Clinical Trial for the Prevention of Vasovagal Syncope: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Trial for the Prevention of Vasovagal Syncope (NCT00118482), a randomized phase 4 study. The primary outcome is The Primary Outcome Measure Will be the Recurrence of Syncope in Follow up Period..

2. Clinical Question

The clinical question is about recurrence during follow-up, not about every fainting episode accumulated over the study. The primary outcome counts participants who had at least one syncopal spell within the stated period. A participant with one recorded event and a participant with more than one event both contribute to this participant-level endpoint as having had a recurrence; the endpoint description does not report the total number of spells for each group.

The registry summary presents the study as a test of a proposed mechanism: retaining salt and water might help prevent fainting. It also notes that the investigators saw uncertainty in the prior evidence. The randomized comparison is intended to assess whether recurrence was less frequent in the fludrocortisone group than in the placebo group under the trial conditions. The registry record does not report a more detailed hypothesis, a prespecified magnitude of benefit, or the investigators’ original statistical justification.

The posted results indicate a lower observed recurrence proportion in the fludrocortisone group than in the placebo group, while the confidence interval for the risk difference includes no difference. Those results describe the data and their uncertainty; they do not by themselves establish what would happen for every patient or in other settings.

3. Trial Design

The registry identifies POST II as a randomized, quadruple-masked, parallel-group Phase 4 clinical trial. The sponsor was the University of Calgary. The record lists the study as completed, with a start date of 2005-05 and primary completion in 2011-07. Enrollment is listed as 213. The two primary-outcome groups each have a reported group size of 105; the registry record does not explain the relationship between the enrollment figure and these outcome-specific group counts.

Random allocation is intended to make comparison groups similar, on average, with respect to characteristics that could affect the outcome. That is a general feature of randomized trials, not proof that all possible sources of imbalance were eliminated in this study. The registry does not report the allocation sequence method, concealment procedures, stratification factors, or any covariate-adjustment plan. It identifies the design as parallel, meaning the comparison is between groups assigned to different study conditions rather than a crossover of treatments.

The record describes masking as quadruple, but does not specify which roles were masked or how masking was maintained. Therefore, the label can be reported, but the details of its implementation are not reported in the registry record. The listed intervention is fludrocortisone acetate, and the comparator is placebo.

The primary outcome was participant-level recurrence of syncope within 12 months. The record also lists secondary measures concerning syncope frequency; presyncope frequency, duration, and intensity, individually and as a composite; and quality of life. Numeric results are posted for quality of life, but results for the other secondary measures are not reported in the registry record.

The registry record does not report the original sample-size assumptions, a detailed statistical analysis plan, the analysis population, or the handling of missing outcome data. It lists no reported analyses. The posted group summaries and unadjusted comparisons can therefore be described, but they should not be mistaken for a complete account of the trial’s prespecified analysis procedures.

4. Participant Flow and Accounting

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

Overall Study

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.

Population: Median age was 30.5 years and 146 were women.

6. Primary Endpoint

The registry lists the primary outcome as The Primary Outcome Measure Will be the Recurrence of Syncope in Follow up Period., measured over Within 12 months.

The primary endpoint is the recurrence of syncope within 12 months, measured as the number of participants with at least one syncopal spell during that follow-up period. This is a binary, participant-level outcome: each participant is classified according to whether a qualifying recurrence occurred. The registry’s outcome description does not provide further details about event adjudication, the exact definition of a qualifying spell, or how incomplete follow-up was handled.

This endpoint addresses whether participants experienced any recurrence, rather than how often they fainted after the first recurrence. That distinction matters. A participant-level recurrence measure can summarize the proportion of each group that experienced the event, but it does not capture the full distribution of event counts, the timing of recurrences, or differences in severity. Those questions require other measures or analyses.

As a general statistical rationale, a binary recurrence outcome can be useful when the clinical question is whether an event happens at least once during a defined period. It creates a direct comparison between the groups’ event proportions. The fixed follow-up window also gives the result a clear time context, although interpretation depends on the completeness and consistency of follow-up. The registry record does not report enough detail to assess those aspects.

The posted primary result should therefore be read as a comparison of participants with at least one recurrence within 12 months. It is not a comparison of total fainting episodes, time to first recurrence, or all symptoms experienced during follow-up.

7. Results Posted in the Registry

• Fludrocortisone Acetate: 40.0% (42/105) versus 51.4% (54/105) on control; risk difference -11.4 percentage points (95% CI -24.8 to 2.0), risk ratio 0.78 (0.58–1.05); unadjusted two-proportion z-test p = 0.096.

