Combined Vaginal Misoprostol and Perivascular Vasopressin: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Combined Vaginal Misoprostol and Perivascular Vasopressin (NCT03815344), a randomized phase 4 study. The primary outcome is Hemoglobin Levels Difference Between Pre and Post Surgery..

2. Clinical Question

The registry summary describes the rationale for the comparison: vasopressin was used to constrict blood vessels around fibroids, while misoprostol was considered as an additional approach intended to reduce operative blood loss through increased uterine muscle tone. Those proposed mechanisms are context for the question, not outcome measurements. The trial’s primary measure was hemoglobin change, rather than a direct measurement of blood loss.

3. Trial Design

This was a randomized, parallel-group, phase 4 trial with quadruple masking. The registry lists an enrollment of 74 participants and a completed status. The recorded start date was 2017-04-26, and primary completion was 2019-06-30. The registry record does not provide further details about the randomization sequence, allocation concealment, or the people included in the quadruple-masking description.

The two groups shared the use of laparoscopic injection of diluted vasopressin throughout the myomectomy, before incision. The intervention group also received 400mcg of vaginal misoprostol at HUMI/foley placement. The comparator group received the vasopressin regimen without the additional misoprostol described for the intervention. The comparison therefore concerns adding vaginal misoprostol to the stated vasopressin regimen, rather than comparing vasopressin with no vasopressin.

The posted primary outcome is a continuous measure: the difference in hemoglobin levels between pre-surgery and post-surgery, in g/dL, measured at 1 hour. The registry reports a mean and standard deviation for each arm. It records 42 participants in the standard arm and 32 in the standard-vaginal-misoprostol arm. The reason for the unequal arm counts is not reported in the registry record.

The registry does not report the trial’s original sample-size justification, its planned statistical analysis, or the exact analysis population. It also does not report details such as eligibility criteria, recruitment procedures, treatment adherence, or follow-up beyond the stated primary outcome timeframe. These absences limit how fully the design and conduct can be reconstructed from the 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.

Overall Study

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Hemoglobin Levels Difference Between Pre and Post Surgery., measured over 1 hour.

The primary endpoint is the difference between pre-surgery and post-surgery hemoglobin levels, expressed in g/dL and measured at 1 hour. The registry describes the endpoint as a mean, with standard deviation as the measure of spread. The posted arm means are 0.76 g/dL for standard treatment and 0.93 g/dL for standard treatment plus vaginal misoprostol; the corresponding standard deviations are 0.89 and 1.36.

Hemoglobin change is a laboratory measure that can reflect changes associated with blood loss, but it is not itself a direct measurement of the volume of blood lost during surgery. A group mean describes the average change within a group; it does not show how every participant’s result was distributed. The standard deviations convey variability among observed values, but do not reveal the full shape of those distributions.

The endpoint is relevant to the registry’s stated rationale of examining perioperative blood loss, but the registry record does not specify a direct blood-loss endpoint among the posted outcomes. It also does not give further details about the precise timing or procedure used to obtain the post-surgery hemoglobin measurement beyond the 1 hour timeframe. Interpretation should therefore stay focused on the reported hemoglobin measure and its stated timing.

7. Results Posted in the Registry

• Standard-Vaginal Misoprostol: mean 0.93 versus 0.76 on control; difference 0.17 (95% CI -0.37 to 0.71), standardized effect d = 0.15; z-test p = 0.539.

8. Statistical Interpretation

9. Statistical Methods Explained

What does the mean difference describe?

A mean is an average across the participants with observed values in a group. Here, the endpoint is a hemoglobin difference between before and after surgery, measured in g/dL at 1 hour. The group means, 0.76 g/dL and 0.93 g/dL, describe average endpoint values in the standard and combination groups. The reported mean difference of 0.17 g/dL expresses the contrast between those group means, with the combination group compared against standard treatment.

A mean difference keeps the result in the endpoint’s original units, which makes its scale directly interpretable as a difference in g/dL. It does not describe every individual result, and it can conceal differences in the distributions within the two groups. The standard deviations, 0.89 and 1.36, describe the extent of spread around each group mean. They are not confidence intervals and do not indicate the precision of the group means on their own.

What does a confidence interval tell us?

A confidence interval expresses uncertainty around an estimated effect under the statistical method used to construct it. The reported interval for the mean difference is -0.373 to 0.713. Because the interval includes zero, the posted result does not clearly distinguish a positive difference from no difference or a negative difference. The interval also indicates that a range of effect sizes remains compatible with the estimate and its uncertainty. A confidence interval is not a guarantee that the true effect lies within its endpoints, and it does not give the probability that a particular value is correct.

