The REFLECT Trial: Cerebral Protection to Reduce Cerebral Embolic Lesions After Transcatheter Aortic Valve Implantation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The REFLECT Trial: Cerebral Protection to Reduce Cerebral Embolic Lesions After Transcatheter Aortic Valve Implantation (NCT02536196), a randomized na study. The primary outcome is Primary Efficacy Endpoint.

2. Clinical Question

3. Trial Design

REFLECT was a randomized, single-masked, parallel-group trial of cerebral embolic protection during TAVI. The registry lists the phase as NA and the status as completed. Enrollment is 478. The listed study dates are 2016-06 for study start and 2019-05 for primary completion. Keystone Heart is the sponsor.

The intervention was TriGuard embolic protection used with TAVI. The control was TAVI without embolic protection. The registry's brief summary says eligible subjects were randomized 2:1 between these groups. It describes the device's intended function as reducing embolic material entering the carotid, subclavian, and vertebral arteries during valve implantation. The registry does not report the specific masking procedures, who was masked, or whether allocation concealment was used.

The primary efficacy endpoint was hierarchical: patient pairs were compared according to a prespecified ordering of outcomes, with mortality or stroke considered before later tiers. The posted summary reports means and standard deviations for the endpoint, along with a mean difference and an interval estimate. The endpoint description identifies an eITT population as patients who received the device. It also says that 9 patients withdrew before receiving the device among 121 interventional patients in phase 2 of the protocol. The control-population description ends mid-sentence after referring to 2 subjects, so the full population accounting is not reported in the registry record.

The posted outcome summaries list 112.0 participants in the Intervention group and 119.0 in the Control group. These are endpoint-summary group counts and should not be assumed to account for every participant in the enrollment figure or the distinct safety populations. The registry does not reconcile these counts with the enrollment total or give enough detail to establish how every analysis population was formed.

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: The population that received the investigational device, Treatment and Rollin patients against safety performance goal. 5 patients withdrew prior to receiving the device resulting in 157 (121Tx+41RI-5). Control patients did not receive the device and were not evaluated in safety endpoint. Composite endpoint is comprised of the number of events against total number of events in accordance with MACCE. The safety endpoint was pre-specified to be calculated separately for the Roll-In population.

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 Primary Efficacy Endpoint, measured over Pre-discharge through 30-days.

The primary efficacy endpoint combines several outcomes in a hierarchy rather than treating every outcome as interchangeable. The registry describes comparisons between each intervention subject and each control subject. Mortality or any stroke by 30 days comes first. Timing of death or stroke can determine a win; when both patients have the same relevant event timing, the comparison can be a tie or proceed to the next tier. Later tiers include NIHSS worsening, freedom from lesions detected by DW-MRI, and total DW-MRI lesion volume.

This ordering is intended to prioritize more serious clinical outcomes before neurologic assessment and imaging findings. A hierarchical composite can therefore capture outcomes across different levels of importance while retaining a ranking rule for pairwise comparisons. The registry names the Finkelstein-Schoenfeld method for constructing pairwise wins, losses, and ties, and says that the scores are summed for comparison between groups.

The posted primary result is expressed as a mean in units on a scale, with standard deviations. The registry does not explain how the scale's units map to a clinically interpretable amount of benefit or harm, nor does it state a threshold for a meaningful difference. It also does not explain how the displayed continuous summaries relate in detail to the hierarchical ranking procedure. Those omissions limit interpretation of the numerical size of the mean difference, even though its direction and interval can be described.

7. Results Posted in the Registry

• Intervention: mean 587.80 versus 508.20 on control; difference 79.60 (95% CI -197.99 to 357.19), standardized effect d = 0.07; z-test p = 0.574.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is described as a hierarchical composite analyzed using the Finkelstein-Schoenfeld method. In general, a hierarchical pairwise method compares a patient in one group with a patient in the other group, beginning with the most important outcome tier. If a comparison is resolved at an earlier tier, later tiers do not determine that pair's result. If the earlier outcomes do not distinguish the pair, the comparison moves down the hierarchy. A win, loss, or tie is assigned according to the stated rules, and the scores are accumulated for comparison between groups.

In REFLECT, the registry lists mortality or any stroke by 30 days first, followed by timing of death or stroke, NIHSS worsening, freedom from DW-MRI detected lesions, and total DW-MRI lesion volume. It describes how a patient who survives free of stroke can win against a patient who dies or has a stroke, and how comparisons can move to later tiers when early outcomes do not distinguish the pair. This structure gives priority to clinical events over imaging measures. The registry does not provide tier-specific counts or show how many pairwise comparisons were resolved at each level.

