Buccal Versus Vaginal Misoprostol for Third Trimester Induction of Labor: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Buccal Versus Vaginal Misoprostol for Third Trimester Induction of Labor (NCT01519765), a randomized phase 4 study. The primary outcome is Vaginal Delivery Within 24 Hours of Labor Induction.

2. Clinical Question

3. Trial Design

The registry record describes a randomized, parallel-group trial of buccal versus vaginal misoprostol for third-trimester induction of labor. It lists the study as Phase 4 and identifies the University of California, Los Angeles as the sponsor. The registry status is terminated. The recorded enrollment is 73 participants; the reason for termination and the reason enrollment ended at that number are not reported in the registry record.

The registry masking field says quadruple masking. The brief summary describes the study as prospective and double blinded. These are the descriptions appearing in different parts of the registry record; further details about who was masked or how masking was maintained are not reported in the registry record. The listed arms pair active medication by one route with a placebo pill by the other route.

The registry records a start of 2011-07 and primary completion of 2014-12. Its summary describes equal dosages of 25 mcg for the two routes. The primary endpoint is vaginal delivery within 24 hours of labor induction. Secondary outcomes include time to vaginal delivery, time to delivery, time to active labor, rates of vaginal delivery, cesarean delivery rate, number of misoprostol doses, arrest of dilation and failed induction of labor.

There are 21 outcome measures and 24 analyses listed in the record, with 20 secondary outcomes posted. A detailed protocol, the original sample-size justification, planned interim analyses, eligibility criteria, baseline characteristics and the analysis-population definitions are not reported in the registry record. The posted results give 34 participants per arm for the primary endpoint; this endpoint denominator does not, by itself, explain how the total enrollment relates to the analyzed groups.

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: 73 participants were recruited to the study. 5 participants were excluded.

6. Primary Endpoint

The registry lists the primary outcome as Vaginal Delivery Within 24 Hours of Labor Induction, measured over Within 24 hours of labor induction.

The primary endpoint is the percentage of participants who achieved vaginal delivery within 24 hours of labor induction. It captures both the mode of delivery and whether delivery occurred within a specified time after induction. The time limit makes this a different outcome from vaginal delivery at any time before delivery: a participant who delivered vaginally after the stated window would not count as achieving this primary endpoint.

The registry reports the outcome as a number and percentage of participants, with a 95% confidence interval for each arm. The endpoint is useful for comparing the groups on a defined, clinically interpretable event rather than relying only on a measure of elapsed time. It does not, on its own, describe the full course of labor, the timing of all deliveries, or the reasons for cesarean delivery. Those topics are addressed separately among the registered secondary outcomes, although not all corresponding results are presented in the record.

For the primary endpoint, the posted percentages were 14.7% in the buccal group and 23.5% in the vaginal group. The registry also posts an unadjusted comparison and a Fisher Exact test. Those estimates describe the observed participants; their uncertainty and limitations matter when interpreting the apparent difference.

7. Results Posted in the Registry

• Vaginal Misoprostol: 23.5% (8/34) versus 14.7% (5/34) on control; risk difference 8.8 percentage points (95% CI -9.8 to 27.4), risk ratio 1.60 (0.58–4.40); unadjusted two-proportion z-test p = 0.355.

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.

Rates of Vaginal Delivery

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Vaginal Misoprostol: 70.6% (24/34) versus 58.8% (20/34) on control; risk difference 11.8 percentage points (95% CI -10.8 to 34.3), risk ratio 1.20 (0.84–1.71); unadjusted two-proportion z-test p = 0.310.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Vaginal Misoprostol and the control. The interval gives the range of effects that remain compatible with the data.

Cesarean Delivery Rate

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Vaginal Misoprostol: 29.4% (10/34) versus 41.2% (14/34) on control; risk difference -11.8 percentage points (95% CI -34.3 to 10.8), risk ratio 0.71 (0.37–1.38); unadjusted two-proportion z-test p = 0.310.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Vaginal Misoprostol and the control. The interval gives the range of effects that remain compatible with the data.

