Safety and Effectiveness of the Orsiro Sirolimus Eluting Coronary Stent System in Subjects With Coronary Artery Lesions: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Effectiveness of the Orsiro Sirolimus Eluting Coronary Stent System in Subjects With Coronary Artery Lesions (NCT02389946), a randomized na study. The primary outcome is Percentage of Participants With Target Lesion Failure (TLF) at 12 Months Post-Index Procedure by Bayesian Estimation.

2. Clinical Question

The study objective was to assess safety and effectiveness for people with up to three specified coronary lesions. The main endpoint combines cardiac death, target-vessel Q-wave or non-Q-wave myocardial infarction, and clinically driven target lesion revascularization. The registry also reports a posterior probability for non-inferiority. The non-inferiority margin and the complete specifications of that analysis are not reported in the registry record, so the reported probability cannot be interpreted independently of those details.

3. Trial Design

The registry describes a prospective, randomized, multicenter study with a parallel-group model and single masking. Participants were assigned to the Orsiro sirolimus coronary stent system or the Xience everolimus coronary stent system. The registry lists the study phase as NA and enrollment as 1334. The sponsor is Biotronik, Inc. The study start is listed as 2015-05, primary completion as 2017-04, and status as completed.

The primary outcome is the percentage of participants with target lesion failure at 12 months after the index procedure. The registry defines target lesion failure using cardiac death, target-vessel Q-wave or non-Q-wave myocardial infarction, or clinically driven target lesion revascularization. The record reports group-level values for the endpoint and a separate posterior probability of non-inferiority analysis.

Secondary outcomes include lesion device success, lesion success, procedure success, myocardial infarction, myocardial infarction or cardiac death, major adverse cardiac events and their components, target lesion failure and its components, and target vessel failure and its components. Procedure success is reported at hospital discharge, specified as 6-24 hours post-index procedure. The registry lists 10 outcome measures and 2 analyses, but does not give the complete protocol or statistical analysis plan.

The allocation, masking, and parallel-group labels describe broad design features; they do not supply all operational details. How randomization was generated or concealed, what single masking means for each study role, and how the analysis handled deviations from assigned treatment are not reported in the registry record. The original sample-size justification and design assumptions 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

Analysis population for the primary outcome, as defined in the registry: Pre-specified Bayesian analysis: BIOFLOW-V intent-to-treat subjects who experienced the primary endpoint or had at least 330 days of follow-up and BIOFLOW-II (NCT01356888) and BIOFLOW-IV (NCT01939249) subjects who satisfied the BIOFLOW-V inclusion/exclusion criteria and experienced the primary endpoint or had at least 330 days of follow-up.

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 Percentage of Participants With Target Lesion Failure (TLF) at 12 Months Post-Index Procedure by Bayesian Estimation, measured over 12-Months.

Target lesion failure (TLF) is the primary endpoint. The registry defines it as the occurrence of cardiac death, target-vessel Q-wave or non-Q-wave myocardial infarction, or clinically driven target lesion revascularization. The posted outcome is the percentage of participants with TLF at 12 months after the index procedure. These components capture serious cardiac outcomes and repeat treatment directed at the target lesion, combining them into a single endpoint for comparison.

A composite endpoint can summarize whether any of its defined events occurred, but it does not make the components interchangeable. The overall percentage does not by itself show which component contributed most, how often participants experienced more than one component, or how event timing differed. Those details require component-specific results and definitions. The registry lists secondary outcomes that include TLF and individual TLF components, but component-level numerical results are not included in the posted details used for this analysis.

The registry labels the primary analysis as Bayesian estimation and reports a posterior probability of non-inferiority. A non-inferiority conclusion depends on a prespecified margin and analysis choices; those details are not reported in the registry record. The endpoint definition and follow-up time clarify what was measured, but they do not alone establish how the sponsor’s formal conclusion was reached.

