[SOCRATES -Acute Stroke Or Transient IsChaemic Attack TReated With Aspirin or Ticagrelor and Patient OutcomES]: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for [SOCRATES -Acute Stroke Or Transient IsChaemic Attack TReated With Aspirin or Ticagrelor and Patient OutcomES] (NCT01994720), a randomized phase 3 study. The primary outcome is Number of Participants With Composite of Stroke/MI/Death.

2. Clinical Question

SOCRATES was designed to compare treatment over 90 days for prevention of major vascular events. The primary endpoint combined stroke, myocardial infarction and death into one outcome. This asks whether the occurrence of at least one event in that composite differed between the randomized groups; it does not, by itself, establish how each component behaved independently. The registry identifies the primary outcome as the number of participants with the composite and specifies follow-up from randomization up to 97 days.

The posted primary results include participant counts and a sponsor-reported time-to-event comparison. These are related but not identical summaries: counts describe how many participants had an event, while the time-to-event analysis also uses event timing and censoring. The statistical evidence should therefore be read with attention to the particular estimate and its uncertainty, rather than as a single definitive measure of every possible treatment difference.

3. Trial Design

SOCRATES (NCT01994720) was a Phase 3, randomized, double-blind, parallel-group study sponsored by AstraZeneca. The registry lists 13307 enrolled participants and marks the study as completed. The recorded study start was 2014-01-07, and the primary completion date was 2016-03-02.

The two study groups received ticagrelor or acetylsalicylic acid (ASA), also described as aspirin. The brief description specifies a loading dose on Day 1 and a maintenance regimen for the remainder of the study: ticagrelor 180 mg followed by 90 mg twice daily, or aspirin 300 mg followed by 100 mg once daily. The stated treatment period was 90 days. The registry labels the design randomized, double-blind and parallel, but further details of the randomization procedure, allocation concealment, and how masking was maintained are not reported in the registry record.

The primary endpoint population was the full analysis set, defined in the registry as all randomized patients. The posted group sizes for the primary outcome were 6589.0 in the ticagrelor group and 6610.0 in the aspirin group. Those outcome denominators need not be identical to the overall enrollment count, and the registry excerpt does not explain the difference. The primary outcome was assessed from randomization up to 97 days, with censoring specified in relation to the last event assessment, end of treatment or Day 97.

The registry lists 18 outcome measures and 13 analyses. It does not report the trial’s original sample-size justification, the planned allocation ratio, or a complete statistical analysis plan. Those details cannot be inferred from the posted results or from planning calculations based on the observed effect.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: Enrolled patients randomised to study drug: 99.2%; n=13199 Patients who were not randomised: 0.8%; n=108 Patients with eligibility criteria not fulfilled: 0.7%; n=93 Patient decision: 0.1%; n=15

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The population was the full analysis set, which included all randomized patients.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Composite of Stroke/MI/Death, measured over From randomization up to 97 days.

The primary endpoint was the number of participants with a composite of stroke, myocardial infarction (MI) or death. It was assessed from randomization up to 97 days. The registry states that a participant without an event was censored at the minimum of the last date of event assessment, the end of treatment date, or Day 97. The primary population was the full analysis set, including all randomized patients.

A composite endpoint combines several clinically relevant events into a single outcome. In general, this can capture a broader range of events than any one component alone and can provide a measure of whether participants experienced at least one event in the defined group. The composite result does not show whether each component contributed equally, whether one component accounted for most events, or whether effects were consistent across components. Component-specific counts are therefore useful context, but they do not replace the primary composite analysis.

The endpoint is also summarized in two statistical forms. The participant counts describe event occurrence, while the sponsor’s Cox regression analysis reports a hazard ratio and incorporates the timing of events and censoring. These estimands answer related but distinct questions. The registry’s event definition and censoring rule are stated, but further details of endpoint adjudication and the treatment of particular event types are not reported in the registry record.