Arrest of Dilation

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Vaginal Misoprostol: 14.7% (5/34) versus 29.4% (10/34) on control; risk difference -14.7 percentage points (95% CI -34.1 to 4.7), risk ratio 0.50 (0.19–1.31); unadjusted two-proportion z-test p = 0.144.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Vaginal Misoprostol and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several aspects of the induction and delivery process, including timing, delivery mode, medication use and labor progress. The posted results include rates of vaginal delivery, cesarean delivery and arrest of dilation. Across these outcomes, the observed estimates do not all point in one direction: some are numerically higher in the vaginal group and some lower. Their confidence intervals are broad, and the individual comparisons do not provide a consistent, precise pattern that resolves the primary result.

These outcomes complement the primary endpoint but do not answer exactly the same question. Vaginal delivery at any time before delivery is not interchangeable with vaginal delivery within 24 hours of induction. Cesarean delivery and arrest of dilation describe different outcomes again. Considering them together can provide context about the broader delivery experience, but they should not be combined informally into a single conclusion or used to redefine the primary question after seeing the results.

Unadjusted secondary analyses generally carry less weight than a prespecified primary comparison when many outcomes or analyses are examined. In general, testing multiple outcomes increases the opportunity for a seemingly notable result to arise by chance. The registry lists 21 outcome measures and 24 analyses, and 20 secondary outcomes are posted; a multiplicity strategy is not reported in the registry record. The secondary findings are therefore best treated as exploratory context unless further prespecified analysis details are available.

The secondary outcomes may be useful for identifying questions for future research, but they do not establish that one route is superior, equivalent or different across all dimensions of induction. Their uncertainty, the number of analyses and the lack of reported multiplicity handling should be considered alongside the primary result.

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

• Time to Vaginal Delivery
• Time to Delivery
• Time to Active Labor
• Rates of Vaginal Delivery
• Cesarean Delivery Rate
• Number of Misoprostol Doses
• Arrest of Dilation
• Failed Induction of Labor

9. Statistical Interpretation

10. Statistical Methods Explained

What the arm percentages represent. The primary outcome is binary: each participant either achieved vaginal delivery within 24 hours of induction or did not. The arm percentages estimate the proportion with the event among participants represented in each group. The registry reports 14.7% for buccal misoprostol and 23.5% for vaginal misoprostol, with 34 participants in each primary endpoint group. A percentage is easy to interpret, but its precision depends on the number of participants and events supporting it.

How to read the comparison. The recalculated risk difference is 0.088, defined as the vaginal-group event proportion minus the buccal-group event proportion. A value of zero would correspond to no difference in the observed proportions. The associated 95% confidence interval ranges from -0.098 to 0.274. Because the interval includes zero, these summary data do not rule out no difference under this interval-based analysis. Its span also indicates uncertainty about the size and direction of the underlying difference. This is a general explanation of risk differences and confidence intervals, not a claim that the interval establishes equivalence.

What a confidence interval means. In general, a confidence interval is a range of estimates compatible with the data under the method used to calculate it. It is not a guarantee that the true effect lies inside the interval, and it does not assign a probability to the effect after observing the data. A wide interval signals that the estimate is not very precise. The registry reports 95% confidence intervals for the individual arm percentages as well as a recalculated interval for the risk difference; these intervals answer related but distinct questions.

What the tests address. The registry reports a Fisher Exact test for the primary comparison, with p = 0.161. Fisher’s exact test is a method for comparing categorical outcomes in groups, using the observed counts to assess how compatible the data are with a null hypothesis of no association. The recalculated unadjusted comparison reports p = 0.355. A p-value is not the probability that the null hypothesis is true, nor does it measure the size or practical importance of a difference. It describes how unusual data at least as incompatible with the null would be under the test’s assumptions.

The registry’s p-value and the recalculated p-value differ. Both are identified as unadjusted comparisons in the posted information, and the sponsor’s result is specifically labeled Fisher Exact. The reason for the difference is not reported in the registry record. Without details resolving that difference, the sponsor’s reported result should be presented as the registry analysis and the recalculation should remain clearly identified as a separate, summary-statistics-based analysis rather than a replacement.

Randomization and masking. Random allocation is intended, in general, to make treatment groups comparable on average with respect to measured and unmeasured baseline factors. It does not guarantee that the groups will be balanced in a small trial. The registry lists randomized allocation and a parallel model. Its masking field says quadruple, while the brief summary says double blinded. Further operational details are not reported in the registry record, so the extent and conduct of masking cannot be evaluated from these entries alone.

