Safety and Efficacy Study of Lotus Valve for Transcatheter Aortic Valve Replacement: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy Study of Lotus Valve for Transcatheter Aortic Valve Replacement (NCT02202434), a randomized na study. The primary outcome is Percentage of Participants With Events Included in the Primary Safety Endpoint.

2. Clinical Question

The endpoint combines all-cause mortality, stroke, life-threatening and major bleeding events, stage 2 or 3 acute kidney injury, and major vascular complications. The registry also lists effectiveness as part of the study objective, but the posted primary outcome described in this record is the composite safety measure. The randomized comparison should be distinguished from the additional single-arm cohorts: outcomes in those cohorts do not provide a randomized estimate against the CoreValve/Evolut R arm.

3. Trial Design

REPRISE III is a randomized, parallel-group clinical evaluation of transcatheter aortic valve replacement devices in participants with symptomatic, calcific, severe native aortic stenosis considered at extreme or high surgical risk. The registry lists no masking. The study began on 2014-09-22, had primary completion on 2017-03-08, and is marked terminated. The reason for termination is not reported in the registry record.

The randomized arms compare Lotus Valve System with the CoreValve/Evolut R Transcatheter Aortic Valve Replacement System. For the primary endpoint, the registry identifies the implanted population in those randomized arms. Its reported arm denominators are 577 for Lotus and 297 for CoreValve. These outcome denominators should not be treated as the total enrollment: overall enrollment is 1425, and the record also contains nonrandomized cohorts.

Those additional cohorts include a Lotus 21mm cohort, a continued-access cohort, a roll-in cohort, and a LOTUS Edge nested registry using 23mm, 25mm and 27mm devices. Their presence broadens the registry’s device experience but does not make them randomized comparisons. The listed phase is NA. The record gives 31 outcome measures and 4 analyses; detailed protocol and analysis-plan information beyond the posted results is not reported in the registry record.

The registry’s primary and secondary endpoints are specifically applicable to the randomized arms. Results from the single-arm cohorts therefore need to be read as descriptive cohort information rather than as evidence of a randomized treatment difference. The published record does not report the trial’s original sample-size justification or the assumptions used to plan the study.

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: The non-randomized Roll-In phase with only the test device was for centers with no previous experience implanting the Lotus Valve System. Each performed at least two Roll-In cases before starting RCT. Only cohorts that have completed enrollment, reached primary endpoint and were submitted for regulatory approval are included in the Results Section

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Implanted population - all subjects who sign an Informed Consent Form, are enrolled in the trial, and are implanted with the assigned, randomized study device. The Primary and Secondary Endpoints (Outcome Measures 1-3) are only applicable to the two Randomized arms of the study.

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.

Population: Data are reported separately for each cohort as pooled mean and standard deviations across cohorts do not provide meaningful data.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Events Included in the Primary Safety Endpoint, measured over 30 days following procedure.

The primary endpoint is the percentage of participants with an event in a composite safety outcome during the 30 days following the procedure. A participant is counted as having an event if at least one of the listed components occurs: all-cause mortality, stroke, life-threatening or major bleeding, stage 2 or 3 acute kidney injury, or a major vascular complication. The registry reports the endpoint as a percentage of participants, rather than as a continuous measurement or time-to-event estimate.

General explanation: a composite endpoint combines several events into one outcome. This can capture a broader range of clinically important complications than any single component and can make an overall comparison more informative when different types of events are relevant. It also means that the composite result does not tell the reader which component accounts for the overall pattern. Component-specific counts and analyses are needed to understand that pattern, and the registry’s stated primary endpoint alone does not provide them.

The implanted-population definition focuses the endpoint on participants who received the assigned randomized device. This is the population specified for the primary and secondary endpoints in the record. The endpoint does not by itself establish how missing observations were handled, whether all participants had complete follow-up, or whether the treatment groups were analyzed according to another population definition; those details are not reported in the registry record.

7. Results Posted in the Registry

• CoreValve TAVR System - Randomized: 17.2% (51/297) versus 20.3% (117/577) on control; risk difference -3.1 percentage points (95% CI -8.5 to 2.3), risk ratio 0.85 (0.63–1.14); unadjusted two-proportion z-test p = 0.270.