7. Results Posted in the Registry

• Xience Everolimus Coronary Stent System: mean 8.90 versus 6.32 on control; difference 2.58 (95% CI 2.45 to 2.71), standardized effect d = 2.78; z-test p = <0.001.

8. Secondary Efficacy Endpoints

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

Number of Participants With Procedure Success

• 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:
  • Xience Everolimus Coronary Stent System: 90.1% (401/445) versus 93.9% (827/881) on control; risk difference -3.8 percentage points (95% CI -7.0 to -0.6), risk ratio 0.96 (0.93–0.99); unadjusted two-proportion z-test p = 0.014.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Xience Everolimus Coronary Stent System than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary outcomes covering procedural and lesion success, myocardial infarction, cardiac death, major adverse cardiac events, target lesion failure, and target vessel failure. The detailed secondary result available for interpretation is procedure success at hospital discharge. Numerical findings for the other listed outcomes are not reported in the registry record used for this analysis, so the overall pattern across all secondary endpoints cannot be characterized from these results alone.

Procedure success is measured soon after the index procedure, whereas the primary TLF endpoint is assessed at 12 months. The outcomes therefore address different aspects of the study and different follow-up periods. The procedure-success comparison does not confirm or negate the primary result; it is a separate endpoint with its own definition and uncertainty. Likewise, the primary composite does not supply component-level results for the secondary measures.

There are multiple listed secondary outcomes, and the procedure-success p-value is unadjusted. In general, repeated testing across outcomes can increase the chance of observing a nominally small p-value even when the tested effects are absent. The registry record does not report a multiplicity strategy, such as a prespecified hierarchy or adjustment. For that reason, unadjusted secondary comparisons carry less confirmatory weight than a prespecified primary analysis, particularly when the full analysis plan and the remaining numerical secondary results are unavailable.

The secondary findings should therefore be read as supportive descriptive information rather than as an independent basis for a broad conclusion. Their interpretation depends on their definitions, analysis populations, missing-data handling, and any planned control of multiple comparisons, none of which is fully detailed in the registry record.

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

• Number of Lesions With Device Success
• Number of Lesions With Lesion Success
• Number of Participants With Procedure Success
• Number of Participants With Myocardial Infarction
• Number of Participants With Myocardial Infarction or Cardiac Death
• Number of Participants With MACE and Individual MACE Components
• Number of Participants With TLF and Individual TLF Components
• Number of Participants With Target Vessel Failure (TVF) and Individual TVF Components

9. Statistical Interpretation

10. Statistical Methods Explained

The posted results include a sponsor-reported Bayesian non-inferiority analysis and a simple unadjusted recalculation from the group summaries. These approaches use different statistical frameworks and should not be conflated. The recalculation is a descriptive statistical comparison of the posted values. The registry’s Bayesian result is the analysis the sponsor reported for the stated non-inferiority question, but the registry does not give enough detail to reproduce it or evaluate all its assumptions.

What does the unadjusted mean difference describe?

The primary outcome is expressed as a percentage of participants. The posted comparison reports a mean difference of 2.58 for Xience minus Orsiro. That direction is consistent with the posted group values of 8.9 for Xience and 6.32 for Orsiro. The difference is an absolute difference in the reported percentages, not a relative percentage change. The recalculation does not adjust for baseline characteristics, site, or other variables; whether the sponsor’s analysis used adjustment is not reported in the registry record.

An unadjusted comparison is useful as a transparent summary of the posted group values, but it does not necessarily match the estimand or model used in the trial’s formal analysis. In a randomized trial, the allocation is intended to support a comparison between groups, while an analysis plan determines which participants and outcomes contribute to the estimate and how uncertainty is represented. The full analysis plan is not reported in the registry record.

What does a p-value convey?

The unadjusted primary p-value is <0.001. In general, a p-value describes how compatible data are with a specified null model under the assumptions used for the test. It is not the probability that the null hypothesis is true, the probability that a result arose by chance, or a measure of clinical importance. Its interpretation depends on the model, endpoint, and analysis plan. The registry’s primary analysis is described as Bayesian estimation, so the recalculated p-value should be kept distinct from the sponsor’s reported posterior probability.

