A Comparison of Prasugrel at PCI or Time of Diagnosis of Non-ST Elevation Myocardial Infarction: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Comparison of Prasugrel at PCI or Time of Diagnosis of Non-ST Elevation Myocardial Infarction (NCT01015287), a randomized phase 3 study. The primary outcome is The Percentage of Participants With Occurrence of Cardiovascular (CV) Death, Myocardial Infarction (MI), Stroke, Urgent Revascularization (UR), or Glycoprotein (GP) IIb/IIIa Inhibitor Bailout.

2. Clinical Question

The comparison concerns when prasugrel was started and how its loading dose was divided. It is not a comparison of prasugrel with no prasugrel throughout the study: both strategies included prasugrel at PCI and daily prasugrel maintenance. The key clinical-trial question is whether beginning prasugrel at diagnosis, rather than using placebo at diagnosis and giving the full loading dose at PCI, changed the frequency of the prespecified composite outcome during the stated follow-up period.

3. Trial Design

ACCOAST was a phase 3 randomized, quadruple-masked, parallel-group trial sponsored by Eli Lilly and Company. The registry records enrollment of 4033 participants and describes the condition as acute coronary syndromes. The trial began in 2009-12, had primary completion in 2013-01, and is listed as completed.

Participants were assigned to non-pretreatment or pretreatment. In the non-pretreatment strategy, placebo was given at diagnosis and prasugrel was loaded at PCI. In the pretreatment strategy, prasugrel was started at diagnosis as a 30 mg dose, with another 30 mg at PCI. Both strategies continued with daily prasugrel maintenance for 30 days; the registry describes the maintenance dose as 5 mg or 10 mg.

The primary outcome was assessed from the first loading dose through 7 days after that dose. The primary analysis population is described as all randomized participants who received at least 1 dose of study drug. The primary endpoint is a composite: cardiovascular death, myocardial infarction, stroke, urgent revascularization, or glycoprotein IIb/IIIa inhibitor bailout. The registry states that endpoint events were adjudicated by the Clinical Endpoint Committee.

Random allocation and parallel groups support a comparison of the assigned strategies, while masking is recorded as quadruple. The registry record does not describe how randomization was generated, which roles were masked, or the trial's detailed conduct procedures. It also does not report the original sample-size justification or the full statistical analysis plan.

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:

Analysis population for the primary outcome, as defined in the registry: All randomized participants who received at least 1 dose of study drug.

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.

Population: All randomized participants who received at least 1 dose of study drug.

6. Primary Endpoint

The registry lists the primary outcome as The Percentage of Participants With Occurrence of Cardiovascular (CV) Death, Myocardial Infarction (MI), Stroke, Urgent Revascularization (UR), or Glycoprotein (GP) IIb/IIIa Inhibitor Bailout, measured over First loading dose (LD) through 7 days after first LD.

The primary endpoint is the percentage of participants experiencing at least one of five events: cardiovascular death, myocardial infarction, stroke, urgent revascularization, or glycoprotein IIb/IIIa inhibitor bailout. The timeframe begins at the first loading dose and ends 7 days after the first loading dose. Events were adjudicated by the Clinical Endpoint Committee, as stated in the registry.

This is a composite endpoint: several distinct outcomes are combined into one measure. In general, composite outcomes can capture a wider range of clinically relevant events and may occur more often than any single component. Their interpretation depends on which events are included and how much each component contributes. The registry record does not give component-specific results for the primary endpoint, so the overall percentage does not show which component accounted for the recorded events.

The endpoint is reported as a percentage of participants, rather than as an event rate over person-time. The numerator is the number of participants experiencing a listed event, and the denominator is the number in the treatment arm. The endpoint addresses the early period after the first loading dose; it does not by itself describe outcomes beyond the stated 7-day timeframe. The specified analysis population excludes randomized participants who did not receive at least 1 dose of study drug.