7. Results Posted in the Registry

• ASA 100 mg: 7.5% (497/6610) versus 6.7% (442/6589) on control; risk difference 0.8 percentage points (95% CI -0.1 to 1.7), risk ratio 1.12 (0.99–1.27); unadjusted two-proportion z-test p = 0.070.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Number of Participants With Ischaemic Stroke

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • ASA 100 mg: 6.7% (441/6610) versus 5.8% (385/6589) on control; risk difference 0.8 percentage points (95% CI 0.0 to 1.7), risk ratio 1.14 (1.00–1.30); unadjusted two-proportion z-test p = 0.049.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for ASA 100 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Net Clinical Outcome

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • ASA 100 mg: 7.7% (508/6610) versus 6.9% (457/6589) on control; risk difference 0.7 percentage points (95% CI -0.1 to 1.6), risk ratio 1.11 (0.98–1.25); unadjusted two-proportion z-test p = 0.098.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between ASA 100 mg and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Composite of Ischaemic Stroke, MI and CV Death

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • ASA 100 mg: 7.2% (475/6610) versus 6.4% (423/6589) on control; risk difference 0.8 percentage points (95% CI -0.1 to 1.6), risk ratio 1.12 (0.99–1.27); unadjusted two-proportion z-test p = 0.080.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between ASA 100 mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists 17 secondary outcomes as posted. Across the secondary participant-count outcomes described in detail, the overall pattern is generally more events in the aspirin group than in the ticagrelor group. The sponsor-reported Cox estimates for the displayed secondary analyses also point in the same direction as the primary point estimate. This broad directional consistency is useful context, but it does not independently confirm the primary result or establish a uniform effect across different outcomes.

Secondary outcomes address other aspects of vascular events, mortality, stroke severity and disability. Some overlap conceptually with the primary composite, while others represent different outcomes. Shared event components mean results are not necessarily independent: a participant’s event can contribute to more than one endpoint definition. The registry does not report enough detail to establish how the secondary measures relate analytically or whether they were ranked in a prespecified hierarchy.

Unadjusted secondary results carry less weight as confirmatory evidence when many outcomes or analyses are considered. In general, testing multiple hypotheses increases the chance that at least one result will appear notable by chance. A multiplicity procedure can address that concern, but the registry record does not report whether one was used. Nor does it state whether these secondary analyses were prespecified, exploratory, or adjusted for covariates. Their estimates are therefore best read as supportive descriptive evidence, with attention to their intervals and analysis context, rather than as independent proof of treatment differences.

The secondary pattern can add perspective on the primary composite, but component and related outcomes should not be counted as separate confirmations without considering overlap and multiplicity. The primary comparison remains the central result, and the registry does not report a formal procedure for drawing an overall conclusion across the secondary endpoints.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Number of Participants With Ischaemic Stroke
• Net Clinical Outcome
• Number of Participants With Composite of Ischaemic Stroke, MI and CV Death
• Number of Participants With All-Cause Death
• Number of Participants With CV Death
• Number of Participants With MI
• Number of Participants by Severity of Stroke and Overall Disability
• Number of Participants With Stroke

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary at the participant level: a participant either had at least one event in the stroke, MI or death composite during the stated follow-up, or did not. The posted event counts and group sizes give a direct description of the observed outcomes. A risk difference compares the event proportions between groups by subtraction; the posted recalculation expresses this as aspirin minus ticagrelor. The estimate of 0.008 is in that direction. Its interval, from -0.001 to 0.017, includes zero, the null value for a risk difference.

What the participant counts describe

Counts are easy to interpret, but they do not use the full timing information for each event. A participant who experiences an event earlier and a participant who experiences one later both contribute to the event count. In a time-to-event analysis, the event time is used, and participants without an event may contribute follow-up until they are censored. The registry’s primary-outcome description states that censoring occurs at the minimum of the last date of event assessment, end of treatment date, or Day 97. It does not provide further details on how censoring was implemented in the sponsor’s analysis.

What a hazard ratio means

The registry reports a Cox regression analysis and gives the result as a hazard ratio. In general, a hazard ratio compares the event rates over follow-up between groups, conditional on the model used; a value of 1 is the null value. It is not the same quantity as a risk difference or a ratio of the total participant counts, and it should not be read as a direct percentage change in the number of participants with an event. The reported primary hazard ratio is 0.89. Its 95% confidence interval is 0.78 to 1.01, and the reported p-value is 0.067.

Cox regression is a time-to-event method. Its interpretation depends on the model and data handling. The registry identifies the method but does not report the covariates, checks of model assumptions, or whether the analysis was adjusted. In general, the proportional-hazards assumption concerns whether the relative event rate represented by the hazard ratio is sufficiently stable over time. Whether that assumption was assessed, and what those assessments showed, are not reported in the registry record.

