The Randomized OPTIMAL-ACT Trial: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The Randomized OPTIMAL-ACT Trial (NCT03772613), a randomized phase 2 study. The primary outcome is Bleeding.

2. Clinical Question

3. Trial Design

The Randomized OPTIMAL-ACT Trial is a phase 2, randomized, double-masked, parallel-group trial sponsored by Mayo Clinic. The registry records enrollment of 180 and a completed status. The study start date is 2019-02-08, and the primary completion date is 2021-10-25. These record details describe the trial’s administrative design and timing; they do not establish how participants were recruited or whether the posted outcome counts include every enrolled participant.

Unfractionated heparin is the listed drug intervention. Participants were allocated among Low ACT Target, Medium ACT Target, and High ACT Target arms. For participants without a planned glycoprotein IIb/IIIa inhibitor, the target ACT ranges before PCI were 225 to 275 seconds, 275 to 325 seconds, and 325 to 375 seconds, respectively. The posted primary outcome counts use 61.0 participants in the low group, 60.0 in the medium group, and 57.0 in the high group. The registry does not explain the relationship between these outcome denominators and its overall enrollment figure.

The primary endpoint is bleeding, assessed from randomization until the first documented event up to 24 hours. Stent thrombosis is listed as a secondary outcome with a 30 days timeframe. The record also reports adverse-event counts by arm. The main posted comparisons are unadjusted comparisons of each higher target group with the low-target group. The registry record does not report the randomization procedure, the masking procedures, details of the analysis population, or the original statistical analysis plan. It also does not report the trial’s original sample-size assumptions or justification, so the planning illustrations should not be mistaken for the design basis of this completed trial.

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 Bleeding, measured over From date of randomization until the date of first documented bleeding event up to 24 hours.

The primary endpoint counts participants who experienced a qualifying bleeding event. The registry defines bleeding as Bleeding Academic Research Consortium (BARC) 1, 2, 3 or 5, or an EASY hematoma classification after transradial/ulnar procedures. The stated observation period begins at randomization and ends at the first documented bleeding event, with follow-up up to 24 hours. The outcome is therefore a participant count for a defined period, not a measure of how long a bleed lasted, its total volume, or the number of separate bleeding episodes.

A binary event endpoint can be used to compare the proportion of participants who experienced at least one qualifying event across randomized groups. That makes it relevant to the study’s question about different ACT targets while keeping the outcome definition tied to recorded bleeding classifications. The definition combines specified BARC grades with a procedure-specific hematoma classification, so interpretation depends on those criteria and the event documentation used in the trial. The registry record does not report adjudication procedures or further detail about how the classifications were applied.

The posted counts are 14.0 participants with bleeding among 61.0 in the Low ACT Target group, 15.0 among 60.0 in the Medium ACT Target group, and 15.0 among 57.0 in the High ACT Target group. These are observed event counts, not estimates of the number of events that would occur in other populations. The short, up-to-24-hours endpoint also does not represent later bleeding outcomes. Stent thrombosis is listed separately as a secondary outcome, with a 30 days timeframe.

7. Results Posted in the Registry

• Medium ACT Target: 25.0% (15/60) versus 23.0% (14/61) on control; risk difference 2.0 percentage points (95% CI -13.2 to 17.3), risk ratio 1.09 (0.58–2.06); unadjusted two-proportion z-test p = 0.792.
• High ACT Target: 26.3% (15/57) versus 23.0% (14/61) on control; risk difference 3.4 percentage points (95% CI -12.2 to 18.9), risk ratio 1.15 (0.61–2.16); unadjusted two-proportion z-test p = 0.671.

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.

Stent Thrombosis

• 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:
  • Medium ACT Target: 0.0% (0/60) versus 1.6% (1/61) on control; risk difference -1.6 percentage points (95% CI -4.8 to 1.5); unadjusted two-proportion z-test p = 0.319.
  • High ACT Target: 0.0% (0/57) versus 1.6% (1/61) on control; risk difference -1.6 percentage points (95% CI -4.8 to 1.5); unadjusted two-proportion z-test p = 0.332.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Medium ACT Target and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between High ACT Target and the control. The interval gives the range of effects that remain compatible with the data.

