Study Comparing the MiStent SES Versus the XIENCE EES Stent: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study Comparing the MiStent SES Versus the XIENCE EES Stent (NCT02385279), a randomized na study. The primary outcome is Number of Participants With Occurrence of a Device Oriented Composite Endpoint (DOCE).

2. Clinical Question

The registry describes the objective as comparing the performance of MiStent and XIENCE in an all-comers population with symptomatic ischemic heart disease. It also describes follow-up through 3 years for major clinical events. The posted primary outcome, however, is specifically assessed at 12 months. That distinction matters: the primary result addresses the stated endpoint and timeframe, not every possible clinical outcome or the entire planned follow-up period.

The study is a randomized comparison of two device strategies. The clinical question is therefore comparative: how the recorded outcomes differed between participants allocated to MiStent and participants allocated to XIENCE EES. It is not a comparison against no intervention, and the registry record does not describe a non-stent control group.

3. Trial Design

The registry describes a multicenter randomized study using a parallel-group design with single masking. It lists MiStent and XIENCE EES as the two device interventions and records enrollment of 1398 participants. The record identifies coronary stenosis as the condition under study. The phase is listed as NA.

Participants were assigned to one of the two device groups. The posted primary outcome uses an intention-to-treat population, meaning the registry identifies the primary analysis population by randomized assignment rather than by a reported treatment received classification. The arm counts for the primary outcome are 703 for MiStent and 695 for XIENCE EES.

The intervention descriptions specify percutaneous coronary intervention with the respective stent system. MiStent is described as sirolimus-eluting with an absorbable polymer coating; XIENCE EES is described as everolimus-eluting with a non-erodible or durable polymer coating. These are registry descriptions of the devices, not evidence that the study isolates any single device feature as the cause of an outcome difference.

The brief summary describes planned follow-up through 3 years for major clinical events. The primary endpoint reported in the results is at 12 months postprocedure. The registry record does not report the randomization sequence generation, allocation concealment, the identity of the party or parties masked, or details of how masking was maintained. It also does not report the trial's original sample-size justification or the statistical analysis plan. Those details should not be inferred from the randomized, single-masked, parallel design labels.

The study is marked completed. The registry record gives a primary completion date, but the results concern the posted endpoint counts and comparisons rather than the study's complete follow-up history. The record does not report whether all participants completed every planned follow-up assessment.

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: Intention-to-treat

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 Number of Participants With Occurrence of a Device Oriented Composite Endpoint (DOCE), measured over 12 months postprocedure.

The primary endpoint is the number of participants with a device-oriented composite endpoint at 12 months postprocedure. The composite includes cardiac death, myocardial infarction not clearly attributable to a non-target vessel, and clinically indicated target lesion revascularization. A participant is counted as having the endpoint if an event meeting the registry definition occurred; the reported outcome is a participant count rather than a count of every event episode.

Composite endpoints are used in clinical research to bring several clinically relevant outcomes into one prespecified measure. General statistical explanation: combining outcomes can capture a wider range of ways participants may experience an event and can make a single comparison possible when individual components occur less often. But the combined result does not show which component accounts for the overall pattern. Components can differ in clinical importance, frequency, and how they are determined. The registry record does not report the component-specific counts for the primary endpoint.

The endpoint's timeframe is 12 months postprocedure, and the population is identified as intention-to-treat. The registry reports 40 participants with the endpoint among 703 in the MiStent group and 45 among 695 in the XIENCE EES group. These counts describe the endpoint under the stated definition and timeframe; they do not by themselves establish a causal explanation for any difference between groups.

The registry record does not report additional detail about endpoint adjudication, the operational criteria for each component, or the handling of events with incomplete classification. Such details could help readers assess how consistently events were identified, but they cannot be recovered from the posted endpoint description alone.

7. Results Posted in the Registry

• XIENCE EES: 6.5% (45/695) versus 5.7% (40/703) on control; risk difference 0.8 percentage points (95% CI -1.7 to 3.3), risk ratio 1.14 (0.75–1.72); unadjusted two-proportion z-test p = 0.539.

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.

POCE

• 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 EES: 14.5% (101/695) versus 13.2% (93/703) on control; risk difference 1.3 percentage points (95% CI -2.3 to 4.9), risk ratio 1.10 (0.85–1.43); unadjusted two-proportion z-test p = 0.481.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between XIENCE EES and the control. The interval gives the range of effects that remain compatible with the data.