How to read the p-value

A p-value describes how unusual the observed data, or data more extreme, would be under a specified null hypothesis and statistical model. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. The registry reports p = 0.067 for the primary Cox analysis, while the unadjusted recalculation reports p = 0.07. These values arise from different summaries and should not be treated as though they were outputs of the same analysis. The registry record does not state the trial’s decision threshold or the full testing plan.

Uncertainty and the null value

A confidence interval gives a range of values compatible with the data under the method used. For a hazard ratio, the null is 1; for a risk difference, it is zero. The primary sponsor-reported interval extends from 0.78 to 1.01, and the unadjusted risk-difference interval extends from -0.001 to 0.017. Each includes its relevant null value. This is a reason to avoid treating the point estimate alone as a settled result. Confidence intervals do not include every possible source of uncertainty, such as uncertainty created by choices not described in the registry.

Why event-time analysis and recalculation differ

The unadjusted recalculation is based on the posted group counts and denominators. It does not reproduce the sponsor’s Cox regression, which uses event-time information and may also reflect analytic choices not stated in the registry record. The recalculation is useful as a simple comparison of observed participant outcomes, but it is not a replacement for the sponsor’s analysis. Because the registry reports no discrepancy flag, the two summaries can be read as different analytical views of the same trial data rather than as a documented conflict.

In general, over-dispersion matters when a statistical model assumes less variability than the data contain: standard errors may then be too small and intervals too narrow if that extra variability is ignored. That concept is most directly relevant to outcomes modeled as counts or rates. The primary outcome is posted as participants with an event, and the registry does not report an over-dispersion assessment. It would not be appropriate to assume that such a problem was present or absent.

11. Confidence Intervals and Precision

The sponsor’s primary time-to-event estimate is a hazard ratio of 0.89, with a 95% confidence interval from 0.78 to 1.01. The interval includes 1, the null value for a hazard ratio. Values below and slightly above the null remain compatible with this estimate under the reported method. The point estimate alone therefore gives a less complete picture than the interval: the result does not pin down a clearly separated hazard ratio.

The unadjusted risk-difference estimate is 0.008, with an interval from -0.001 to 0.017. This interval includes zero, the null value for a difference. It spans estimates in both directions, so the observed difference is not estimated with enough precision to exclude no difference using this interval. The registry does not state the confidence level for this recalculated interval, so it should not be described as a 95% interval.

In general, a confidence interval conveys both a point estimate and the range of values compatible with the data under its method and assumptions. A wider interval indicates less precision than a narrower interval, but neither interval captures every possible source of uncertainty. These intervals do not account for unreported analysis decisions or the possible effects of testing multiple outcomes.

The event counts are close enough in scale that a modest difference in counts should not be mistaken for a precise estimate of treatment effect. The primary outcome counts and the hazard ratio are also different summaries: the former concerns whether a participant experienced an event, while the latter uses event timing and censoring. The most defensible reading is that the posted estimates point toward fewer events in the ticagrelor group, while the intervals leave meaningful uncertainty about the size and direction of the underlying contrast.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrations based on the observed effect, not the trial’s original design calculation. For this binary outcome, the figures are participants per arm, rather than a total across both groups or a total number of events. The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

For the primary outcome, planning for 100% of the observed effect gives 15,779 participants per arm for 80% power and 21,123 participants per arm for 90% power. Planning for 75% of the observed effect gives 27,682 participants per arm for 80% power and 37,058 participants per arm for 90% power. Planning for 50% of the observed effect gives 61,452 participants per arm for 80% power and 82,266 participants per arm for 90% power.

In general, power is the chance that a study would detect an effect of the specified size under the calculation’s assumptions if that effect were present. The 80% and 90% columns show the participant requirements for those respective planning targets. A smaller assumed effect requires more participants because it is harder to distinguish from random variation. The time-to-event planning approach uses total events, but the primary endpoint figures are participants per arm. These are planning illustrations, not observed power.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.067; treatment proportion p₁ = 0.075; average p̄ = 0.071.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3635 = 0.7125.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3635 = 0.3059.
4. n = (0.7125 + 0.3059)² / (0.0081)² = 15,778.2, rounded up to 15,779 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.0670814994688117                          # control proportion
p1 <- 0.0751891074130106                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(1994720)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 15,779 (80% power), 21,123 (90% power)
 75% of observed effect: n per arm = 27,682 (80% power), 37,058 (90% power)
 50% of observed effect: n per arm = 61,452 (80% power), 82,266 (90% power)
power.prop.test: 15778.2 
Simulated power at n = 15,779 per arm: 0.797 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor’s primary analysis is a Cox regression with a hazard ratio of 0.89, a 95% confidence interval from 0.78 to 1.01, and p = 0.067. The unadjusted recalculation from the posted participant counts gives a risk difference of 0.008, with an interval from -0.001 to 0.017 and p = 0.07. Both summaries have point estimates in a direction corresponding to fewer observed events in the ticagrelor group, but they express different quantities and use different methods.