The procedure-success comparison has an unadjusted p-value of 0.014. This value concerns a secondary outcome, not the primary endpoint. When many outcomes or comparisons are examined, the chance of obtaining one or more small p-values under null conditions can increase. Whether and how the trial addressed multiplicity is not reported in the registry record. That uncertainty is one reason not to treat an unadjusted secondary p-value as a definitive standalone finding.

What does the Bayesian result represent?

In general, Bayesian analysis combines a statistical model and prior distributions with observed data to form a posterior distribution. A posterior probability can express the probability assigned to a specified parameter claim given the model, prior, and data. For a non-inferiority question, interpretation depends on the prespecified margin and on how the posterior probability is defined. The registry reports a posterior probability of non-inferiority of 100, but does not report the margin, prior distributions, likelihood or model, or posterior interval. It is therefore not possible to reconstruct the result or assess sensitivity to those choices from the registry entry alone.

The registry’s primary population description refers to BIOFLOW-V intent-to-treat subjects who experienced the primary endpoint or had at least 330 days of follow-up, as well as eligible BIOFLOW-II and BIOFLOW-IV subjects who experienced the primary endpoint. The available wording is truncated, so the complete inclusion rules are not reported in the registry record. This population description appears specifically within the prespecified Bayesian analysis entry; it should not automatically be assumed to describe every posted outcome analysis.

Why can over-dispersion matter?

In general, over-dispersion occurs when observed variability exceeds what a statistical model assumes. If a model underestimates variability, uncertainty intervals may be too narrow and tests may appear more decisive than the data warrant. That concept is relevant when evaluating count or binary outcomes and their models, but the registry does not report whether over-dispersion was assessed or how it was handled. No conclusion about its presence or effect can be made from the posted summary statistics alone.

For the primary outcome, the posted group spreads are labelled standard deviations. The simple recalculation uses the posted summaries and is not a reconstruction of the sponsor’s Bayesian analysis. The analysis method behind the sponsor’s result is not specified, and the record does not explain how the standard deviations relate to the model used for the posterior probability.

How should the secondary analysis be separated?

Procedure success is a binary outcome reported at hospital discharge. The posted group counts and risk difference support a simple comparison, but they do not identify whether the sponsor used covariate adjustment or other modeling choices. A risk difference expresses an absolute difference between group proportions, while a risk ratio or odds ratio expresses a relative comparison on a different scale. The posted estimates should be read in their stated form and should not be substituted for the primary TLF analysis.

In general, confidence intervals describe a range of values compatible with a statistical procedure and its assumptions; they do not remove uncertainty or establish causality by themselves. A confidence interval for an unadjusted recalculation is not the same as a Bayesian credible interval. The registry does not post a credible interval for the reported posterior probability. The distinction matters because different methods can yield intervals with different interpretations and depend on different assumptions.

Finally, the registry does not report the randomization implementation, detailed handling of missing observations, endpoint adjudication procedures, or full analysis plan. These are not minor technicalities: they help determine what quantity an estimate represents and how trustworthy its uncertainty assessment is. The posted calculations are best treated as a readable summary of the available results, while the sponsor’s reported analysis remains a separate result whose complete specification is not available in the registry record.

11. Confidence Intervals and Precision

The recalculated primary mean difference is 2.58, with a confidence interval from 2.454 to 2.706. The interval is narrow relative to the point estimate and excludes zero. In general, a confidence interval gives a range of values compatible with the data and the statistical procedure used to construct it. Its width reflects sampling uncertainty under that procedure; it does not account automatically for bias, incomplete reporting, model misspecification, or every source of uncertainty.

