PREvention of VENous ThromboEmbolism Following Radical Prostatectomy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for PREvention of VENous ThromboEmbolism Following Radical Prostatectomy (NCT03006562), a randomized phase 4 study. The primary outcome is Number of Participants With Symptomatic Venous Thromboembolism.

2. Clinical Question

3. Trial Design

The PREVENTER Trial was a randomized, parallel-group, phase 4 study sponsored by Johns Hopkins University. The registry record lists an enrollment of 501 and a single masking designation. Which trial participants or staff were masked is not reported in the registry record. Allocation was randomized, but the method used to generate or conceal the allocation sequence is not reported in the registry record.

The recorded study start was 2017-07-01, and primary completion was 2019-11-01. The study status is listed as terminated. The reason for termination, the timing of the decision, and whether termination affected recruitment or follow-up are not reported in the registry record. The original recruitment target and the assumptions used to choose it are also not reported in the registry record.

The intervention was subcutaneous heparin administered before incision and after surgery until discharge. The control arm received routine care with intermittent pneumatic compression devices. The registry summary frames the comparison as pharmacologic prophylaxis with heparin versus intermittent pneumatic compression devices alone. Outcomes include symptomatic venous thromboembolism, any venous thromboembolism, surgical blood loss, drain output, and use of postoperative diagnostic imaging.

For the primary outcome, the posted arm denominators are 251 in the heparin arm and 249 in the control arm. The registry record notes that one participant in the control arm was lost to follow-up before the primary outcome could be assessed. The posted denominator therefore reflects outcome assessment rather than simply repeating the enrollment figure. The registry record does not describe a broader analysis population, such as an intention-to-treat population, or give details of exclusions beyond that note.

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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: One participant in the control arm was lost to follow-up precluding outcome assessment.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Symptomatic Venous Thromboembolism, measured over 30 days.

The primary endpoint counts participants diagnosed with symptomatic venous thromboembolism within 30 days after surgery. Venous thromboembolism includes deep vein thrombosis and pulmonary embolism. The diagnosis required imaging prompted by symptoms. The registry description lists symptoms that could lead to investigation, including lower-extremity swelling or pain and chest pain or shortness of breath, among other signs and symptoms.

This endpoint focuses on clinically prompted diagnoses rather than every clot found through routine screening. That makes it relevant to symptomatic events, but it also means that the chance of an event being recorded may depend on whether symptoms are noticed, whether clinicians investigate them, and which imaging methods are used. The registry record separately lists postoperative imaging as a secondary outcome, reflecting the potential importance of diagnostic investigation when interpreting event counts.

A participant count is a binary outcome at the individual level: each assessed participant either did or did not have the specified event during the stated follow-up period. The endpoint does not measure the number of clots per participant, their severity, or time to diagnosis. Those measures are not reported as the primary outcome. The 30-day window also limits the result to diagnoses within that period; it does not describe events after the recorded follow-up window.

7. Results Posted in the Registry

• Subcutaneous Heparin: 0.8% (2/251) versus 2.0% (5/249) on control; risk difference -1.2 percentage points (95% CI -3.3 to 0.8), risk ratio 0.40 (0.08–2.03); unadjusted two-proportion z-test p = 0.249.

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.

Number of Participants With Occurrence of Any Venous Thromboembolism

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Subcutaneous Heparin: 2.8% (4/141) versus 2.9% (4/137) on control; risk difference -0.1 percentage points (95% CI -4.0 to 3.8), risk ratio 0.97 (0.25–3.81); unadjusted two-proportion z-test p = 0.967.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Subcutaneous Heparin and the control. The interval gives the range of effects that remain compatible with the data.