MACE

• 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 EES: 9.4% (65/695) versus 9.2% (65/703) on control; risk difference 0.1 percentage points (95% CI -2.9 to 3.2), risk ratio 1.01 (0.73–1.40); unadjusted two-proportion z-test p = 0.945.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between XIENCE EES and the control. The interval gives the range of effects that remain compatible with the data.

Target Vessel Failure (TVF)

• 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 EES: 7.6% (53/695) versus 6.4% (45/703) on control; risk difference 1.2 percentage points (95% CI -1.5 to 3.9), risk ratio 1.19 (0.81–1.75); unadjusted two-proportion z-test p = 0.370.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between XIENCE EES and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover a range of clinical events, including a broader composite, major adverse cardiac events, target vessel failure, death, myocardial infarction, revascularization, and stent thrombosis. Not all of these have posted numerical results in the record. The secondary outcomes with counts and comparisons at 12 months show no clear separation between the groups in the unadjusted comparisons, and their estimates are uncertain. This broad pattern is consistent with the primary comparison’s uncertainty, rather than providing a distinct, decisive pattern that overturns it.

Secondary endpoints help describe whether the primary result sits within a wider set of clinical outcomes. They can show whether outcome patterns appear directionally consistent or whether a particular outcome might merit further study. But they do not automatically validate or invalidate the primary result. Outcomes may overlap in their components, have different definitions, and occur with different frequency. The registry record does not report enough detail to determine how much overlap exists among all secondary outcomes.

Unadjusted secondary results carry less weight when several outcomes are examined. General statistical explanation: with multiple comparisons, the chance of obtaining at least one apparently unusual result can increase even when no underlying effect exists. Adjustment procedures or a prespecified hierarchy can address that issue, but the registry record does not report whether such procedures were planned or used. The secondary comparisons should therefore be regarded as descriptive rather than treated as a set of independent confirmatory tests.

The registry record lists secondary outcome measures but does not report analyses for several of them. The absence of a posted analysis is not evidence that no events occurred; it means that a corresponding result is not reported in the registry record. Interpretation should be limited to outcomes with posted counts and comparisons, and should not extrapolate from them to unreported outcomes or later follow-up.

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

• POCE
• MACE
• Target Vessel Failure (TVF)
• All-cause Death
• Myocardial Infarction
• Any Revascularization
• Stent Thrombosis

9. Statistical Interpretation

10. Statistical Methods Explained

The results are binary participant outcomes: each participant is classified according to whether the endpoint occurred within the stated timeframe. General statistical explanation: for a binary outcome, a group’s event proportion is the number of participants with the event relative to the number assessed in that group. Comparing proportions makes the groups interpretable on a common scale, while counts retain the actual number of participants represented. The registry posts both group counts and comparison measures for the primary and several secondary outcomes.

What does the risk difference describe?

The posted risk difference compares the event proportion in XIENCE EES with the event proportion in MiStent. A positive value means the proportion is higher in XIENCE EES; a negative value means it is higher in MiStent. A value of zero corresponds to equal proportions. The primary estimate is 0.008. Its confidence interval extends from -0.017 to 0.033, so it includes zero. The comparison is presented as unadjusted; the registry record does not report a sponsor-adjusted estimate for this endpoint.

Risk differences are expressed on an absolute scale. General statistical explanation: this scale describes how far apart the two event proportions are, rather than how many times one proportion is the other. The posted risk ratio and odds ratio are relative scales. Their values compare the groups multiplicatively, but they can be less direct to interpret clinically when the underlying proportions are not stated alongside them. These different measures answer related questions and should not be treated as separate studies or independent evidence.

How should the confidence interval be understood?

A confidence interval expresses uncertainty in an estimate under the statistical method used to construct it. General statistical explanation: a wider interval indicates less precision, while a narrower interval indicates greater precision. For a risk difference, an interval that includes zero leaves open the possibility of no difference in the underlying proportions. It can also include meaningful differences in either direction. The interval does not show the probability that the true value lies within its particular bounds, and it does not account for possible bias, missing outcomes, or analysis choices that are not represented by the calculation.

The primary risk-difference interval is reported as -0.017 to 0.033. The relative-measure intervals are also reported: 0.753 to 1.72 for the risk ratio and 0.739 to 1.781 for the odds ratio. General statistical explanation: the no-difference reference is zero for a risk difference and one for ratio measures. Since the posted intervals include their respective reference values, none of these interval estimates rules out no association at the level represented by the interval calculation.

