Ticagrelor and Eptifibatide Bolus-Only Versus Ticagrelor and Eptifibatide Bolus Plus Abbreviated Infusion: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Ticagrelor and Eptifibatide Bolus-Only Versus Ticagrelor and Eptifibatide Bolus Plus Abbreviated Infusion (NCT01919723), a randomized phase 2 study. The primary outcome is Change in Percent Inhibition of Platelet Aggregation (%IPA).

2. Clinical Question

The central comparison is the added abbreviated eptifibatide infusion, since the two groups both received ticagrelor and the same eptifibatide boluses. The primary outcome is a laboratory measure of platelet response rather than a clinical event. The registry also lists bleeding complications and periprocedural myocardial infarction as secondary outcomes, each assessed up to 24 hours. Those outcomes address clinical events over a short timeframe, while the primary endpoint addresses pharmacodynamic response at 2 hours.

The posted results describe outcome data for 33 participants in each group. The registry record lists enrollment of 70, but the outcome description specifically says that two subjects in each arm did not meet inclusion criteria because of hemolyzed blood and lacked primary and secondary outcome data. The record does not explain further how the enrollment figure relates to the outcome counts.

3. Trial Design

This was a randomized, phase 2, parallel-group trial sponsored by the University of Alabama at Birmingham. The registry record describes the study as completed, with a start date of 2014-02 and primary completion in 2015-12. Its title and brief description identify the comparison as ticagrelor and eptifibatide bolus-only versus the same drugs with an abbreviated eptifibatide infusion after cardiac catheterization in patients undergoing non-emergent percutaneous coronary intervention.

Both groups received ticagrelor 180 mg i.v. and two eptifibatide boluses of 180µg/Kg, 10 minutes apart. In the bolus-plus-infusion group, eptifibatide was then infused at 2µg/Kg/min for 2 hours. The primary endpoint was change from baseline in %IPA at 2 hours. The registry lists 70 as enrollment, while the outcome results include 33 participants in each group; the endpoint description identifies two participants in each arm whose hemolyzed blood samples meant their outcomes were unavailable.

The trial was unmasked. The registry record does not report the method used to generate the random sequence, how allocation was concealed, or whether laboratory staff assessing platelet response were masked. The parallel model means participants were assigned to a group rather than crossing between both regimens, but the record does not describe the timing or procedures for assignment beyond identifying the trial as randomized.

The registry lists high on-treatment platelet reactivity, bleeding complications, and periprocedural myocardial infarction among secondary outcomes. The endpoint results include bleeding complications and periprocedural myocardial infarction at up to 24 hours. Further detail about assessment procedures, adjudication, and the definition of each clinical event is not reported in the registry record. The trial's original sample-size calculation, enrollment target rationale, and planned statistical analysis are also not reported in the registry record.

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: 2 subjects in each arm did not meet the inclusion criteria (blood hemolyzed) and thus we do not have the primary and secondary outcomes for them.

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 Change in Percent Inhibition of Platelet Aggregation (%IPA), measured over Baseline and 2 hours.

The primary endpoint is change from baseline in percent inhibition of platelet aggregation (%IPA), assessed at 2 hours after stimulation with 20µM ADP. Blood was measured using an aggregometer. The registry describes the result as a mean and gives standard deviation as the measure of spread. In simple terms, %IPA represents the platelet inhibition observed in the laboratory assay; the change-from-baseline endpoint focuses on how the measurement differs at follow-up from the participant's baseline measurement.

This is a pharmacodynamic endpoint: it assesses a biological response to the drug regimen rather than a clinical outcome such as bleeding or myocardial infarction. Such a measure can be useful for comparing how regimens affect platelet activity over a specified period. It does not, on its own, establish whether participants experience better or worse clinical outcomes. The registry's secondary outcomes provide separate clinical event measures, but they have different meanings and are assessed over a short timeframe.