7. Results Posted in the Registry

• Pre-treatment: 10.0% (203/2037) versus 9.8% (195/1996) on control; risk difference 0.2 percentage points (95% CI -1.6 to 2.0), risk ratio 1.02 (0.85–1.23); unadjusted two-proportion z-test p = 0.835.

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.

Percentage of Participants With All-Cause Death, Myocardial Infarction (MI), Stroke, or All Coronary Artery Bypass Graft (CABG) and Non-CABG Thrombolysis in Myocardial Infarction (TIMI) Major Bleeding

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Pre-treatment: 8.6% (176/2037) versus 7.6% (151/1996) on control; risk difference 1.1 percentage points (95% CI -0.6 to 2.8), risk ratio 1.14 (0.93–1.41); unadjusted two-proportion z-test p = 0.211.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pre-treatment and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Incidence of Cardiovascular (CV) Death, Myocardial Infarction (MI), or Stroke Through 30 Days From First Loading Dose (LD)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Pre-treatment: 7.1% (144/2037) versus 7.2% (144/1996) on control; risk difference -0.1 percentage points (95% CI -1.7 to 1.4), risk ratio 0.98 (0.78–1.22); unadjusted two-proportion z-test p = 0.858.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pre-treatment and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Incidence of Cardiovascular (CV) Death or Myocardial Infarction (MI) Through 30 Days From First Loading Dose (LD)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Pre-treatment: 6.6% (135/2037) versus 6.5% (130/1996) on control; risk difference 0.1 percentage points (95% CI -1.4 to 1.6), risk ratio 1.02 (0.81–1.28); unadjusted two-proportion z-test p = 0.883.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pre-treatment and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes broaden the assessment beyond the primary composite and include composites involving death, myocardial infarction, stroke, bleeding, and urgent revascularization, as well as outcomes assessed through 30 days. Across the secondary comparisons with numerical results, the observed differences are small in relation to their uncertainty. Some point estimates favor one assigned strategy and others the other strategy; the overall pattern does not form a consistent directional signal.

This broad pattern is compatible with the primary result, which also has a point estimate close to zero and an interval spanning values on both sides of no difference. The secondary outcomes do not provide a clear, independent resolution of the uncertainty in the primary comparison. Their definitions and follow-up windows differ, so they are related evidence rather than interchangeable versions of the primary endpoint.

General statistical point: multiple outcomes create multiple opportunities for a chance finding. When many endpoints are examined, an isolated nominally unusual result can occur even if there is no underlying effect. Interpretation therefore depends on whether outcomes and analyses were prespecified, whether multiplicity was addressed, and whether findings are consistent across related measures. The registry record does not report a multiplicity adjustment or a hierarchy for secondary outcomes.

The registry record also lists secondary outcomes for which results are not detailed in the posted numerical summaries. Their estimates and uncertainty are not reported in the registry record. The available secondary findings should be treated as supporting context, not as a replacement for the primary comparison or as proof of benefit or harm. In particular, the posted results do not establish that every component or later outcome follows the same pattern as the primary composite.

Because the reported secondary comparisons are unadjusted and no additional analysis results are listed, they carry less inferential weight than a prespecified primary analysis interpreted within a documented statistical plan. Their main contribution is to show whether the broader outcome pattern appears compatible with the primary finding, while leaving uncertainty about multiplicity, analysis choices, and outcomes without posted estimates.

