadequate allocation concealment, high levels of post‐randomization losses or exclusions, and uncertain or unblinded outcome assessment (Deeks 2011).