For the reported primary results, the mean was 99.59 in the bolus group and 99.88 in the bolus-plus-infusion group. The comparison is expressed as the mean difference for the infusion group relative to the bolus group. Because the outcome is a change from baseline, interpretation depends on the stated endpoint definition and units; the registry labels the unit as percentage of IPA. More detailed information about the assay's measurement properties, clinical interpretation thresholds, or a prespecified meaningful difference is not reported in the registry record.

7. Results Posted in the Registry

• Ticagrelor & Eptifibatide Bolus+Infusion: mean 99.88 versus 99.59 on control; difference 0.29 (95% CI -0.08 to 0.66), standardized effect d = 0.38; z-test p = 0.126.

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.

Bleeding Complications

• 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 & Eptifibatide Bolus+Infusion: 3.0% (1/33) versus 0.0% (0/33) on control; risk difference 3.0 percentage points (95% CI -2.8 to 8.9); unadjusted two-proportion z-test p = 0.314.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ticagrelor & Eptifibatide Bolus+Infusion and the control. The interval gives the range of effects that remain compatible with the data.

Periprocedural Myocardial Infarction (PMI)

• 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 & Eptifibatide Bolus+Infusion: 21.2% (7/33) versus 27.3% (9/33) on control; risk difference -6.1 percentage points (95% CI -26.7 to 14.6), risk ratio 0.78 (0.33–1.84); unadjusted two-proportion z-test p = 0.566.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ticagrelor & Eptifibatide Bolus+Infusion and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary endpoints cover clinical events rather than the laboratory platelet-response measure used as the primary endpoint. Both bleeding complications and periprocedural myocardial infarction are assessed within up to 24 hours. Across these outcomes, the reported event counts are small, and the unadjusted uncertainty intervals include no difference. Taken together, the secondary results do not provide a precise or consistent basis for distinguishing the two regimens on short-term clinical events.

These outcomes relate to the primary result by addressing a different layer of the study question. The primary endpoint measures pharmacodynamic response at 2 hours, while the secondary endpoints record clinical events over a short follow-up period. A laboratory change cannot be assumed to predict a clinical event, and the registry does not report an analysis linking individual %IPA results to bleeding or myocardial infarction. Therefore, the secondary findings neither validate nor negate the primary endpoint result.

All secondary comparisons are unadjusted in the posted results. In general, when several outcomes are examined, the chance of encountering a striking result by chance can increase, especially if no prespecified hierarchy or multiplicity adjustment is used. Conversely, a non-significant result for a sparse outcome can be inconclusive rather than evidence of no effect. The registry record does not report a multiplicity plan, a hierarchy among outcomes, or a complete statistical analysis plan. This makes the secondary results more exploratory in interpretation than a single prespecified primary comparison.

The registry lists high on-treatment platelet reactivity as a secondary outcome, but the posted endpoint results do not include a result for it. Its definition, group values, and analysis are not reported in the registry record. The overall secondary pattern should therefore be understood as limited to the posted bleeding and periprocedural myocardial infarction results, without assuming that unreported outcomes were measured or showed any particular pattern.

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

• High On-treatment Platelet Reactivity (HPR)
• Bleeding Complications
• Periprocedural Myocardial Infarction (PMI)

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary comparison is between two independent parallel groups. Each participant contributes to the group assigned, and the principal summary is the group mean for a continuous measurement. The registry reports means, standard deviations, a mean difference, a confidence interval, and an unadjusted p-value. This is a straightforward way to describe the average observed contrast, while the standard deviations describe how much individual measurements varied within each group.

What does a mean difference represent?

In general, a mean difference subtracts the comparator group's mean from the intervention group's mean. Here, the registry's contrast is for ticagrelor and eptifibatide bolus plus infusion relative to ticagrelor and eptifibatide bolus alone. The posted estimate is 0.29, so the observed mean is higher in the bolus-plus-infusion group. The estimate describes the observed average contrast; it does not by itself establish that the regimens differ in the wider population or that any difference is clinically important.