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

• Percentage of Participants With All-Cause Death, Myocardial Infarction (MI), Stroke, or All Coronary Artery Bypass Graft (CABG) and Non-CABG Thrombolysis in Myocardial Infarction (TIMI) Major Bleeding
• Percentage of Participants With Incidence of Cardiovascular (CV) Death, Myocardial Infarction (MI), or Stroke Through 30 Days From First Loading Dose (LD)
• Percentage of Participants With Incidence of Cardiovascular (CV) Death or Myocardial Infarction (MI) Through 30 Days From First Loading Dose (LD)
• Percentage of Participants With Incidence of Cardiovascular (CV) Death, Myocardial Infarction (MI), or Urgent Revascularization (UR) Through 30 Days From First Loading Dose (LD)
• Percentage of Participants With Incidence of Cardiovascular (CV) Death Through 30 Days From First Loading Dose (LD)
• Percentage of Participants With Incidence of Definite or Probable Stent Thrombosis (ST) According to the Academic Research Consortium (ARC) Criteria Through 30 Days From First Loading Dose (LD)
• Percentage of Participants With All-cause Death, Myocardial Infarction (MI), Stroke, or All Coronary Artery Bypass Graft (CABG) and Non-CABG Thrombolysis in Myocardial Infarction (TIMI) Major Bleeding Through 30 Days From First Loading Dose (LD)
• Change in Standardized Troponin From Baseline to Percutaneous Coronary Intervention (PCI)

9. Statistical Interpretation

10. Statistical Methods Explained

What does the percentage measure? The primary outcome is a binary participant-level measure: each participant either experienced at least one listed component during the specified period or did not. The percentage expresses the event count relative to the number of participants in that group. General statistical point: a percentage is an intuitive summary of frequency, but it does not convey uncertainty by itself. The interval estimate adds information about how much uncertainty accompanies the observed group comparison.

What is a risk difference? The risk difference compares the event proportions directly by subtracting one group's risk from the other's. The posted estimate is 0.002 for pretreatment relative to non-pretreatment. General statistical point: a risk difference is measured on the absolute probability scale and retains the direction of the comparison. A value of zero represents equal risks. The confidence interval, -0.016 to 0.020, includes zero, so the observed data are compatible with no difference as well as with values on either side of zero.

How do relative measures differ? The relative risk compares the two event proportions as a ratio, while the odds ratio compares event odds. The posted relative risk is 1.02, with a confidence interval from 0.846 to 1.229; the odds ratio is 1.022, with a confidence interval from 0.831 to 1.257. General statistical point: the no-association value for a ratio is 1, whereas the no-difference value for a risk difference is zero. These measures use different scales, so their numerical values should not be compared as though they represented the same quantity.

What does the p-value describe? The unadjusted p-value for the primary comparison is 0.835. General statistical point: a p-value describes how compatible the observed data are with a specified null model, assuming the model and analysis are appropriate. It is not a measure of the size or clinical importance of an effect, and it does not give the probability that a treatment strategy is effective or ineffective. The registry record does not identify the specific test used to obtain this p-value.

Why distinguish unadjusted from adjusted analyses? An unadjusted comparison uses the group outcome summaries without accounting for additional covariates. An adjusted analysis can incorporate measured characteristics or design variables, depending on its prespecified model. General statistical point: adjustment can change an estimate or its uncertainty, and its validity depends on appropriate model specification and complete reporting. The registry record does not report an adjusted primary result, a list of covariates, or the full analysis plan, so no adjusted interpretation can be made from the posted results.

What does randomization contribute? General statistical point: random allocation is intended to make groups comparable at assignment with respect to both measured and unmeasured prognostic factors, on average. This supports a causal comparison of assigned strategies when follow-up and analysis preserve the randomized comparison. The registry reports randomization, but does not provide details on sequence generation, allocation concealment, adherence, crossovers, or handling of participants without outcome data. Those details matter when judging how closely the reported comparison reflects the randomized assignment.

What is the role of masking and adjudication? The registry records quadruple masking and says that primary endpoint events were adjudicated by the Clinical Endpoint Committee. General statistical point: masking can reduce the influence of knowledge of assignment on participant behavior, care, outcome assessment, or analysis, while independent adjudication can apply defined endpoint criteria consistently. The record does not state which parties were masked or describe the committee's procedures, so the labels alone do not establish how these safeguards operated in practice.

