SPIRIT V: A Clinical Evaluation of the XIENCE V® Everolimus Eluting Coronary Stent System in the Treatment of Patients With de Novo Coronary Artery Lesions (Diabetic Sub-Study): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for SPIRIT V: A Clinical Evaluation of the XIENCE V® Everolimus Eluting Coronary Stent System in the Treatment of Patients With de Novo Coronary Artery Lesions (Diabetic Sub-Study) (NCT01171820), a randomized phase 4 study. The primary outcome is In-stent Late Loss (LL).

2. Clinical Question

3. Trial Design

This was a randomized, single-masked, parallel-group phase 4 clinical evaluation. It was registered as SPIRIT V, a clinical evaluation of the XIENCE V® Everolimus Eluting Coronary Stent System for de novo coronary artery lesions, with the present record identifying a diabetic sub-study. The study status is completed. The registry lists enrollment of 324 and gives a start date of 2006-11 and primary completion date of 2009-07.

The two device groups were TAXUS® Liberté™ and XIENCE V® EECSS. The registry does not provide descriptions of the arms beyond their device names, nor does it report the masking role or the allocation ratio. The posted primary outcome summaries include 106 participants in the TAXUS® Liberté™ arm and 218 in the XIENCE V® EECSS arm. These are endpoint-specific numbers, not a substitute for the overall enrollment figure.

The primary endpoint was assessed at 270 days and required angiographic follow-up. The record states that the analysis was based on the intention-to-treat population, while also noting that some participants did not complete the study and did not have the angiographic follow-up needed to provide endpoint information. How missing endpoint values were handled is not reported in the registry record.

The registry lists 25 outcome measures, including clinical success measures, late-loss measurements, restenosis measures, and percent diameter stenosis. It records no posted analysis entries. A detailed statistical analysis plan, including the original sample-size rationale, allocation procedure, and any interim monitoring, is not reported in the registry record. The available record therefore supports a description of the registered design and posted summaries, but not a reconstruction of all planned procedures.

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.

Before assignment: Subjects were randomized via telephone randomization and stratified by insulin treatment status, number of lesions treated-single vs. multiple. Randomization only occurred after verification of the inclusion/exclusion criteria and successful pre-dilatation. See the Eligibility Criteria (inclusion/exclusion criteria) for details.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analysis based on intention to treat (ITT) population. Patients were required to have angiographic follow-up to provide this endpoint information. Some patients not completing the study, did not have this 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 In-stent Late Loss (LL), measured over 270 days.

In-stent late loss measures the change in the minimum lumen diameter inside the stent between the post-procedure measurement and the follow-up measurement. The registry defines it as post-procedure in-stent minimal lumen diameter minus in-stent minimal lumen diameter at follow-up. It is reported as a mean in millimeters, with standard deviations, at 270 days.

In general, a positive late-loss value reflects a smaller measured lumen at follow-up than immediately after the procedure. This makes the endpoint a way to describe change in the treated vessel segment over the follow-up interval. It is an angiographic measurement, rather than a direct count of clinical events or a measure of how participants feel or function.

In-stent late loss is useful for comparing the observed vessel measurements between device groups. Its interpretation depends on the availability and quality of angiographic follow-up. The registry explicitly says that participants needed follow-up angiography to contribute endpoint information and that some study non-completers lacked this follow-up. The numbers contributing to the endpoint were therefore 106 for TAXUS® Liberté™ and 218 for XIENCE V® EECSS, rather than the overall enrollment figure.

The endpoint gives information about a specific anatomical measurement at a specified follow-up time. It should be read alongside the uncertainty around the group comparison and the study’s other outcomes, rather than treated as a complete description of clinical benefit or harm.

7. Results Posted in the Registry

• XIENCE V® EECSS: mean 0.19 versus 0.39 on control; difference -0.20 (95% CI -0.31 to -0.09), standardized effect d = -0.48; 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.

Clinical Procedure Success (Per-patient)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • XIENCE V® EECSS: 96.7% (205/212) versus 93.1% (95/102) on control; risk difference 3.6 percentage points (95% CI -1.9 to 9.0), risk ratio 1.04 (0.98–1.10); unadjusted two-proportion z-test p = 0.152.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between XIENCE V® EECSS and the control. The interval gives the range of effects that remain compatible with the data.