The interval’s width is important alongside its midpoint. A point estimate such as 0.17 g/dL offers one summary of the contrast, while the interval communicates that the estimate is uncertain. A result should not be reduced to whether the interval includes zero; the plausible sizes and directions represented by the endpoints also matter. In this trial, both directions are represented in the reported interval.

How should the p-value be read?

The unadjusted p-value is 0.539. In general, a p-value measures how compatible the observed data are with a specified null model, given the test and assumptions used. It is not the probability that the null hypothesis is true, and it does not measure the probability that the result happened “by chance.” It also does not express the size or clinical importance of an effect.

The registry record does not report enough detail to reconstruct the analysis procedure behind the p-value or to identify its full assumptions. It is therefore appropriate to treat it as the posted unadjusted result rather than infer unreported model choices. A p-value should be considered with the effect estimate, confidence interval, endpoint, and design information rather than interpreted alone.

Why does variability matter?

Variation in outcome values affects how precisely a group mean and between-group contrast can be estimated. The posted standard deviations differ between arms, with values of 0.89 and 1.36. More variability generally makes it harder to estimate a mean difference precisely when other features are unchanged. The available summaries do not establish the cause of the differing spread or describe the distribution of individual observations.

In general, over-dispersion means that outcome variability is greater than a statistical model expects. It can make standard errors too small and confidence intervals too narrow if a model fails to account for it. That concept is relevant to statistical interpretation broadly, but the registry record does not report an over-dispersion assessment or identify a model for this endpoint. The arm standard deviations alone are not enough to conclude that over-dispersion occurred.

What can the design contribute to interpretation?

Random allocation is intended, in general, to make treatment groups comparable in expectation with respect to measured and unmeasured factors. Masking can, in general, limit the influence of expectations on care, assessment, or reporting. The registry labels the trial randomized and quadruple masked, but the operational details and masking roles are not reported in the registry record. These labels are useful design information, but they do not replace details on implementation or analysis.

The parallel-group structure means participants were allocated to one of the two treatment regimens rather than crossing between them. Both regimens included vasopressin; the added component in the intervention arm was vaginal misoprostol. Consequently, the contrast pertains to the regimen difference as recorded, not to the independent effect of each drug. The record does not describe an analysis that separates the effects of the components.

The comparison and confidence interval are reported for the primary continuous endpoint. The registry lists no secondary outcomes and no posted analyses. It does not report whether analysis was adjusted for baseline values, whether the endpoint was analyzed using a particular model, or how missing data were handled. Those choices can affect interpretation and should not be inferred from the displayed summary statistics.

10. Confidence Intervals and Precision

The estimated mean difference is 0.17 g/dL, with a confidence interval from -0.373 to 0.713. The point estimate is a single summary of the contrast, while the interval indicates that its precision is limited. Values on both sides of zero fall within the interval, so the record does not provide a precise estimate of the direction of the difference. The interval also includes contrasts larger than the point estimate in either direction.

A confidence interval is useful because it makes uncertainty visible rather than presenting the point estimate alone. In general, it is constructed by a method with a stated coverage property under its assumptions. It does not mean that every value between its endpoints is equally plausible, nor that the interval contains the true effect with certainty. The registry record does not report the exact interval method or the assumptions used to calculate it.

Precision depends on factors including sample size and outcome variability. The posted arm counts are 42 and 32, and the standard deviations are 0.89 and 1.36. These summaries give context for the interval but do not independently reconstruct every aspect of its calculation. The unequal counts and observed variability should be kept in mind when reading the estimate, without inferring an unreported reason for either.

The interval’s inclusion of zero is not proof that the groups are identical. To establish equivalence or non-inferiority, a study ordinarily needs a prespecified margin and a corresponding analysis; neither is reported in the registry record. The most direct reading is that the posted estimate remains uncertain and does not sharply resolve the direction or size of the mean difference.

11. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are expressed as participants per arm, not as total events. They are an illustration based on the observed effect, not a report of the trial’s original design assumptions. 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 as a stated fraction of the observed effect. The trial’s own original sample-size justification and assumptions are not reported in the registry record.

For planning at 100% of the observed effect, the illustration gives 678 participants per arm for 80% power and 908 participants per arm for 90% power. At 75% of the observed effect, it gives 1,205 participants per arm for 80% power and 1,613 participants per arm for 90% power. At 50% of the observed effect, it gives 2,711 participants per arm for 80% power and 3,629 participants per arm for 90% power.