The sponsor’s hazard ratio uses time-to-event information, including event timing and censoring. The recalculation compares the participant outcomes without adjustment using the posted counts and denominators. It cannot reproduce the Cox regression because it does not use the same time-to-event data or analytic procedure. The registry record does not provide sufficient model details to reconstruct the sponsor’s analysis independently.

The primary interval from the sponsor’s Cox analysis includes the null value for a hazard ratio, while the recalculated risk-difference interval includes zero. The registry does not flag a discrepancy between the posted sponsor result and the simple recalculation. The sponsor’s analysis is the trial’s reported analysis; the recalculation is supplementary context and should not be treated as a substitute or as a correction to it.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies the primary endpoint and lists secondary outcomes, but it does not report a complete statistical analysis plan. In particular, the multiplicity strategy is not reported in the registry record. It is therefore not possible to tell from this information whether testing across outcomes was controlled with a prespecified procedure, whether secondary outcomes were arranged in a testing hierarchy, or whether any reported secondary p-values were adjusted.

Multiplicity matters because examining several outcomes can increase the likelihood of finding an apparently unusual result even when there is no underlying effect. This does not make secondary findings uninformative, but it changes how strongly they can support a confirmatory claim. The posted secondary analyses should be interpreted in light of this missing information, rather than assumed to have the same evidential status as the primary comparison.

The primary population is described as the full analysis set, including all randomized patients. However, details about missing outcome data, withdrawals, loss to follow-up, and the handling of incomplete observations are not reported in the registry record. The primary outcome description gives a censoring rule for participants without an event, but it does not explain how missing assessments or deviations from the intended treatment regimen were handled.

The registry reports Cox regression for the sponsor’s primary analysis but does not identify model covariates, assumption checks, or additional sensitivity analyses. It also does not report a detailed account of how endpoint events were adjudicated. These omissions do not show that the trial lacked such procedures; they mean only that the registry record does not provide them. Interpretation should remain tied to the information actually reported, particularly when considering secondary results and the robustness of the primary analysis.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: transient ischaemic attack (1.0%), carotid artery stenosis (0.4%), atrial fibrillation (0.4%), pneumonia (0.3%), hypertension (0.2%).

The registry lists serious adverse events for 533 of 6581 participants at risk in the aspirin group and 532 of 6549 participants at risk in the ticagrelor group. These are event-related participant counts with the listed at-risk denominators; they are not a comparison adjusted for follow-up time or other factors. The registry also lists other adverse events for 85 of 6581 participants at risk in the aspirin group and 383 of 6549 participants at risk in the ticagrelor group. The registry record does not provide further definitions or analysis details for these categories in the information.

Several serious adverse event terms are listed with percentages: transient ischaemic attack, 1.0%; carotid artery stenosis, 0.4%; atrial fibrillation, 0.4%; pneumonia, 0.3%; hypertension, 0.2%; and angina unstable, 0.2%. The registry does not report death counts in the adverse-event summary. These figures describe reported safety events; they should not be interpreted as a complete assessment of comparative safety without the definitions, ascertainment procedures and analytic context.

17. What the Result Does, and Does Not, Mean

The posted results describe a randomized comparison of ticagrelor and aspirin among patients with acute ischaemic stroke or transient ischaemic attack. For the primary composite of stroke, MI or death, the participant counts were 442.0 in the ticagrelor group and 497.0 in the aspirin group. The sponsor’s time-to-event estimate and the unadjusted comparison of counts both point toward fewer events in the ticagrelor group, while their intervals include the relevant null values.

This means the observed data do not provide a precise estimate that excludes no difference under the reported summaries. It does not mean that the treatments are identical, and it does not show that a difference of any particular size is established. A point estimate is not a guarantee of the true effect, and a p-value is not a direct measure of clinical importance. The uncertainty intervals should be considered alongside the event definitions, the analysis method, and the follow-up period.