The posted group results also describe the endpoint using means and standard deviations, treating it as a continuous measure. A mean is a measure of the center of a set of values, while a standard deviation describes their spread around that center. The displayed means are 587.8 for the Intervention group and 508.2 for the Control group, and the displayed standard deviations are 1028.0 and 1124.0, respectively. The registry calls the unit “units on a scale,” but does not explain how that scale is constructed or how the mean summaries connect to the hierarchical pairwise scores. That is an important interpretive limitation: the hierarchical method and the continuous summary should not automatically be treated as identical descriptions of the same calculation.

The posted mean difference is 79.6, calculated in the direction Intervention minus Control in the listed results. Its interval is -198.0 to 357.2, and the unadjusted p-value is 0.574. An interval estimate conveys a range of values compatible with the observed data under the method used to calculate it. It is not a guarantee that the true effect lies within the interval. The registry does not report the interval's confidence level or the precise statistical procedure used for that interval. The p-value is labeled unadjusted; details of the test that produced it are not reported in the registry record.

Dispersion matters because standard errors and uncertainty in group comparisons depend on variability as well as group size. In general, greater variability makes it harder to estimate a group difference precisely when other aspects of the design remain unchanged. The posted results give standard errors of 103.0 for the Control mean and 97.18 for the Intervention mean. The registry's summary does not describe adjustment for baseline characteristics or other covariates. It also does not provide diagnostic information about the score distribution, missing values, or how any unusual observations were handled.

The registry names an eITT population consisting of patients who received the device, that is, patients who did not withdraw before receiving the investigational device. It reports that 9 patients withdrew before receiving it among 121 interventional patients in phase 2 of the protocol. The description of the control population is incomplete, ending after the statement that 2 subjects did something not fully specified. The endpoint-summary counts are 112.0 and 119.0; the registry does not explain how these relate to enrollment, withdrawals, or other exclusions. The precise handling of missing endpoint data and the analysis population used for each posted statistic are not reported in the registry record.

Multiplicity concerns arise when a study evaluates more than one endpoint, time point, or analysis and makes multiple statistical comparisons. In general, repeated testing can increase the chance of a nominally notable result unless the analysis plan accounts for it. REFLECT's primary endpoint itself has several ordered tiers, but the registry does not report a multiplicity-adjustment method or enough detail to determine how the primary analysis controlled interpretation across its components. It lists 2 outcome measures and 0 posted analyses. No secondary outcome results are posted in the registry record.

The sample-size illustrations use the observed mean difference as a planning reference and apply stated fractions of that effect. They assume a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation. In general, a power calculation estimates how many participants a future study would plan for to have a specified chance of detecting an assumed effect under stated assumptions. Such planning estimates are sensitive to the effect chosen and to assumptions about variability and allocation. They are not evidence about the probability that the completed trial detected an effect, and they do not replace the trial's own design information. The original design assumptions, including its sample-size justification and any interim-analysis plan, are not reported in the registry record.

10. Confidence Intervals and Precision

The mean difference is 79.6 units, with a reported interval from -198.0 to 357.2. The interval is wide relative to the point estimate and crosses zero. That means the posted result is compatible with a negative difference as well as a positive difference, and it does not pin down the size of the group contrast closely. The registry does not report the confidence level for this interval, so it should not be assigned a confidence percentage based on assumptions.

Precision is affected by the amount of variation in the endpoint and the information available from the analysis population. The standard deviations are 1028.0 for Intervention and 1124.0 for Control. The posted standard errors are 97.18 for Intervention and 103.0 for Control. These figures describe considerable variability in the continuous summary. The registry does not report a distributional assessment or explain whether the interval accounts for the hierarchical structure of the endpoint.

The interval's breadth is an important complement to the point estimate and the unadjusted p-value of 0.574. The point estimate alone should not be read as a precise estimate of the difference, and the p-value does not quantify the range of effects compatible with the data. Because the scale is described only as units on a scale, the clinical importance of values within the interval is also not reported in the registry record. The numerical uncertainty can be described, but the registry does not establish what interval values would represent a meaningful clinical difference.

11. 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 illustrations are planning calculations based on the observed effect, not a report of the trial's original design justification. The assumptions listed are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect used for planning is set at the stated fraction of the observed effect. The registry record does not report the trial's own original sample-size assumptions.

Each row describes planning for a different proportion of the observed effect: 100% of the observed effect, 75% of the observed effect, or 50% of the observed effect. The columns state participants per arm for 80% power and participants per arm for 90% power. In plain terms, power is the chance that a study with the stated assumptions will detect the assumed effect using the specified test. The 90% power column represents a higher planned chance of detection than the 80% power column, assuming the other inputs remain as stated.