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.

Quality of Life Will be the Third Secondary Outcome Measure. The Investigators Will Compare the Quality of Life in Treated and Untreated Patients.

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Fludrocortisone Acetate: mean 69.00 versus 84.00 on control; difference -15.00 (95% CI -20.27 to -9.73), standardized effect d = -0.91; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Fludrocortisone Acetate than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary questions covering syncope frequency, presyncope frequency, duration and intensity, a presyncope composite, and quality of life. Numeric results are posted for quality of life; the other secondary outcome results are not reported in the registry record. Therefore, the available secondary evidence does not form a complete numerical account of the broader symptom and frequency questions.

The posted quality-of-life comparison is statistically separated from a zero mean difference in its unadjusted interval, while the primary recurrence interval includes no difference. These outcomes measure different aspects of the study experience. A quality-of-life contrast cannot determine whether the primary recurrence result would have been different, and the primary endpoint does not summarize all dimensions of quality of life or presyncope. The results should be read as outcome-specific rather than combined into a single overall effect.

Secondary outcomes commonly provide additional context about how participants fare beyond the primary endpoint. General statistical caution is needed when many outcomes are examined: the more comparisons made, the greater the possibility that one may appear statistically unusual by chance. Adjustment procedures or a prespecified hierarchy can help govern interpretation, but the registry record does not report a multiplicity strategy or adjusted secondary analyses.

The quality-of-life result is labelled unadjusted, and no reported analyses are listed. Its statistical result therefore carries less confirmatory weight than a result from a clearly described, prespecified analysis with a reported multiplicity plan. This does not erase the posted estimate; it means its interpretation should remain cautious and should not be treated as independent confirmation of the primary endpoint. The registry record also does not report whether the secondary measures were collected or analyzed for all participants, or how missing observations were handled.

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

• The Frequency of Syncope Will be the First Secondary Outcome Measure.
• Presyncope Frequency, Duration, and Intensity Will be the Second Secondary Outcome Measures, Both Alone and in a Composite Score.
• Quality of Life Will be the Third Secondary Outcome Measure. The Investigators Will Compare the Quality of Life in Treated and Untreated Patients.

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference mean?

For a binary endpoint, the risk difference subtracts one group’s event proportion from the other group’s event proportion, following the comparison’s stated direction. A negative estimate in this comparison indicates a lower observed proportion in the fludrocortisone acetate group than in the placebo group. The estimate, -0.114, is an absolute contrast between proportions, not a count of participants and not a relative percentage change. It should be read together with its confidence interval, from -0.248 to 0.020.

The risk difference is useful because it expresses the observed contrast on the same absolute scale as the event proportions. It can be easier to interpret clinically than an odds ratio, although its practical meaning still depends on the outcome, follow-up, study population, and uncertainty. The registry record does not report a threshold for what difference would be considered important to patients or investigators.

How do the risk ratio and odds ratio differ?

The risk ratio compares the event proportions between groups. The odds ratio compares odds, where odds describe the ratio of event occurrence to non-occurrence within a group. These measures are both derived from the same binary outcome but use different scales. In this trial, the risk ratio is 0.778 with a confidence interval from 0.577 to 1.049; the odds ratio is 0.630 with a confidence interval from 0.364 to 1.088. For each measure, a value of one corresponds to no relative difference. Both confidence intervals contain that value.

Risk ratios and odds ratios can look numerically different because odds are not the same as probabilities. General statistical interpretation should avoid treating an odds ratio as if it were a risk ratio. The risk difference, risk ratio, and odds ratio provide complementary descriptions, but they do not represent independent evidence: they are alternative summaries of the same group outcomes.

What does a confidence interval communicate?

A confidence interval describes statistical uncertainty around an estimated effect under the assumptions of the method used. In repeated use, a procedure that constructs 95% confidence intervals would cover the underlying parameter in 95% of repetitions under its model assumptions. For an individual study, the interval is not a probability statement that the true effect lies within the observed limits. It communicates which effect values are relatively compatible with the data and the calculation procedure.

For the primary risk difference, the interval includes zero, the value corresponding to no absolute difference. This indicates that the posted estimate is not precise enough to rule out no difference at the conventional confidence level. It also includes values in the direction of lower recurrence in the fludrocortisone group and extends slightly in the opposite direction. The interval should not be reduced to a yes-or-no decision based only on whether it includes zero; its width and the range of plausible effects also matter.

