Determine the Safety/Efficacy of Ticagrelor for Maintaining Patency of Arterio-Venous Fistulae Created for Hemodialysis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Determine the Safety/Efficacy of Ticagrelor for Maintaining Patency of Arterio-Venous Fistulae Created for Hemodialysis (NCT02335099), a randomized phase 1, phase 2 study. The primary outcome is Feasibility and Safety of Ticagrelor in Hemodialysis Patients.

2. Clinical Question

The trial also addressed whether ticagrelor could preserve hemodialysis vascular-access patency. That efficacy question was registered as a secondary outcome, with a 1-year timeframe. Keeping these questions distinct matters: the primary outcome concerns prolonged bleeding and is described as a safety and feasibility measure, while patency concerns whether vascular access remains usable.

The clinical context is therefore a comparison of a drug and placebo in people with an existing, functioning fistula who receive chronic hemodialysis. The registry record does not report further detail about the primary-outcome population beyond the trial’s stated population. It also does not report the clinical criteria used to define a functioning fistula or to determine patency.

3. Trial Design

The registry describes a randomized, placebo-controlled, single-blind, parallel-group trial in Phase 1 and Phase 2. The sponsor is the University of Virginia, and the record lists the trial as completed. The recorded start was 2014-12, and primary completion was 2019-06.

Participants were assigned to ticagrelor or placebo. The treatment description specifies oral ticagrelor at 90 mg twice a day for 6 months; the placebo was also given twice a day for 6 months. The record identifies the study as single blind, but does not report which people involved in the trial were blinded or how blinding was maintained. The method used to generate the random allocation sequence and the process used to conceal it are not reported in the registry record.

The registry enrollment field reports 54. The brief summary describes a recruitment plan of 70 patients, so the planned recruitment stated in that summary and the recorded enrollment are not the same figure. The outcome results list 17 participants in each group for the primary comparison. The registry record does not explain the relationship between the enrollment figure, the recruitment plan, and the group counts in the posted results.

The primary outcome is a participant count for prolonged bleeding after needle removal over 6 months. Vascular-access patency is listed as a secondary outcome with a 1-year timeframe. Although the brief summary describes a number of clinical and treatment characteristics that would be documented, the registry record does not establish which of those were used for adjustment in the analyses. The original design’s sample-size assumptions and statistical plan are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: 10 of 54 consented subjects failed screening and were not assigned to the study arms.

Treatment

Reasons for not completing this period:

Follow-up

Reasons for not completing this period:

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 Feasibility and Safety of Ticagrelor in Hemodialysis Patients, measured over 6 months.

The primary endpoint counts participants who experienced prolonged bleeding after removal of hemodialysis needles. Prolonged bleeding is defined in the registry as lasting more than 30 minutes. The outcome is reported as a count of participants, with the timeframe specified as 6 months.

This measure was used to address the trial’s stated safety and feasibility question. In general, a binary endpoint records whether each participant did or did not meet a defined outcome criterion during the specified observation period. Reporting participant counts makes the number of recorded events visible, while comparing the groups gives context for how often the endpoint occurred under each assigned treatment.

The record reports 1 participant with prolonged bleeding in the treatment group and 3 in the placebo group; each group has 17 participants in the posted primary results. The registry’s outcome description does not provide further detail about how bleeding was assessed, whether reports were independently adjudicated, or how an event was handled if the participant had more than one episode. Those endpoint procedures are not reported in the registry record.

The endpoint is not itself a measure of fistula patency. Patency was addressed separately as a secondary outcome. Treating these as distinct outcomes avoids conflating bleeding after needle removal with the continued usability of vascular access.

7. Results Posted in the Registry

• Treatment: 5.9% (1/17) versus 17.6% (3/17) on control; risk difference -11.8 percentage points (95% CI -33.1 to 9.5), risk ratio 0.33 (0.04–2.89); unadjusted two-proportion z-test p = 0.287.

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.