This interval belongs to the simple unadjusted recalculation, not to the sponsor-reported Bayesian non-inferiority analysis. The registry reports no interval around the posterior probability of non-inferiority. It also does not report the non-inferiority margin or sufficient model details to judge how the sponsor’s probability result should be quantified. The narrow recalculated interval therefore cannot fill in those missing Bayesian details.

The procedure-success comparison has a posted risk difference of -0.038, with a confidence interval from -0.070 to -0.006. That interval is also from an unadjusted comparison and concerns the secondary endpoint measured at hospital discharge. It should not be used to infer the precision of the primary 12-month endpoint or of the sponsor’s primary Bayesian analysis.

Precision is not the same as importance, absence of bias, or certainty about a broader clinical interpretation. The primary interval’s location and width describe the recalculated comparison under its assumptions. The registry does not report enough information to assess all analysis choices, missing-data effects, or the influence of the specified analysis population on the sponsor’s result.

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 illustrative sample sizes per arm, not totals of trial participants. They use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The primary sample-size illustration is based on the observed primary difference; it gives participants per arm for 80% power and participants per arm for 90% power at each stated effect fraction. For the procedure-success outcome, the figures likewise refer to participants per arm, not total events.

The 80% power column describes the number of participants per arm in a hypothetical planning scenario intended to have an 80% chance of detecting the chosen effect under the stated assumptions. The 90% column describes a corresponding scenario with a higher target probability of detecting that effect. In general, the higher target requires a larger planned sample. The rows for 75% and 50% of the observed effect illustrate that smaller effects require more participants per arm under the same planning assumptions.

For example, the primary illustration lists 3 participants per arm for 80% power and 3 for 90% when planning for 100% of the observed effect. Planning for 75% of the observed effect gives 4 and 5 participants per arm, respectively; planning for 50% gives 9 and 11. The procedure-success illustration lists 818 and 1,095 participants per arm for 100% of the observed effect, 1,377 and 1,842 for 75%, and 2,920 and 3,908 for 50%.

These are planning illustrations computed from observed effects, not the trial’s original design calculations. They are not observed power. The trial’s own sample-size assumptions and justification are not reported in the registry record, so the illustrations should not be read as evidence that the study was planned using these values.

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 = 2.580; pooled standard deviation σ = 0.930.
2. n = 2 × (1.96 + 0.842)² × 0.930² / 2.580² = 2.0, rounded up to 3 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 <- 2.58                      # observed difference in means
sigma <- 0.929545365840723                     # 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(2389946)
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 = 3 (80% power), 3 (90% power)
 75% of observed effect: n per arm = 4 (80% power), 5 (90% power)
 50% of observed effect: n per arm = 9 (80% power), 11 (90% power)
power.t.test: 3.3 
Simulated power at n = 3 per arm: 0.719 (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. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as a Bayesian posterior probability of non-inferiority of 100. The posted recalculation is a simple unadjusted comparison of the group summaries: the mean difference is 2.58 for Xience minus Orsiro, with a confidence interval of 2.454 to 2.706 and an unadjusted p-value of <0.001. These are not two versions of the same statistic. One is the stated Bayesian non-inferiority result; the other is a conventional unadjusted recalculation.

The sponsor’s result should be distinguished from the recalculated estimate rather than replaced by it. The registry does not report the non-inferiority margin, the Bayesian model, priors, or an interval for the posterior probability, which limits independent evaluation of the sponsor analysis. The recalculation provides a transparent comparison of posted summaries but does not reproduce the sponsor’s analysis or establish that the same assumptions and analysis population were used.

The discrepancy flag is false, so the registry’s reported value and the recalculation are not identified as discrepant. Their differing statistical forms still matter: a p-value and a posterior probability answer different questions and use different frameworks. The registry entry does not provide enough methodological detail to reconcile them more fully.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and several secondary outcomes, but does not report a complete statistical analysis plan. In particular, the multiplicity strategy for secondary endpoints and component analyses is not reported in the registry record. When several outcomes are tested, unadjusted p-values do not control the overall chance of false-positive findings across the family of comparisons. A nominal p-value should consequently be interpreted in the context of the prespecified testing strategy, which is not available.