Surveillance Bias by Differential Use of Imaging as Assessed by Number of Participants Receiving Postoperative Diagnostic Imaging for Venous Thromboembolism Relative to Symptoms

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Subcutaneous Heparin: 10.0% (25/251) versus 12.4% (31/249) on control; risk difference -2.5 percentage points (95% CI -8.0 to 3.0), risk ratio 0.80 (0.49–1.31); unadjusted two-proportion z-test p = 0.377.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Subcutaneous Heparin and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary results cover two distinct aspects of the trial: any venous thromboembolism within 30 days and postoperative diagnostic imaging relative to symptoms. For the any-event outcome, the recorded event counts are equal across the posted arms, and the estimated risk difference is close to 0. For imaging, the observed counts differ, with a negative estimated risk difference for heparin versus control. The confidence intervals for both comparisons include 0, and their unadjusted p-values do not indicate a clear between-arm difference.

These outcomes provide context for the primary symptomatic endpoint but do not independently settle its interpretation. The any-event endpoint is broader than the primary symptomatic endpoint, while imaging is a measure of ascertainment activity rather than a clinical event itself. A comparison of imaging use may help readers consider whether diagnostic investigation differed, but the posted counts cannot establish why imaging occurred or whether all events were detected similarly.

The registry lists other secondary outcomes, including estimated blood loss during surgery and surgical drain output after surgery, but their results are not reported in the registry record. The registry lists four secondary outcomes in total, while results are posted for only two of them. This limits the extent to which the full secondary outcome pattern can be evaluated.

Secondary comparisons carry less weight when they are unadjusted and when no plan for handling multiple outcomes is reported. If many outcomes are examined, some differences can arise by chance even when there is no underlying effect. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting secondary endpoints. Accordingly, these comparisons are best treated as descriptive and hypothesis-generating rather than as confirmatory evidence. They should be considered alongside the primary endpoint and its uncertainty, not as replacements for it.

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

• Number of Participants With Occurrence of Any Venous Thromboembolism
• Estimated Blood Loss During Surgery
• Surgical Drain Output After Surgery
• Surveillance Bias by Differential Use of Imaging as Assessed by Number of Participants Receiving Postoperative Diagnostic Imaging for Venous Thromboembolism Relative to Symptoms

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

A risk difference compares the proportion of participants with an event in one arm with the proportion in the other. In this comparison, the sign is oriented as heparin minus control. A negative estimate means the observed event proportion was lower in the heparin arm; a positive estimate would mean it was higher. The risk difference is an absolute-scale measure: it describes the separation between event proportions, rather than the size of one proportion relative to the other.

Here, the posted estimate is -0.012. This is a recalculated, unadjusted comparison based on the arm counts and denominators. The calculation does not account for covariates, stratification, or time to event. No adjusted analysis is reported in the registry record. With a rare outcome, a small change in the number of observed events can have a noticeable effect on the estimated contrast, which is one reason the interval matters alongside the point estimate.

How should the confidence interval be read?

A confidence interval describes a range of values that are reasonably compatible with the observed data under the statistical procedure used. It conveys uncertainty around an estimate; it is not a guarantee that the true effect lies in the interval, nor does it assign a probability to each possible effect. The interval around the risk difference extends from -0.033 to 0.009. Because it includes 0, the posted data do not distinguish the estimate from no difference using this interval criterion.

The interval should be interpreted together with the outcome scale and design. For the risk difference, 0 represents equal event proportions. For a ratio measure, 1 represents equal relative event occurrence. The posted risk ratio is 0.397, and its interval extends from 0.078 to 2.026, including 1. These are not competing answers; they are different ways to express the same arm comparison, with different interpretations and sensitivity to the low event frequency.

What does the p-value add?

The unadjusted p-value of 0.249 summarizes how unusual a result at least as inconsistent with a no-difference model would be if that model and the test assumptions held. It is not the probability that the null hypothesis is true, and it does not show the probability that the result is due to chance. A large p-value can occur when an effect is absent, but it can also occur when the data are too imprecise to distinguish a potentially meaningful effect from no effect.

The registry record does not report the test used for this comparison, so the precise test procedure cannot be assessed from the posted record. The recalculated p-value is unadjusted, and there is no sponsor-reported analysis listed. Statistical significance alone would not determine clinical importance; the magnitude, interval, endpoint definition, and trial conduct also matter.