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.

Percentage of Participants With Moderate or Greater Paravalvular Aortic Regurgitation

• 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:
  • CoreValve TAVR System - Randomized: 6.9% (21/305) versus 0.8% (5/607) on control; risk difference 6.1 percentage points (95% CI 3.1 to 9.0), risk ratio 8.36 (3.18–21.95); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for CoreValve TAVR System - Randomized than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry posts one secondary endpoint result: moderate or greater paravalvular aortic regurgitation at 1 year. It is a distinct outcome with a later follow-up time than the 30-day composite primary endpoint. The secondary result shows a clearer separation between the randomized arms than the unadjusted primary comparison. This difference in pattern is not necessarily inconsistent because the outcomes capture different events over different periods.

The secondary endpoint does not answer the primary safety question. It should be interpreted as endpoint-specific evidence, rather than as confirmation or refutation of the composite result. The registry lists 31 outcome measures and 4 analyses, while the number of posted secondary outcomes is 1. The available record does not state how many analyses were planned, how outcomes were selected for posting, or whether the reported secondary analysis was prespecified.

General explanation: when many outcomes or comparisons are examined, the chance of finding at least one apparently unusual result by chance can increase. Multiplicity procedures can address this issue, but the registry record does not report whether any adjustment was planned or applied. In the absence of that information, unadjusted secondary findings generally carry less confirmatory weight than a prespecified primary analysis with a clearly reported statistical plan.

These limitations do not erase the posted secondary result; they shape the strength of the inference that can be drawn from it. The result should be considered alongside its endpoint definition, follow-up, analysis method, and the lack of reported multiplicity details. The secondary finding cannot by itself establish a broader treatment effect across outcomes or substitute for missing information about the primary analysis.

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

• Percentage of Participants With Moderate or Greater Paravalvular Aortic Regurgitation

9. Statistical Interpretation

10. Statistical Methods Explained

General explanation: the primary outcome is binary at the participant level. Each participant is classified as having or not having at least one event in the composite during the stated follow-up. A percentage is the arm-level proportion with an event. A comparison of those proportions is different from an analysis of event timing: the record does not report a time-to-event primary analysis.

What does a risk difference describe?

The unadjusted recalculation expresses the comparison as a risk difference: the event proportion in one randomized arm minus the event proportion in the other, using the orientation stated with the estimate. A value below zero indicates a lower observed proportion in the first arm of that stated comparison; a value above zero indicates a higher observed proportion. The recalculated primary risk difference is -0.031 for CoreValve compared with Lotus. This is a simple comparison of the posted summary statistics, not an adjusted model-based result.

General explanation: the risk difference is an absolute measure. It describes the separation between two event proportions on the proportion scale. Other relative measures, such as a risk ratio or odds ratio, express the comparison differently and can give a different impression of the size of an association. No single measure removes the need to consider the outcome definition, follow-up, uncertainty, and analysis population.

How should the confidence interval be read?

General explanation: a confidence interval expresses the uncertainty around an estimate under the method used to calculate it. A wide interval allows a broader range of plausible values than a narrow one. For the unadjusted primary risk difference, the recalculated interval crosses no difference. This means the posted summaries do not pin down the direction of the underlying difference with high precision under that calculation. A confidence interval is not a guarantee that the true value lies within its limits, and it does not replace the assumptions of the analysis.

What does the p value test?

General explanation: a p value measures how incompatible the data are with a specified null hypothesis under the statistical model. The unadjusted primary p value of 0.27 is associated with a test of no difference, not a test that one device is noninferior to the other. A nonsignificant equality-based test does not establish equivalence, noninferiority, or absence of a meaningful difference. Those claims require an appropriate design and a stated criterion.

The sponsor’s primary analysis is reported as a noninferiority analysis using the Farrington-Manning method. General explanation: noninferiority methods assess whether the data are sufficiently inconsistent with a difference that crosses a prespecified margin in the unfavorable direction. The margin is essential to interpret the question being tested. It is not reported in this registry record, so the reported noninferiority test cannot be independently contextualized from this entry alone. Because the record flags a discrepancy between the sponsor analysis and the simple recalculation, the sponsor’s own analysis takes precedence.