How should composite outcomes be considered? General statistical point: a composite combines multiple event types into one endpoint, which can improve efficiency when events are relatively uncommon, but its overall result may be driven by components that differ in severity or frequency. The primary summary does not report the individual component counts, so it cannot show whether the composite's components moved in the same direction or contributed similarly. Component-level primary results are not reported in the registry record.

What does the time window imply? The primary endpoint covers the period from the first loading dose through 7 days after the first loading dose. Other posted outcomes include periods through 30 days from the first loading dose. General statistical point: a finding in one follow-up window does not automatically describe another window, and results for different endpoints should be interpreted according to their own definitions and timeframes. The primary result is therefore specific to its composite definition, analysis population, and stated early follow-up period.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.002, and its confidence interval extends from -0.016 to 0.020. Because the interval crosses zero, the data do not rule out no difference under this interval-based summary. They also do not rule out differences in either direction within the interval. The estimate is close to zero, but precision is determined by the full interval, not only by the point estimate.

General statistical point: a confidence interval expresses uncertainty around an estimated effect under the assumptions of the method used. It is not a guarantee that the true effect lies within the interval, and it is not a range of observed individual outcomes. The registry record does not state the confidence level or the method used to construct the primary interval, so those details are not reported in the registry record.

The relative risk interval, 0.846 to 1.229, and the odds-ratio interval, 0.831 to 1.257, also include their respective no-association values. These measures reinforce that the estimates are not highly precise enough to determine a single direction of effect. They do not replace the absolute risk-difference summary; each expresses the comparison on a different scale.

There were 1996 participants in the non-pretreatment group and 2037 in the pretreatment group. The primary event counts were 195 and 203, respectively. The record does not report a separate precision analysis for each endpoint component or for subgroups. Thus, the overall interval cannot be used to infer precision for a particular component or participant subgroup.

In general, precision depends on the amount of outcome information and the variability of the observed data, as well as on analysis assumptions. The posted interval is the relevant summary for uncertainty in this primary comparison; the p-value alone would not communicate the range of effects compatible with the data.

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 calculations. The assumptions listed are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario targets a stated fraction of the observed effect. The trial's own sample-size justification and original design assumptions are not reported in the registry record.

For these binary outcomes, the planning figures are participants per arm, not total participants across both arms and not total events. Read a row as the number of participants that would be needed in each arm under the stated effect scenario and assumptions. The 80% power column gives the planned per-arm sample size associated with an 80% chance of detecting the specified effect if that effect and the assumptions were true. The 90% power column gives the corresponding per-arm sample size for a 90% chance. These are design concepts, not guarantees about results.

The rows describe planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. Smaller target effects require more participants to distinguish them from random variation under otherwise unchanged assumptions. Accordingly, the planning figures rise as the target fraction gets smaller. The curve expresses the same general relationship: less separation between groups requires a larger sample to achieve a given planned power.

These figures are not observed power. They do not estimate the probability that the completed trial detected an effect after seeing its results, and they should not be used as a substitute for interpreting the confidence interval. They are hypothetical planning illustrations anchored to the observed effect, whose size is itself uncertain.

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 = 0.098; treatment proportion p₁ = 0.100; average p̄ = 0.099.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4218 = 0.8266.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4218 = 0.3550.
4. n = (0.8266 + 0.3550)² / (0.0020)² = 363,067.9, rounded up to 363,068 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 <- 0.0976953907815631                          # control proportion
p1 <- 0.0996563573883162                          # 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(1015287)
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 = 363,068 (80% power), 486,045 (90% power)
 75% of observed effect: n per arm = 644,027 (80% power), 862,169 (90% power)
 50% of observed effect: n per arm = 1,445,846 (80% power), 1,935,577 (90% power)
power.prop.test: 363067.9 
Simulated power at n = 363,068 per arm: 0.799 (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. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary endpoint and several secondary outcomes, but does not describe a statistical hierarchy, family-wise error procedure, false-discovery procedure, or other multiplicity strategy. It also does not report a complete statistical analysis plan. These procedures are not reported in the registry record, so it is not possible to determine whether a formal adjustment was planned or used.

