Comparison of Misoprostol Ripening Efficacy With Dilapan: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparison of Misoprostol Ripening Efficacy With Dilapan (NCT03670836), a randomized phase 4 study. The primary outcome is Number of Women Achieving Vaginal Delivery Within 36 Hours After Initiation of Cervical Ripening in ITT Population.

2. Clinical Question

3. Trial Design

This was a randomized, unmasked, parallel-group Phase 4 trial sponsored by Columbia University. The registry lists enrollment as 307 and reports the study as completed. Its start date is 2018-11-15, and its primary completion date is 2021-07-21. The registry record does not provide further detail about the randomization procedure, allocation concealment, or whether any procedures other than treatment delivery were standardized between groups.

The comparison was between Dilapan, listed as a device, and Misoprostol, listed as a drug. The registry describes the Dilapan group as receiving 3-5 rods inserted into the cervix. Its Misoprostol description refers to baseline assessment, cardiotocogram monitoring for 20 minutes, continuous fetal monitoring, and dosing up to a maximum of 6 doses. The available descriptions are truncated, so a complete treatment schedule, criteria for repeat treatment, and further care details are not reported in the registry record.

The primary outcome was a participant count for vaginal delivery within 36 hours after cervical ripening. The stated primary population is intent-to-treat: randomized participants are analyzed in the group to which they were assigned, regardless of treatment actually received. The posted arm counts are 151 in the Dilapan group and 152 in the Misoprostol group for this outcome. Whether there were exclusions, missing endpoint data, or deviations from the stated population is not reported in the registry record.

The record lists 13 outcome measures and 11 posted secondary outcomes. It does not report a formal statistical analysis plan, the original sample-size justification, or the trial's prespecified decision criteria for comparing treatments. The registry lists no reported analyses. These gaps limit how far the posted summary statistics can be used to reconstruct the trial's planned inferential approach.

4. Participant Flow and Accounting

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

Before assignment: A total of 306 participants were needed , 153 in each group, to evaluate the primary outcome with 85% power to confirm the noninferiority with one sided confidence level of 97.5%

Intent-to-treat Population (ITT)

Reasons for not completing this period:

Per Protocol Population (PP)

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: Baseline Characteristics were analyzed in the intent to treat population

6. Primary Endpoint

The registry lists the primary outcome as Number of Women Achieving Vaginal Delivery Within 36 Hours After Initiation of Cervical Ripening in ITT Population, measured over Up to 36 hours after intervention.

The primary endpoint counts participants who achieved vaginal delivery within 36 hours after initiation of cervical ripening. The registry describes the endpoint as a measure of efficacy for the two cervical-ripening approaches and specifies the intent-to-treat population. It therefore captures a clinically relevant event within a stated time window while preserving randomized group assignment in the analysis definition.

A time-bounded delivery outcome can reflect more than cervical change alone: it records whether vaginal delivery occurred within the specified window, not just whether the cervix ripened. It should not be interpreted as a direct measure of the speed of cervical change, the overall vaginal-delivery rate, or the safety of either approach. The registry lists change in Bishop Score and delivery outcomes at other time windows among the secondary outcomes, indicating that those are distinct measures rather than interchangeable versions of the primary endpoint.

The posted result is a count in each assigned group, with 93 participants in the Dilapan group and 90 in the Misoprostol group. The comparison is presented as a risk difference of -0.024 for Misoprostol relative to Dilapan, with a confidence interval from -0.134 to 0.086. The interval describes uncertainty about the group contrast; it does not by itself establish equivalence. The registry does not report a prespecified noninferiority or equivalence margin, so the result cannot be read as a formal test that the treatments are sufficiently similar.

7. Results Posted in the Registry

• Misoprostol Group: 59.2% (90/152) versus 61.6% (93/151) on control; risk difference -2.4 percentage points (95% CI -13.4 to 8.6), risk ratio 0.96 (0.80–1.15); unadjusted two-proportion z-test p = 0.672.

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.

Percentage of Women Delivering Vaginally in 24 Hours After the Initiation of Intervention

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Misoprostol Group: 38.2% (58/152) versus 41.1% (62/151) on control; risk difference -2.9 percentage points (95% CI -13.9 to 8.1), risk ratio 0.93 (0.70–1.23); unadjusted two-proportion z-test p = 0.606.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Misoprostol Group and the control. The interval gives the range of effects that remain compatible with the data.