In-segment Late Loss

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • XIENCE V® EECSS: mean 0.12 versus 0.22 on control; difference -0.10 (95% CI -0.20 to 0.00), standardized effect d = -0.23; z-test p = 0.055.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between XIENCE V® EECSS and the control. The interval gives the range of effects that remain compatible with the data.

Proximal Late Loss

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • XIENCE V® EECSS: mean 0.13 versus 0.17 on control; difference -0.04 (95% CI -0.12 to 0.04), standardized effect d = -0.11; z-test p = 0.336.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between XIENCE V® EECSS and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover different aspects of procedure performance and vessel measurements, so they should not be treated as interchangeable measures of a single underlying result. Across the posted comparisons, the estimates do not all have the same degree of precision. The clinical procedure success estimate is directionally favorable to XIENCE V® EECSS, but its interval includes no difference. The continuous late-loss secondary estimates are also in the direction of lower values for XIENCE V® EECSS, yet their intervals reach or cross zero. These patterns provide context for the primary comparison without reproducing its strength of evidence.

The primary result concerns in-stent late loss and has an interval excluding zero. The secondary late-loss outcomes concern a broader segment or a particular vessel region, and their estimates are less precise. Procedure success is a separate binary outcome measured immediately after the procedure, not an angiographic measurement at the primary endpoint’s follow-up time. Thus, a difference or lack of clear difference in one outcome does not directly settle another outcome’s interpretation.

Unadjusted secondary results carry less weight because multiple outcomes are being considered and the registry does not report a multiplicity adjustment or a hierarchy for interpreting them. In general, testing many outcomes increases the chance that one or more comparisons will appear notable through random variation. The record lists numerous outcome measures, while no analysis entries are posted. Without the complete prespecified analysis plan, it is difficult to determine which secondary analyses were intended as confirmatory and which were exploratory.

Overall, the secondary findings are compatible with a pattern of numerically lower late-loss measurements in the XIENCE V® EECSS group, alongside uncertainty in the individual secondary comparisons. They do not independently establish a consistent effect across all measures, nor should they override the primary endpoint’s own estimate and limitations.

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

• Clinical Device Success (Per-lesion)
• Clinical Procedure Success (Per-patient)
• In-segment Late Loss
• Proximal Late Loss
• Distal Late Loss
• In-stent Angiographic Binary Restenosis Rate
• In-segment Angiographic Binary Restenosis Rate
• In-stent Percent Diameter Stenosis (% DS)

9. Statistical Interpretation

10. Statistical Methods Explained

What does a mean difference describe?

The primary endpoint is continuous: each participant’s measurement is expressed in millimeters, and the arm-level result is summarized by a mean. A mean difference compares those arm averages. The reported difference is calculated in the direction XIENCE V® EECSS minus TAXUS® Liberté™, so a negative value means the XIENCE V® EECSS mean is lower. This sign convention is important: reversing the order of the arms would reverse the sign without changing the underlying comparison.

The group means are 0.19 and 0.39, and the reported mean difference is -0.2. The accompanying standard deviations are 0.37 and 0.49. In general, a standard deviation describes the spread of participant measurements around an arm’s mean; it is not a confidence interval and does not give the precision of the mean by itself. The standard error, by contrast, describes uncertainty in an estimated mean or comparison under the statistical model.

How should the confidence interval be understood?

A confidence interval gives a range of estimates compatible with the observed data under the method used. For the primary mean difference, the interval is -0.305 to -0.095. Its limits are both below zero, which is consistent with the reported unadjusted p-value of <0.001 for a comparison against no mean difference. In general, an interval that includes zero does not establish a directional difference at the corresponding conventional significance threshold; it also does not prove that the groups are identical. An interval can include effects in more than one direction because the estimate remains uncertain.

The confidence interval is tied to its analysis assumptions. The record does not give a full statistical analysis plan, so it is not possible to assess every model choice from the registry entry alone. The posted comparison is an unadjusted comparison derived from the arm summaries. It should not be confused with an adjusted model that accounts for participant characteristics or other covariates.

What does an unadjusted p-value say?

A p-value is a measure of how unusual the observed data, or data more extreme, would be if a specified null hypothesis and test assumptions held. It does not measure the size or practical importance of an effect. It is not the probability that the result happened by chance, and it is not the probability that one device is better. The primary unadjusted p-value is reported as <0.001. The accompanying estimate and confidence interval are needed to understand direction and magnitude.