General statistical point: testing multiple outcomes increases the chance that at least one result may appear notable by chance. A prespecified hierarchy or multiplicity adjustment can help control how such results are interpreted. Without documentation of that approach, secondary p-values should be read as unadjusted and exploratory rather than as definitive evidence. The registry does not list additional reported analyses for the secondary outcomes.

The primary analysis population is described as all randomized participants who received at least 1 dose of study drug. That description excludes randomized participants who received no study drug, but the registry record does not report how many participants, if any, fell into that category. It does not explain how missing primary outcome data were handled, whether participants were analyzed according to assigned group regardless of adherence, or how treatment discontinuations and crossovers were addressed.

These omissions matter because analysis populations and missing-data methods can affect the interpretation of a randomized comparison. General statistical point: missing outcomes can introduce bias if the probability of missingness is related to participant prognosis or outcome, and different assumptions or methods can lead to different estimates. No missing-data strategy, sensitivity analysis, or imputation method is reported in the registry record.

The record does state that primary endpoint events were adjudicated by the Clinical Endpoint Committee and that masking was quadruple. It does not provide the adjudication procedures, the roles masked, or the operational details needed to assess those safeguards further. Overall, the available reporting supports interpretation of the posted unadjusted group summaries, but does not resolve multiplicity, missing-data, or analysis-population questions beyond the stated primary population.

15. 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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: percutaneous coronary intervention (0.8%), myocardial infarction (0.7%), chest pain (0.4%), cardiogenic shock (0.3%), ventricular fibrillation (0.3%).

The registry records serious adverse events for 167 of 1996 participants in the non-pretreatment group and 206 of 2037 participants in the pretreatment group. Other adverse events are recorded for 860 of 1996 and 876 of 2037 participants, respectively. These are counts recorded in the groups; they are not the primary efficacy endpoint and should not be interpreted as a causal comparison without additional safety analysis details.

The most frequent serious adverse-event terms listed are percutaneous coronary intervention at 0.8%, myocardial infarction at 0.7%, chest pain at 0.4%, cardiogenic shock at 0.3%, ventricular fibrillation at 0.3%, and acute myocardial infarction at 0.3%. The record does not provide arm-specific rates for these terms in the summary, so the listed percentages do not establish a between-group difference for any individual event.

Deaths are not reported in the adverse-event summary. The registry record does not explain the event-collection period, seriousness criteria, attribution to study drug, or the handling of repeated events. These limitations mean the counts are descriptive and do not, by themselves, identify cause or comparative safety.

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

The posted primary result describes the frequency of a composite outcome in two randomized strategies for timing prasugrel around diagnosis and PCI. The group percentages were 9.77% and 9.97%, and the estimated unadjusted risk difference was 0.002. Its confidence interval, -0.016 to 0.020, includes zero and spans effects in either direction. The result therefore does not provide a precise estimate that distinguishes the strategies on this endpoint.

This does not establish equivalence. Demonstrating equivalence or noninferiority generally requires a prespecified margin and an analysis designed for that question. Such a margin and a corresponding analysis are not reported in the registry record. Similarly, a non-significant p-value does not prove that the strategies have the same effect. The result should be described as an uncertain comparison, rather than as evidence that the strategies are identical.

The result is specific to the endpoint components, analysis population, and follow-up period recorded for the primary outcome. It does not identify the contribution of each component, describe outcomes outside that timeframe, or establish how results apply to populations not represented in the trial. The registry record also does not report subgroup estimates, so no subgroup-specific conclusion can be drawn from these summaries.

The secondary outcomes provide additional descriptive context, but their unadjusted status and the absence of a reported multiplicity plan limit the weight that can be placed on individual findings. The adverse-event counts are also descriptive; they do not provide a complete comparative safety analysis, particularly because death counts and details of event collection are not reported.