Stent thrombosis is the secondary outcome listed in the registry record, with a 30 days timeframe. The overall pattern is sparse: there is one recorded event in the Low ACT Target group and none in the Medium ACT Target or High ACT Target groups. The posted unadjusted comparisons do not identify a clear difference, and their confidence intervals include zero. With so few events, the estimates are highly uncertain; a group with no observed event should not be interpreted as having no underlying risk.

This secondary outcome addresses a different clinical event from the primary bleeding endpoint. Its pattern does not resolve the uncertainty in the primary comparison, and it should not be treated as confirmation or contradiction of the bleeding findings. The registry reports one secondary outcome and does not list reported analyses for it beyond the posted comparisons. Whether other outcomes were measured, analyzed, or planned is not reported in the registry record.

Unadjusted secondary findings generally carry less weight than a prespecified primary analysis when there may be multiple outcomes or comparisons. Testing multiple hypotheses without an adjustment can increase the chance that at least one result appears noteworthy by chance. The record does not report a multiplicity strategy, a hierarchy of secondary hypotheses, or a confirmatory analysis plan. This does not invalidate the descriptive counts; it means they are best treated as exploratory context rather than definitive evidence about differences between target groups.

The small number of secondary events also limits the information available for estimating a difference. A zero count is an observed result in the follow-up period, not proof that the event cannot occur under that target. These secondary results should therefore be read as a brief, uncertain description of recorded stent thrombosis rather than as a stand-alone basis for broader conclusions.

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

• Stent Thrombosis

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary outcome is binary at the participant level: a participant either had a qualifying bleeding event during the specified observation period or did not. The registry reports the number of participants with events and the number in each arm. This type of outcome can be expressed as an event risk, meaning the proportion of participants in a group who experienced the event. The comparisons use risk differences, which subtract the reference group’s event risk from the comparison group’s event risk. A value above zero denotes a higher estimated event risk in the comparison arm; a value below zero denotes a lower estimated risk. The interpretation always depends on which arm is designated as the reference.

What does a confidence interval express?

A confidence interval describes uncertainty around an estimated contrast under the statistical method used. It is not a range containing a fixed percentage of individual participants’ outcomes, and it does not assign a probability to the true effect being at any particular point in the interval. In general, a wider interval indicates less precision, while a narrower interval indicates greater precision. For the posted primary comparisons, the intervals extend across zero and include values in both directions. That means the estimates are compatible with no difference as well as with a range of positive or negative differences under the calculation used. The interval width matters: a non-significant result is not by itself evidence of equivalence.

How should the p-values be read?

The unadjusted p-value summarizes how unusual data at least as discrepant as those observed would be under a statistical model whose null hypothesis has no group difference. It is not the probability that the null hypothesis is true, nor does it measure the probability that results will replicate. The primary comparisons have unadjusted p-values of 0.792 and 0.671. Those values do not provide evidence against the null hypothesis at commonly used significance thresholds, but they do not show that the groups are the same. The registry record does not report a threshold prespecified in the trial’s own analysis plan, so these p-values should be read as posted unadjusted results rather than as evidence of a documented decision rule.

What does “unadjusted” mean in these comparisons?

Unadjusted means the posted pairwise estimates are not reported as controlling for other variables or for the number of comparisons. The record gives one contrast for Medium ACT Target versus Low ACT Target and another for High ACT Target versus Low ACT Target. It does not give a direct medium-versus-high contrast. It also does not describe a regression model, stratification, covariate adjustment, or multiplicity correction. Those methods may be used in some trials, but whether they were used for any additional analysis is not reported in the registry record.

Why does the endpoint definition matter?

Statistical comparisons depend on what counts as an event and when an event is counted. Here, the primary outcome combines specified BARC categories with an EASY hematoma classification for transradial/ulnar procedures, and the observation window runs from randomization until the first documented event up to 24 hours. This is a participant count, not a recurrent-event analysis or time-to-event estimate. In general, a clear endpoint definition supports consistent comparisons, while different definitions or follow-up windows can produce results that are not directly comparable. The registry record does not report further outcome adjudication or missing-data procedures.

What can randomization establish?