What does the p-value add?

The posted unadjusted p-value for the primary comparison is 0.539. General statistical explanation: a p-value measures how compatible the observed data, or more extreme data, are with a specified null model, assuming the model and analysis conditions hold. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The registry record does not state the exact testing procedure used for the posted comparison, so the p-value should be described as reported rather than attributed to an unreported test.

The estimate, interval, and p-value serve different purposes. The estimate gives the direction and size of the observed contrast, the interval indicates the range of values compatible with the data and calculation, and the p-value summarizes compatibility with a null model. They should be read together. A p-value alone cannot tell readers whether an estimate is precise or whether possible values are consequential.

Why does the outcome definition matter?

The primary endpoint combines cardiac death, myocardial infarction not clearly attributable to a non-target vessel, and clinically indicated target lesion revascularization. General statistical explanation: a composite can increase the number of participants counted as having an outcome, but an overall composite may conceal differences among its components. A composite result is most interpretable when the components are clinically coherent and component results are available. The registry record does not report component-specific primary endpoint results, so the overall count cannot identify which component contributed to the observed cases.

The posted primary population is intention-to-treat. General statistical explanation: intention-to-treat analysis generally preserves comparison by randomized assignment and can help maintain the balance created by randomization. The registry record does not describe how participants with missing endpoint data were handled, whether all randomized participants were included in the posted counts, or whether any other analysis population was used. The arm denominators are posted, but the missing-data approach is not reported in the registry record.

The posted comparisons are unadjusted. The registry record does not report adjustment for baseline covariates, stratification factors, or multiplicity. It also does not report a statistical analysis plan or explain whether the displayed comparisons were designated as confirmatory. Those omissions limit what can be inferred about the intended testing framework. The appropriate reading is descriptive and comparative: note the group counts, contrast, uncertainty, and stated analysis population without supplying unreported methods.

11. Confidence Intervals and Precision

The primary estimate is accompanied by a 95% confidence interval for the risk difference from -0.017 to 0.033. The estimate itself is 0.008. Because the interval spans zero, the data are compatible with a small difference in either direction as well as no difference. The interval is the main guide to the precision of the risk-difference estimate; the point estimate alone would give an incomplete account.

General statistical explanation: a confidence interval reflects sampling uncertainty under the method used to calculate it. It does not include every source of uncertainty. For example, it cannot by itself show the effects of measurement error, outcome misclassification, unreported analysis decisions, or missing data. The registry record does not report enough detail to evaluate all those possibilities for this endpoint.

The posted relative estimates are less precise in the sense that their intervals also cover values on both sides of the no-association reference: the risk ratio is 1.138, with an interval from 0.753 to 1.72, and the odds ratio is 1.147, with an interval from 0.739 to 1.781. The three measures present the same comparison on different scales. Their intervals should not be interpreted as three independent replications.

Precision is not the same as importance. General statistical explanation: an estimate can be precise yet clinically unimportant, or imprecise while still allowing effects that would matter to a decision. The registry record does not report a prespecified threshold for a clinically important difference, so these intervals cannot be classified against such a threshold from the available record. They indicate uncertainty around the estimated comparison, not a direct judgment about clinical relevance.

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 sample-size figures are planning illustrations based on the observed effect, not the study’s original design calculation. For these binary outcomes, the displayed values are participants per arm. The 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 registry record does not report the trial’s own sample-size justification or original design assumptions.

The 80% power column describes the planned number of participants per arm under those assumptions for a design with an 80% chance of detecting the stated effect if that effect were true. The 90% power column gives the corresponding planning target for a 90% chance under the same assumptions. Power is a property of a hypothetical design and its assumed effect, not a measure of the probability that the posted finding is true.

Each planning row uses a different fraction of the observed effect. Planning for 75% of the observed effect and planning for 50% of the observed effect ask what sample size would be needed to target a smaller effect than planning for 100% of the observed effect. Smaller effects are harder to distinguish from sampling variation, so they require more participants under the stated assumptions. The figures are illustrations and should not be read as a reconstruction of the trial’s actual planning process.

These figures are not observed power. Observed power is not an informative substitute for reading the estimate and its confidence interval after results are available. The uncertainty in the posted comparison is better assessed from the effect estimate and interval, while the planning calculations show how assumptions about a target effect and desired power influence a hypothetical sample size.