How should the p-values be read?

The primary p-value is 0.096 and is labelled unadjusted. A p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that null hypothesis and the test assumptions were true. It is not the probability that the null hypothesis is true, and it is not the probability that the findings occurred by chance. A p-value also does not measure the size or importance of an effect.

The secondary quality-of-life p-value is <0.001 and is also unadjusted. That value indicates a stronger statistical incompatibility with a no-mean-difference null under the calculation used, but it does not resolve questions about the scale’s clinical interpretation, the outcome’s secondary status, or multiplicity. The registry does not report adjusted p-values or a multiplicity procedure.

Why can over-dispersion matter?

General explanation: over-dispersion occurs when observed variability is greater than a statistical model expects. It can make standard errors too small if the model assumes less variability than the data contain, which in turn can make confidence intervals too narrow and p-values too small. For a simple binary participant-level endpoint, the displayed comparison is based on group event counts and does not report a model-based over-dispersion parameter. The registry record does not report whether any more complex model was used for other outcomes, and over-dispersion cannot be assessed from the posted primary summary alone.

What can be said about recalculation?

The binary and continuous comparisons are unadjusted recalculations from the posted summary statistics. Such calculations summarize the displayed group data but may not reproduce a prespecified analysis that used different assumptions, covariates, missing-data rules, or a different analysis population. The discrepancy indicator is false, so there is no stated conflict requiring the sponsor’s own analysis to take precedence. However, the registry record does not report the detailed sponsor analysis or enough of the statistical plan to verify every analysis choice.

For the continuous quality-of-life outcome, the posted comparison is a mean difference. The reported group means are 69 and 84, and the mean difference is -15.0. The standard deviations describe variability of participant scores within each group; they are not confidence intervals for the means. The confidence interval for the mean difference, from -20.27 to -9.731, expresses uncertainty about the contrast under the calculation used. Because the registry does not describe the score range or interpretation, the statistical contrast should not be translated into a clinical judgment.

11. Confidence Intervals and Precision

Precision concerns how narrowly an estimate is determined by the data and the calculation method. The primary risk-difference estimate is -0.114, and its 95% confidence interval runs from -0.248 to 0.020. This interval includes zero and covers effects in both directions. It therefore leaves substantial uncertainty about the size and direction of the underlying difference, even though the point estimate favors a lower observed recurrence proportion in the fludrocortisone group.

The relative measures reinforce the same uncertainty rather than providing separate confirmation. The risk-ratio interval, from 0.577 to 1.049, includes one; the odds-ratio interval, from 0.364 to 1.088, also includes one. These intervals indicate that the posted data do not precisely distinguish a relative reduction from no relative difference, and they allow some values in the opposite direction. The measures are based on the same event counts, so they should not be treated as independent replications.

The quality-of-life mean-difference interval, from -20.27 to -9.731, lies below zero. It is more clearly separated from the no-difference value in the posted unadjusted comparison, but precision alone does not establish clinical importance. The scale’s range and a meaningful-difference threshold are not reported in the registry record. Its secondary status and the lack of reported multiplicity handling also matter when interpreting the apparent statistical strength.

Confidence intervals reflect sampling uncertainty under a method’s assumptions; they do not capture every source of uncertainty. They do not account automatically for unreported outcome definitions, missing data, departures from the planned analysis, or limits on generalizing beyond the study population. Those matters cannot be resolved from the intervals themselves. The registry record also does not provide a detailed analysis plan with which to assess whether the posted intervals match the original inferential approach.

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 80% power and participants per arm for 90% power. They are not total events. The planning illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. For the binary primary outcome, the listed values are 298 and 398 participants per arm for planning for 100% of the observed effect; 532 and 711 for planning for 75% of the observed effect; and 1,200 and 1,606 for planning for 50% of the observed effect, respectively.

In plain language, the 80% power column gives the estimated participants per arm for a design that would have an 80% chance of meeting the specified statistical criterion if the assumed effect and planning assumptions held. The 90% power column gives the corresponding illustration for a 90% chance. These are prospective planning quantities, not evidence about the trial’s results. This is not observed power.

The effect fractions refer to the observed effect used as a starting point for the illustration. Planning for a smaller effect requires more participants because a smaller difference is harder to distinguish from random variation under the same assumptions. The figures are not the original trial’s sample-size justification. The trial’s own design assumptions and sample-size justification are not reported in the registry record.