How does the secondary analysis differ?

The secondary endpoint is also reported as a percentage of participants, but it measures moderate or greater paravalvular aortic regurgitation at 1 year rather than the 30-day composite. The sponsor reports a Chi-squared analysis of the difference in percentages and labels it a superiority analysis. General explanation: a Chi-squared test evaluates whether categorical outcome proportions differ, subject to the assumptions of the method. The recalculated secondary comparison is an unadjusted risk difference with a confidence interval and p value. These methods and estimates should be interpreted in light of the endpoint-specific population and follow-up, not treated as interchangeable with the primary analysis.

General explanation: unadjusted analyses compare observed groups without accounting for additional covariates. They can be easy to interpret, but may not match a trial’s prespecified primary analysis. Registry summaries do not establish that a recalculation reproduces the sponsor’s analysis, particularly when methods, populations, or handling of missing data may differ. The record does not report enough detail to explain the discrepancy or verify every analysis choice.

11. Confidence Intervals and Precision

The primary arm percentages are 20.3% for Lotus and 17.2% for CoreValve. The unadjusted risk-difference interval crosses no difference, and its p value is 0.27. This combination indicates that the recalculated comparison is not precise enough to rule out a range of underlying differences that includes no difference. It should not be read as proof that the groups are identical.

General explanation: precision concerns how narrowly an estimate is determined by the data and the analysis. A confidence interval makes that uncertainty more visible than a point estimate alone. A point estimate gives one value from the observed data; the interval shows that other values remain compatible with the data under the chosen method. The interval does not address every source of uncertainty, such as missing information, analysis choices, or limitations in the registry record.

The sponsor’s noninferiority result has a different analytic purpose from the unadjusted equality-based recalculation. Its interpretation depends on the noninferiority margin, which is not reported in the registry record. The sponsor analysis is the controlling reported analysis because a discrepancy is flagged, but the missing margin limits independent assessment of what degree of difference the analysis was designed to exclude.

For the secondary endpoint, the reported arm percentages and its confidence interval indicate a more clearly separated estimate than the unadjusted primary comparison. That endpoint is measured at 1 year and concerns a different outcome. Its precision cannot be transferred to the primary composite, and its statistical result does not resolve uncertainty about the primary endpoint.

General explanation: precision is not the same as importance, validity, or clinical relevance. A narrow interval can still be centered on an estimate whose meaning depends on the endpoint and design; a broader interval can leave meaningful possibilities unresolved. The registry does not report all details needed to judge precision under alternative assumptions or to account for missing observations.

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 for this binary participant-level outcome, not total event counts. The listed 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 defined as the stated fraction of the observed effect. These are planning illustrations calculated from the observed effect; the original trial design assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the specified effect under its assumptions, if that effect and model were correct. The 90% power column describes the corresponding planning target for a 90% chance. These are design probabilities under assumptions, not probabilities that the observed result is true, and they do not measure the achieved certainty of the completed trial.

Reading across the effect scenarios, planning for a smaller fraction of the observed effect requires more participants per arm. That is a general feature of power calculations: smaller differences are harder to distinguish from random variation, so a larger planned sample is generally needed to detect them at the same significance and power targets.

The listed sample-size assumptions do not establish how the original study was designed. They are illustrations based on the observed effect and should not be treated as the study’s protocol rationale. They are not observed power.

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 = 0.203; treatment proportion p₁ = 0.172; average p̄ = 0.187.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5517 = 1.0813.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5513 = 0.4640.
4. n = (1.0813 + 0.4640)² / (-0.0311)² = 2,475.8, rounded up to 2,476 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 <- 0.202772963604853                          # control proportion
p1 <- 0.171717171717172                          # 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(2202434)
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 = 2,476 (80% power), 3,314 (90% power)
 75% of observed effect: n per arm = 4,473 (80% power), 5,987 (90% power)
 50% of observed effect: n per arm = 10,219 (80% power), 13,680 (90% power)
power.prop.test: 2475.8 
Simulated power at n = 2,476 per arm: 0.804 (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. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as a Farrington-Manning noninferiority analysis, with a reported difference of 3.1, an upper confidence limit of 8.32, a 97.5% confidence level, and p = 0.003. The analysis is labelled noninferiority. However, the noninferiority margin is not reported in the registry record, so the criterion used to interpret that analysis cannot be checked from this entry.