The primary result is reported as a Bayesian posterior probability of non-inferiority. The non-inferiority margin, model, prior distributions, and posterior interval are not reported in the registry record. Those details are important for interpreting what probability was calculated and what threshold defined non-inferiority. The registry also does not report whether interim analyses were planned or conducted.

The primary population description refers to BIOFLOW-V intent-to-treat subjects meeting an endpoint or follow-up condition and eligible BIOFLOW-II and BIOFLOW-IV subjects. The description is truncated. The complete analysis-population definition, and whether the other outcome analyses used the same population, are not reported in the registry record. The use of a population incorporating subjects from other studies is described in the primary analysis entry, but its full eligibility and pooling details are unavailable.

Missing-data methods are not reported in the registry record. The record does not specify how incomplete follow-up, missing outcome status, withdrawals, or other deviations were handled. It also does not give enough detail to determine how participants without a full 12-month observation contributed to the primary analysis, beyond the partial wording about follow-up in the Bayesian population description. These omissions limit assessment of potential bias and of how closely the posted analysis follows the randomized assignment.

These are reporting limitations, not evidence that a particular method was or was not used. The available record supports a description of the posted estimates and stated analysis result, but not a complete audit of multiplicity control, missing-data handling, or analysis-population decisions.

16. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: coronary artery stenosis (13.0%), angina pectoris (10.9%), non-cardiac chest pain (10.4%), angina unstable (7.1%), acute myocardial infarction (5.3%).

The serious adverse event listing reports 548 affected participants among 884 at risk for the Orsiro group and 293 among 450 at risk for the Xience group. Deaths are listed as 56 for Orsiro and 27 for Xience. These figures are reported as separate safety information; the registry entry does not specify in this summary whether the deaths were attributed to treatment or to a particular cause. The safety denominators differ from the primary outcome group sizes, and the reasons for the denominator differences are not reported in the registry record.

The registry lists serious adverse event terms including coronary artery stenosis at 13.0%, angina pectoris at 10.9%, non-cardiac chest pain at 10.4%, angina unstable at 7.1%, acute myocardial infarction at 5.3%, and coronary artery dissection at 4.4%. These are listed terms and percentages; the posted summary does not give additional detail on attribution, timing, overlap between terms, or how each percentage was calculated.

Serious adverse event counts should be interpreted in light of their definitions, observation period, and participant-level denominators. The registry does not provide those details in the available safety summary, so these numbers alone do not establish comparative causation or explain the nature of individual events.

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

The posted results describe a randomized comparison of two coronary stent systems and report a 12-month target lesion failure percentage for each group. The primary group values are 6.32 for Orsiro and 8.9 for Xience. The unadjusted recalculation estimates a mean difference of 2.58 for Xience minus Orsiro, with a confidence interval of 2.454 to 2.706. Separately, the registry reports a Bayesian posterior probability of non-inferiority of 100.

These results do not all have the same interpretation. The recalculated difference is an unadjusted comparison based on posted summary statistics. The posterior probability is the registry’s reported Bayesian non-inferiority result, but the margin and complete analysis method are not reported. The two should not be collapsed into a single conclusion, and the recalculation does not reproduce the sponsor’s analysis.

The endpoint is a composite of cardiac death, target-vessel myocardial infarction, and clinically driven target lesion revascularization. A single composite percentage does not reveal the contribution or clinical course of each component. The registry lists component-related secondary outcomes, but numerical results for those outcomes are not available in the posted detail used. The result also applies to the stated endpoint and follow-up, not automatically to other outcomes, populations, or durations.

The registry does not report the complete analysis plan, missing-data methods, the non-inferiority margin, or all analysis-population details. Those gaps limit what can be concluded about the robustness and scope of the sponsor’s analysis. The posted statistics describe the recorded results and their stated precision; they do not by themselves establish a universal or individual-level outcome, nor do they provide medical advice.

