Ticagrelor in Severe Community Acquired Pneumonia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Ticagrelor in Severe Community Acquired Pneumonia (NCT01998399), a randomized phase 2 study. The primary outcome is All-cause Mortality.

2. Clinical Question

The registry describes the question as whether ticagrelor would be an effective treatment for patients with severe community acquired pneumonia, with mortality as the primary objective. Statistically, the posted outcome is a comparison of the number of participants who died during the stated study period. The reported counts are four participants in the ticagrelor group and two in the placebo group. These counts describe the observed trial results; they do not by themselves establish whether the groups differ beyond what could plausibly arise from sampling variation. The trial was randomized, which is intended to support a fair comparison of assigned groups, but the small enrollment and the uncertainty around the estimated difference matter when interpreting the result. The registry does not report further eligibility criteria, the original sample-size rationale, or details about the analysis population.

3. Trial Design

The registry describes a randomized, quadruple-masked, parallel-group phase 2 trial of ticagrelor versus placebo in severe community acquired pneumonia. The recorded enrollment was 25. The trial status is terminated; the registry does not report the reason for termination. The study start is recorded as 2014-08 and primary completion as 2015-12.

The ticagrelor regimen was a 180 mg loading dose followed by 90 mg BID for 90 days. The placebo regimen is described using the same loading-dose and subsequent-dose schedule. The primary endpoint was all-cause mortality during the 90-day study period. Other outcomes named in the registry include shock-free days, ventilator-free days, in-hospital mortality, hospital-free days, stroke, a combined outcome of stroke, myocardial infarct, and mortality, and myocardial infarction.

Randomization means treatment assignment was determined by chance rather than by a clinician selecting a group. Masking is intended to limit the influence of knowledge of assigned treatment on care, outcome assessment, or other trial processes; the registry labels the masking quadruple but does not specify which roles were masked. A parallel design means the assigned groups were followed as separate groups rather than participants switching between assigned treatments. These general design features support interpretation of the group comparison, but they do not remove uncertainty from a small trial. The registry record does not report the randomization procedure, allocation concealment details, or the original design assumptions.

The registry names Gordon Bernard as sponsor. It does not report the reason the trial was terminated, or whether termination was related to recruitment, safety, efficacy, or another consideration. No explanation should be inferred from the status alone.

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.

Overall Study

Reasons for not completing this period:

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 All-cause Mortality, measured over 90 days.

The primary endpoint is all-cause mortality, defined in the registry as death during the 90-day study period. The outcome is expressed as the number of participants with the event. The posted results record four deaths among participants assigned to ticagrelor and two among participants assigned to placebo. The corresponding group sizes in the primary outcome record are 12 and 13.

Mortality is a direct, clinically important outcome because it records whether a participant died during the specified follow-up period, without restricting the event to a particular cause. Using all-cause mortality avoids the need to classify deaths by cause for this endpoint. The time window is part of the definition: deaths outside the 90-day study period are not what this endpoint describes.

As a binary outcome, each participant is classified according to whether the event occurred within the defined period. The event counts can be compared between groups, while an effect estimate and its confidence interval convey the direction and precision of that comparison. A count alone does not show how uncertain the group difference is. The registry record does not report additional endpoint-adjudication details or further information about how deaths were ascertained.

7. Results Posted in the Registry

• Ticagrelor: 33.3% (4/12) versus 15.4% (2/13) on control; risk difference 17.9 percentage points (95% CI -15.2 to 51.1), risk ratio 2.17 (0.48–9.76); unadjusted two-proportion z-test p = 0.294.

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.

In-hospital Mortality

• 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:
  • Ticagrelor: 16.7% (2/12) versus 15.4% (2/13) on control; risk difference 1.3 percentage points (95% CI -27.5 to 30.1), risk ratio 1.08 (0.18–6.53); unadjusted two-proportion z-test p = 0.930.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ticagrelor and the control. The interval gives the range of effects that remain compatible with the data.