The unadjusted recalculation uses the posted arm summaries and produces a different comparison: its risk difference is -0.031, its confidence interval crosses no difference, and its p value is 0.27. The recalculation is not a substitute for the sponsor’s analysis and does not test the same stated noninferiority question. The record explicitly flags a discrepancy; under that circumstance, the sponsor’s own analysis takes precedence.

The two results should not be blended into one conclusion. They arise from different reported analytic approaches, and the available record does not explain the discrepancy. Without the margin and fuller analysis details, the sponsor result can be described as the registry’s reported noninferiority analysis, but its threshold and implementation cannot be independently evaluated from this record alone.

15. Multiplicity, Missing Data and Analysis Populations

The registry entry does not report a multiplicity plan. It lists 31 outcome measures and 4 analyses, and one secondary outcome is posted. Without information about which outcomes and analyses were prespecified, or whether an adjustment was used, it is not possible to determine how the possibility of multiple statistical comparisons was handled. General explanation: when several hypotheses are tested, unadjusted p values do not account for the full set of opportunities to observe a result that appears statistically unusual by chance.

The record also does not report a missing-data strategy. It does not describe whether all randomized participants had outcome information, how incomplete follow-up was handled, or whether any imputation or sensitivity analysis was used. These details matter because the primary endpoint is defined in an implanted population, and a reader needs to know how participants without complete endpoint data were treated to assess possible effects on the estimate.

The endpoint population is described as participants who signed an Informed Consent Form, enrolled, and were implanted with the assigned randomized device. The record does not provide enough detail to determine whether other analysis populations were used for the sponsor’s reported analysis, or how its analysis set relates to the simple recalculation from posted summaries. The discrepancy is flagged, but its cause is not explained.

The noninferiority margin and the original sample-size justification are also not reported in the registry record. These omissions limit assessment of the sponsor’s noninferiority claim and the relationship between the trial’s design and the observed precision. No interim analyses or other protocol-level statistical procedures should be inferred from the available entry.

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: atrioventricular block complete (22.2%), cardiac failure congestive (12.5%), bundle branch block left (7.8%), atrioventricular block (6.9%), cerebrovascular accident (6.6%).

For the randomized Lotus safety group, the registry lists 607 participants at risk for serious adverse events and 431 affected; for CoreValve, it lists 305 at risk and 207 affected. For other adverse events, the corresponding figures are 607 at risk and 458 affected for Lotus, and 305 at risk and 210 affected for CoreValve. These are adverse-event summaries, separate from the primary endpoint denominators and the primary composite outcome.

The registry also lists 70 deaths for the randomized Lotus group and 40 for the randomized CoreValve group. It does not provide enough detail in this summary to reconcile these counts with the primary endpoint population or to specify their relationship to every adverse-event reporting period. They should not be treated as component-specific primary endpoint estimates.

The most frequent serious adverse event terms listed include complete atrioventricular block, congestive cardiac failure, left bundle branch block, atrioventricular block, cerebrovascular accident, and atrial fibrillation. The percentages are event-term summaries; the record does not give a detailed account of timing, severity grading, recurrent events, or overlap between terms. Adverse-event counts are descriptive and do not by themselves establish a causal relationship to a device.

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

The posted results describe a randomized comparison for the specified outcomes in the implanted population. For the primary composite safety endpoint during the 30 days following the procedure, the arm percentages are 20.3% for Lotus and 17.2% for CoreValve. The unadjusted recalculation does not show a statistically detectable difference under its equality-based test, and its confidence interval includes no difference. That is not evidence of equivalence and does not answer the sponsor’s noninferiority question.

The sponsor’s own primary analysis is labelled noninferiority and takes precedence because the record flags a discrepancy. The registry does not report the noninferiority margin, which is needed to assess the criterion. Thus, the sponsor’s reported analysis can be accurately described, but the record does not contain all the information needed to evaluate its threshold independently.