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 = 0.057; treatment proportion p₁ = 0.065; average p̄ = 0.061.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3380 = 0.6625.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3380 = 0.2844.
4. n = (0.6625 + 0.2844)² / (0.0078)² = 14,553.6, rounded up to 14,554 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 <- 0.0568990042674253                          # control proportion
p1 <- 0.0647482014388489                          # 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(2385279)
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 = 14,554 (80% power), 19,483 (90% power)
 75% of observed effect: n per arm = 25,484 (80% power), 34,115 (90% power)
 50% of observed effect: n per arm = 56,458 (80% power), 75,581 (90% power)
power.prop.test: 14553.6 
Simulated power at n = 14,554 per arm: 0.805 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

The registry record does not report a multiplicity strategy for the secondary outcomes. It does not state that the study used a correction across multiple comparisons, a hierarchy of hypotheses, or another procedure to control the overall false-positive risk. The posted secondary comparisons are therefore described as unadjusted. They can be useful for context, but should not be treated as equivalent to a single prespecified primary test or as independently confirmatory findings.

The record lists seven secondary outcomes, but does not provide reported analyses for every listed measure. For several outcomes, the underlying counts, estimates, intervals, and p-values are not reported in the registry record. No result should be inferred from an outcome name alone. The registry also does not report whether the absence of an analysis reflects unavailable data, a decision not to post a result, or another reason.

The primary endpoint population is identified as intention-to-treat. The registry record does not report the detailed analysis population for the secondary outcomes, nor whether any additional per-protocol or safety population was analyzed. It does not describe how participants who withdrew, missed a visit, or had incomplete outcome information were handled. The posted arm denominators do not establish that there were no missing observations or that all randomized participants contributed complete follow-up.

Missing-data methods can affect interpretation when outcome status is unavailable. General statistical explanation: complete-case analysis, imputation, and other approaches rely on different assumptions about why data are missing and what the unobserved outcomes might have been. Without a reported method, readers cannot assess how missingness was addressed or conduct a meaningful sensitivity assessment from the registry summary alone.

The registry record also does not report a full statistical analysis plan, the prespecified testing framework, or the detailed handling of endpoint adjudication. These gaps do not negate the posted counts, but they constrain claims about confirmatory inference, robustness, and the impact of multiple testing or incomplete data.

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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: other (58.9%), myocardial infarction (2.4%), definite stent thrombosis (0.7%).

The registry reports serious adverse event counts for 434 participants in the MiStent group and 426 in the XIENCE EES group. It reports other, non-serious adverse event counts for 76 and 71 participants, respectively. Death counts are listed as 85 for MiStent and 78 for XIENCE EES. These are participant counts in the safety groups, whose at-risk denominators are reported as 703 and 695.

The record lists the most common serious adverse event terms as Other at 58.9%, myocardial infarction at 2.4%, and definite stent thrombosis at 0.7%. The registry record does not state the denominator used for these percentages in the summary, nor does it provide the full event-term breakdown in the listed details. The percentages should therefore be read as registry-listed summaries, not recalculated or assigned an unstated denominator.

These safety counts are descriptive. They do not by themselves establish that the devices differ in safety, because the record does not provide a comparative safety analysis, uncertainty estimates, or details about event ascertainment and follow-up. Serious adverse event totals may also include different types of events, as indicated by the broad Other category. The counts should be interpreted alongside the definitions and limitations reported in the registry record, without assuming that unposted safety analyses were performed.

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

The results describe the recorded participant outcomes for two randomized device groups. At 12 months, the primary device-oriented composite occurred in 40 participants in the MiStent group and 45 in the XIENCE EES group. The posted unadjusted risk difference is 0.008, and its 95% confidence interval, -0.017 to 0.033, includes zero. This means the posted estimate does not precisely distinguish between no difference and differences in either direction within the interval.

The result does not demonstrate that the devices are identical. Failure to show a clear difference is not the same as evidence of equivalence. An equivalence conclusion requires a prespecified margin and an analysis designed to evaluate whether the difference lies within that margin; the registry record does not report such a margin or conclusion. Similarly, a non-inferiority conclusion requires a defined non-inferiority framework, which is not reported in the registry record.

The result also does not establish that either device is superior. The point estimate favors MiStent on the observed event proportion, but the interval includes zero and extends to values in the other direction. The posted p-value does not establish the probability that either device is better. Statistical uncertainty should be kept distinct from clinical importance, for which the registry record does not report a prespecified threshold.