Randomization is intended, in general, to make assigned groups comparable at the start of a trial with respect to both measured and unmeasured characteristics. It supports a causal interpretation of a well-conducted comparison of assigned groups, but it does not by itself establish that follow-up, measurement, or analysis was complete and unbiased. The registry records random allocation, double masking, and a parallel model. It does not describe the allocation sequence, concealment, masking implementation, adherence, or analysis population. These missing details limit how fully the trial’s conduct can be assessed from the registry record alone.

How should sparse counts be understood?

For binary outcomes, event counts and group sizes determine how much information is available for estimating group differences. When events are few, estimates can be sensitive to the occurrence or absence of individual events, and intervals may remain wide. Stent thrombosis has very few posted events, so its estimates are especially uncertain. General statistical methods for sparse binary data can differ in their treatment of zero-event groups; the record does not report enough information to identify a specific method beyond the posted unadjusted risk-difference results. The primary endpoint has more events than the secondary endpoint, but its intervals still span both directions of effect.

11. Confidence Intervals and Precision

The primary risk-difference estimates are imprecise. For Medium ACT Target compared with Low ACT Target, the posted estimate is 0.021, with a 95% confidence interval from -0.132 to 0.173. For High ACT Target compared with Low ACT Target, the estimate is 0.034, with a 95% confidence interval from -0.122 to 0.189. Both intervals include zero, and both include values on either side of zero. The data therefore do not narrowly locate the difference between the groups.

Precision is distinct from whether a result crosses a significance threshold. The confidence intervals communicate the range of effect sizes that remain compatible with the data and the method used, rather than proving that any one value is correct. In general, a confidence interval that includes zero does not establish equivalence. Demonstrating equivalence would require a prespecified margin and an analysis designed to assess whether effects fall within it; that information is not reported in the registry record.

The posted outcome groups contain 61.0 participants for Low ACT Target, 60.0 for Medium ACT Target, and 57.0 for High ACT Target. The observed bleeding counts are 14.0, 15.0, and 15.0, respectively. These counts support the displayed comparisons, but the limited number of events means substantial uncertainty remains. The registry record does not report additional analyses that would narrow or otherwise qualify these intervals.

For stent thrombosis, the observed event count is sparse, and the posted risk-difference intervals also include zero. Sparse outcomes generally yield less precise estimates, particularly when one or more groups have no observed events. Those secondary estimates should not be interpreted as showing that the risk is absent in groups with zero events. The record reports observed counts over 30 days, not certainty about the underlying risk.

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 describe participants per arm for 80% power and participants per arm for 90% power. They are planning illustrations based on the observed effect, not the original trial’s design assumptions. For the primary comparisons, each row represents a planning scenario using 100% of the observed effect, 75% of the observed effect, or 50% of the observed effect. Under the listed assumptions, planning for 75% of the observed effect requires more participants per arm than planning for 100% of the observed effect; planning for 50% requires more again. In general, smaller effects are harder to distinguish from random variation and therefore require more participants to achieve the same target power.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The primary outcome is binary, so these figures refer to participants per arm, not total events. The registry’s note distinguishes this from time-to-event planning displays, which report total events using the Schoenfeld method; the primary endpoint is not a time-to-event outcome.

For example, the planning values for 80% power are 6,813 participants per arm for 100% of the observed effect, 12,024 for 75%, and 26,852 for 50% in the Medium ACT Target comparison. For the High ACT Target comparison, the corresponding values are 2,573, 4,522, and 10,054 participants per arm. The 90% power column gives larger planning counts for the same effect scenarios because it targets a higher chance of detecting the specified effect if it is present. These are planning illustrations, not observed power.

The trial’s original design assumptions and sample-size justification are not reported in the registry record. The planning values should not be interpreted as evidence that the completed trial was planned around the observed effect or that its results have a particular probability of being true.