Why do event counts and ascertainment matter?

For a binary endpoint, the arm summaries record whether each assessed participant had the event during follow-up. The primary outcome is a count of participants, not a count of all event episodes. The estimate is therefore influenced by how many participants were assessed and how many met the endpoint definition. Small event counts generally provide less information about the underlying event probabilities than larger counts, and produce less precise comparisons.

The endpoint requires symptoms to prompt diagnostic imaging. In general, outcome ascertainment can differ if clinical suspicion, access to imaging, or decisions to investigate vary across groups. The registry lists the number receiving postoperative diagnostic imaging relative to symptoms as a secondary outcome, which makes this issue relevant to interpretation. The posted imaging result does not establish that all diagnosed events were found or that diagnostic practices were identical.

These estimates are simple unadjusted recalculations from summary statistics; they are not a substitute for a reported trial analysis. The registry record does not report a prespecified model, covariate adjustment, stratification factors, a multiplicity plan, or interim analysis procedures. There is no discrepancy flagged between the recalculated result and a sponsor analysis, but the registry record does not list a sponsor-reported analysis to compare against. Any conclusions should remain tied to the posted counts and the stated endpoint.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.012, and its confidence interval runs from -0.033 to 0.009. This span covers negative and positive values and includes 0, the value corresponding to equal event proportions. The estimate therefore does not pin down the direction of the underlying difference. It is consistent with a lower observed event proportion in the heparin arm, but the interval also allows values on the other side of no difference.

The risk ratio is 0.397, with an interval from 0.078 to 2.026. Because the interval includes 1, the data also leave open a range of relative comparisons that includes no difference. The risk-difference and risk-ratio intervals are expressed on different scales, so their numerical widths should not be compared directly. Both indicate substantial uncertainty around the point estimate.

Precision depends on the amount of information in the data, including the number of outcome events and the number of participants assessed. The primary outcome was recorded in 2 participants in the heparin arm and 5 in the control arm. Such sparse event data limit how finely the arm contrast can be estimated. The registry record also notes one control participant was lost before outcome assessment. The interval reflects statistical uncertainty under its calculation, while the registry's brief missing-outcome note is a separate consideration.

A confidence interval is not a range of effects that are equally likely, and it does not establish that all values inside it are clinically important. The registry record does not give a threshold for a clinically meaningful risk difference. As a result, the posted interval can be described statistically, but its clinical importance cannot be classified using a threshold not reported in the record.

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 outcome, not total event counts. They illustrate the group size that a future study might require under the listed assumptions and selected effect sizes. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The original trial's own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column means the illustrated design would have an 80% probability of rejecting the no-difference hypothesis if the selected effect were the true effect and the planning assumptions held. The 90% power column describes the corresponding target of 90%. These are design targets, not probabilities that the observed study result is correct. The figures are planning illustrations computed from the observed effect, not observed power.

For the primary comparison, planning for 100% of the observed effect gives 1,479 participants per arm for 80% power and 1,979 participants per arm for 90% power. Planning for 75% of the observed effect gives 2,909 participants per arm for 80% power and 3,894 participants per arm for 90% power. Planning for 50% of the observed effect gives 7,173 participants per arm for 80% power and 9,602 participants per arm for 90% power.

The pattern follows a general design principle: smaller effects are harder to distinguish from random variation, so detecting smaller effects generally requires more participants. These calculations inherit the uncertainty of the observed effect, which is based on few primary events. They should not be treated as a definitive recommendation or as evidence about the original design.

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 = 0.020; treatment proportion p₁ = 0.008; average p̄ = 0.014.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.1663 = 0.3259.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.1661 = 0.1398.
4. n = (0.3259 + 0.1398)² / (-0.0121)² = 1,478.4, rounded up to 1,479 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 <- 0.0200803212851406                          # control proportion
p1 <- 0.00796812749003984                          # 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(3006562)
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 = 1,479 (80% power), 1,979 (90% power)
 75% of observed effect: n per arm = 2,909 (80% power), 3,894 (90% power)
 50% of observed effect: n per arm = 7,173 (80% power), 9,602 (90% power)
power.prop.test: 1478.4 
Simulated power at n = 1,479 per arm: 0.810 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary outcome and several secondary outcomes, but does not report a statistical analysis plan or a procedure for controlling multiplicity. When several hypotheses are examined, the chance of at least one apparently notable result can increase. A prespecified hierarchy, adjustment method, or clear designation of exploratory outcomes can help readers understand how multiple comparisons were intended to be interpreted. None of those details is reported in the registry record.