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:
  • Ticagrelor: 8.3% (1/12) versus 0.0% (0/13) on control; risk difference 8.3 percentage points (95% CI -7.3 to 24.0); unadjusted two-proportion z-test p = 0.288.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ticagrelor and the control. The interval gives the range of effects that remain compatible with the data.

Stroke, Myocardial Infarct, Mortality

• 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:
  • Ticagrelor: 41.7% (5/12) versus 15.4% (2/13) on control; risk difference 26.3 percentage points (95% CI -7.8 to 60.4), risk ratio 2.71 (0.64–11.43); unadjusted two-proportion z-test p = 0.144.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ticagrelor and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes span mortality, stroke, a combined outcome involving stroke, myocardial infarct and mortality, and outcomes related to days free of shock, ventilation, or hospitalization. The posted numerical results include in-hospital mortality, stroke, and the combined outcome. Numerical results for shock-free days, ventilator-free days, hospital-free days, and myocardial infarction are not reported in the registry record.

Across the posted secondary outcomes, the observed group patterns are not uniform. The in-hospital mortality counts are equal between groups, while stroke and the combined outcome have more observed events in the ticagrelor group. The associated recalculated intervals are broad and include no difference. These secondary findings do not resolve the uncertainty in the primary 90-day mortality comparison, and they should not be treated as independent confirmation of a treatment effect.

Secondary outcomes often help describe other aspects of a trial, but examining multiple outcomes creates more opportunities for apparently notable results to arise by chance. The registry record does not report whether a multiplicity adjustment, testing hierarchy, or other prespecified strategy was used. Without such information, unadjusted secondary results carry less inferential weight than a primary result designated in advance, and individual secondary comparisons warrant cautious interpretation.

The primary and secondary outcomes also differ in definition and, in some cases, follow-up period. Their estimates therefore answer different questions rather than providing interchangeable measures of one effect. The registry does not report enough detail to determine how the unposted secondary outcomes were analyzed or whether they were collected but not reported.

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

• Shock Free Days
• Ventilator Free Days
• In-hospital Mortality
• Hospital Free Days
• Stroke
• Stroke, Myocardial Infarct, Mortality
• Myocardial Infarction

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: a participant either died during the 90-day study period or did not. The registry reports the number with the event and the number in each group. A risk is the event count relative to the group size. The recalculated risk difference compares those group risks, with the direction defined as ticagrelor minus placebo. A positive value therefore indicates a higher observed risk in the ticagrelor group; a negative value would indicate a lower observed risk in that group. The primary recalculated risk difference is 0.179.

A risk difference is an absolute contrast on the risk scale. It preserves the comparison in the units of probability rather than expressing a relative increase or decrease. The posted confidence interval for this estimate ranges from -0.152 to 0.511. Because the interval includes zero, it does not isolate a single direction of difference. Its breadth also indicates substantial uncertainty in the magnitude of the group contrast.

The posted recalculated relative risk for the primary endpoint is 2.167, with a confidence interval from 0.481 to 9.76. A relative risk compares the risk in one group with the risk in the other, rather than subtracting them. It is a different way of expressing the contrast, and its interval is also broad. Estimates on different scales can help describe the same observed data, but they do not remove the uncertainty reflected in the small event counts.

The unadjusted recalculated p-value for the primary comparison is 0.294. A p-value is calculated under a statistical model that represents a null hypothesis of no group difference. It indicates how unusual data at least as inconsistent with that null model would be if the model and its assumptions held. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. A p-value should therefore be read alongside the estimated contrast and confidence interval.

The registry separately reports a chi-squared analysis with p = 0.41. This is the sponsor-reported analysis for the primary comparison. The recalculated p-value is an unadjusted recalculation from posted summary statistics, and the two reported values are not identical. The record does not give additional details about the sponsor's analysis beyond naming the chi-squared method.

What does the confidence interval add?

A confidence interval communicates a range of estimates compatible with the observed data under the method used to construct it. In repeated use of a valid interval procedure, its stated coverage has a long-run interpretation; it is not a probability statement about a fixed effect after the interval has been calculated. In this trial, the interval's inclusion of zero and its breadth both matter: the estimate does not clearly establish the direction of the difference, and the magnitude remains uncertain.