Overall Vaginal Delivery Rate

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Misoprostol Group: 68.4% (104/152) versus 68.9% (104/151) on control; risk difference -0.5 percentage points (95% CI -10.9 to 10.0), risk ratio 0.99 (0.85–1.16); unadjusted two-proportion z-test p = 0.932.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Misoprostol Group and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Cesarean Deliveries

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Misoprostol Group: 27.6% (42/152) versus 27.2% (41/151) on control; risk difference 0.5 percentage points (95% CI -9.6 to 10.5), risk ratio 1.02 (0.71–1.47); unadjusted two-proportion z-test p = 0.925.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Misoprostol Group and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover delivery timing and mode, cervical change, hospital stay, and maternal and newborn outcomes. The available results include vaginal delivery within 24 hours, overall vaginal delivery, and cesarean delivery. The registry lists additional outcomes, but does not post comparative results for all of them. These outcomes broaden the clinical picture beyond the primary time-bounded endpoint, yet each addresses a different question and should not be treated as a substitute for the primary endpoint.

Across the secondary comparisons with posted estimates, the point estimates are close to no difference, and their confidence intervals include the no-difference value for the reported risk differences. This broad pattern is directionally consistent with the primary result's uncertainty rather than offering a sharply contrasting signal. It does not prove that the treatments are the same across outcomes. The secondary endpoints have their own sampling uncertainty, definitions, and observation windows, and similarity in point estimates does not establish a common effect.

Secondary results generally carry less weight than a prespecified primary result because they may be exploratory, may involve many comparisons, and may not have been the basis for the trial's main design or decision. Looking across many outcomes raises the chance that some estimates will appear notable by chance. The registry does not report a multiplicity strategy, a hierarchy for secondary outcomes, or which of these outcomes were designated confirmatory. The posted secondary p-values are unadjusted, so they should be interpreted cautiously and not as independent confirmation of a treatment difference.

The registry identifies 11 posted secondary outcomes, while the broader list of measures includes outcomes without posted numerical results. The absence of a result for a listed measure should not be read as no events or no difference; the result is not reported in the registry record. Similarly, summary comparisons do not reveal whether the analyses used adjusted models, how missing outcomes were handled, or whether outcome definitions changed. Overall, the secondary pattern does not materially resolve the uncertainty in the primary comparison, and it does not support a definitive conclusion about effects across the full set of outcomes.

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

• Change in Bishop Score
• Percentage of Women Delivering Vaginally in 24 Hours After the Initiation of Intervention
• Overall Vaginal Delivery Rate
• Number of Participants With Cesarean Deliveries
• Total Length of Hospital Stay
• Percentage of Women Who Developed Chorioamnionitis
• Percentage of Women Who Developed Postpartum Hemorrhage
• Percentage of Newborns With Apgar Score <7 at 5 Min

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either achieved vaginal delivery within 36 hours after cervical ripening or did not. For a binary outcome, a group risk is the proportion of participants with the event. A risk difference expresses the absolute contrast between those proportions. The registry reports the contrast as Misoprostol relative to Dilapan, so its negative point estimate indicates a lower observed event proportion in the Misoprostol group in this summary. The estimate is -0.024. This direction describes the arithmetic orientation of the comparison; it does not establish a causal effect beyond the randomized-trial context or show that the difference is clinically important.

The confidence interval from -0.134 to 0.086 gives a range of values compatible with the observed data under the interval method and its assumptions. A confidence interval is not a range containing a fixed percentage of individual participant outcomes, and it is not a probability statement about the true value after observing the data. It is useful to read the point estimate together with the interval: the estimate is near no difference, but the interval also allows effects in both directions. The registry does not report the exact method used to form this interval.

The registry also gives a relative risk and an odds ratio. Relative risk compares group event proportions as a ratio; an odds ratio compares event odds. These measures answer related but distinct questions and can differ in magnitude, especially when outcomes are common. Their null values are 1, whereas the null value for a risk difference is 0. The primary relative risk is 0.961 with an interval of 0.801 to 1.154, and the odds ratio is 0.905 with an interval of 0.571 to 1.435. Because these intervals include their respective null values, they do not resolve the direction of the underlying contrast. The three effect measures are alternate presentations of the same endpoint data, not separate tests of efficacy.