The standard deviations are 0.43 and 1.0. In general, a standard deviation describes the spread of observations around a group mean, whereas a standard error describes uncertainty in an estimated mean or contrast. These are not interchangeable. The registry also reports standard errors for each group mean, but the exact method used to calculate the comparison and its interval is not reported in the registry record. The reported comparison is therefore best interpreted as the result posted by the registry, rather than as an opportunity to infer an unreported analysis plan.

How should the p-value be understood?

The primary unadjusted p-value is 0.126. In general, a p-value describes how compatible the observed data are with a specified null model, under the assumptions of the test used. It is not the probability that the null hypothesis is true, nor is it a measure of effect size. A p-value above a conventional cutoff does not prove that the groups are identical. The registry record does not identify the exact test, whether it was one- or two-sided, or any adjustment used for this primary comparison. The planning illustration refers to a two-sided significance level of 0.05, but that planning assumption should not be treated as confirmation of the trial's original analysis plan.

The comparison is unadjusted. In general, an unadjusted analysis reports the contrast without accounting for other variables or for the number of outcomes examined. No adjusted primary estimate or model covariates are reported in the registry record. Consequently, it is not possible to assess whether adjustment for baseline characteristics, stratification factors, or other design features was planned or performed.

Why does over-dispersion matter?

In general, over-dispersion occurs when the variation in observed data is greater than a statistical model assumes. A model that understates variability can make uncertainty look smaller than it is. This issue is especially relevant to count outcomes or clustered data when a model relies on restrictive variance assumptions. The primary endpoint is continuous, and the registry reports group standard deviations; it does not report a model-based analysis that allows for over-dispersion. The record also does not provide individual-level values or enough detail to assess distributional assumptions, outliers, or whether the variance differs materially by group. The presence or impact of over-dispersion is therefore not reported in the registry record and should not be inferred from the summaries alone.

For the binary secondary outcomes, small event counts mean that estimates can be imprecise. In general, a risk difference contrasts the observed proportions in two groups, while a risk ratio compares those proportions as a ratio. The registry posts risk differences for the two secondary comparisons and also posts risk ratio and odds ratio summaries for periprocedural myocardial infarction. These measures answer related but distinct questions, and their uncertainty is important when event counts are sparse. No adjusted regression model or detailed method for interval estimation is reported in the registry record.

What can be inferred about missing outcomes?

The primary endpoint description says two subjects in each arm did not meet inclusion criteria because blood was hemolyzed and that primary and secondary outcomes were unavailable for them. The posted outcome groups each contain 33 participants. In general, missing outcome data can affect interpretation if the chance of missingness is related to the outcome or differs by group. The fact that the stated number of hemolyzed samples is the same in both arms does not, by itself, show that their missingness has no effect on the comparison. The registry record does not report whether those participants were excluded from all analyses, whether another analysis population was used, or whether sensitivity analyses were performed.

The record identifies the study as randomized and unmasked, but does not report allocation concealment, the sequence-generation method, the specified primary analysis model, or an analysis plan. It also does not report interim analyses or stopping rules. Those omissions prevent a complete reconstruction of the statistical procedures and should be distinguished from the estimates that are explicitly posted. The numerical results can be described as reported, while conclusions about unreported procedures remain unavailable.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate an estimated effect. For the primary endpoint, the posted mean difference is 0.29. Its confidence interval extends from below zero to above zero, so it includes no difference as well as positive and negative differences. That span indicates substantial uncertainty about the exact size and direction of the population contrast. The unadjusted p-value of 0.126 is consistent with the interval's inclusion of zero, although a p-value and a confidence interval express uncertainty in different ways.

In general, a confidence interval is a range produced by a statistical procedure that, under its assumptions, is designed to cover the underlying parameter at a stated rate over repeated studies. It is not a range containing a known proportion of individual participant measurements, and it is not a guarantee that the true value lies inside the specific interval. The registry record does not state the confidence level explicitly in the primary outcome description, although it posts an interval for the comparison. The posted interval should therefore be read as the interval reported, without assuming unreported details about its construction.