The composite result also cannot be generalized to each component without examining component-specific evidence. Nor do the primary results establish effects beyond the studied population, treatment regimens or follow-up described in the registry. The secondary outcomes add context but are subject to the limitations of multiple testing and incomplete reporting of the analysis plan.

These registry results are statistical descriptions, not treatment recommendations. They do not resolve every question about benefits, harms, event timing, or the consistency of effects across patient groups. Several design and analysis details—including the original sample-size justification, multiplicity approach, and missing-data handling—are not reported in the registry record. Any broad interpretation should preserve those limits rather than reduce the evidence to a binary claim of success or failure.

18. Why This Trial Matters Statistically

This trial illustrates why the statistical summary matters as much as the direction of a point estimate. The primary outcome was a composite, and the registry presents both participant counts and a time-to-event analysis. The counts communicate how many participants experienced an event, while the Cox hazard ratio incorporates event timing and censoring. These approaches answer related questions but are not interchangeable, so readers need to distinguish them rather than treat every estimate as the same quantity.

The primary estimates also show why precision deserves attention. The sponsor’s confidence interval crosses the null value for a hazard ratio, and the recalculated risk-difference interval crosses zero. The point estimates favor one direction, but the uncertainty leaves a range of possibilities. Reading only the point estimate, or only a p-value, would conceal that uncertainty.

SOCRATES also provides a useful context for interpreting secondary analyses. Multiple outcomes can broaden the clinical description of a trial, but without a reported multiplicity strategy their statistical evidence needs careful qualification. Related endpoints may share events, and results across them are not necessarily independent confirmations. Reporting what is and is not known about the analysis plan is therefore part of sound interpretation.

Finally, planning calculations based on an observed effect should not be confused with the trial’s original design rationale. The registry record does not report that rationale, while the available planning illustrations make their assumptions explicit. Keeping those distinct helps prevent retrospective calculations from being mistaken for evidence that the trial was designed around those exact effect sizes or assumptions.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record leaves several trial-specific details unavailable. The original sample-size justification and design assumptions are not reported, so the posted planning illustrations cannot be used to reconstruct the trial’s intended power or design targets. The record also does not report the planned allocation ratio, details of the randomization procedure, or how double masking was implemented.

The primary outcome is defined as a composite of stroke, MI or death, with follow-up up to 97 days and a stated censoring rule. Further details about event adjudication, component-specific definitions, and how incomplete assessments were handled are not reported in the registry record. The outcome description refers to participants with an event, while the sponsor’s primary analysis is a Cox regression; additional information about the underlying time-to-event data and model specification is not available.

The registry does not report the covariates used in the Cox model, checks of model assumptions, missing-data methods, or sensitivity analyses. It also does not state whether secondary tests were adjusted for multiplicity, whether the secondary outcomes were prespecified as confirmatory, or how the analyses were prioritized. These gaps limit evaluation of robustness and of the strength of secondary evidence.

The adverse-event summary gives counts and selected serious-event terms, but deaths are not reported there and further safety-analysis details are unavailable. The registry excerpt also does not explain the difference between overall enrollment and the primary-outcome denominators. These reporting limits do not establish that the underlying trial lacked procedures or analyses; they constrain what can be concluded from the registry record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: [SOCRATES -Acute Stroke Or Transient IsChaemic Attack TReated With Aspirin or Ticagrelor and Patient OutcomES] — NCT01994720.
• Registry record last updated 2017-06-12; status last verified 2017-05.
• Results first posted 2017-06-12.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

SOCRATES (NCT01994720) was a completed, randomized, double-blind, parallel-group Phase 3 study sponsored by AstraZeneca. It enrolled 13307 participants with acute ischaemic stroke or transient ischaemic attack and compared ticagrelor with acetylsalicylic acid (aspirin). The stated treatment period was 90 days.

The primary outcome was a composite of stroke, MI or death, assessed from randomization up to 97 days in the full analysis set. The sponsor-reported Cox analysis gave a hazard ratio of 0.89, with a 95% confidence interval from 0.78 to 1.01 and p = 0.067. The unadjusted recalculation from participant counts also had an interval that included its null value.

The posted estimates point toward fewer primary events in the ticagrelor group, but their intervals leave uncertainty about the size and direction of the difference. Details about the original sample-size justification, multiplicity, missing-data handling and several model specifications are not reported in the registry record.