The unadjusted p-value for the primary comparison is 0.672. A p-value measures how unusual data at least as discrepant as those observed would be if a specified null hypothesis and the test assumptions held. It does not measure the probability that there is no difference, and it does not quantify how likely the observed estimate is to be replicated. The word unadjusted indicates that the reported value has not been corrected for multiple comparisons. The registry does not report whether this was the prespecified test or which test procedure generated it.

Randomization assigns participants to treatment groups by chance and, when properly implemented, supports comparison by assigned group. The intent-to-treat definition in the registry keeps randomized participants in their original groups regardless of treatment received. This approach can preserve the benefits of randomization, but its practical interpretation depends on the handling of missing outcomes and protocol deviations. Those details are not reported in the registry record. It is therefore not possible to verify from the posted summary how completely the stated population was represented in the endpoint analysis.

General statistical context: estimates from binary outcomes can be imprecise when there are relatively few participants or when the observed event proportions are similar. The width of an interval reflects sampling uncertainty as well as the method used to calculate it. A broad interval may include both a potentially favorable and an unfavorable contrast, even when the point estimate is close to no difference. Failure to find a small p-value is not proof that groups are equal; a claim of equivalence or noninferiority requires a defined margin and a suitable analysis. Neither a margin nor a reported equivalence analysis is available in the registry record.

The trial is described as randomized and parallel, but the detailed analysis plan is not reported. In particular, the record does not describe covariate adjustment, a stratification scheme, interim analyses, handling of multiplicity, or missing-data methods. The registry lists no reported analyses. As a result, the interpretation should remain anchored to the posted counts and unadjusted comparisons, without attributing unreported procedures to the investigators.

11. Confidence Intervals and Precision

The primary confidence interval for the risk difference runs from -0.134 to 0.086, around a point estimate of -0.024 for Misoprostol relative to Dilapan. The interval crosses zero, the no-difference value for a risk difference. Thus the posted data are compatible with a lower event proportion in the Misoprostol group, little or no difference, or a higher event proportion. The point estimate alone should not be treated as the settled effect.

The breadth of the interval matters: it leaves appreciable uncertainty about the size and direction of the group contrast. The relative-risk interval, 0.801 to 1.154, includes 1, as does the odds-ratio interval, 0.571 to 1.435. These different measures all retain uncertainty around their null values. They should not be combined as though they were independent evidence, because they summarize the same outcome in the same groups.

A confidence interval describes statistical precision, not clinical acceptability. To decide whether a range of differences is small enough to regard treatments as practically equivalent, a clinically justified equivalence or noninferiority margin would be needed. Such a margin is not reported in the registry record. Nor does the record state a target precision for the primary estimate. The observed interval therefore cannot be classified as adequate or inadequate against an unreported threshold.

Confidence intervals also do not account automatically for every source of uncertainty. The registry does not report the interval method, missing-data procedures, or adjustments for multiple outcomes. The posted interval is informative about sampling uncertainty under the analysis used, but those absent details limit a full assessment of precision and robustness.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations are based on the observed effect, not on the trial's original design assumptions. For the participant-count outcomes, the displayed figures are participants per arm, not total participants. 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 the stated fraction of the observed effect. The registry's original sample-size justification and design assumptions are not reported in the registry record.

The 80% power column describes an illustrative design that would have an 80% chance of detecting the specified effect under the planning assumptions, if that effect and those assumptions were correct. The 90% power column uses a higher chance of detecting that effect and therefore generally requires more participants per arm. These are design-planning quantities, not results about the trial's ability to detect effects after it has been completed.

Rows for planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect show the consequences of choosing different target effects. Smaller effects require more participants because they are harder to distinguish from random variation. For the primary endpoint, the displayed requirement for 100% of the observed effect is 6,634 participants per arm for 80% power and 8,880 participants per arm for 90% power. For 75% of the observed effect, the corresponding figures are 11,764 and 15,747; for 50%, they are 26,397 and 35,338.

These illustrations are not observed power. They are conditional planning calculations based on the observed effect, which itself is uncertain. They should not be used to infer that the completed trial did or did not have adequate power under its original plan. The record does not report that plan, and the illustrative calculations do not substitute for it.