Limits of interpretation. The primary result concerns one defined endpoint and the participants included in the posted result. It should not automatically be generalized to all outcomes, populations or settings. The record does not report the analysis population definition, missing-data methods, treatment of protocol deviations, adjustment covariates or a detailed statistical analysis plan. These details can affect interpretation, particularly when enrollment, endpoint denominators and safety denominators do not match exactly.

General statistical practice also distinguishes absence of statistically persuasive evidence from evidence of no effect. A trial may yield a nonsignificant test because the effect is small, because the estimate is imprecise, or both. The confidence interval is therefore important alongside the p-value. The posted primary interval includes both no difference and effects on either side, so precision and direction should be discussed together rather than treating the test result as a binary verdict.

11. Confidence Intervals and Precision

The primary arm estimates have substantial uncertainty. The 95% confidence interval for the buccal group is 2.6% to 26.8%; for the vaginal group it is 9.1% to 38.0%. These ranges overlap, but comparing overlap between separate arm intervals is not the same as directly testing the difference between groups. The direct comparison is the recalculated risk difference of 0.088, with a 95% confidence interval from -0.098 to 0.274.

That interval includes zero, so the posted summary does not identify a clear direction for the underlying difference at the interval’s stated confidence level. It also spans values that would represent meaningfully different estimates. This is the central precision issue: the point estimate is one summary of the observed contrast, while the interval shows that a broad range of contrasts remains compatible with the data under the calculation method.

The small primary endpoint groups—34 participants per arm—contribute to the uncertainty, although sample size is not the only determinant of precision. The number of observed events and the statistical method also matter. The posted arm confidence intervals are wide, and the comparison interval crosses zero. These features warrant cautious interpretation rather than treating the point estimates as exact.

A confidence interval does not show the probability that a particular treatment effect is true, nor does it establish that all values within the range are equally plausible. It reflects uncertainty under a specified method and assumptions. The registry record does not report enough detail to evaluate every assumption behind the sponsor’s analysis, while the recalculated interval is based on an unadjusted comparison of the posted summary statistics.

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 illustrations based on the observed effect, not the trial’s original design calculations. For the primary endpoint, they are participants per arm, rather than a total across both arms or a count of events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms and a normal approximation. The assumed effect to detect is a stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the planned number of participants per arm for a hypothetical study designed to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect and assumptions were correct. The 90% power column uses a higher probability of detecting that specified effect, and therefore calls for a larger planned sample. For the primary endpoint, planning for 100% of the observed effect gives 311 participants per arm for 80% power and 416 for 90% power. Planning for 75% of the observed effect gives 529 participants per arm for 80% power and 707 for 90% power. Planning for 50% of the observed effect gives 1,133 participants per arm for 80% power and 1,516 for 90% power.

The direction of this pattern is expected: smaller target effects are harder to distinguish from random variation, so detecting them requires more participants. The estimates depend on the planning assumptions and the observed effect used as their starting point; they are not forecasts of the results of a future trial. These figures are not observed power. They are planning illustrations and should not be read as evidence that the completed trial had a particular probability of detecting its actual effect.

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 = 0.147; treatment proportion p₁ = 0.235; average p̄ = 0.191.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5561 = 1.0900.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5526 = 0.4651.
4. n = (1.0900 + 0.4651)² / (0.0882)² = 310.6, rounded up to 311 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 <- 0.147058823529412                          # control proportion
p1 <- 0.235294117647059                          # 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(1519765)
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 = 311 (80% power), 416 (90% power)
 75% of observed effect: n per arm = 529 (80% power), 707 (90% power)
 50% of observed effect: n per arm = 1,133 (80% power), 1,516 (90% power)
power.prop.test: 310.6 
Simulated power at n = 311 per arm: 0.805 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry’s own primary analysis is a Fisher Exact test and reports p = 0.161. The separate recalculation from the posted counts is an unadjusted comparison and reports p = 0.355, alongside a risk difference of 0.088 with a 95% confidence interval from -0.098 to 0.274. The record does not indicate a discrepancy flag, but the two p-values are not the same.