Treatment Efficacy of Ticagrelor to Preserve Patency of Hemodialysis Vascular Access

• 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:
  • Treatment: 70.6% (12/17) versus 76.5% (13/17) on control; risk difference -5.9 percentage points (95% CI -35.5 to 23.7), risk ratio 0.92 (0.62–1.38); unadjusted two-proportion z-test p = 0.697.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Treatment and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcome concerns preservation of hemodialysis vascular-access patency, with a 1-year timeframe. Its group percentages are close in magnitude, and both the unadjusted comparison and the sponsor’s time-to-event analysis have broad confidence intervals that include their respective no-difference values. Taken together, the secondary results do not provide a precise estimate of a group difference.

This outcome is related to the trial’s clinical aim but is distinct from the primary prolonged-bleeding endpoint. The primary endpoint is a count of participants with bleeding beyond the specified duration after needle removal over 6 months; the secondary endpoint addresses patency over 1 year. One cannot be used as a direct substitute for the other, and a result on one outcome does not establish a result on the other.

The registry lists one posted secondary outcome. Secondary outcomes can help describe aspects of a trial beyond its primary question, but they generally need cautious interpretation, particularly when several outcomes or analyses are considered. Testing multiple outcomes can increase the chance of observing an apparently unusual result by chance. Whether and how multiplicity was addressed is not reported in the registry record. The unadjusted secondary p-value therefore should not be read as confirmatory evidence on its own.

In general, secondary findings are most informative when their prespecified status, analysis plan, and relationship to the primary question are clear. Those details are not reported in the registry record. The secondary endpoint adds context about the trial’s patency objective, but its uncertainty and the absence of reported multiplicity procedures limit the strength of conclusions that can be drawn from it.

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

• Treatment Efficacy of Ticagrelor to Preserve Patency of Hemodialysis Vascular Access

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary: each participant either met the prolonged-bleeding definition or did not, within the specified 6-month timeframe. For this type of outcome, several summaries describe the treatment comparison in different ways. A risk difference expresses the difference between the groups’ event proportions. A risk ratio compares those proportions as a ratio, while an odds ratio compares the odds of the event. These measures use the same underlying event information but have different scales and interpretations.

What does the unadjusted risk difference describe?

The recalculated primary risk difference is -0.118, comparing treatment with placebo, and its 95% confidence interval runs from -0.331 to 0.095. The negative point estimate reflects the direction of the treatment-minus-placebo contrast as calculated from the posted counts. It should not be read as a stable estimate of the size of an effect: the interval extends across zero and includes differences in either direction. The unadjusted p-value is 0.287.

“Unadjusted” means the calculation uses the posted group summaries without accounting for other participant characteristics. It does not mean the estimate is wrong; it means it answers a narrower question than an analysis that adjusts for prespecified factors. The registry record does not report a covariate-adjusted primary estimate.

Why is Fisher Exact reported?

The sponsor’s primary analysis is identified as Fisher Exact, with an odds ratio as the parameter. Fisher’s exact test is a method for comparing binary outcomes in a two-group setting. It calculates evidence against a null hypothesis using the observed counts, rather than relying on a large-sample approximation for the test. This can be useful when counts are small. The sponsor’s reported odds ratio is 3.77, its 95% confidence interval is 0.27 to 217.52, and its p-value is 0.32. The record does not specify the odds-ratio coding direction, so the reported number should be considered alongside the stated groups and analysis method rather than assigned a direction without that detail.

How should a confidence interval be read?

In general, a confidence interval describes the statistical uncertainty around an estimate under the assumptions of the analysis. A wider interval signals less precision. For the primary sponsor analysis, the interval from 0.27 to 217.52 is wide, so the odds-ratio estimate is imprecise. The interval includes 1, the value corresponding to no odds ratio difference. For the recalculated risk difference, zero is the corresponding no-difference value, and the interval includes it. These features indicate uncertainty; they do not prove that there is no effect.

What does the secondary time-to-event analysis estimate?

The secondary outcome concerns patency at 1 year and includes a sponsor-reported Log Rank analysis with a Cox proportional-hazards value of 0.86. Time-to-event methods use information about when an outcome occurs, rather than reducing the comparison only to whether an event happened by a fixed point. A Cox proportional-hazards model summarizes the relative event rate over follow-up under its model assumptions. The registry reports a 95% confidence interval from 0.23 to 3.20 and p = 0.82. The interval includes 1 and is broad, so the estimate has limited precision. The registry record does not report details about censoring, the definition of an event for this analysis, or checks of model assumptions.