The primary endpoint is a composite assessed at 12 months. The reported result does not identify which component contributed to the events, and it cannot be extended to every component, every secondary endpoint, or the full follow-up described in the study objective. Likewise, safety counts alone are not a comparative safety conclusion.

The registry summary does not provide details needed to resolve questions about missing data, multiplicity, the exact statistical test, or the original design assumptions. The most defensible interpretation is limited to the posted counts, unadjusted comparisons, confidence intervals, and stated endpoint definitions. Further claims require information not reported in the registry record.

17. Why This Trial Matters Statistically

This trial illustrates how a randomized comparison can produce a clear description of observed group outcomes while leaving substantial uncertainty about the underlying difference. The primary event counts are close in scale, and the posted risk-difference interval crosses zero. The central statistical lesson is to read the estimate together with its interval rather than treat the observed direction or the p-value as a complete answer.

The endpoint also demonstrates the trade-offs involved in composite outcomes. Combining cardiac death, specified myocardial infarction, and clinically indicated target lesion revascularization creates one summary endpoint, but the overall count cannot show whether its components have similar patterns. Component-level results would help readers distinguish what drives the composite; those results are not reported in the registry record.

The study is randomized and the primary population is identified as intention-to-treat, features that are important to the design and interpretation. Yet design labels do not supply every methodological detail. The registry does not report the allocation procedure, complete masking details, analysis plan, sample-size justification, or missing-data handling. Statistical interpretation depends both on the numerical result and on understanding how that result was generated.

The secondary outcomes further emphasize the importance of prespecification. Unadjusted comparisons across several outcomes can be informative as context, but they require caution when no multiplicity strategy or hierarchy is reported. A collection of secondary results should not be treated as a set of independent tests that each carries the same evidential weight as the primary endpoint.

For biostatistical reading, the case is a reminder to separate descriptive counts, estimated contrasts, uncertainty, and claims of equivalence or superiority. Those are distinct questions. The posted data address the observed outcomes and estimated comparisons; they do not settle every clinical or methodological question about the devices.

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 a concise outcome summary rather than a complete report of trial conduct and analysis. It does not report the original sample-size justification, so the planning illustrations based on the observed effect cannot be taken as evidence about the study’s prospective design choices. The record also does not report a detailed statistical analysis plan, including the exact test used for the posted comparisons or whether any adjusted primary analysis was conducted.

The primary endpoint is composite, but the registry record does not provide component-specific counts. Readers therefore cannot determine from the posted primary result how much each component contributed. The endpoint description also does not include detailed adjudication procedures or operational criteria beyond the listed definitions.

Missing-data handling is not reported. Although the primary outcome population is identified as intention-to-treat, the record does not specify whether all randomized participants had known endpoint status or how incomplete observations were treated. The posted denominators alone do not resolve that question.

The record does not report a multiplicity plan for the secondary outcomes, and analyses are not posted for all listed secondary measures. This limits confirmatory interpretation of the secondary findings and prevents conclusions about outcomes without reported results. Follow-up through 3 years is described in the study objective, while the posted primary endpoint is at 12 months; the registry summary does not provide the complete later outcome pattern.

Finally, the registry lists serious adverse event counts and selected terms but does not provide a full safety analysis with comparative uncertainty, complete event definitions, or all event-term details. These limitations do not change the reported values, but they restrict how broadly those values can be interpreted.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Study Comparing the MiStent SES Versus the XIENCE EES Stent — NCT02385279.
• Registry record last updated 2023-05-08; status last verified 2022-07.
• Results first posted 2023-05-08.
• 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 describes a completed, multicenter randomized parallel-group study comparing MiStent with XIENCE EES in an all-comers population with symptomatic ischemic heart disease. Enrollment was 1398, and the primary outcome population is identified as intention-to-treat.

The primary endpoint was the number of participants with a device-oriented composite of cardiac death, specified myocardial infarction, or clinically indicated target lesion revascularization at 12 months postprocedure. The posted comparison gives 40 events among 703 participants assigned to MiStent and 45 among 695 assigned to XIENCE EES. Its unadjusted risk difference is 0.008, with a 95% confidence interval from -0.017 to 0.033.

The registry also lists secondary outcomes and safety counts. The record does not report the original sample-size justification, a complete statistical analysis plan, detailed missing-data methods, or a multiplicity strategy. The posted results therefore support a focused interpretation of the observed counts and their uncertainty, not broader conclusions that depend on unreported analyses.