The record contains no posted analysis entries. The available unadjusted calculations should thus be read as comparisons of the reported summaries, not as a substitute for a full sponsor analysis plan or a detailed model specification. No covariate adjustment is described in the registry record.

Why does follow-up matter for this endpoint?

The primary outcome requires an angiographic follow-up measurement. The registry says the analysis population was intention to treat, but it also says that some participants did not complete the study and lacked the follow-up needed for endpoint information. In general, an intention-to-treat approach aims to analyze participants according to their randomized assignment. Missing outcome measurements can complicate that goal, because the method used to address missing values may affect the estimates. The record does not report whether imputation, weighting, or another missing-data method was used. It also does not report how missingness was assessed or whether its reasons differed between groups.

For this reason, the endpoint-specific arm counts should be kept distinct from overall enrollment. The reported primary results use 106 participants in the TAXUS® Liberté™ arm and 218 in the XIENCE V® EECSS arm. The record does not give enough detail to infer the characteristics of participants without angiographic follow-up or the effect of their absence on the comparison.

Why does variation matter?

The standard deviations show that individual measurements vary within both groups. In general, greater variation makes it harder to estimate a group mean precisely when the number of observations is unchanged. The standard errors shown for the arm means are 0.048 and 0.025. They describe estimated uncertainty for each arm’s mean, while the confidence interval for the mean difference describes uncertainty in the contrast between arms.

Variation can also signal that a mean alone does not describe every participant’s experience or measurement. The posted summary does not show the full distribution of participant values, so it cannot establish whether measurements were symmetric, skewed, or affected by outliers. The record does not report a diagnostic assessment of distributional assumptions.

How do secondary comparisons fit in?

The secondary outcomes include both continuous measures and a percentage-based clinical success measure. A mean difference is used for continuous outcomes, while a risk difference expresses the difference between event proportions. In general, confidence intervals for a risk difference can include zero even when the observed percentages are not identical. That means the data may be compatible with no difference as well as with effects in either direction.

The posted secondary comparisons are unadjusted. When multiple outcomes are evaluated, each test adds another opportunity for a chance finding. In general, multiplicity procedures can control the error rate across a family of tests, but the registry does not report such a procedure. Secondary results therefore warrant a more cautious reading than a prespecified primary comparison, especially when the analysis plan and hierarchy among outcomes are not available.

11. Confidence Intervals and Precision

The primary mean difference is -0.2 millimeters, with a confidence interval from -0.305 to -0.095. The interval is entirely below zero, and the unadjusted p-value is <0.001. These features indicate that the posted summary data estimate a directional difference with more precision than would be conveyed by a broad interval spanning zero. The interval still permits a range of possible magnitudes; it does not identify a single exact underlying difference.

Precision is distinct from clinical importance. A narrow interval can indicate a relatively precise estimate without answering whether the difference matters to patients or clinicians. The registry does not report a threshold for clinical importance, and the endpoint is an angiographic measurement. The posted result should therefore be interpreted as a comparison of measured late loss, not as a direct measure of the importance of that difference.

For the secondary comparisons, the intervals are less conclusive about direction. The clinical procedure success risk-difference interval ranges from -0.019 to 0.090. The in-segment late-loss interval ranges from -0.202 to 0.002, and the proximal late-loss interval ranges from -0.121 to 0.041. Each interval includes zero, so these estimates remain compatible with no difference under the corresponding unadjusted comparison. The precision varies across outcomes, and the outcomes also measure different features.

In general, confidence intervals reflect both the amount of information and the variability in the data, under the method’s assumptions. Unequal endpoint counts and missing angiographic measurements are relevant context for precision. The registry does not provide enough information to determine how alternative missing-data assumptions would change these intervals. The bounds should thus be read as uncertainty under the posted comparison, not as a guarantee that the true effect lies within the interval in every practical sense.

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 participants per arm, not totals across both arms. They are illustrations calculated from the observed effect, using the stated assumptions: a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. For the continuous primary outcome, planning for 100% of the observed effect gives 67 participants per arm for 80% power and 90 participants per arm for 90% power. Planning for 75% gives 119 and 160 participants per arm, while planning for 50% gives 268 and 359.