The recalculated secondary risk difference is -0.059, with a 95% confidence interval from -0.355 to 0.237 and p = 0.697. This is an unadjusted comparison of the posted proportions, not a replacement for the sponsor’s time-to-event analysis. The measures answer related but not identical questions: a fixed-time percentage describes the proportion meeting the outcome by the stated time, whereas a time-to-event analysis uses event timing and follow-up information.

Why can small counts make results uncertain?

General statistical explanation: when event counts are limited, a change in a small number of outcomes can substantially affect a group proportion or effect estimate. The uncertainty is reflected in confidence intervals, which can be wide. A non-significant p-value does not establish equivalence, and a point estimate does not erase the uncertainty around it.

The recalculated planning illustrations use the observed effect as a starting point and consider smaller fractions of that effect. They are not the trial’s original design calculations. The registry record does not report the original sample-size justification, a prespecified statistical plan, or interim analyses. The interpretation should therefore stay close to the posted analyses and their stated limitations.

11. Confidence Intervals and Precision

The primary estimates are not precise. The recalculated risk-difference interval runs from -0.331 to 0.095, spanning the no-difference value of zero and allowing values on either side. The sponsor’s odds-ratio interval, 0.27 to 217.52, is especially broad. It includes the no-difference value of 1 and a wide range of possible odds ratios. The posted primary counts are 1 participant in treatment and 3 in placebo, with 17 participants in each group; limited event counts are consistent with the considerable uncertainty reflected in the intervals.

The same caution applies to patency. The recalculated risk-difference interval runs from -0.355 to 0.237, again spanning zero. The sponsor’s Cox proportional-hazards interval runs from 0.23 to 3.20 and spans 1. These intervals are compatible with a range of possible group differences, rather than providing a narrowly estimated effect.

In general, a confidence interval is a measure of statistical precision under the assumptions of the analysis, not a guarantee that the true value lies within a particular interval. An interval that includes the no-difference value does not prove equivalence or absence of an effect. Conversely, the point estimate alone should not be treated as the most likely clinical conclusion while uncertainty remains substantial. The registry record does not report additional information that would narrow these intervals, such as an adjusted analysis or further outcome data.

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 illustrations are based on the observed effect and are not the trial’s original sample-size justification. For these binary outcomes, the figures are participants per arm, not total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect targeted in each planning scenario is the stated fraction of the observed effect.

The 80% power column describes the illustrative number of participants per arm for a design with an 80% chance of detecting the target effect under those assumptions, if the assumed effect and statistical model apply. The 90% power column describes the corresponding number per arm for a design targeting 90% power. Higher power generally requires more participants when other assumptions are held constant. The illustrations show that planning for 75% of the observed effect requires more participants per arm than planning for 100%, and planning for 50% requires more still.

For the primary outcome, the listed figures for 100% of the observed effect are 117 participants per arm for 80% power and 156 for 90% power. For 75% of the observed effect, they are 231 and 308; for 50%, they are 568 and 760. For patency, the corresponding listed figures are 882 and 1,181 for 100% of the observed effect; 1,541 and 2,062 for 75%; and 3,402 and 4,553 for 50%.

These are planning illustrations, not observed power. They depend on the stated assumptions and the observed effect used as a planning input. The trial’s own original design assumptions are not reported in the registry record.