The sponsor’s result and the recalculation should therefore be kept distinct. The reported test is the registry’s own analysis; the recalculation is a simple unadjusted analysis of the summary counts and is useful as a transparent cross-check, not as a substitute for an analysis using the full participant-level data. The reason the p-values differ is not reported in the registry record. It would be speculative to attribute the difference to a particular test implementation, dataset, adjustment or analysis population.

Both results should be interpreted with the estimated effect and its uncertainty, rather than as a decision based only on whether a p-value crosses a conventional threshold. The registry-reported p-value does not indicate the probability that the treatment routes are equivalent, and the recalculated p-value does not resolve the uncertainty in the effect estimate. The posted confidence interval for the risk difference includes zero and a range of values on either side.

15. Multiplicity, Missing Data and Analysis Populations

The record lists 21 outcome measures, 24 analyses and 20 posted secondary outcomes. Evaluating many outcomes can increase the chance that at least one result appears unusual simply through random variation. This is a general statistical concern known as multiplicity. Researchers may address it through prespecified hierarchies, adjustment procedures or by designating secondary analyses as exploratory. The registry record does not report a multiplicity plan or indicate whether any adjustment was used.

The record identifies a primary endpoint, which helps distinguish the central question from additional outcomes. However, the detailed protocol and statistical analysis plan are not reported in the registry record. It is therefore not possible to verify from the posted information when all analyses were specified, whether outcome definitions changed, or how the 24 analyses relate to the outcome measures. No conclusion about selective reporting should be drawn from that absence alone.

Missing-data handling and analysis populations are also not reported in the registry record. The primary outcome results list 34 participants per arm, while total enrollment is 73. Safety results list 37 participants at risk in the buccal group and 36 in the vaginal group. These denominators refer to different posted results; the record does not explain their relationship or report whether any participants lacked outcome data, were excluded from an analysis or were handled by imputation. Consequently, the completeness of the primary outcome analysis and the use of an intention-to-treat or other analysis population cannot be assessed.

The registry also does not report planned interim analyses, covariate adjustment, protocol deviations or the handling of participants who did not follow the assigned route. These are important aspects of a trial’s analysis plan, but their absence from the record is not proof that no such procedures existed. They are simply not reported in the registry record, limiting independent assessment of analysis choices and the robustness of the findings.

16. 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.

The posted safety figures report zero serious adverse events among 37 participants at risk in the buccal misoprostol group and zero among 36 participants at risk in the vaginal misoprostol group. The record also reports zero other adverse events in each of those at-risk groups. These counts describe the recorded safety results for the stated denominators; they do not establish that the treatments have no adverse effects.

Zero observed events in a limited group can coexist with uncertainty about the event rate in a broader population. The safety denominators also differ from the primary endpoint denominators, and the registry does not explain why. Death counts are not reported in the registry record; a missing death count should not be interpreted as zero deaths. The registry lists no serious adverse event terms. Further detail about event definitions, collection procedures, severity, relatedness or follow-up is not reported in the registry record, so the safety information is limited.

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

The posted results describe a randomized comparison of buccal and vaginal misoprostol for third-trimester labor induction. For the primary endpoint—vaginal delivery within 24 hours—the observed percentages were 14.7% and 23.5%, respectively. The recalculated risk difference has a 95% confidence interval that includes zero and spans values on both sides. The registry’s Fisher Exact test reports p = 0.161; a separate unadjusted recalculation reports p = 0.355. Taken together, these results leave substantial uncertainty about the size and direction of the difference.

They do not demonstrate that the routes are equivalent. Equivalence requires a defined margin and an analysis designed to assess whether the plausible difference falls within that margin; such a margin or an equivalence analysis is not reported in the registry record. Nor do the results establish that one route is superior. The observed percentages are descriptive estimates from the analyzed groups, not guarantees of outcomes for future participants.

The findings also do not answer every question about induction or delivery. The primary endpoint concerns a specific time window and mode of delivery. Other outcomes address different aspects, and their estimates are also uncertain. The record’s safety counts report no serious adverse events in the listed at-risk groups, but that limited observation does not establish absence of risk; death counts and further safety details are not reported in the registry record.