The group standard deviations, 0.43 and 1.0, also show that the observed spread differs between the groups. The registry provides no individual-level measurements or distribution plots in the registry record described by the record, and no additional variance model is reported. The estimate's precision should be considered alongside the limited outcome counts and the missing blood samples identified in the endpoint description.

The secondary risk-difference intervals also span zero. This means that their estimates are compatible with no difference and with effects in either direction. Their width is especially important because the event counts are low. A point estimate alone can make a comparison look more definite than the evidence permits; the intervals communicate that these data do not pin down the size of a difference precisely. Neither the primary nor secondary intervals establish equivalence, and the registry does not report an equivalence margin or a non-inferiority margin.

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 observed effects, not the trial's original design justification. For continuous and binary outcomes, the figures are participants per arm. They do not represent total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The illustration considers detecting 100%, 75%, or 50% of the observed effect. The trial's own original design assumptions and sample-size rationale are not reported in the registry record.

In plain language, the 80% power column gives the planned number of participants per arm for a hypothetical study designed to have an 80% chance of detecting the specified effect if that effect were the true one and the assumptions held. The 90% power column uses a higher target chance of detecting it and therefore generally requires more participants per arm. These are planning calculations; this is not observed power. Observed power is not an appropriate way to reinterpret the results after the study has been completed.

The figures are tied to the observed effect and are not promises that a future study will reproduce it. The observed contrast may be imprecise, and the registry does not report a clinically meaningful target difference. Planning for 75% of the observed effect requires more participants per arm than planning for the full observed effect, and planning for 50% requires more still. This illustrates the general principle that smaller effects are harder to distinguish from random variation and therefore need more participants, assuming the other planning conditions remain the same.

For the primary continuous endpoint, the posted planning illustrations range from 111 participants per arm for 80% power and 100% of the observed effect to 443 participants per arm for 80% power and 50% of the observed effect. The corresponding 90% power figures are 149 and 593 participants per arm. These are planning examples only, not a retrospective judgment about whether the completed trial was adequately powered. The registry record does not report the assumptions used when the trial was originally designed.

For periprocedural myocardial infarction, the planning illustration uses the observed risk difference and gives much larger participant-per-arm requirements. Sparse events and uncertain estimates make such illustrations sensitive to the observed effect. The bleeding comparison has no posted planning illustration. The sample-size assumptions state that time-to-event results, if present, would give total events; no time-to-event planning result is posted for these outcomes.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.290; pooled standard deviation σ = 0.770.
2. n = 2 × (1.96 + 0.842)² × 0.770² / 0.290² = 110.6, rounded up to 111 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
delta <- 0.289999999999992                      # observed difference in means
sigma <- 0.76970773674168                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(1919723)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 111 (80% power), 149 (90% power)
 75% of observed effect: n per arm = 197 (80% power), 264 (90% power)
 50% of observed effect: n per arm = 443 (80% power), 593 (90% power)
power.t.test: 111.6 
Simulated power at n = 111 per arm: 0.801 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 lists a primary pharmacodynamic endpoint and multiple secondary outcomes, including high on-treatment platelet reactivity, bleeding complications, and periprocedural myocardial infarction. The posted results include the primary endpoint and results for bleeding and periprocedural myocardial infarction. A prespecified multiplicity strategy, such as adjustment of significance thresholds or a formal hierarchy for testing outcomes, is not reported in the registry record. Without that information, the secondary p-values should be treated as unadjusted results rather than as confirmatory evidence across a family of outcomes.

Multiplicity matters because testing several outcomes can increase the chance of at least one apparently notable result even when no true effects exist. In general, adjustment can control that chance but may reduce sensitivity to individual effects. A hierarchy can also specify which comparisons are intended to support confirmatory conclusions. The registry does not report whether either approach was planned. The primary endpoint is identified, but the record does not provide enough information to establish the broader inferential strategy.

Missing data are specifically noted for the primary endpoint. Two subjects in each arm had hemolyzed blood samples and did not meet inclusion criteria, so primary and secondary outcomes were unavailable for them. The posted outcome groups each contain 33 participants. The record does not report whether missing observations were excluded under a prespecified rule, whether any replacement or imputation procedure was used, or whether sensitivity analyses assessed departures from the assumptions about missingness. It also does not state whether the same analysis population was used for every endpoint.