The posted secondary comparisons are unadjusted. Their p-values therefore describe each comparison individually and do not account for the set of outcomes examined. They should not be treated as independent confirmation of the primary result. The registry record also does not report interim analyses, stopping rules, or whether any analyses were planned before data collection ended. The terminated status alone does not establish why the trial ended or whether interim results informed that decision.

For the primary endpoint, the record specifically notes that one participant in the control arm was lost to follow-up before outcome assessment. The posted outcome denominators are 251 in the heparin arm and 249 in the control arm. The record does not explain how missing outcomes were handled beyond noting that this participant's outcome could not be assessed. It does not report a sensitivity analysis or an imputation method for missing data.

The registry record does not describe the trial's analysis populations, such as whether participants were analyzed according to randomized assignment regardless of treatment received. It also does not report treatment adherence, crossovers, protocol deviations, or exclusions by arm. Without those details, it is not possible to determine whether the posted summaries represent an intention-to-treat analysis or another population. These are reporting gaps, not proof that a particular analysis was or was not performed.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: clavien iii or greater complication (3.6%).

The posted serious adverse event summaries list 9 affected participants in each arm. The corresponding at-risk counts are 251 for heparin and 250 for control. The record also lists 34 participants with other adverse events in the heparin arm and 30 in the control arm, with the same respective at-risk counts. Deaths are recorded as 0 in each arm. The registry identifies Clavien III or Greater Complication at 3.6% among the leading serious-event terms.

These are descriptive safety summaries. Counts alone do not show whether an event was caused by the assigned intervention, how severe or prolonged the events were, or whether participants could experience more than one event. The registry record does not provide detailed event narratives, event-specific timing, or an analysis comparing adverse-event rates. The at-risk denominators for the safety summaries also differ from the control denominator used for the primary endpoint, so the outcome-specific populations should not be conflated.

Equal recorded serious-event counts do not demonstrate that the interventions have identical safety profiles, especially without a reported comparative analysis and detailed definitions. Likewise, differences in other adverse-event counts are not by themselves evidence of a treatment-related difference. The safety data should be interpreted as posted counts within the record's reporting scope.

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

The posted primary result is a comparison of symptomatic venous thromboembolism diagnosed within 30 days after radical prostatectomy. The event count was 2 in the heparin arm and 5 in the control arm. The unadjusted risk-difference estimate favors a lower observed proportion in the heparin arm, but its interval includes 0 and the unadjusted p-value is 0.249. The available data therefore do not provide a precise estimate of the difference between arms.

This result does not establish that the interventions are equivalent. Equivalence requires an appropriate design and a prespecified margin, neither of which is reported in the registry record. Nor does the result establish that heparin prevents venous thromboembolism or that it has no effect. The point estimate alone should not be treated as a definitive conclusion, especially given the small number of recorded primary events and the interval's inclusion of effects in both directions.

The findings concern the endpoint as defined: symptomatic events that prompted diagnostic imaging within the 30-day timeframe. They do not describe asymptomatic events, events diagnosed after that period, or outcomes beyond those recorded. The secondary imaging outcome offers context about diagnostic use but does not resolve all questions about ascertainment. Results for some listed secondary endpoints are not reported in the registry record.

The registry entry also does not report key details needed for a complete evaluation of trial conduct and analysis, including the original sample-size rationale, a full statistical plan, analysis populations, and the reason for termination. Those omissions limit interpretation of how the posted estimates relate to the original design. The results are most appropriately read as an uncertain, unadjusted comparison of the recorded outcomes rather than a conclusive statement about treatment effects.