The continuous quality-of-life outcome has its own planning illustration, with participant counts per arm under the same general stated assumptions. Those figures are based on that outcome’s observed mean difference and should not be compared with the binary-outcome figures as if they addressed the same effect scale or question. The record gives no planning illustration in terms of total events for these outcomes.

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 = 0.514; treatment proportion p₁ = 0.400; average p̄ = 0.457.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7045 = 1.3808.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6999 = 0.5890.
4. n = (1.3808 + 0.5890)² / (-0.1143)² = 297.1, rounded up to 298 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 <- 0.514285714285714                          # control proportion
p1 <- 0.4                          # 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(118482)
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 = 298 (80% power), 398 (90% power)
 75% of observed effect: n per arm = 532 (80% power), 711 (90% power)
 50% of observed effect: n per arm = 1,200 (80% power), 1,606 (90% power)
power.prop.test: 297.1 
Simulated power at n = 298 per arm: 0.807 (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 identifies a primary endpoint and several secondary outcome areas, but the statistical plan for managing multiple comparisons is not reported in the registry record. No multiplicity adjustment is reported for the posted p-values. When multiple outcomes are tested, the chance of at least one apparently significant result can increase, depending on how many comparisons are made and how they relate to one another. This is a general concern, not evidence that any particular finding is false.

The quality-of-life p-value is unadjusted. Without a reported testing hierarchy, correction method, or prespecified distinction between confirmatory and exploratory outcomes, its evidential role is less certain. The registry record also lists no reported analyses, so it is not possible to establish from the record whether the posted comparisons represent the full set of analyses undertaken.

Missing-data handling is not reported in the registry record. This matters because a participant without an observed outcome cannot automatically be classified as having or not having a recurrence. Different assumptions about missing outcomes can affect event proportions and estimated contrasts. The record does not state how many outcome observations were missing, whether follow-up was complete, or whether any imputation or sensitivity analysis was used. No conclusion about the influence of missingness can be drawn from the available information.

The analysis population is also not reported in the registry record. The record does not state whether the primary comparison followed an intention-to-treat approach, a per-protocol approach, or another population definition. Randomization provides the basis for a fair comparison, but the analysis population and handling of participants after assignment are important to the interpretation of randomized trials. The posted group counts should not be treated as proof of a particular analysis strategy.

Interim analyses, stopping rules, and any adjustment associated with repeated looks at the data are not reported in the registry record. The original sample-size justification and the trial’s prespecified statistical plan are also not reported. These omissions limit assessment of whether the displayed analyses followed the original design, but they do not establish that the procedures were inadequate.

15. Safety Results

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

Other (non-serious) adverse events

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

Most frequent non-serious adverse event terms

The registry reports zero serious adverse events attributed in the posted fields for the fludrocortisone acetate group and zero for the placebo group. It reports 8 other adverse events in each group. The record lists 105 participants at risk for each of these group summaries. Death counts are not reported in the registry record.

These figures should be read as registry-reported counts, not as a complete safety assessment. The record does not provide the specific terms for the other adverse events, their severity, timing, duration, or the criteria used to classify seriousness or attribution. It also does not report a breakdown by event type or a narrative explaining whether events led to treatment changes.

A zero count in a posted category means no events were recorded in that category in the registry summary; it does not prove that the possibility of such events is absent. Likewise, equal counts of other adverse events do not establish that the events were the same in type or seriousness. The available safety figures are descriptive and should not be used to make a broader claim about comparative safety beyond the information recorded.

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

The posted primary data show fewer participants with at least one syncope recurrence in the fludrocortisone acetate group than in the placebo group. The estimated risk difference is -0.114, but its 95% confidence interval, from -0.248 to 0.020, includes no difference. The unadjusted p-value is 0.096. Taken together, these statistics indicate that the observed direction favors a lower recurrence proportion in the fludrocortisone group, while the data do not estimate that contrast with enough precision to rule out no difference using the displayed interval.

This result does not establish that fludrocortisone does or does not prevent syncope. A trial estimate is subject to uncertainty, and the registry record does not supply the full protocol, analysis plan, missing-data information, or all secondary results needed for a complete assessment. It also does not show whether the observed estimate would apply to people or settings beyond those studied.

The quality-of-life result is a separate finding. The posted mean was lower in the fludrocortisone group, with an unadjusted mean difference of -15.0 and a 95% confidence interval from -20.27 to -9.731. The scale’s clinical interpretation is not reported in the registry record, and the analysis is secondary and unadjusted. It should not be interpreted as an explanation for the primary recurrence result.