In general, power is the chance that a study will detect an effect of a specified size under the assumed statistical model, if that effect is real. The 80% column means the planning illustration targets an 80% chance of detecting its assumed effect; the 90% column targets a 90% chance. These are design calculations, not summaries of what happened in the completed study. This is not observed power.

The effect fractions describe progressively smaller target effects relative to the observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants under the same assumptions. The figures do not reconstruct the trial’s original design: the original sample-size assumptions and rationale are not reported in the registry record. They also rely on equal allocation, while the posted primary endpoint counts are unequal.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.200; pooled standard deviation σ = 0.413.
2. n = 2 × (1.96 + 0.842)² × 0.413² / -0.200² = 66.9, rounded up to 67 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.2                      # observed difference in means
sigma <- 0.41297962893228                     # 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(1171820)
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 = 67 (80% power), 90 (90% power)
 75% of observed effect: n per arm = 119 (80% power), 160 (90% power)
 50% of observed effect: n per arm = 268 (80% power), 359 (90% power)
power.t.test: 67.9 
Simulated power at n = 67 per arm: 0.800 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple outcomes, including the primary in-stent late-loss endpoint and secondary measures of clinical success, late loss in other locations, restenosis, and percent diameter stenosis. It reports 25 outcome measures and no analysis entries. A detailed statistical analysis plan, including any testing hierarchy or multiplicity adjustment, is not reported in the registry record.

In general, multiplicity arises when several hypotheses are tested in the same study. If each is assessed without accounting for the others, the chance of at least one false-positive result across the set can increase. Adjustments or prespecified testing sequences can address this issue, but no such method is described in the registry record. The secondary p-values should therefore be read as unadjusted, and should not be treated as if they provide family-wise confirmation across all endpoints.

The primary outcome description says the analysis was based on the intention-to-treat population. It also states that participants needed angiographic follow-up to provide endpoint information and that some participants who did not complete the study lacked this follow-up. The posted primary endpoint counts are 106 and 218 by arm. How missing measurements were handled is not reported in the registry record. There is no stated imputation method, sensitivity analysis, or account of reasons for missing angiograms. It is consequently not possible to assess whether the missingness could have influenced the arm comparison.

The registry also does not report whether any interim analyses were conducted, whether stopping rules were used, or how the original sample size was justified. These omissions do not negate the posted summary statistics, but they limit assessment of the intended testing process and the robustness of inferences beyond the reported unadjusted comparisons.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: angina pectoris (12.4%), myocardial infarction (8.6%), coronary artery stenosis (6.0%), arrhythmia (1.9%), in-stent coronary artery restenosis (1.9%).

The adverse-event summaries report serious adverse events for 41 of 105 participants at risk in the TAXUS® Liberté™ group and 100 of 215 at risk in the XIENCE V® EECSS group. Other adverse events are reported for 13 of 105 and 26 of 215, respectively. These are counts of participants affected, not event totals, and the risk-set numbers differ from the endpoint-specific sample sizes.

The registry lists serious-event terms including angina pectoris (12.4%), myocardial infarction (8.6%), coronary artery stenosis (6.0%), arrhythmia (1.9%), in-stent coronary artery restenosis (1.9%), and myocardial ischaemia (1.9%). The record does not establish in this listing that these percentages are arm-specific, so they should be read as the displayed serious-event terms and percentages rather than assigned to one device group. Death counts are not reported in the registry record.

These summaries are descriptive. The registry does not provide a comparative safety analysis, adjustment for differences between groups, or enough detail to attribute events to a device. Counts alone do not establish whether a difference is statistically meaningful or causal.

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

The central result is a comparison of mean in-stent late loss at 270 days. The XIENCE V® EECSS arm had a lower posted mean than the TAXUS® Liberté™ arm, with an unadjusted mean difference of -0.2 millimeters and a confidence interval entirely below zero. This indicates a statistical difference in the posted angiographic measurements under the reported unadjusted comparison.

That finding does not answer every question about the devices or the participants’ clinical outcomes. Late loss is a specific measurement of vessel diameter change inside the stent. It is not, by itself, a measure of symptoms, quality of life, survival, or the full balance of benefits and harms. The registry includes other outcomes, but the available secondary comparisons are less conclusive, and the record does not report a multiplicity procedure.