In plain language, the 80% power column gives the planned number per arm under the stated assumptions for a design with an 80% chance of detecting the specified effect if that effect were the true one. The 90% column describes the larger planned group size for a design targeting a 90% chance under those same assumptions. These figures are planning illustrations, not observed power.

Smaller effects require more participants to detect under otherwise unchanged assumptions. The progression across the three rows reflects that general relationship. The illustration should not be treated as a recommendation or as evidence that the trial was designed around these numbers. The actual randomized group counts were 42 and 32, and the registry does not report the rationale used to select the original enrollment target.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.170; pooled standard deviation σ = 1.117.
2. n = 2 × (1.96 + 0.842)² × 1.117² / 0.170² = 677.6, rounded up to 678 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 0.17                      # observed difference in means
sigma <- 1.11687622411796                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(3815344)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 678 (80% power), 908 (90% power)
 75% of observed effect: n per arm = 1,205 (80% power), 1,613 (90% power)
 50% of observed effect: n per arm = 2,711 (80% power), 3,629 (90% power)
power.t.test: 678.5 
Simulated power at n = 678 per arm: 0.797 (20000 replicates)

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

13. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, comparisons, subgroups, or analyses are examined. Testing multiple hypotheses can increase the chance of at least one apparently notable result, so trial analysis plans often specify how outcomes and comparisons will be prioritized or adjusted. The registry lists one primary outcome and no secondary outcomes. It records zero posted analyses. This reporting does not establish how many analyses were conducted or planned outside the information in the record.

A multiplicity plan, including any adjustment procedure or hierarchy among outcomes, is not reported in the registry record. The posted p-value is described as unadjusted. It should therefore be read as an unadjusted comparison, not as a value known to account for other possible tests. There is not enough information to determine whether multiplicity was relevant to the trial’s full analysis or how it was handled.

The record also does not report the analysis population: for example, whether the primary comparison was intended to include all randomized participants, only those who received the assigned regimen, or another defined group. Such populations address different questions and can yield different estimates. It would be inappropriate to assign an analysis population from the group counts alone.

Missing-data procedures are not reported in the registry record. The available outcome summaries do not specify whether all randomized participants had a measured hemoglobin difference, how missing measurements were handled, or whether any imputation or sensitivity analysis was performed. These details matter because missing outcomes can affect both the estimated group means and the uncertainty around their comparison.

The registry record also does not report the prespecified statistical model, adjustment for baseline hemoglobin, covariates, interim analyses, or a protocol-level analysis plan. These absences limit assessment of whether the posted comparison followed a prespecified approach. They do not establish that such procedures were absent from the conduct of the trial; they mean the record does not report them.

14. Safety Results

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

Deaths

Other (non-serious) adverse events

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

The registry reports zero serious adverse events in the standard group among 42 participants at risk, and zero in the standard-vaginal-misoprostol group among 32 participants at risk. It also reports zero other adverse events in the corresponding groups, with 42 and 32 participants at risk, respectively. The deaths count is zero in each group.

These figures describe the adverse-event information posted in the registry record. A count of zero means no events were reported in that category for the listed group; it does not establish that no adverse events occurred outside the reported information or that either regimen has no risk. The record does not provide event definitions, ascertainment procedures, severity details for other events, or a timeframe for collecting adverse-event data.

The registry’s serious adverse-event terms list is empty. This indicates that no serious-event terms are posted in that list, not that the record provides a detailed account of every possible safety outcome. The group sizes and absence of reported events offer limited information about uncommon harms. These counts should be interpreted as a description of the registry reporting, not as a complete safety assessment.

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

The posted result estimates a mean difference of 0.17 g/dL in the pre-to-post surgery hemoglobin measure at 1 hour, comparing standard vasopressin plus vaginal misoprostol with standard vasopressin. The confidence interval, -0.373 to 0.713, includes zero and spans both negative and positive values. The unadjusted p-value is 0.539. Together, these figures describe an uncertain estimate rather than a precise determination of the direction or size of the difference.

The finding does not show that the two regimens are equivalent. Equivalence requires an appropriate prespecified margin and analysis, neither of which is reported in the registry record. Nor does the result establish that one regimen is superior. A non-significant p-value does not demonstrate that there is no effect; it indicates that the posted test did not provide strong evidence against its null model under the analysis used.

The comparison is specifically between the regimen with vasopressin alone and the regimen with vasopressin plus vaginal misoprostol. It cannot isolate the effect of vasopressin because both arms received it. The measured endpoint is hemoglobin difference, not a direct measurement of blood-loss volume, and the record does not report further outcomes that would connect this estimate to other aspects of surgery.