Randomization supports comparison of assigned groups, but the outcome analysis population and treatment of missing measurements are important to interpreting the resulting estimates. The registry record does not report an intention-to-treat analysis, a per-protocol analysis, or another named analysis population. It does not report baseline balance, covariate adjustment, or the handling of protocol deviations. These omissions do not change the posted estimates, but they limit assessment of how faithfully those estimates reflect the randomized comparison and how robust they are to alternative analysis choices.

The record also does not report a formal analysis plan, interim looks at accumulating data, stopping boundaries, or rules for handling multiple measures within the platelet assay. These details should not be inferred from the result values or from the planning illustration. The trial's original sample-size justification and the design assumptions used at initiation are likewise not reported in the registry record.

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 1% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: periprocedural myenecrosis (27.3%), death (3.0%), nstemi (3.0%), gastrointestinal bleeding (3.0%), target lesion revascularization (tlr) (3.0%).

The registry's serious adverse event figures show 10 affected in the bolus group and 10 in the bolus-plus-infusion group, with 33 at risk in each group. The figures for other adverse events are 0 in each group, also among 33 at risk. These are descriptive counts and do not establish whether the regimens have the same safety profile. The registry's death-count field is not populated, so the number of deaths is not reported in the registry record.

The serious adverse event terms listed include Periprocedural Myenecrosis at 27.3%, as recorded, and Death, NSTEMI, Gastrointestinal Bleeding, and Target Lesion Revascularization (TLR), each at 3.0%. Those percentages describe listed terms, not a complete account of severity, timing, recurrence, or causal attribution. The record does not explain whether the terms overlap within participants, how they were adjudicated, or whether investigators considered them related to treatment. The registry also reports bleeding complications as a separate secondary outcome, so those endpoint results should not be conflated with the broader adverse-event listing.

Because the groups are small and the reporting details are limited, the serious adverse event counts are best read as a concise descriptive safety record rather than a definitive comparison. Missing definitions and the unreported death count constrain interpretation.

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

The primary result describes a small observed difference in mean change in %IPA between the two regimens: 99.59 in the bolus group and 99.88 in the bolus-plus-infusion group, with a mean difference of 0.29. The uncertainty interval includes zero, and the unadjusted p-value is 0.126. These findings mean that the posted data do not clearly distinguish the average laboratory response between groups. They do not demonstrate that the regimens are equivalent, and they do not establish that any difference is clinically unimportant.

The endpoint is a laboratory measure at 2 hours after ADP stimulation. It is not a direct measure of patient benefit, bleeding risk, or longer-term cardiovascular outcome. The registry reports bleeding and periprocedural myocardial infarction over up to 24 hours, but the event counts are sparse and their uncertainty intervals also span zero. These data do not establish that one regimen causes fewer or more clinical events than the other.

The trial is a phase 2 randomized comparison and the reported outcome groups are small. The primary endpoint description identifies hemolyzed samples that left two subjects in each arm without primary or secondary outcome data. The registry does not report a clinically important threshold for %IPA, the trial's original power assumptions, detailed analysis procedures, or a multiplicity strategy. These gaps limit how far the estimates can support broader conclusions.

The results apply to the specific comparison described: ticagrelor and eptifibatide boluses, with or without a 2-hour eptifibatide infusion, in patients undergoing non-emergent percutaneous coronary intervention. They do not address other dosing regimens, other populations, other procedures, or outcomes beyond those posted. The appropriate interpretation is descriptive and comparative: the registry reports closely placed primary group means but substantial uncertainty around the contrast, alongside limited short-term clinical event data.

Nothing in these results alone establishes a treatment recommendation. The posted findings describe what was measured in this trial and the precision available in those measurements; they do not resolve questions of longer-term effectiveness, rare harms, or the relevance of platelet assay changes to clinical outcomes.