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 = 0.230; treatment proportion p₁ = 0.250; average p̄ = 0.240.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6038 = 1.1834.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6036 = 0.5080.
4. n = (1.1834 + 0.5080)² / (0.0205)² = 6,812.7, rounded up to 6,813 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 <- 0.229508196721311                          # control proportion
p1 <- 0.25                          # 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(3772613)
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 = 6,813 (80% power), 9,120 (90% power)
 75% of observed effect: n per arm = 12,024 (80% power), 16,096 (90% power)
 50% of observed effect: n per arm = 26,852 (80% power), 35,947 (90% power)
power.prop.test: 6812.7 
Simulated power at n = 6,813 per arm: 0.802 (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 posted primary comparisons include Medium ACT Target versus Low ACT Target and High ACT Target versus Low ACT Target. Stent thrombosis is the listed secondary outcome, and the record reports comparisons for it as well. Considering multiple groups, outcomes, or contrasts raises a multiplicity question: when many hypotheses are tested, the chance of at least one apparently unusual result can increase even if none of the underlying effects is real. Common strategies include defining a primary contrast in advance, controlling a family-wise error rate, or treating secondary comparisons as exploratory. These are general approaches, not claims about what this trial did.

The registry record does not report a multiplicity adjustment, a hierarchy for secondary outcomes, a prespecified threshold for statistical significance, or the trial’s full statistical analysis plan. The posted p-values are unadjusted. They should not be treated as multiplicity-controlled confirmatory evidence. The record lists Stent Thrombosis as a secondary outcome, but does not report further planned-analysis details or a broader set of secondary results.

Missing-data handling is also not reported in the registry record. The outcome denominators are 61.0 for Low ACT Target, 60.0 for Medium ACT Target, and 57.0 for High ACT Target. The record does not explain whether any participants lacked endpoint data, how missing outcomes were handled, or whether participants were analyzed according to their randomized assignment. It does not report an intention-to-treat or per-protocol analysis population. The presence of outcome denominators alone does not establish how missingness was addressed.

These omissions matter because missing outcomes can affect event estimates if their occurrence differs across arms or is related to prognosis. In general, complete-case, imputation, and sensitivity analyses make different assumptions about missing data. No such approach can be attributed to this trial from the registry record. Similarly, random allocation is reported, but details of the allocation process, masking, adherence, and analysis implementation are not included. These gaps constrain evaluation of the statistical evidence; they do not change the posted event counts, but they limit assessment of how robustly those counts represent the intended randomized comparison.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports serious adverse events, other adverse events, and deaths separately by ACT target. No serious adverse events are recorded in any group, and deaths are recorded as 0 for each group. Other adverse events are recorded for 4 participants in Low ACT Target, 5 in Medium ACT Target, and 8 in High ACT Target. The corresponding at-risk counts are 61, 61, and 58. These are descriptive safety counts, not adjusted comparisons or evidence of a causal difference.

The adverse-event at-risk counts do not exactly match the primary endpoint denominators: the high-target safety count is 58, while the primary outcome denominator is 57. The registry record does not explain this difference. The safety counts should therefore be read using their own reported denominators, without assuming that they refer to the same analysis population as the primary outcome. No serious-event terms are listed. A zero recorded count means none was reported in that category in this record; it does not establish that an event is impossible or that all events were captured.

The registry does not provide event severity details, timing, causal attribution, or a statistical comparison for these adverse-event figures. They are best understood as a descriptive account of recorded events in the stated groups.

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

The registry reports similar observed bleeding counts across the three ACT target groups, with 14.0 participants in the low-target group, 15.0 in the medium-target group, and 15.0 in the high-target group experiencing the primary endpoint. The posted unadjusted risk differences have confidence intervals that include zero and span effects in both directions. These findings do not precisely establish a difference between either higher target and the low target. They also do not demonstrate that the targets are equivalent, because an equivalence margin and an equivalence analysis are not reported.

The results concern a specific endpoint definition and time window: qualifying bleeding from randomization until the first documented event up to 24 hours. They do not answer questions about bleeding beyond that interval or about other clinical outcomes. Stent thrombosis is separately listed over 30 days, but its event count is sparse and its comparisons are uncertain. The adverse-event figures are descriptive and have a difference in the reported at-risk denominator for the high-target arm compared with the primary endpoint denominator.

Randomization is an important design feature because, in general, it supports a fair comparison of assigned groups. The record also describes double masking and a parallel design. However, details of allocation, masking implementation, adherence, analysis populations, missing outcome data, and the original analysis plan are not reported in the registry record. The estimates should therefore be interpreted with the information that is documented, without assuming unreported methods or analyses.