The findings also do not resolve the uncertainty about missing measurements, analysis populations, or unreported statistical methods. The registry lists 74 enrolled participants, but the recorded arm counts are 42 and 32; the record does not explain this allocation count pattern. No secondary outcomes or posted analyses are listed. Those limits constrain conclusions beyond the stated primary comparison.

In general, a trial result should be interpreted in relation to its endpoint, design, estimate, precision, and completeness of reporting. Here, the defensible conclusion is that the posted summaries yield an uncertain mean-difference estimate for the stated 1 hour hemoglobin measure. The data described in the registry record do not settle whether the regimens differ, and they do not support conclusions about unreported outcomes.

16. Why This Trial Matters Statistically

This trial illustrates why an effect estimate and its precision should be read together. The mean difference of 0.17 g/dL is the central estimate, but the interval from -0.373 to 0.713 leaves substantial uncertainty about both direction and size. A single point estimate can appear definite when read alone; the interval shows that the posted result is compatible with a wider range of contrasts.

It also highlights the distinction between a statistical outcome and the clinical process motivating it. The registry’s rationale concerns operative blood loss, while the primary endpoint is a hemoglobin difference at 1 hour. That laboratory measure is relevant to the rationale but is not the same as directly measuring the amount of blood lost. Clear alignment between the research question and the endpoint is important when interpreting what a result can answer.

The active comparator structure matters as well. Both groups received vasopressin, and the intervention group additionally received vaginal misoprostol. The contrast therefore addresses the added component in this specific regimen, rather than the effects of either treatment independently. This distinction is essential for interpreting the scope of the estimate.

Finally, the record illustrates how incomplete statistical reporting can limit evaluation even when arm summaries and a confidence interval are available. The analysis population, missing-data approach, multiplicity plan, and original sample-size justification are not reported. Their absence from the registry record does not prove they were absent from trial conduct, but it prevents readers from assessing those aspects from the posted information. Transparent reporting of these elements helps readers judge robustness and relevance.

17. Limitations

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

The registry record offers limited detail about trial conduct and the primary analysis. It does not report eligibility criteria, recruitment procedures, the randomization method, allocation concealment, or which roles were masked under the quadruple-masking label. Without those details, the implementation of the design features cannot be assessed fully.

The endpoint is described as a difference in hemoglobin before and after surgery measured at 1 hour, but the record does not give further measurement procedures or clarify the exact timing relative to surgery. It reports group means and standard deviations, but not individual-level distributions or the number with an observed endpoint. The reason the recorded group counts are 42 and 32 is not reported in the registry record.

The record does not report the prespecified analysis method, whether the comparison was adjusted for baseline hemoglobin or other variables, the analysis population, or how missing outcome data were handled. It also does not report a multiplicity plan, interim analyses, or the trial’s original sample-size justification. These missing details make it difficult to evaluate whether the posted comparison reflects a prespecified analysis and how sensitive it might be to analytic choices.

Only one outcome is listed, and no secondary outcomes or posted analyses are recorded. The registry’s adverse-event information is limited to event counts, with zero serious and other adverse events recorded in both groups and zero deaths. Event definitions, surveillance methods, and collection timeframes are not reported. The record therefore supports interpretation of the posted summaries but not a comprehensive assessment of efficacy, safety, or the full trial analysis.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Combined Vaginal Misoprostol and Perivascular Vasopressin — NCT03815344.
• Registry record last updated 2024-01-09; status last verified 2024-01.
• Results first posted 2024-01-09.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

21. Record Summary

NCT03815344 is a completed, randomized, parallel-group, phase 4 trial with quadruple masking. The registry lists an enrollment of 74, a start date of 2017-04-26, and primary completion on 2019-06-30. The sponsor is Antonios Likourezos.

The trial compared laparoscopic vasopressin during myomectomy with the same vasopressin regimen plus 400mcg of vaginal misoprostol. The primary outcome was the mean difference in hemoglobin levels between before and after surgery, measured at 1 hour. The recorded group means were 0.76 g/dL and 0.93 g/dL; the mean difference was 0.17 g/dL, with a confidence interval from -0.373 to 0.713 and an unadjusted p-value of 0.539.

No secondary outcomes or posted analyses are listed. The registry records zero serious adverse events, zero other adverse events, and zero deaths in each group. Several details of the statistical plan, analysis population, and missing-data handling are not reported in the registry record.