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 = 0.176; treatment proportion p₁ = 0.059; average p̄ = 0.118.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4556 = 0.8930.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4480 = 0.3770.
4. n = (0.8930 + 0.3770)² / (-0.1176)² = 116.5, rounded up to 117 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 <- 0.176470588235294                          # control proportion
p1 <- 0.0588235294117647                          # 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(2335099)
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 = 117 (80% power), 156 (90% power)
 75% of observed effect: n per arm = 231 (80% power), 308 (90% power)
 50% of observed effect: n per arm = 568 (80% power), 760 (90% power)
power.prop.test: 116.5 
Simulated power at n = 117 per arm: 0.819 (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 a sponsor analysis for the primary outcome using Fisher Exact, with an odds ratio of 3.77, a 95% confidence interval from 0.27 to 217.52, and p = 0.32. The unadjusted recalculation based on the posted group counts reports a risk difference of -0.118, a 95% confidence interval from -0.331 to 0.095, and p = 0.287. The recalculation also reports an odds ratio of 0.292, with a 95% confidence interval from 0.027 to 3.133.

The sponsor’s result and the recalculations should not be treated as identical analyses. The risk difference and odds ratio are different effect measures, and the registry does not specify the coding direction for the sponsor’s odds ratio. The sponsor’s confidence interval is also much wider than the recalculated odds-ratio interval. The record does not explain the reasons for that difference or provide further calculation details. The discrepancy indicator is false, so the record does not flag a discrepancy. Neither analysis gives a precise primary estimate: both reported p-values are above 0.05, and the confidence intervals include their respective no-difference values.

The sponsor’s analysis is the analysis posted in the registry; recalculated values are simple, unadjusted calculations from the posted summaries. They offer a way to read the counts on a different scale, not a substitute for an analysis with additional participant-level data or a prespecified analysis plan.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary outcome and a secondary patency outcome, but the multiplicity strategy is not reported in the registry record. It is not reported whether the secondary outcome was formally tested within a prespecified hierarchy, whether significance thresholds were adjusted for multiple outcomes, or whether additional analyses were planned. Without those details, the secondary result should be treated as exploratory or supportive rather than assumed to control the overall chance of a false-positive finding.

The record reports outcome counts and estimates, but does not describe missing-data handling. It does not report how participants with incomplete follow-up were treated, whether any outcomes were missing, or how missing observations were addressed in either analysis. The analysis populations are also not reported in the registry record. The posted group sizes alone do not establish whether the analyses followed intention-to-treat, per-protocol, or another population definition.

For the patency analysis, the registry reports Log Rank and Cox proportional-hazards methods, but does not report censoring rules, follow-up completeness, or checks of proportional-hazards assumptions. These details matter because time-to-event estimates depend on how observation time and incomplete follow-up are handled. The record also does not provide further detail on endpoint adjudication or whether outcome assessors were blinded.

These omissions do not show that the trial lacked procedures for multiplicity or missing data; they mean the relevant procedures are not reported in the registry record. The statistical interpretation should therefore be limited to the analyses and summaries that are actually described, without assuming an unreported design or analysis decision.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cardiac arrest (5.9%), myocardial infarction (5.9%).

The serious-adverse-event figures list 17 participants at risk in each group and 1 affected participant in each group. For other adverse events, the record lists 3 affected participants in treatment and 2 in placebo, with 17 at risk in each group. It also lists 1 death in each group. The registry lists cardiac arrest and myocardial infarction among the top serious-event terms, each at 5.9%.

These figures describe the adverse-event information recorded in the registry; they do not establish that an event was caused by the assigned treatment. The record does not provide further detail about event timing, severity grading, relatedness assessments, overlap between event categories, or the relationship between the listed terms and the group-level affected-participant counts. The number at risk is not necessarily the number with complete safety follow-up, which is not reported in the registry record.

With small group counts, safety summaries are descriptive and uncertain. The posted figures should not be interpreted as a precise comparison of risk or as evidence that an event is or is not associated with treatment.

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

The posted results describe a randomized comparison of ticagrelor and placebo in hemodialysis patients with a functioning arteriovenous fistula. For the primary safety and feasibility outcome, the registry reports prolonged bleeding in 1 treatment participant and 3 placebo participants, with 17 participants per group in the posted results. The recalculated estimate is uncertain, and the sponsor’s reported odds-ratio estimate also has a broad confidence interval. The data therefore do not yield a precise estimate of the difference between groups.

For the secondary patency outcome, the posted percentages are similar in magnitude, while the recalculated and sponsor-reported analyses remain imprecise. Those results do not establish equivalence, nor do they provide a precise estimate of a difference. The primary and secondary endpoints address different aspects of the trial question and have different timeframes.