The adverse-event summary reports zero serious adverse events and 8 other adverse events in each group, but does not provide enough detail to characterize the events or their clinical importance. These registry figures should not be generalized into a complete assessment of risk.

Overall, the record supports a careful description of the posted estimates, not a definitive treatment recommendation. Statistical evidence, clinical importance, study conduct, and applicability are related but distinct considerations. The posted confidence intervals and the gaps in the record should remain part of any interpretation.

17. Why This Trial Matters Statistically

This trial offers a useful example of why a point estimate and its uncertainty should be considered together. The observed primary contrast favors a lower recurrence proportion in the fludrocortisone acetate group, but the confidence interval includes no difference and extends across a range of possible effects. A directional point estimate alone would give an incomplete account of what the data can support.

The multiple effect measures also illustrate how one set of binary outcomes can be expressed on absolute and relative scales. The risk difference conveys an absolute contrast, while the risk ratio and odds ratio express relative contrasts. Their numerical values differ because the scales differ; all should be interpreted in relation to their confidence intervals and the same underlying event data.

The posted secondary quality-of-life result demonstrates a separate statistical issue: a small unadjusted p-value does not by itself establish clinical importance or resolve the implications of multiple comparisons. The registry record does not report the scale’s interpretive context, a multiplicity strategy, or the analysis plan. This makes it important to distinguish statistical evidence from clinical meaning and from confirmatory evidence.

The planning illustrations provide another teaching point. They are derived from observed effects and stated planning assumptions, not the original study design. Smaller assumed effects require larger participant counts under those assumptions, but such illustrations are not a retrospective measure of whether the completed study was adequately powered.

Finally, the registry’s limited analysis and missing-data details show why a results summary is not a substitute for a full protocol and statistical analysis plan. Careful reading requires noting both what the posted estimates say and what cannot be assessed from the record.

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.

Several trial-specific limitations of interpretation arise from the registry information. The record does not report the detailed eligibility criteria, so the characteristics of the population beyond its association with vasovagal syncope cannot be assessed. It also does not describe how the quadruple masking was implemented or which roles were masked. The design labels establish the reported framework, but not those operational details.

The primary outcome is described as the number of participants with at least one syncopal spell within 12 months, but the registry does not give a detailed event definition or explain event verification. It does not report the timing of first recurrence or the total number of spells. As a result, the posted primary summary cannot address whether recurrence patterns differed in timing or frequency beyond the binary participant-level classification.

The registry does not report missing-outcome counts, follow-up completeness, an analysis population, or the procedures used to handle missing data. Those omissions limit assessment of whether the posted group summaries reflect all randomized participants and how sensitive the results may be to unavailable outcomes. The relationship between the listed enrollment and the primary-outcome group counts is not explained in the record.

There is also no reported original sample-size justification or detailed statistical analysis plan. The planning illustrations are based on observed effects and should not be read as evidence of the study’s intended design. The registry lists no reported analyses, and the results for several secondary outcome areas are absent. The multiplicity approach and any interim analyses are not reported in the registry record.

Finally, the quality-of-life scale’s range and meaningful-difference threshold are not reported, and the adverse-event summaries lack event-level descriptions. These gaps restrict clinical interpretation of those results. They do not show that the trial methods were deficient; they identify information the registry record does not make available for evaluating the posted findings.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Clinical Trial for the Prevention of Vasovagal Syncope — NCT00118482.
• Registry record last updated 2019-10-15; status last verified 2019-09.
• Results first posted 2017-06-28.
• 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

POST II is listed as a completed, randomized, quadruple-masked, parallel-group Phase 4 trial sponsored by the University of Calgary. The registry gives a start date of 2005-05, primary completion in 2011-07, and enrollment of 213. The comparison is fludrocortisone acetate versus placebo.

The primary endpoint was whether participants had at least one syncope recurrence within 12 months. The posted risk difference is -0.114, with a 95% confidence interval from -0.248 to 0.020 and an unadjusted p-value of 0.096. The interval includes no difference. The posted secondary quality-of-life comparison is an unadjusted mean difference of -15.0, with a 95% confidence interval from -20.27 to -9.731 and p < 0.001.

The registry also reports zero serious adverse events and 8 other adverse events in each group; deaths are not reported in the registry record. Important details, including the original analysis plan, missing-data handling, analysis population, and multiplicity procedures, are not reported.