17. Why This Trial Matters Statistically

This trial illustrates a common challenge in clinical biostatistics: a pharmacodynamic marker can be measured with a continuous scale, while the outcomes of direct clinical interest are relatively infrequent events. The primary endpoint therefore offers a quantitative comparison of platelet response at a defined time, but it cannot substitute for evidence about bleeding or myocardial infarction. Keeping those questions separate is essential to avoid overstating what a laboratory result means.

The primary estimate is a useful example of why effect size and uncertainty should be read together. The mean difference is 0.29, the confidence interval spans zero, and the unadjusted p-value is 0.126. The p-value alone cannot say whether the observed difference matters, while the interval makes clear that the estimate is not precise enough to establish a definite direction. The record does not report a clinically meaningful threshold, so statistical evidence and clinical importance cannot be aligned using a prespecified benchmark.

The secondary outcomes demonstrate another practical issue: sparse events produce uncertain comparisons. Counts and point estimates can look different across groups, yet the uncertainty intervals may still include no difference and a range of effects. That is not a contradiction; it reflects limited information. Reporting the uncertainty alongside the event counts helps prevent an overconfident reading.

Finally, the registry identifies missing outcome measurements due to hemolyzed blood, but does not report detailed analysis methods, missing-data sensitivity analyses, or a multiplicity plan. These absences show why transparent reporting of analysis populations, prespecification, and sensitivity checks matters. The trial's posted results can be described, but their inferential context remains incomplete where the registry does not report those details.

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.

The registry record gives limited detail about methods beyond identifying randomization, no masking, and a parallel-group design. The method of sequence generation and allocation concealment is not reported in the registry record. Nor does the record state whether laboratory personnel were masked to assignment. These omissions make it difficult to assess potential sources of bias in assignment or endpoint measurement.

The primary endpoint is reported as change from baseline in %IPA, but the registry does not describe the calculation at the participant level, assay reproducibility, or a clinically important difference. The observed group means are close to the upper end of the percentage scale, so interpretation may depend on assay behavior near that range; details needed to evaluate this are not reported in the registry record. No baseline group summaries or individual-level measurements are posted in the registry record described by the record.

Two subjects in each arm had hemolyzed blood, and their primary and secondary outcomes were unavailable. The record does not describe missing-data methods or sensitivity analyses. Although the numbers identified as missing are equal by group, that alone does not establish that missingness had no influence on the estimates.

Clinical outcomes were assessed over a short period, up to 24 hours. The event counts are limited, and the registry does not report detailed definitions or adjudication procedures. The record also does not report multiplicity adjustment, the original sample-size rationale, the planned statistical analysis, or interim monitoring. These limitations make the posted findings useful as a description of this trial but constrain conclusions about clinical outcomes, long-term effects, and robustness to alternative analyses.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Ticagrelor and Eptifibatide Bolus-Only Versus Ticagrelor and Eptifibatide Bolus Plus Abbreviated Infusion — NCT01919723.
• Registry record last updated 2017-02-28; status last verified 2017-01.
• Results first posted 2017-02-28.
• 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

The registry record describes a completed randomized phase 2 parallel-group trial, sponsored by the University of Alabama at Birmingham, in patients with acute coronary syndrome undergoing non-emergent percutaneous coronary intervention. It compared ticagrelor and two eptifibatide boluses with the same regimen followed by a 2-hour eptifibatide infusion. The trial was unmasked.

The primary endpoint was change from baseline in %IPA at 2 hours after 20µM ADP stimulation. The posted group means were 99.59 and 99.88, with a mean difference of 0.29, an unadjusted p-value of 0.126, and an interval that spans zero. Secondary results covered bleeding complications and periprocedural myocardial infarction up to 24 hours. Their event counts were small and their uncertainty intervals included no difference.

The outcome description notes hemolyzed blood samples for two subjects in each arm and unavailable outcomes for those subjects. Detailed analysis methods, the original sample-size rationale, multiplicity procedures, and sensitivity analyses are not reported in the registry record.