Why are the event counts important?

With few observed events, a change in one participant's outcome can have a substantial influence on a group comparison. This makes estimates more sensitive to the particular outcomes observed in a small study. The intervals reflect that imprecision. The counts are useful for understanding what happened in the trial, but they do not provide the precision needed for a strong conclusion on their own.

Why distinguish sponsor and recalculated analyses?

The sponsor-reported result is the analysis recorded by the registry, while a recalculated result is an unadjusted calculation from the posted summary statistics. They can be described together, but should not be presented as if they were one analysis. The registry record does not report enough detail to reconcile their numerical difference or to establish whether other analytic choices were made. The discrepancy indicator is false, so the record does not flag a discrepancy between the sponsor result and the posted outcome in its own discrepancy assessment.

All statistical interpretations depend on the outcomes and group sizes as recorded, and on assumptions of the analysis. Further details about handling missing outcomes, analysis populations, covariate adjustment, or outcome adjudication are not reported in the registry record.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.179, with a confidence interval from -0.152 to 0.511. The interval includes zero, so the results do not pin down whether the underlying group difference is positive or negative. It also spans a wide range of values, which means the magnitude is not estimated precisely.

A confidence interval is useful because a point estimate alone can give a false impression of certainty. The point estimate is the value calculated from the observed groups; the interval expresses the uncertainty around that estimate under the interval method. It is not a guarantee that the true value lies in the interval, nor is it a probability distribution over possible treatment effects. Its interpretation depends on the method and assumptions used.

The relative-risk estimate is 2.167, with a confidence interval from 0.481 to 9.76. This interval also covers a broad range, including values on either side of no relative difference. Both the absolute and relative comparisons therefore convey substantial uncertainty. The primary event counts are small, and such counts generally provide limited information for estimating a difference precisely.

The confidence interval should be considered with the trial design and outcome definition. It pertains to all-cause mortality during the 90-day study period, not to other outcomes or follow-up periods. The registry record does not report the original precision target or sample-size rationale, so the observed interval cannot be compared with a stated design goal.

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 participants per arm, not total participants and not total events. They are illustrations based on the observed primary effect, not the trial's original design assumptions. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each scenario uses the stated fraction of the observed effect.

For 100% of the observed effect, the planning illustration gives 89 participants per arm for 80% power and 119 participants per arm for 90% power. For 75% of the observed effect, it gives 149 participants per arm for 80% power and 198 participants per arm for 90% power. For 50% of the observed effect, it gives 310 participants per arm for 80% power and 414 participants per arm for 90% power.

In general, a power target describes the chance that a planned study would detect an effect of a specified size if that effect were real and the planning assumptions held. The 90% column targets a greater chance of detecting the specified effect than the 80% column, and therefore requires more participants per arm in these illustrations. Smaller effects are harder to distinguish from random variation, so the figures increase as the assumed effect becomes a smaller fraction of the observed effect.

These are planning illustrations, not observed power. They should not be read as evidence that the trial had a particular chance of finding an effect after its results were known. The registry record does not report the trial's original sample-size justification or its original design assumptions.

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 = 0.154; treatment proportion p₁ = 0.333; average p̄ = 0.244.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6070 = 1.1898.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5936 = 0.4996.
4. n = (1.1898 + 0.4996)² / (0.1795)² = 88.6, rounded up to 89 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 <- 0.153846153846154                          # control proportion
p1 <- 0.333333333333333                          # 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(1998399)
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 = 89 (80% power), 119 (90% power)
 75% of observed effect: n per arm = 149 (80% power), 198 (90% power)
 50% of observed effect: n per arm = 310 (80% power), 414 (90% power)
power.prop.test: 88.6 
Simulated power at n = 89 per arm: 0.807 (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 registry reports a sponsor analysis using a chi-squared method, with p = 0.41. The recalculated unadjusted analysis from the posted summary statistics gives p = 0.294 and a risk-difference estimate of 0.179, with a confidence interval from -0.152 to 0.511. The recalculated estimate and interval help describe the observed group contrast and its uncertainty; the sponsor-reported p-value is the analysis recorded by the registry.