These findings do not establish that any target works or does not work, and they do not provide medical advice. They describe the posted results for this trial and the uncertainty around the reported comparisons. Broader conclusions would require evidence beyond the registry results, including appropriate consideration of the trial’s conduct, population, endpoint definitions, and other evidence.

17. Why This Trial Matters Statistically

OPTIMAL-ACT illustrates an important distinction between the direction of an estimate and the strength of evidence for that estimate. Both posted primary risk-difference point estimates are positive for comparisons with the low target, but their confidence intervals are wide and include zero. Focusing only on the point estimates or on whether a p-value meets a threshold would miss the uncertainty. Reading the estimates together with their intervals gives a more complete account of what the observed data can and cannot distinguish.

The trial also shows why event counts and follow-up definitions matter. The primary endpoint is a participant-level count of qualifying bleeding within a short, specified window, while stent thrombosis is reported over 30 days and has sparse events. These outcomes capture different events and periods, so their estimates should not be merged into a single claim about overall outcomes. The safety record further illustrates the importance of checking denominators: its high-target at-risk count differs from the primary endpoint denominator, and the registry does not explain why.

Finally, the planning illustrations emphasize the difference between study design and retrospective planning. Their assumptions are stated, but the original design justification is not reported. The illustrations show that detecting smaller effects requires more participants per arm under the stated assumptions; they do not establish the trial’s original power or the probability that its observed findings are true. Taken together, the record offers a useful example of cautious interpretation: separate observed counts from comparisons, consider interval width, distinguish primary from secondary outcomes, and recognize where registry documentation leaves methods unresolved.

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 leaves important details about the trial population and conduct unreported. It does not give detailed eligibility criteria, participant characteristics, allocation procedures, masking implementation, adherence, or the analysis population. These omissions make it difficult to assess how broadly the results apply and how closely the posted comparisons follow the intended randomized assignment. The record also does not describe missing outcome data or its handling.

The primary endpoint is limited to specified BARC categories or an EASY hematoma classification after transradial/ulnar procedures, ending at the first documented event up to 24 hours. The registry does not describe how events were adjudicated or whether endpoint assessment was blinded in practice. The short follow-up and specific event definition limit interpretation to that measure rather than later bleeding or other outcomes.

The primary comparison estimates are imprecise, with confidence intervals extending across zero. The registry does not report a prespecified clinically meaningful difference or equivalence margin, so the nonsignificant unadjusted p-values cannot establish equivalence. The record also does not report multiplicity handling, covariate adjustment, the complete statistical analysis plan, or further reported analyses. Secondary stent thrombosis counts are sparse, limiting the precision of those comparisons.

There is a denominator mismatch in the posted safety and primary endpoint figures: the high-target adverse-event at-risk count is 58, while the primary outcome denominator is 57. The registry record does not explain the mismatch. The overall enrollment figure is 180, while the primary endpoint counts use arm denominators of 61.0, 60.0, and 57.0; the record does not explain how these outcome denominators relate to overall enrollment. These are documentation limitations, not grounds for inferring why participants are not represented in a given denominator.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: The Randomized OPTIMAL-ACT Trial — NCT03772613.
• Registry record last updated 2023-04-04; status last verified 2023-03.
• Results first posted 2023-04-04.
• 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 Randomized OPTIMAL-ACT Trial is a completed phase 2, randomized, double-masked, parallel-group study sponsored by Mayo Clinic, with enrollment recorded as 180. It compared low, medium, and high ACT target ranges during PCI, using unfractionated heparin as the listed drug intervention. The primary endpoint was the count of participants with qualifying bleeding from randomization until the first documented event up to 24 hours.

The posted primary event counts were 14.0 of 61.0 for Low ACT Target, 15.0 of 60.0 for Medium ACT Target, and 15.0 of 57.0 for High ACT Target. The unadjusted risk-difference intervals include zero and are wide. Stent thrombosis is listed as a secondary outcome over 30 days, with sparse observed events. The registry does not report the original sample-size rationale, the full statistical plan, multiplicity handling, or missing-data methods. The results are therefore best read as uncertain comparisons of the recorded outcomes, not as evidence of equivalence or definitive differences between targets.