The illustrations require more participants per arm when the assumed effect is smaller. For example, planning for 75% of the observed effect requires more participants per arm than planning for 100% of the observed effect, and planning for 50% requires still more. This is a general feature of power planning: a smaller difference is harder to distinguish from random variation. The displayed figures are not observed power for the completed trial; they are planning illustrations based on chosen assumptions.

The figures are expressed per arm, not as total enrollment. The sample-size assumptions specify equal allocation for these illustrations, which is a planning assumption and differs from the registry's description that trial subjects were randomized 2:1. The posted curve, where applicable, should be interpreted as a visual presentation of planning relationships rather than as an additional result from the completed trial.

12. 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 = 79.600; pooled standard deviation σ = 1078.707.
2. n = 2 × (1.96 + 0.842)² × 1078.707² / 79.600² = 2,882.8, rounded up to 2,883 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 <- 79.6                      # observed difference in means
sigma <- 1078.70748294056                     # 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(2536196)
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 = 2,883 (80% power), 3,860 (90% power)
 75% of observed effect: n per arm = 5,126 (80% power), 6,861 (90% power)
 50% of observed effect: n per arm = 11,532 (80% power), 15,438 (90% power)
power.t.test: 2883.8 
Simulated power at n = 2,883 per arm: 0.801 (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.

13. Multiplicity, Missing Data and Analysis Populations

The primary efficacy outcome is hierarchical, with comparisons proceeding from mortality or stroke through later neurologic and imaging outcomes when earlier tiers do not resolve the comparison. This ordering sets priority among endpoint components, but it does not by itself explain how statistical error was controlled across all analyses. The registry record does not report a multiplicity-adjustment procedure, a detailed statistical analysis plan, or whether additional inferential tests were prespecified.

The registry lists 2 outcome measures and 0 posted analyses, and no secondary outcome results are posted. It does not provide a comprehensive account of all outcomes measured, analyses conducted, or reasons for any analyses not appearing in the record. Therefore, the posted primary summary cannot be assumed to represent the full set of trial analyses.

The registry describes an eITT population as those patients who received the device, and reports 9 withdrawals before device receipt among 121 interventional patients in phase 2 of the protocol. The control-population sentence is incomplete, ending after it mentions 2 subjects. The primary result lists 112.0 participants for Intervention and 119.0 for Control, while the registry reports enrollment of 478. It does not reconcile these figures or fully define the populations used for the endpoint and safety summaries.

Missing-data handling is not reported in the registry record. The record does not say how unavailable endpoint measurements, incomplete DW-MRI assessments, withdrawals after treatment, or other missing observations were treated. It also does not report sensitivity analyses that might assess the impact of missing data. The original sample-size justification, interim analyses, covariate-adjustment plan, and prespecified analysis details are not reported. These omissions make it difficult to assess whether the posted summary captures all intended analyses or how robust it is to alternative assumptions.

14. 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: vascular bleed (3.2%).

The registry reports serious adverse events by group, with separate figures for the number at risk and the number affected. In Intervention, 157 were at risk and 2 were affected by serious adverse events. In Control, 63 were at risk and 2 were affected. The Roll In group lists 41 at risk and 1 affected. These are group-specific registry counts; the record does not explain the relationship between these safety populations and the endpoint-analysis groups.

The most frequent listed serious event term is Vascular Bleed, reported as 3.2%. The registry does not specify in the posted summary the denominator or further detail underlying that percentage. Deaths are listed as 4 in Intervention, 1 in Control, and 0 in Roll In. The record does not establish that these deaths were caused by treatment or provide enough detail to interpret their timing or relationship to adverse events.

Other adverse events are separately listed as 130 affected among 157 at risk in Intervention, 43 among 63 at risk in Control, and 0 among 41 at risk in Roll In. These counts should be read as registry safety summaries, not as a comparison adjusted for differences in group size or follow-up. The record does not provide event-level timing, severity detail beyond the serious-event classification, or a complete account of how adverse events were collected.

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

The posted primary result is a mean difference of 79.6 units favoring the positive direction for Intervention minus Control, with an interval from -198.0 to 357.2 and an unadjusted p-value of 0.574. The interval crosses zero and is broad, so the numerical estimate is not precise enough to establish the direction or size of the difference from this summary alone. The result is not a direct statement that the device does or does not work.