The result also depends on the endpoint data available. Angiographic follow-up was required, some participants did not have it, and the posted endpoint sample sizes differ by arm. Although the record describes an intention-to-treat analysis, it does not explain how missing endpoint values were handled. This leaves uncertainty about the potential effect of missingness on the estimate.

The trial’s single-masked randomized parallel design is relevant context, but details of masking, allocation procedures, the statistical analysis plan, and the original sample-size justification are not reported in the registry record. The posted results therefore support a focused interpretation of this outcome, rather than a broad conclusion about all aspects of comparative performance. No treatment recommendation follows from these statistical summaries alone.

17. Why This Trial Matters Statistically

This study illustrates why an endpoint’s definition and data availability matter as much as the headline comparison. In-stent late loss is a continuous angiographic measurement, and the comparison summarizes average values rather than the experience of every participant. The result is more interpretable when the direction of subtraction, units, follow-up time, group counts, and uncertainty interval are all considered together.

It also shows the distinction between enrollment and endpoint information. The registry records 324 participants enrolled, while the primary outcome summaries include 106 and 218 participants by arm. Because angiographic follow-up was required, missing measurements are a substantive issue for interpreting the primary comparison. An intention-to-treat label alone does not explain how unavailable outcomes were addressed.

The primary comparison and secondary outcomes also demonstrate why evidence across multiple endpoints needs careful organization. The primary interval excludes zero, while the posted secondary intervals include zero. Without the full analysis plan or a reported multiplicity procedure, secondary findings should be treated as contextual rather than as a collection of confirmatory claims.

Finally, the planning illustrations are not the trial’s original design calculation. They show how assumed effect size and target power relate to required participants under stated assumptions, but the original rationale is not reported. Separating observed results, uncertainty, missing-data limitations, and planning illustrations helps prevent each from being mistaken for another.

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.

A principal limitation is the requirement for angiographic follow-up to contribute the primary endpoint. The registry notes that some participants who did not complete the study lacked this follow-up, but does not report the number missing, their reasons, or how missing measurements were handled. This makes it difficult to assess possible bias from incomplete endpoint data.

The primary endpoint counts are markedly unequal between arms, and are not the same as overall enrollment. The registry does not explain the sources of this difference in the endpoint summaries. Although the study is described as randomized and the analysis as intention to treat, the record does not give enough detail to determine how randomization assignment and incomplete measurements were reconciled in the endpoint analysis.

The registry does not report a full statistical analysis plan, the trial’s original sample-size assumptions, interim analysis procedures, allocation ratio, or details of who was masked. It also does not report a multiplicity adjustment for the many listed outcomes. These gaps limit assessment of prespecification, analysis choices, and the strength of secondary inferences.

The available adverse-event information is descriptive, and death counts are not reported in the registry record. The serious-event percentages are not clearly identified as arm-specific in the listed terms. These limitations mean the summaries do not support detailed comparative attribution of adverse events.

The trial concerns a diabetic sub-study of participants with de novo coronary artery lesions. The registry record does not give enough demographic or clinical detail to assess how broadly these results apply to populations outside the registered study context. The endpoint itself is an angiographic measure, so it does not capture all dimensions of clinical outcome.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: SPIRIT V: A Clinical Evaluation of the XIENCE V® Everolimus Eluting Coronary Stent System in the Treatment of Patients With de Novo Coronary Artery Lesions (Diabetic Sub-Study) — NCT01171820.
• Registry record last updated 2016-06-27; status last verified 2016-06.
• Results first posted 2010-10-21.
• 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

SPIRIT V was a completed, randomized, single-masked, parallel-group phase 4 study registered as a diabetic sub-study. It compared TAXUS® Liberté™ with XIENCE V® EECSS in participants with de novo coronary artery lesions. Enrollment was 324, and the registry gives study dates from 2006-11 to primary completion in 2009-07.

The primary endpoint was mean in-stent late loss at 270 days, measured in millimeters and requiring angiographic follow-up. Posted means were 0.39 for TAXUS® Liberté™ and 0.19 for XIENCE V® EECSS; the unadjusted difference was -0.2, with a confidence interval excluding zero and p <0.001.

Interpretation is limited by incomplete angiographic follow-up, the absence of reported missing-data methods, and the lack of a detailed statistical analysis plan or multiplicity procedure in the registry record. Secondary outcomes and adverse-event counts provide context but do not replace the primary endpoint comparison or establish broader clinical conclusions.