General statistical point: an estimate, its uncertainty, the endpoint definition, and the analysis plan all contribute to interpretation. A point estimate alone cannot establish clinical importance, while a p-value alone cannot establish the probability of benefit or harm. The posted data support a cautious account of the observed groups and their uncertainty, not a medical recommendation.

17. Why This Trial Matters Statistically

Statistically, ACCOAST illustrates the importance of separating the estimated effect from the precision of that estimate. The primary point estimate is close to zero, but the confidence interval is the more informative guide to the range of effects compatible with the posted comparison. Because it crosses zero and extends in both directions, the data do not settle the direction or magnitude of a difference.

The trial also highlights how endpoint construction shapes interpretation. A composite can bring several event types into a single outcome, but the overall percentage does not reveal which component contributed most. Without component-level primary results, readers cannot determine whether the composite reflects a consistent pattern across its elements or is dominated by one type of event.

Timing is another key design feature. The strategies differed in whether prasugrel began at diagnosis or whether placebo was used at diagnosis and the loading dose delayed until PCI. Both strategies included prasugrel at PCI and daily maintenance. Making that distinction explicit prevents the comparison from being mistaken for prasugrel versus no prasugrel.

Finally, the registry's incomplete reporting of the original sample-size justification, multiplicity handling, missing-data methods, and detailed analysis plan shows why outcome estimates should be read alongside documentation of how they were planned and analyzed. The observed results can be described, but the record leaves important questions about the inferential framework unanswered.

18. 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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record does not report the original sample-size assumptions or justification, so the planning illustrations based on the observed effect should not be confused with the trial's own design calculations. The record also does not provide a complete statistical analysis plan, the method for the primary confidence interval, or the test used for the unadjusted p-value.

The primary outcome is composite, yet component-specific primary results are not reported. This prevents assessment of whether cardiovascular death, myocardial infarction, stroke, urgent revascularization, and glycoprotein IIb/IIIa inhibitor bailout contributed similarly or differently to the total. The primary follow-up is limited to the period through 7 days after the first loading dose; it does not answer questions about outcomes outside that timeframe.

The registry does not report missing-data handling, protocol deviations, adherence, crossovers, or an intention-to-treat analysis description. It defines the primary population as randomized participants who received at least 1 dose of study drug, but does not state how many participants were excluded by that condition or whether any outcome data were missing.

Multiplicity procedures and a hierarchy for secondary outcomes are not reported. The posted secondary comparisons therefore require caution, particularly when considered individually. Some listed secondary outcomes do not have numerical estimates in the posted summaries, and the record does not supply subgroup analyses.

Safety reporting is also limited in the summary: deaths are not reported, serious-event term percentages are not presented by treatment group, and adverse-event collection and attribution details are not described. The record's quadruple-masking label does not specify which roles were masked. These reporting gaps do not negate the recorded findings, but they limit how fully the trial's conduct, analysis, and safety profile can be assessed.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Comparison of Prasugrel at PCI or Time of Diagnosis of Non-ST Elevation Myocardial Infarction — NCT01015287.
• Registry record last updated 2014-02-28; status last verified 2014-01.
• Results first posted 2014-02-28.
• 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.

22. Record Summary

ACCOAST was a completed phase 3 randomized, quadruple-masked, parallel-group trial with 4033 participants. It compared split-dose prasugrel beginning at diagnosis with placebo at diagnosis followed by a prasugrel loading dose at PCI; both strategies included daily maintenance prasugrel for 30 days.

The primary outcome was a composite of cardiovascular death, myocardial infarction, stroke, urgent revascularization, or glycoprotein IIb/IIIa inhibitor bailout through 7 days after the first loading dose. The observed group percentages were 9.77% and 9.97%. The unadjusted risk difference was 0.002, with a confidence interval from -0.016 to 0.020 and an unadjusted p-value of 0.835.

The posted result is compatible with differences in either direction and does not establish equivalence. Interpretation is limited by missing details about the original design assumptions, full statistical plan, multiplicity, and missing-data handling.