The endpoint's hierarchical structure is relevant to meaning. It places mortality or stroke ahead of NIHSS worsening and DW-MRI findings, but the registry does not post tier-specific results. A mean score cannot show how much of the comparison came from each outcome tier. The scale is described only as units on a scale, and the record does not state what change would be clinically meaningful. Readers therefore cannot translate the mean difference into a clear clinical interpretation using the registry summary alone.

The comparison concerns embolic protection used during TAVI versus TAVI without embolic protection. It should not be generalized beyond the population and procedures described in the record. The registry reports a randomized, single-masked, parallel design and an enrollment of 478, but does not specify who was masked or fully reconcile enrollment with endpoint and safety populations.

The posted adverse-event counts describe events observed in the listed safety groups, but do not establish causation or comparative risk. The registry also lacks detailed information about missing data, analysis populations, multiplicity, and the statistical analysis plan. Taken together, the registry record supports a cautious description of the posted numerical estimates and their uncertainty, not a definitive clinical conclusion.

16. Why This Trial Matters Statistically

REFLECT illustrates why a reported point estimate should be read together with its uncertainty. The mean difference of 79.6 is accompanied by an interval from -198.0 to 357.2. Because the interval spans zero and extends in both directions, it permits a broad range of possible group differences. The unadjusted p-value of 0.574 is another summary of the comparison, but it does not communicate the magnitude or practical importance of values compatible with the data.

The trial also highlights the interpretive challenge of hierarchical composite endpoints. A hierarchy can prioritize outcomes by importance, allowing later measures to contribute when earlier events do not distinguish a pair. Yet a single overall summary can conceal which tiers influenced the comparison. Without tier-specific results, it is difficult to assess whether the overall number reflects clinical events, neurologic assessments, imaging findings, or a combination.

Statistical interpretation also depends on knowing who was analyzed and how missing observations were handled. The record's eITT description is incomplete, endpoint group counts do not reconcile with the enrollment figure, and safety groups use different denominators. The absence of posted secondary analyses and detailed methods further limits assessment of multiplicity and robustness. These issues show why transparent reporting of analysis populations, endpoint construction, and uncertainty is essential alongside a headline comparison.

Finally, planning calculations based on the observed effect can illustrate how assumptions about effect size and power influence a future study's planned sample size. They should not be mistaken for evidence that the completed trial had a particular probability of detecting an effect. Distinguishing observed results from planning scenarios is central to sound interpretation.

17. 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 does not explain the endpoint scale beyond describing it as units on a scale. It does not state how the displayed mean and standard deviation summaries relate to the described Finkelstein-Schoenfeld pairwise hierarchy, or how to interpret a unit difference clinically. The interval's confidence level and its calculation method are also not reported in the registry record.

The endpoint-population description is incomplete. It reports the eITT definition and 9 pre-device withdrawals among 121 interventional patients in phase 2, but the control description ends after mentioning 2 subjects. The endpoint summaries list 112.0 and 119.0 participants, while enrollment is 478; the record does not reconcile those figures or specify all exclusions. The handling of missing endpoint data is not reported.

The record does not provide tier-specific efficacy results, an analysis plan, details of any interim analyses, multiplicity procedures, or covariate adjustments. It lists 2 outcome measures and 0 posted analyses, with no secondary results posted. The sponsor's sample-size justification and original design assumptions are not reported. The single-masked designation is not accompanied by details of who was masked.

Safety groups differ from the endpoint-summary groups, and the registry does not explain the relationship between them. The serious event percentage is listed without a denominator in the posted summary, and event timing and attribution details are not given. These reporting gaps constrain interpretation of both efficacy and safety summaries.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: The REFLECT Trial: Cerebral Protection to Reduce Cerebral Embolic Lesions After Transcatheter Aortic Valve Implantation — NCT02536196.
• Registry record last updated 2021-02-18; status last verified 2021-02.
• Results first posted 2021-02-18.
• 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.

21. Record Summary

REFLECT (NCT02536196) was a completed randomized, single-masked, parallel-group trial sponsored by Keystone Heart. It compared TriGuard embolic protection during TAVI with TAVI without embolic protection in patients with symptomatic aortic stenosis. The registry reports enrollment of 478 and lists study start as 2016-06 and primary completion as 2019-05.

The primary efficacy outcome was a hierarchical composite assessed from pre-discharge through 30-days. The posted means were 587.8 for Intervention and 508.2 for Control, with a mean difference of 79.6, an interval from -198.0 to 357.2, and an unadjusted p-value of 0.574. The registry does not explain the scale's clinical meaning or fully specify the analysis population and methods.

Serious adverse events and deaths are reported for Intervention, Control, and Roll In groups. The record does not reconcile the safety and endpoint populations or provide a complete account of missing-data handling, multiplicity, or the original statistical plan.