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 = 0.616; treatment proportion p₁ = 0.592; average p̄ = 0.604.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6916 = 1.3556.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6914 = 0.5819.
4. n = (1.3556 + 0.5819)² / (-0.0238)² = 6,633.6, rounded up to 6,634 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 <- 0.615894039735099                          # control proportion
p1 <- 0.592105263157895                          # 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(3670836)
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 = 6,634 (80% power), 8,880 (90% power)
 75% of observed effect: n per arm = 11,764 (80% power), 15,747 (90% power)
 50% of observed effect: n per arm = 26,397 (80% power), 35,338 (90% power)
power.prop.test: 6633.6 
Simulated power at n = 6,634 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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates more than one outcome or performs more than one comparison. Even when each individual test is conducted appropriately, examining many tests without an adjustment or an outcome hierarchy can increase the chance of at least one apparently unusual result. The registry lists 13 outcome measures and reports 11 secondary outcomes, but it does not describe a multiplicity plan, such as a prespecified testing sequence or adjustment method. The posted comparisons are unadjusted. Their p-values should therefore be treated as descriptive evidence rather than as a family-wise confirmatory set.

The primary endpoint is identified, which helps distinguish the main efficacy question from secondary questions. However, the record does not report the original statistical analysis plan, confirmatory status for secondary outcomes, or rules for interpreting multiple endpoints. It is not possible to determine from the record whether additional analyses were planned, whether any outcomes were selected after examining data, or whether adjustment was used outside the posted summary. Those matters are not reported in the registry record and should not be inferred.

Missing-data handling is also not reported. The primary population is defined as intent-to-treat and includes all randomized participants analyzed in their assigned groups, regardless of the treatment actually received. That definition does not by itself specify how participants with an unknown delivery outcome were handled, whether follow-up was complete, or whether any imputation or sensitivity analysis was performed. The arm counts are reported, but the registry does not provide an account of exclusions or missing primary outcomes.

The registry lists no reported analyses. It therefore does not provide details on model choice, covariate adjustment, interim monitoring, or sensitivity analyses. Without those details, the safest interpretation is to describe the posted group counts and unadjusted comparisons as they stand. No unstated analysis procedure should be assumed, and the absence of a reported procedure is not evidence that it was or was not used.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: postpartum hemorrhage (2.0%).

The adverse-event summary reports serious events affecting 1 participant in the Dilapan group and 3 in the Misoprostol group. The registry reports no deaths in either group. It also lists other adverse events affecting 39 participants in the Dilapan group and 81 in the Misoprostol group. These are registry counts, not adjusted estimates of comparative risk, and the record does not provide enough detail to determine the clinical severity or overlap of events within participants.

Postpartum hemorrhage is listed among the top serious adverse-event terms at 2.0%. The record does not provide a full term-by-term accounting or enough context to interpret that figure as a treatment-specific rate. Serious and other adverse-event categories also depend on how events were defined, collected, and attributed; those procedures are not reported in the registry record. The numerical difference in counts alone cannot establish a safety advantage or disadvantage.

Safety comparisons require attention to event definitions, follow-up duration, exposure, and the completeness of reporting. The registry summary does not describe these details or provide uncertainty intervals for the adverse-event comparisons. The figures are therefore best read as descriptive safety information from the posted record, not as proof that either approach is safer.

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

The posted primary result describes vaginal delivery within 36 hours after cervical ripening among participants assigned to Dilapan or Misoprostol. The counts are 93 of 151 and 90 of 152, respectively, and the reported risk difference for Misoprostol relative to Dilapan is -0.024. The confidence interval includes no difference and extends in both directions. The registry thus reports no precise separation between groups on this endpoint, but the uncertainty also means the result does not establish that the treatments have the same effect.

A non-significant or unadjusted comparison should not be translated into proof of equivalence. Equivalence and noninferiority questions require a prespecified margin that defines how large a difference could be and still be considered acceptable, together with an appropriate analysis. The registry record does not report such a margin or a formal equivalence or noninferiority analysis. The point estimate's proximity to zero cannot replace those elements.

The endpoint captures vaginal delivery within a particular time window; it does not summarize every aspect of labor induction, cervical response, overall delivery experience, or maternal and newborn safety. Other outcomes are listed, but many do not have posted results, and the reported secondary comparisons are also uncertain. Safety counts are descriptive and lack sufficient information for a definitive comparative safety conclusion.