The secondary endpoint concerns a different event and follow-up period, so its result cannot be generalized to the primary composite or to all aspects of safety. Similarly, outcomes in the single-arm cohorts cannot be interpreted as randomized comparisons with CoreValve/Evolut R. A device comparison on one endpoint does not establish a general advantage across other outcomes or populations.

The registry record does not report the reason the study was terminated, its original sample-size justification, missing-data methods, a multiplicity plan, or sufficient details to explain the difference between the sponsor’s analysis and the unadjusted recalculation. These gaps limit how confidently the results can be interpreted beyond the specific posted analyses. The findings describe the reported data and analyses; they do not, on their own, establish what should be chosen for an individual patient.

18. Why This Trial Matters Statistically

This trial illustrates why an endpoint’s statistical question matters as much as its numerical result. The unadjusted recalculation tests for a difference, while the sponsor’s primary analysis is labelled noninferiority. Those are not interchangeable questions. A result that does not show a statistically detectable difference under an equality-based test does not establish that two interventions are sufficiently similar under a noninferiority criterion.

The discrepancy between the sponsor’s analysis and the recalculation makes analytic transparency especially important. The sponsor’s result takes precedence, but the noninferiority margin is not reported in the registry record. Without that margin, readers cannot judge the boundary the analysis was intended to assess. The posted arm percentages alone cannot resolve the discrepancy or reproduce the sponsor’s inference.

The trial also demonstrates the interpretive trade-offs of a composite endpoint. Combining mortality, stroke, bleeding, kidney injury, and vascular complications gives a broad summary of early safety events, but the composite cannot show which components drive the overall result. Component-level information and clear analysis definitions are needed to understand that detail.

Finally, the primary and secondary outcomes concern different events and timeframes. A secondary result may have a different statistical pattern without contradicting the primary finding, but unadjusted secondary analyses deserve caution when multiplicity handling is not reported. These issues are central to reading clinical trial statistics: the estimand, population, method, uncertainty, and reporting completeness all shape what a result can support.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry marks the study terminated but does not report the reason. The entry also does not report the original sample-size justification or the assumptions used in the trial’s design. The posted planning illustrations are based on observed effects and should not be mistaken for the original design plan.

A central limitation is the discrepancy between the sponsor’s reported noninferiority analysis and the unadjusted recalculation from the posted arm summaries. The sponsor analysis takes precedence, but its noninferiority margin is not reported. The available entry does not explain the discrepancy, provide enough detail to reproduce the sponsor’s analysis, or show how its analysis population relates to the summary denominators.

The primary endpoint is a composite. The overall percentage does not indicate which component contributed to the result, and the registry summary does not provide component-specific primary estimates in the registry record. The secondary endpoint has a different definition and follow-up period, so it does not fill that gap.

Missing-data methods, completeness of follow-up, multiplicity procedures, and interim analyses are not reported in the registry record. The record also contains single-arm cohorts alongside the randomized comparison; results from those cohorts cannot be interpreted as randomized evidence against the comparator. The unmasked design is reported, but the registry entry does not describe whether outcome assessment used any additional safeguards. These limitations constrain interpretation of the posted results without determining what the unreported details were.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Efficacy Study of Lotus Valve for Transcatheter Aortic Valve Replacement — NCT02202434.
• Registry record last updated 2021-12-17; status last verified 2021-12.
• Results first posted 2019-07-30.
• 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

NCT02202434 is a randomized, unmasked, parallel-group evaluation of Lotus and CoreValve/Evolut R transcatheter aortic valve replacement systems for participants with symptomatic, calcific, severe native aortic stenosis considered at extreme or high surgical risk. Overall enrollment is 1425. The record is marked terminated; the reason is not reported.

The primary endpoint is the percentage of implanted participants with a composite safety event during the 30 days following the procedure. The registry reports arm percentages of 20.3% for Lotus and 17.2% for CoreValve. The sponsor’s reported analysis is labelled noninferiority, while the unadjusted recalculation differs; the sponsor analysis takes precedence, and the margin is not reported. The posted secondary endpoint is moderate or greater paravalvular aortic regurgitation at 1 year. Missing-data and multiplicity methods are not reported.