18. Why This Trial Matters Statistically

This trial illustrates why the estimand, analysis method, and endpoint definition matter as much as a headline result. The primary endpoint combines multiple events, while the registry’s formal result is a Bayesian non-inferiority probability. The posted unadjusted recalculation supplies a different lens on the same group summaries. Keeping these quantities separate helps prevent a descriptive difference or a p-value from being mistaken for the sponsor’s non-inferiority analysis.

The trial also demonstrates the importance of reporting the margin and model for a non-inferiority analysis. A posterior probability is not self-interpreting: readers need to know the claim being evaluated and the statistical assumptions used to evaluate it. The registry reports a probability value but omits those key specifications, limiting independent scrutiny.

Secondary outcomes and safety results broaden the record, but they raise additional interpretive questions. Several outcomes are listed, while detailed numerical secondary findings are not available for most of them. The procedure-success comparison is unadjusted, and multiplicity handling is not reported. The serious adverse event summary gives counts and selected terms but does not supply full attribution or observation details. Together, these features show why transparent reporting of populations, uncertainty, missing data, and outcome components is essential for clinical trial interpretation.

Finally, planning calculations based on an observed effect are not a substitute for the original sample-size rationale. A planning illustration can show how required sample size changes as the target effect changes, but it cannot reveal what assumptions governed the completed study. Distinguishing illustrative planning from trial design and observed outcomes is important when assessing evidence strength.

19. Limitations

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

Several trial-specific limitations of interpretation follow from incomplete registry reporting. The primary population description is truncated and refers to participants from BIOFLOW-V, BIOFLOW-II, and BIOFLOW-IV under eligibility and follow-up conditions. The full criteria and the relationship between those groups in the analysis are not reported in the registry record. That makes it difficult to determine the exact population represented by the reported Bayesian result.

The registry does not provide the non-inferiority margin, Bayesian model, prior distributions, or posterior interval. Without those details, readers cannot independently reproduce the sponsor’s primary analysis or assess sensitivity to its assumptions. The recalculated confidence interval is an unadjusted comparison and cannot remedy this limitation.

Detailed methods for randomization, masking, endpoint adjudication, missing observations, and deviations from assigned treatment are not reported in the registry record. The original sample-size justification and the trial’s own design assumptions are also not reported. The planning illustrations are based on observed effects and should not be treated as documentation of the original design.

The posted secondary information does not include numerical findings for most listed secondary outcomes, and a multiplicity plan is not reported. Safety counts and selected serious adverse event terms are available, but the summary does not provide full attribution, timing, overlap, or other context. These reporting gaps restrict interpretation of the breadth, robustness, and safety profile of the results without establishing that any specific method was omitted or any specific event was caused by a stent.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Effectiveness of the Orsiro Sirolimus Eluting Coronary Stent System in Subjects With Coronary Artery Lesions — NCT02389946.
• Registry record last updated 2022-08-03; status last verified 2022-08.
• Results first posted 2019-08-01.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT02389946 is a completed, randomized, single-masked, parallel-group study comparing the Orsiro sirolimus coronary stent system with the Xience everolimus coronary stent system. The registry describes it as prospective and multicenter, lists enrollment as 1334, and names Biotronik, Inc. as sponsor. The study start is 2015-05 and primary completion is 2017-04.

The primary outcome is the percentage of participants with TLF at 12 months. The posted group values are 6.32 for Orsiro and 8.9 for Xience. The registry reports a Bayesian posterior probability of non-inferiority of 100; the margin and full analysis specifications are not reported in the registry record. A separate unadjusted recalculation gives a mean difference of 2.58 for Xience minus Orsiro, with a confidence interval of 2.454 to 2.706 and p < 0.001.

Procedure success is reported as a secondary outcome at hospital discharge. The record also lists other secondary and safety outcomes, but detail is incomplete for independent interpretation of several methods and results.