The p-values are not identical, and the registry does not report sufficient additional detail to explain the difference. They should be kept distinct rather than combined or described as repeated versions of the same calculation. The recalculated result is not a substitute for an analysis plan or a fuller trial report. The registry record does not report further specifications of the sponsor's analysis beyond the chi-squared method and its p-value.

The discrepancy indicator is false. Accordingly, the record does not flag the posted results as discrepant from the sponsor analysis. That status does not make the two p-values numerically identical; it simply means the record does not identify a discrepancy under its own assessment. Interpretation should consider the observed counts, effect estimate, interval, and sponsor-reported analysis together.

15. Multiplicity, Missing Data and Analysis Populations

The registry names several secondary outcomes in addition to the primary mortality endpoint. When investigators evaluate multiple outcomes or make multiple statistical comparisons, the chance of observing an apparently unusual result by chance can increase. A prespecified strategy can address this concern, for example by defining an order for testing or adjusting the threshold used for inference. The registry record does not report whether any such multiplicity strategy was planned or used.

The record reports one primary analysis and a chi-squared method with p = 0.41. It does not report a full statistical analysis plan, whether the primary analysis was adjusted for other variables, or whether secondary outcomes were considered exploratory. The absence of these details in the registry should not be taken as evidence that no plan existed; the relevant information is simply not reported in the registry record.

Missing-data handling and analysis populations are also not reported in the registry record. It is not stated whether all randomized participants were included in each analysis, how participants with missing outcome data were handled, or whether any imputation or sensitivity analyses were performed. The primary outcome counts and group sizes are posted, but those numbers alone do not document how missing data or analysis-population definitions were addressed.

The record also does not report details about protocol deviations, outcome adjudication, or interim analyses. These omissions limit the ability to assess whether the posted results follow a prespecified analysis approach or how robust the conclusions are to alternative decisions. No assumptions about these procedures should be made from the results alone.

Because the trial was terminated, it may be especially relevant to understand the planned analysis and reason for termination when interpreting the record. The reason is not reported in the registry record, and it would be inappropriate to infer whether it affected recruitment, follow-up, or analysis. The available information supports description of the posted estimates, but not a complete audit of the conduct or analysis plan.

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: acute respiratory failure (8.3%), type ii mi (8.3%), subarachnoid hemorrhage (8.3%), complicated para-pneumonic effusion (8.3%), deep vein thrombosis-right leg (8.3%).

The adverse-event record reports serious adverse events affecting 5 of 12 participants in the ticagrelor group and 1 of 13 participants in the placebo group. Other adverse events are reported for 4 of 12 participants assigned to ticagrelor and 1 of 13 assigned to placebo. These are participant counts in the recorded groups; the figures should not be added together because the record does not say that the categories are mutually exclusive.

The registry lists acute respiratory failure, type II MI, subarachnoid hemorrhage, complicated para-pneumonic effusion, deep vein thrombosis-right leg, and urinary tract infection among the top serious terms. Each listed term is reported as 8.3%. The record does not identify a group for each listed term in this summary, so these percentages should not be assigned to one treatment group without further information.

These figures describe reported events in a small trial and are not, on their own, a complete comparison of safety. The record does not report deaths in the adverse-event data, and deaths are not reported there. Event definitions, severity grading details, and the relationship of events to assigned treatment are not reported in the registry record. The observed counts should therefore be read descriptively, without inferring causation.

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

The posted results answer a narrow statistical question: what mortality counts were observed in the randomized groups during the specified 90-day period, and how uncertain is the estimated difference? The record reports more deaths in the ticagrelor group than in the placebo group, but the recalculated risk-difference interval is wide and includes zero. The result therefore does not establish a clear direction or magnitude of a group difference.