More generally, the absence of a statistically significant result is not proof that the treatments have identical effects. It can reflect uncertainty, including uncertainty associated with limited event information. Likewise, a numerical difference between the posted group counts does not by itself establish a real or clinically important effect. Interpretation depends on the effect estimate, its precision, the outcome definition, and the analysis methods.

The registry record does not report the original sample-size justification, detailed analysis populations, missing-data procedures, or a multiplicity plan. These omissions limit how fully the posted analyses can be assessed. The findings should be read as the results recorded for this trial, not as medical advice or as a conclusion that can automatically be applied to other populations or settings.

18. Why This Trial Matters Statistically

This trial illustrates why an endpoint’s definition and timeframe matter. Prolonged bleeding after needle removal is a specific safety and feasibility measure over 6 months, while vascular-access patency is a separate secondary outcome assessed over 1 year. Their results should be interpreted separately rather than combined into a single judgment about the intervention.

It also illustrates the difference between a point estimate and its precision. A numerical contrast can appear to favor one group while its confidence interval remains broad and includes values on either side of the no-difference point. In that situation, the data do not pin down the direction or magnitude of the underlying difference. That distinction is especially important when event counts are limited, as in the posted primary results.

The record additionally offers a comparison between a sponsor-reported analysis and unadjusted recalculations from the group summaries. Different effect measures answer related but non-identical questions; coding conventions and analysis methods also affect how estimates are presented. Clear reporting of the analysis population, missing-data approach, endpoint procedures, and multiplicity strategy would help readers assess how the results were generated.

Finally, the planning illustrations show how strongly required sample sizes depend on the effect a future study aims to detect. Smaller target effects require more participants per arm under the stated assumptions. Such illustrations can aid study planning, but they do not show the probability that the observed trial result is correct and do not replace the original design rationale, which is not reported in the registry record.

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.

The posted primary group results include 17 participants in each group, and the number of prolonged-bleeding events is limited. This results in broad uncertainty around the effect estimates. The registry record reports both sponsor and unadjusted analyses, but does not fully explain the sponsor odds-ratio coding direction or why its reported interval differs from the recalculated interval.

Several design and analysis details are not reported in the registry record: the method for generating and concealing randomization, who was blinded, the analysis populations, handling of missing outcomes, and the original sample-size justification. For the patency analysis, censoring procedures and model-assumption checks are also not reported. Multiplicity handling across outcomes and analyses is not reported.

The record gives a recruitment plan of 70 patients in the brief summary and an enrollment figure of 54, but does not explain the difference. It also does not explain how the posted outcome group sizes relate to enrollment or provide detail about completeness of follow-up. This makes it difficult to assess attrition and the extent to which the posted analyses represent all enrolled participants.

These limitations concern the information available in the registry record; they do not establish that procedures were absent. They mean that readers cannot verify those procedures from the reported details. The results are therefore best interpreted as imprecise estimates from the posted outcomes, with limited information for assessing design and analysis choices.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Determine the Safety/Efficacy of Ticagrelor for Maintaining Patency of Arterio-Venous Fistulae Created for Hemodialysis — NCT02335099.
• Registry record last updated 2022-06-08; status last verified 2022-05.
• Results first posted 2022-06-08.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes a completed randomized, placebo-controlled, single-blind, parallel-group Phase 1 and Phase 2 trial sponsored by the University of Virginia. It compares oral ticagrelor at 90 mg twice a day with placebo, both given for 6 months, in hemodialysis patients with a functioning arteriovenous fistula.

The primary outcome was the number of participants with prolonged bleeding after needle removal, defined as lasting more than 30 minutes, over 6 months. The secondary outcome addressed vascular-access patency at 1 year. The record reports enrollment of 54; the brief summary described a recruitment plan of 70.

The posted estimates for both outcomes are imprecise. The registry does not report important details about the original sample-size rationale, analysis populations, missing-data procedures, or multiplicity handling. Those limitations should be kept in view when interpreting the posted results.