17. Why This Trial Matters Statistically

This trial illustrates why the size of an observed difference and the precision of that estimate need to be considered together. The primary outcome counts were small, and the estimated risk difference was negative, but its confidence interval crossed 0. Focusing only on the point estimate could overstate certainty; focusing only on a p-value could obscure the range of effects still compatible with the data.

It also highlights a measurement issue central to clinical outcomes research: a symptomatic diagnosis that requires imaging reflects both the occurrence of disease and the process by which it is detected. The registry lists diagnostic imaging as a secondary outcome, making ascertainment an explicit part of the study context. Event counts can be difficult to compare when diagnostic evaluation is potentially influenced by symptoms and clinical decisions.

The record makes a distinction between a randomized trial's enrollment and the denominators used for an outcome. It notes a control participant who could not have the primary outcome assessed, and the posted analysis denominators reflect the reported outcome data. Transparent reporting of such details helps readers assess missingness and understand what population underlies an estimate.

Finally, the sample-size illustrations show how planning depends on the effect assumed to be worth detecting. Smaller assumed effects require more participants under the stated planning approach. Because the observed effect is uncertain, especially with few events, these illustrations are not a substitute for a design rationale. Together, the trial's data and reporting gaps demonstrate the value of complete analysis plans, explicit missing-data methods, and careful distinction between exploratory and confirmatory comparisons.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The primary endpoint is based on symptomatic events that prompted imaging. The registry description does not indicate routine screening for all participants, so the recorded count may not capture asymptomatic thromboses. The likelihood of identifying an event can depend on symptom recognition and diagnostic decisions. Although postoperative diagnostic imaging is listed as a secondary outcome, the posted record cannot establish whether ascertainment was otherwise comparable or whether all relevant events were found.

The primary follow-up window is 30 days. The result does not address events outside that interval, and the record does not describe longer-term follow-up. Only 2 and 5 primary events were recorded in the two arms, respectively, so the effect estimate is imprecise. The confidence interval includes no difference and values on either side. A single control participant was lost before outcome assessment; the record does not give a missing-data sensitivity analysis.

Important design and analysis details are not reported in the registry record. These include the original sample-size justification, the exact masking procedures, allocation concealment, analysis populations, adherence, protocol deviations, covariate adjustment, and the prespecified approach to multiplicity. The reason for termination is also not reported. These gaps prevent a full appraisal of whether the posted summaries follow the original analysis plan.

Results for estimated blood loss and surgical drain output are not reported in the registry record, despite those outcomes being listed. Secondary comparisons that are posted are unadjusted, and no multiplicity plan is given. Finally, the registry entry's brief safety counts do not provide detailed causal assessments or event timing. These limitations concern what can be established from the registry record and do not, by themselves, show that the trial was conducted improperly.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: PREvention of VENous ThromboEmbolism Following Radical Prostatectomy — NCT03006562.
• Registry record last updated 2020-08-05; status last verified 2020-07.
• Results first posted 2020-02-28.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The PREVENTER Trial was a randomized, parallel-group, phase 4 study of subcutaneous heparin versus routine intermittent pneumatic compression devices after radical prostatectomy. The primary endpoint was symptomatic deep vein thrombosis or pulmonary embolism diagnosed within 30 days after surgery. The registry lists enrollment of 501, a single masking designation, and terminated status.

The posted primary counts were 2 participants in the heparin arm and 5 in the control arm. The unadjusted risk-difference estimate was -0.012, with a confidence interval from -0.033 to 0.009 and an unadjusted p-value of 0.249. The interval includes 0, and the limited number of events leaves substantial uncertainty about the size and direction of the underlying difference.

The registry record notes one control participant lost before primary outcome assessment. It does not report the original sample-size rationale, a complete statistical plan, the reason for termination, or results for all listed secondary outcomes. The posted estimates are best interpreted as an unadjusted comparison of recorded outcomes, not as conclusive evidence of equivalence or a definitive treatment effect.