A non-significant or uncertain result is not proof that the groups are equivalent. Equivalence requires a design and analysis that define an acceptable range of differences and assess whether the data rule out differences beyond that range. Such an equivalence objective is not reported in the registry record. Similarly, the observed direction of the point estimate does not prove that treatment caused an increase in mortality.

The p-values do not measure the probability that the treatment works or that the result arose by chance. They also do not express clinical importance. The effect estimate and its interval are more informative about the range of differences compatible with the data, while the trial's design, sample size, endpoint definition, and analysis details shape how much confidence can be placed in the result.

The trial was randomized and masked, but its recorded enrollment was 25 and the primary result is imprecise. The registry does not report the reason for termination, the original sample-size justification, or important details of missing-data and analysis-population handling. Those limitations mean the registry results should be understood as a limited account of one trial, not as a complete basis for clinical decisions or a definitive answer about treatment effects.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate should not be interpreted in isolation. The primary risk difference is positive, but its confidence interval extends across zero and covers a broad range. The observed direction is a description of the sample, while the interval shows that the data leave substantial uncertainty about the underlying difference.

It also illustrates how small event counts can make binary-outcome comparisons unstable. When relatively few participants experience the event, each observed outcome contributes meaningfully to the estimate. The group counts are essential context, and the interval helps communicate the resulting imprecision.

The record offers another useful statistical lesson: analyses of the same trial can be reported in different forms. The sponsor reports a chi-squared p-value, while the unadjusted recalculation reports a risk difference, confidence interval, and a different p-value. These outputs need to be distinguished and interpreted according to what each represents. A p-value alone cannot convey the estimated magnitude or its precision.

Finally, the trial includes multiple secondary outcomes, but the registry does not report a multiplicity strategy or complete analysis details. This makes it important to distinguish the primary question from exploratory patterns across additional outcomes. The record is useful for understanding the observed data, while its reporting gaps and uncertainty show why registration results should be interpreted carefully rather than treated as a conclusive answer.

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 recorded enrollment was 25, and the primary comparison includes few events. The resulting estimate is imprecise, as reflected by the wide confidence interval. The trial status is terminated, but the reason for termination is not reported in the registry record. It is therefore not possible to assess whether termination affected recruitment, follow-up, or the planned analysis.

The registry record does not report the original sample-size justification or the trial's own design assumptions. The planning illustrations based on the observed effect do not fill that gap. Details about eligibility criteria, randomization procedures, allocation concealment, and which roles were masked are also not reported beyond the high-level design labels.

Information about missing outcomes, the analysis population, protocol deviations, and sensitivity analyses is not reported. The record also does not provide a full statistical analysis plan or describe any approach to multiplicity across the primary and secondary outcomes. These omissions restrict assessment of how the reported analyses relate to prespecified methods.

Several secondary outcomes are named, but numerical results for shock-free days, ventilator-free days, hospital-free days, and myocardial infarction are not reported in the registry record. Adverse-event details are also limited: the record does not provide event-level attribution to treatment in the summary, and adverse-event deaths are not reported. These limitations are specific to what the registry record documents; they do not establish that the information was not collected elsewhere.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Ticagrelor in Severe Community Acquired Pneumonia — NCT01998399.
• Registry record last updated 2017-12-11; status last verified 2017-11.
• Results first posted 2016-03-11.
• 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

The registry describes NCT01998399, a randomized, quadruple-masked, parallel-group phase 2 trial of ticagrelor versus placebo in severe community acquired pneumonia. Recorded enrollment was 25; the status is terminated. The primary outcome was all-cause mortality during the 90-day study period.

The primary outcome record reports four deaths among 12 participants in the ticagrelor group and two among 13 in the placebo group. The recalculated risk difference is 0.179, with a confidence interval from -0.152 to 0.511. The sponsor-reported chi-squared analysis has p = 0.41; the unadjusted recalculated p-value is 0.294.

The record lists secondary outcomes and adverse events, but does not report several analysis and design details, including the original sample-size justification, the reason for termination, missing-data handling, and a multiplicity strategy. The results describe the observed trial data but leave substantial uncertainty about the primary comparison.