The results apply to the trial's stated population and setting, which the registry describes as women undergoing induction of labor at or beyond 37 weeks gestation. The registry provides limited details on participant characteristics and treatment procedures, and does not report the full analysis plan. Generalization beyond the enrolled trial population therefore requires caution. The results do not warrant an individual treatment recommendation; they are a statistical account of the registry's posted comparison, with substantial limits on what can be concluded.

17. Why This Trial Matters Statistically

This trial illustrates an important distinction between a small point estimate and a precise estimate. The primary risk-difference estimate is near zero, but its confidence interval includes values in both directions. A reader who considers only the point estimate might conclude that the groups were nearly identical; a reader who considers the interval sees that the data leave room for a wider range of differences. Reporting both estimate and uncertainty is essential to a sound interpretation.

It also shows why a conventional failure to detect a difference cannot answer an equivalence question. The registry frames the comparison around whether Dilapan works as well as Misoprostol, but the posted record does not report an equivalence margin or a noninferiority analysis. Without a threshold defining acceptable difference, the phrase works as well cannot be confirmed statistically by a point estimate near zero or by a p-value that does not indicate a clear difference.

The trial's planning illustrations provide another useful lesson. Calculations based on an observed effect can imply substantial sample-size requirements, especially when the target effect is smaller. Such illustrations are sensitive to the observed estimate and are not a replacement for the original prospective design calculation. The original justification is not reported, so the illustrative requirements must not be used to judge the trial's planned power.

Finally, a randomized design does not remove the need for transparent analysis reporting. Multiplicity, missing-data procedures, outcome hierarchy, and exact methods affect how results should be interpreted. The registry gives a useful endpoint and group-level summary, but the absence of a detailed analysis plan limits assessment of robustness. Together, these features make the record a practical example of why uncertainty, design intent, and completeness of reporting matter alongside the treatment comparison itself.

18. Limitations

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

The primary estimate is imprecise: its confidence interval spans zero and includes effects in either direction. The registry does not report a clinically justified margin, so the result cannot establish equivalence or noninferiority. The unadjusted p-value is a limited summary and does not indicate the probability that there is no treatment difference.

The registry record does not report the original sample-size justification or the complete statistical analysis plan. It also does not describe multiplicity adjustment, interim analyses, covariate adjustment, or the methods used to calculate the reported intervals. Missing-data handling, completeness of follow-up, and any deviations from the stated intent-to-treat population are not reported. These gaps prevent a detailed assessment of analytic robustness.

Several listed outcomes lack posted results, and the registry provides no full set of outcome definitions or a clear hierarchy for secondary analyses. The secondary comparisons are unadjusted and should be considered less conclusive than a prespecified primary analysis. The adverse-event summary is also limited: it gives counts and a listed serious-event term but does not describe collection procedures, event attribution, follow-up, or uncertainty around group differences.

The treatment descriptions available in the registry are incomplete, which limits evaluation of the exact intervention schedules and co-interventions. Participant characteristics beyond the broad population description are not reported in the registry record for this analysis. Consequently, the results cannot be assumed to apply beyond the population and care context represented in the trial. These limitations affect interpretation of the record; they do not show that an unreported procedure was absent or improperly conducted.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Comparison of Misoprostol Ripening Efficacy With Dilapan — NCT03670836.
• Registry record last updated 2024-07-19; status last verified 2024-07.
• Results first posted 2024-07-19.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry describes a completed, randomized, unmasked, parallel-group Phase 4 comparison of Dilapan and Misoprostol for cervical ripening before labor induction. Columbia University is listed as sponsor. The primary outcome is vaginal delivery within 36 hours after initiation of cervical ripening in the intent-to-treat population.

The posted counts are 93 of 151 for Dilapan and 90 of 152 for Misoprostol. The risk difference for Misoprostol relative to Dilapan is -0.024, with a confidence interval from -0.134 to 0.086 and an unadjusted p-value of 0.672. The interval includes no difference and effects in either direction, so the result does not establish superiority or equivalence.

Secondary results and adverse-event counts provide additional descriptive information, but the registry does not report a full statistical analysis plan, multiplicity strategy, missing-data procedures, or the original sample-size justification. The posted findings should be interpreted with those limitations in mind.