Because the trial is marked terminated, and its termination reason is not reported, the circumstances of completion cannot be evaluated. The enrolled total and the outcome denominators are not the same, and their relationship is not explained. The posted results should be read as a small, imprecise trial record that contributes evidence about a specific comparison, while leaving important questions about completeness, analysis choices and generalizability unresolved.

18. Why This Trial Matters Statistically

This trial is statistically informative because its question is framed around a direct randomized comparison of two routes for administering misoprostol, with a clearly defined primary outcome. The endpoint combines mode of delivery with a stated time window, making the contrast more specific than a broad measure of whether vaginal delivery occurred at any point. The parallel-group randomized design is relevant to estimating a comparative effect, although the record does not provide the details needed to assess all aspects of implementation.

The results also illustrate why an observed difference and its uncertainty must be read together. The vaginal group had a higher posted percentage for the primary endpoint, but the recalculated confidence interval includes no difference and extends in either direction. A point estimate alone can appear more decisive than the data warrant, while a p-value alone omits the scale and precision of the estimate. Presenting both supports a more measured interpretation.

The registry’s own Fisher Exact result and the recalculated unadjusted result differ, and the reason is not reported. That makes transparent separation of sponsor-reported and recalculated analyses important. The trial also has many listed outcomes and analyses, while the multiplicity plan is not reported. These features offer useful examples of questions researchers should ask when reading registry results: which outcome is primary, how precise is the estimate, and how were additional analyses handled?

Finally, the record highlights the distinction between enrollment and the denominator for a particular result. Different posted denominators need explanation before completeness can be judged. In that sense, the study is useful not because it settles the comparison, but because it demonstrates how design, analysis reporting, precision and outcome selection shape what a reader can reasonably conclude.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary endpoint results are based on 34 participants per arm, and the confidence interval for the recalculated risk difference is broad. This limits precision. The registry lists 73 participants enrolled, but does not explain the relationship between enrollment and the primary outcome denominators. It also does not report whether participants were excluded, had missing outcome data or were analyzed according to their assigned group.

The study is marked terminated, but the reason for termination is not reported in the registry record. Without that information, it is not possible to assess whether termination was planned, related to recruitment, or associated with other circumstances. The original sample-size justification and any planned interim analyses are also not reported, so the intended precision and stopping procedures cannot be evaluated.

The masking descriptions differ across registry entries: the masking field says quadruple, while the brief summary says double blinded. Further details about who was masked, how masking was implemented and whether it remained intact are not reported in the registry record. The registry also does not provide baseline participant characteristics, eligibility criteria or enough information to judge how broadly the results apply.

There are 21 outcome measures and 24 analyses, but the multiplicity plan and detailed statistical analysis plan are not reported. The reason the registry-reported and recalculated primary p-values differ is likewise not reported. Safety denominators differ from primary endpoint denominators, and death counts are not reported. These limitations do not invalidate the posted observations, but they constrain independent evaluation of completeness, analysis decisions, precision and generalizability.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Buccal Versus Vaginal Misoprostol for Third Trimester Induction of Labor — NCT01519765.
• Registry record last updated 2016-09-27; status last verified 2016-08.
• Results first posted 2016-09-27.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record identifies NCT01519765 as a Phase 4 randomized, parallel-group trial comparing buccal with vaginal misoprostol for third-trimester induction of labor. The University of California, Los Angeles is listed as sponsor. The record lists 73 participants enrolled, a start of 2011-07, primary completion of 2014-12 and status of terminated.

The primary endpoint was vaginal delivery within 24 hours of induction. The posted percentages were 14.7% for buccal misoprostol and 23.5% for vaginal misoprostol, with 34 participants per arm. The registry reports a Fisher Exact p-value of 0.161; the separate unadjusted recalculation reports p = 0.355. The reason for their difference is not reported in the registry record.

Secondary outcomes cover delivery mode, timing and labor progress. Safety results report zero serious adverse events in the listed at-risk groups, while death counts are not reported. The reason for termination, the original sample-size justification, analysis-population definitions, missing-data procedures and multiplicity plan are not reported in the registry record. The estimates should therefore be read with attention to their uncertainty and the limits of the available analysis details.